Author Response

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

Reviewer 1:

Public review:

In this study, Porter et al report on outcomes from a small, open-label, pilot randomized clinical trial comparing dornase-alfa to the best available care in patients hospitalized with COVID-19 pneumonia. As the number of randomized participants is small, investigators describe also a contemporary cohort of controls and the study concludes about a decrease of inflammation (reflected by CRP levels) aJer 7 days of treatment but no other statistically significant clinical benefit.

Suggestions to the authors:

• The RCT does not follow CONSORT statement and reporting guidelines

We thank you for this suggestion and have now amended the order and content of the manuscript to follow the CONSORT statement as closely as possible.

• The authors have chosen a primary outcome that cannot be at least considered as clinically relevant or interesting. AJer 3 years of the pandemic with so much research, why investigate if a drug reduces CRP levels as we already have marketed drugs that provide beneficial clinical outcomes such as dexamethasone, anakinra, tocilizumab and baricitinib.

We thank the reviewer for bringing up this central topic. The answer to this question has both a historical and practical component. This trial was initiated in June of 2020 and was completed in June of 2021. At that time there were no known treatments for the severe immune pathology of COVID19 pneumonia. In June 2020, dexamethasone data came out and we incorporated dexamethasone into the study design. It took much longer for all other anti-inflammatories to be tested. Hence, our decision to trial an approved endonuclease was based purely on basic science work on the pathogenic role of cell-free chromatin and NETs in murine sepsis and flu models and the ability of DNase I to clear them and reduce pathology in these animal models. In addition, evidence for the presence of cell-free chromatin components in COVID-19 patient plasma had already been communicated in a pre-print. Finally, several studies had reported the anti-inflammatory effects of dornase treatment in CF patients. Hence there was a strong case for a cheap, safe, pulmonary noninvasive treatment that could be self-administered outside the clinical se]ng.

The Identification of novel/repurposed treatments effective for COVID-19 were hampered by patient recruitment to competing studies during a pandemic. This resulted in small studies with inconclusive or contrary findings. In general, effective treatments were only picked up in very large RCTs. For example, demonstrating dexamethasone as effective in COVID-19 required recruitment of 6,425 patients into the RECOVERY study. Multiple trials with anti-IL-6 gave conflicting evidence until RECOVERY recruited 4116 adults with COVID-19 (n=2022, tocilizumab and 2094, control) similar for Baracitinib (4,148 randomised to treatment and 4,008 to standard care). Anakinra is approved for patients with elevated suPAR, based on data from one randomized clinical trial of 594 patients, of whom 405 had active treatment (PMID: 34625750). However, a systematic review analysing over 1,627 patients (anakinra 888, control 739) with COVID-19 showed no benefit (PMID: 36841793). Regarding the choice of the primary endpoint, there is a wealth of clinical evidence to support the relevance of CRP as a prognostic marker for COVID-19 pneumonia patients and it is a standard diagnostic and prognostic clinical parameter in infectious disease wards. This choice in March 2020 was supported by evidence of the prognostic value of IL-6; CRP is a surrogate of IL-6. We also provide our own data from a large study of severe COVID-19 pneumonia in figure 1, showing how well CRP correlates with survival.

In summary, our data suggest that Dornase yields an anti-inflammatory effect that is comparable or potentially superior to cytokine-blocking monotherapies at a fraction of the cost and potentially without the additional adverse effects such as the increase for co-infections.

We now provide additional justification on these points in the introduction on pg.4 as follows:

“The trial was ini.ated in June 2020 and was completed in September of 2021. At the start of the trial only dexamethasone had been proven to benefit hospitalized COVID-19 pneumonia pa.ents and was thus included in both arms of the trial. To increase the chance of reaching significance under challenging constraints in pa.ent access, we opted to increase our sample size by using a combina.on of randomized individuals and available CRP data from matched contemporary controls (CC) hospitalized at UCL but not recruited to a trial. These approaches demonstrated that when combined with dexamethasone, nebulized DNase treatment was an effec.ve an.-inflammatory treatment in randomized individuals with or without the implementa.on of CC data.”

We also added the following explanation in the discussion on pg. 16:

“Our study design offered a solution to the early screening of compounds for inclusion in larger platform trials. The study took advantage of frequent repeated measures of quantifiable CRP in each patient, to allow a smaller sample size to determine efficacy/futility than if powered on clinical outcomes. We applied a CRP-based approach that was similar to the CATALYST and ATTRACT studies. CATALYST showed in much smaller groups (usual care, 54, namilumab, 57 and infliximab, 35) that namilumab that is an antibody that blocks the cytokine GM-CSF reduced CRP even in participants treated with dexamethasone whereas infliximab that targets TNF-α had no significant effect on CRP. This led to a suggestion that namilumab should be considered as an agent to be prioritised for further investigation in the RECOVERY trial. A direct comparison of our results with CATALYST is difficult due to the different nature of the modelling employed in the two studies. However, in general Dornase alfa exhibited comparable significance in the reduction in CRP compared to standard of care as described for namilumab at a fraction of the cost. Furthermore, endonuclease therapies may prove superior to cytokine blocking monotherapies, as they are unlikely to increase the risk for microbial co-infections that have been reported for antibody therapies that neutralize cytokines that are critical for immune defence such as IL-1β, IL-6 or GM-CSF. “

• Please provide in Methods the timeframe for the investigation of the primary endpoint

This information is provided in the analysis on pg. 8:

“The primary outcome was the least square (LS) mean CRP up to 7 days or at hospital discharge whichever was sooner.”

• Why day 35 was chosen for the read-out of the endpointt?

We now state on pg. 8 that “Day 35 was chosen as being likely to include most early mortality due to COVID-19 being 4 weeks after completion of a week of treatment. ( i.e. d7 of treatment +28 (4 x 7 days))”

• The authors performed an RCT but in parallel chose to compare also controls. They should explain their rationale as this is not usual. I am not very enthusiastic to see mixed results like Figures 2c and 2d.

We initially aimed at a fully randomized trial. However, the swiJ implementation of trial prioritization strategies towards large and pre-established trial plamorms in the UK made the recruitment COVID19 patients to small studies extremely challenging. Thus, we struggled to gain access to patients. Our power calculations suggested that a mixed trial with randomized and contemporary controls was the best way forward under these restrictions in patient access that could provide sufficient power.

That being said, we also provide the primary endpoint (CRP) results in Fig. 3B as well as the results for the length of hospitalization (Fig. S3D) for the randomized subjects only.

• Analysis is performed in mITT; this is a major limitation. The authors should provide at least ITT results. And they should describe in the main manuscript why they chose mITT analysis.

We apologize if this point was confusing. We performed the analysis on the ITT as defined in our SAP: “The primary analysis population will be all evaluable patients randomised to BAC + dornase alfa or BAC only who have at least one post-baseline CRP measurement, as well as matched historical comparators.”

We understand that the reason this might be mistaken as an mITT is because the N in the ITT (39) doesn’t match the number randomised and because we had stated on pg. 8 that “ Efficacy assessments of primary and secondary outcomes in the modified inten.on-to-treat popula.on were performed.”

However, we did randomise 41 participants, but:

One participant in the DA arm never received treatment. The individual withdrew consent and was replaced. We also have no CRP data for this participant in the database, so they were unevaluable, and we couldn’t include them in the baseline table even if we wanted to. In addition, 1 participant in BAC only had a baseline CRP measurement available. Hence not evaluable as we only have a baseline CRP measurement for this participant.

We have corrected the confusing statement on pg. 8 and added an additional explanation.

“Efficacy assessments of primary and secondary outcomes in the inten.on-to-treat (ITT) popula.on were performed on all randomised par.cipants who had received at least one dose of dornase alfa if randomized to treatment. For full details see Sta.s.cal Analysis Plan. The ITT was adjusted to mi.gate the following protocol viola.ons where one par.cipant in the BAC arm and one in the DA arm withdrew before they received treatment and provided only a baseline CRP measurement available. The par.cipant in the DA arm was replaced with an addi.onal recruited pa.ent. Exploratory endpoints were only available in randomised par.cipants and not in the CC. In this case, a post hoc within group analysis was conducted to compare baseline and post-baseline measurements.”

• It is also not usual to exclude patients from analysis because investigators just do not have serial measurements. This is lost to follow up and investigators should have pre-decided what to do with lost-to-follow-up.

Our protocol pre-specified that the primary analysis population should have at least one postbaseline CRP measurement (pg. 13 of protocol). The patient that was excluded was one that initially joined the trial but withdrew consent after the first treatment but before the first post-treatment blood sample could be drawn. Hence, the pre-treatment CRP of this patient alone provided no useful information.

• In Table 1 I would like to see all randomized patients (n=39), which is missing. There are also baseline characteristics that are missing, like which other treatments as BAT received by those patients except for dexamethasone.

Table 1 includes all 39 patients plus 60 CCs.<br /> Table 2 shows additional treatments given for COVID-19 as part of BAC.

• In the first paragraph of clinical outcomes, the authors refer to a cohort that is not previously introduced in the manuscript. This is confusing. And I do not understand why this analysis is performed in the context of this RCT although I understand its pilot nature.

One of the main criticisms we have encountered in this study has been the choice of the primary endpoint. The best way respond to these questions was to provide data to support the prognostic relevance of CRP in COVID-19 pneumonia from a separate independent study where no other treatments such as dexamethasone, anakinra or anti-IL6 therapies were administered. We think this is very useful analysis and provides essential context for the trial and the choice of the primary endpoint, indicating that CRP has good enough resolution to predict clinical outcomes.

• Propensity-score selected contemporary controls may introduce bias in favor of the primary study analysis, since controls are already adjusted for age, sex and comorbidities.

The contemporary controls were selected to best match the characteristics of the randomized patients including that the first CRP measurement upon admission surpassed the trial threshold, so we do not see how this selection process introduces biases, as it was blinded with regards to the course of the CRP measurements. Given that this was a small trial, matching for baseline characteristics is necessary to minimize confounding effects.

• The authors do not clearly present numerically survivors and non-survivors at day 34, even though this is one of the main secondary outcomes.

We now provide the mortality numbers in the following paragraph on pg. 13.

“Over 35 days follow up, 1 person in the BAC + dornase-alfa group died, compared to 8 in the BAC group. The hazard ra.o observed in the Cox propor.onal hazards model (95% CI) was 0.47 (0.06, 3.86), which es.mates that throughout 35 days follow-up, there was a 53% reduced chance of death at any given .mepoint in the BAC + dornase-alfa group compared to the BAC group, though the confidence intervals are wide due to a small number of events. The p-value from a log-rank test was 0.460, which does not reach sta.s.cal significance at an alpha of 0.05.”

• It is unclear why another cohort (Berlin) was used to associate CRP with mortality. CRP association with mortality should (also) be performed within the current study.

As we explained above, the Berlin cohort CRP data serve to substantiate the relevance of CRP as a primary endpoint in a cohort that experienced sufficient mortality as this cohort did not receive any approved anti-inflammatory therapy. Mortality in our COVASE trial was minimal, since all patients were on dexamethasone and did not reach the highest severity grade, since we opted to treat patients before they deteriorated further. The overall mortality was 8% across all arms of our study, which does not provide enough events for mortality measurements. In contrast the Berlin cohort did not receive dexamethasone and all patients had reached a WHO severity grade 7 category with mortality at 30%.

My other concerns are:

• This report is about an RCT and the authors should follow the CONSORT reporting guidelines. Please amend the manuscript and Figure 1b accordingly and provide a CONSORT checklist.

We now provide a CONSORT checklist and have amended the CONSORT diagram accordingly.

• Please provide in brief the exclusion criteria in the main manuscript

We have now included the exclusion criteria in the manuscript on pg. 6.

“1.1.1 Exclusion criteria

1. Females who are pregnant, planning pregnancy or breasmeeding

2. Concurrent and/or recent involvement in other research or use of another experimental inves.ga.onal medicinal product that is likely to interfere with the study medica.on within (specify .me period e.g. last 3 months) of study enrolment 3. Serious condi.on mee.ng one of the following:

a. Respiratory distress with respiratory rate >=40 breaths/min

b. oxygen satura.on<=93% on high-flow oxygen

1. Require mechanical invasive or non-invasive ven.la.on at screening

2. Concurrent severe respiratory disease such as asthma, COPD and/or ILD

3. Any major disorder that in the opinion of the Inves.gator would interfere with the evalua.on of the results or cons.tute a health risk for the trial par.cipant

4. Terminal disease and life expectancy <12 months without COVID-19

5. Known allergies to dornase alfa and excipients

6. Par.cipants who are unable to inhale or exhale orally throughout the en.re nebulisa.on period So briefly Patients were excluded if they were:

7. pregnant, planning pregnancy or breasmeeding

8. Serious condition meeting one of the following:

a. Respiratory distress with respiratory rate >=40 breaths/min

b. oxygen satura.on<=93% on high-flow oxygen

1. Require ven.la.on at screening

2. Concurrent severe respiratory disease such as asthma, COPD and/or ILD

3. Terminal disease and life expectancy <12 months without COVID-19

4. Known allergies to dornase alfa and excipients

5. Participants who are unable to inhale or exhale orally throughout the en.re nebulisa.on period”

• "The final trial visit occurred at day 35." "Analysis included mortality at day 35". I am not sure I understand why. In clinicaltrials.gov all endpoints are meant to be studies at day 7 except for mortality rate day 28. Why day 35 was chosen? Please be consistent.

Thank you for identifying this inconsistency. We have amended the record on clinicaltrials.gov to read ‘’the time to event data was censored at 28 days post last dose (up to d35) for the randomised participants and at the date of the last electronic record for the CC.”

• Please provide in Methods the timeframe for the investigation of the primary endpoint

• The authors performed an RCT but in parallel chose to compare also controls. They should explain their rationale as this is not usual. I am not very enthusiastic to see mixed results like Figures 2c and 2d.

• Analysis is performed in mITT; this is a major limitation. The authors should provide at least ITT results. And they should describe in the main manuscript why they chose mITT analysis.

• It is also not usual to exclude patients from analysis because investigators just do not have serial measurements. This is lost to follow up and investigators should have pre-decided what to do with lost-to-follow-up.

• Figure 1b as in CONSORT statement, please provide reasons why screened patients were not enrolled.

• In Table 1 I would like to see all randomized patients (n=39), which is missing. There are also baseline characteristics that are missing, like which other treatment as BAT received those patients except for dexamethasone.

• In the first paragraph of clinical outcomes, the authors refer to a cohort that is not previously introduced in the manuscript. This is confusing. And I do not understand why this analysis is performed in the context of this RCT although I understand its pilot nature.

• In Figure 2 the authors draw results about ITT although in methods describe that they performed an mITT analysis. Please be consistent.

Please see answers provided to these queries above.

Reviewer #2 (Recommendations For The Authors):

1) Suppl Figure 2B would be more informative if presented as a Table with N of patients with per day sampling

We now provide the primary end point daily sampling table in Table 3.

2) The numbers at risk should figure under the KM curves

The numbers at risk for figures 1E, 2C, 2D have been added as graphs either in the main figures or in the supplement.

3) HD in Supplementary figure 3 should be explained

We apologize for this omission. We now provide a description for the healthy donor samples that we used in the cell-free DNA measurements in figure S3B on pg. 14:

“Compared to the plasma of anonymized healthy donors volunteers at the Francis Crick ins.tute (HD), plasma cf-DNA levels were elevated in both BAC and DA-treated COVASE par.cipants.

4) Presentation is inappropriate for Table S4

We thank the reviewer for pointing this issue. We have now formaxed Table S4 to be consistent with all other tables.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript is a focused investigation of the phosphor-regulation of a C. elegans kinesin-2 motor protein, OSM-3. In C-elegans sensory ciliary, kinesin-2 motor proteins Kinesin-II complex and OSM-3 homodimer transport IFT trains anterogradely to the ciliary tip. Kinesin-II carries OSM-3 as an inactive passenger from the ciliary base to the middle segment, where kinesin-II dissociates from IFT trains and OSM-3 gets activated and transports IFT trains to the distal segment. Therefore, activation/inactivation of OSM-3 plays an essential role in its ciliary function.

Strengths:

In this study, using mass spectrometry, the authors have shown that the NEKL-3 kinase phosphorylates a serine/threonine patch at the hinge region between coiled coils 1 and 2 of an OSM-3 dimer, referred to as the elbow region in ubiquitous kinesin-1. Phosphomimic mutants of these sites inhibit OSM-3 motility both in vitro and in vivo, suggesting that this phosphorylation is critical for the autoinhibition of the motor. Conversely, phospho-dead mutants of these sites hyperactivate OSM-3 motility in vitro and affect the localization of OSM3 in C. elegans. The authors also showed that Alanine to Tyrosine mutation of one of the phosphorylation rescues OS-3 function in live worms.

Weaknesses:

Collectively, this study presents evidence for the physiological role of OSM-3 elbow phosphorylation in its autoregulation, which affects ciliary localization and function of this motor. Overall, the work is well performed, and the results mostly support the conclusions of this manuscript. However, the work will benefit from additional experiments to further support conclusions and rule out alternative explanations, filling some logical gaps with new experimental evidence and in-text clarifications, and improving writing before I can recommend publication.

We appreciate Reviewer #1’s comments and suggestions. We have now provided additional evidences and discussions to further support our conclusions and fill the logical gaps. We have also provided alternative explanations to our data and improved writing.

Reviewer #2 (Public review):

Summary:

The regulation of kinesin is fundamental to cellular morphogenesis. Previously, it has been shown that OSM-3, a kinesin required for intraflagellar transport (IFT), is regulated by autoinhibition. However, it remains totally elusive how the autoinhibition of OSM-3 is released. In this study, the authors have shown that NEKL-3 phosphorylates OSM-3 and releases its autoinhibition.

The authors found NEKL-3 directly phosphorylates OSM-3 (although the method is not described clearly) (Figure 1). The phophorylated residue is the "elbow" of OSM-3. The authors introduced phospho-dead (PD) and phospho-mimic (PM) mutations by genome editing and found that the OSM-3(PD) protein does not form cilia, and instead, accumulates to the axonal tips. The phenotype is similar to another constitutive active mutant of OSM-3, OSM-3(G444A) (Imanishi et al., 2006; Xie et al., 2024). osm-3(PM) has shorter cilia, which resembles with loss of function mutants of osm-3 (Figure 3). The authors did structural prediction and showed that G444E and PD mutations change the conformation of OSM-3 protein (Figure 3). In the single-molecule assays G444E and PD mutations exhibited increased landing rate (Figure 4). By unbiased genetic screening, the authors identified a suppressor mutant of osm-3(PD), in which A489T occurs. The result confirms the importance of this residue. Based on these results, the authors suggest that NEKL-3 induces phosphorylation of the elbow domain and inactivates OSM-3 motor when the motor is synthesized in the cell body. This regulation is essential for proper cilia formation.

Strengths:

The finding is interesting and gives new insight into how the IFT motor is regulated.

Weaknesses:

The methods section has not presented sufficient information to reproduce this study.

We appreciate that Reviewer #2 is also positive to our study. We have now provided sufficient information in the revised Methods section.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major Concerns

(1) Why do the authors think that NEKL-3 phosphorylates OSM-3 in the first place? This seems to come out of nowhere and prior evidence indicating that NEKL-3 may be phosphorylating OSM-3 is not even mentioned in the Introduction.

We thank the Reviewer for raising this important point. Our hypothesis that NEKL-3 phosphorylates OSM-3 stems from prior findings in our lab. In a previous study (Yi et al., Traffic, 2018, PMID: 29655266), we identified NEKL-4, a member of the NIMA kinase family, as a suppressor of the OSM-3(G444E) hyperactive mutation. This discovery prompted us to explore the broader role of NIMA kinases in regulating OSM3. Subsequent genetic screens (Xie et al., EMBO J, 2024, PMID: 38806659) revealed that both NEKL-3 and NEKL-4 suppress multiple OSM-3 mutations, further supporting their functional interaction. Given the established role of NIMA kinases in phosphorylation-dependent processes (Fry et al., JCS, 2012, PMID: 23132929; Chivukula et al., Nat. Med., 2020, PMID: 31959991; Thiel, C. et al. Am. J. Hum. Genet. 2011, PMID: 21211617; Smith, L. A. et al., J. Am. Soc. Nephrol., 2006, PMID: 16928806), we hypothesized that NEKL-3/4 may directly phosphorylate OSM-3 to modulate its activity.

To test this hypothesis, we expressed recombinant C. elegans NEKL-3 and OSM-3 proteins and conducted in vitro phosphorylation assays. While we were unable to obtain active recombinant NEKL-4 (limitations noted in the revised text), our experiments with NEKL-3 revealed phosphorylation at residues 487-490 (YSTT motif) in OSM-3’s tail region, as confirmed by mass spectrometry. These findings are now explicitly contextualized in the Introduction and Results sections of the revised manuscript.

Page #4, Line #11:

“...In our previous study (Yi et al., Traffic, 2018, PMID: 29655266), a genetic screen targeting the OSM-3(G444E) hyperactive mutation identified NEKL-4, a member of the NIMA kinase family, as a suppressor of this phenotype. This finding, combined with reports that NIMA kinases regulate ciliary processes independently of their canonical mitotic roles (Fry et al., JCS, 2012, PMID: 23132929; Chivukula et al., Nat. Med., 2020, PMID: 31959991; Thiel, C. et al. Am. J. Hum. Genet. 2011, PMID: 21211617; Smith, L. A. et al., J. Am. Soc. Nephrol., 2006, PMID: 16928806), prompted us to investigate whether NIMA kinases modulate OSM-3-driven intraflagellar transport. We hypothesized that NEKL-3/4, as paralogs within this family, might directly phosphorylate OSM-3 to regulate its motility...”

Page #4, line #26:  

“... To determine whether NIMA kinase family members could directly phosphorylate

OSM-3, we purified prokaryotic recombinant C. elegans NEKL-3/NEKL-4 and OSM3 protein in order to perform in vitro phosphorylation assays. We were able to obtain active recombinant NEKL-3 but not NEKL-4. The in vitro phosphorylation assays showed that NEKL-3, directly phosphorylates OSM-3 (Fig. 1A-B, Appendix Table S1). Subsequent mass spectrometric analysis revealed phosphorylation at residues 487-490, which localize to the conserved "YSTT" motif within OSM-3’s C-terminal tail region ...”

(2) The authors need to characterize the proteins they expressed and purified for in vitro ATPase and motility assays. Are these proteins monomers or dimers?

For our in vitro ATPase and motility assays, OSM-3 was expressed in E. coli BL21(DE3) and purified using established protocols (Xie et al., EMBO J, 2024, PMID: 38806659; Imanishi et al., JCB, 2006, PMID: 17000874). To confirm its oligomeric state, we analyzed recombinant OSM-3 by size-exclusion chromatography coupled with multiangle light scattering (SEC-MALS). As reported in Xie et al. (2024), OSM-3 (~80 kDa monomer) elutes with a molecular weight of 173–193 kDa under physiological buffer conditions, consistent with a homodimeric assembly. These findings confirm that the functional unit used in our assays is the biologically relevant dimer. This characterization has been added to the revised manuscript on Page #35, Line #7.

“…OSM-3 was expressed in E. coli BL21(DE3) and purified for in vitro assays using established protocols (REFs). Size-exclusion chromatography coupled with multiangle light scattering (SEC-MALS) (Xie et al., EMBO J., 2024) confirmed that recombinant OSM-3 forms a homodimer (173–193 kDa) under physiological conditions, ensuring its dimeric state remained intact....” 

(3) The authors primarily used PD and PM mutations, which affect all four amino acids in the region. This may or may not be physiologically relevant. Figure 5 indicates that T489 is a critical regulatory site. However, this conclusion is undermined by reliance on PD mutations, which affect all four amino acids. Creating PM (T489E) and PD (T489A) mutations based on WT OSM-3 would better reflect physiological relevance. In vitro assays with a single phosphomimic or phosphor-dead mutation at residue 489 are missing at the end of this story. This would better link Figure 5 with the rest of the manuscript.

We thank the reviewer for this constructive critique. Below, we address the concerns and integrate new data to strengthen the link between T489 and autoinhibition:

To probe the regulatory role of T489 phosphorylation, we generated osm-3(T489E) (phosphomimetic, PM) and osm-3(T489A) (phospho-dead, PD) mutant animals. Strikingly, both mutants formed axonal puncta (Figure S7), recapitulating the hyperactive phenotype of the OSM-3G444E mutant. While the similar puncta formation in PM and PD mutants initially appeared paradoxical, this observation underscores the necessity of dynamic phosphorylation cycling at T489 for proper autoinhibition. Specifically, the PD mutant (T489A) likely disrupts phosphorylationdependent autoinhibition stabilization, leading to constitutive activation, where as the PM mutant (T489E) may mimic a "locked" phosphorylated state, preventing dephosphorylation-dependent release of autoinhibition in cilia and trapping OSM-3 in an aggregation-prone conformation. These results highlight T489 as a structural linchpin whose post-translational modification dynamically regulates motor activity. While the precise molecular mechanism—such as how phosphorylation modulates tailmotor domain interactions—remains to be elucidated, our data conclusively demonstrate that perturbing T489 (even in isolation) destabilizes autoinhibition, driving puncta formation and the constitutive activity.

We have integrated the above paragraph in the revised manuscript on page #8, line #27.

(4) There seems to be a disconnect between the MT gliding assays in Figure 4C and single molecule motility assays in Figure 4E. The gliding assays show that all constructs can glide microtubules at near WT speeds. Yet, the motility assays show that WT and PM cannot land or walk on MTs. The authors need to explain why this is the case. Is this because surface immobilization of kinesin from its tail disrupts autoinhibition? Alternatively, the protein preparation may include monomers that cannot be autoinhibited and cannot land and processively walk on surface-immobilized microtubules (because they only have one motor domain) but can glide microtubules when immobilized on the surface from their tail.

The surface immobilization of OSM-3 via its tail domain disrupts autoinhibition, a phenomenon previously observed in other kinesins such as kinesin-1 (Nitzsche et al, Methods Cell Biol., 2010, PMID: 20466139). In our assays, OSM-3 was nonspecifically immobilized on glass surfaces, enabling microtubule gliding by motors whose autoinhibition was relieved through tail anchoring. Critically, the PD and PM mutations reside in the tail region and do not alter the intrinsic properties of the motor head domain. Consequently, once autoinhibition is released via immobilization, the gliding velocities reflect the conserved motor head activity, which is expected to remain comparable across all constructs. While we cannot entirely rule out the presence of monomeric OSM-3 in solution, several lines of evidence argue against this possibility. First, the mutations are located in the elbow region, which is dispensable for motor dimerization. Second, SEC-MALS analysis from prior studies confirms that purified OSM-3 exists predominantly as dimers in solution. 

We have discussed these issues in the revised text on page #10, line #18: 

“…In our gliding assays, OSM-3PM has an increased gliding speed of 0.69 ± 0.07 μm/s (Fig. 4 C-D), similar to PD mutant. PD and PM mutations are confined to the elbow region, leaving the motor head’s mechanochemical properties intact. Upon tail immobilization—which releases autoinhibition—the gliding speeds reflect motor head activity. Single-molecule assays, however, directly resolve their native regulatory states: PD mutants are constitutively active, whereas PM mutants persist in an autoinhibited state (Fig. 4E-G). Although monomeric OSM-3 could theoretically mediate singlemotor gliding, the previous SEC-MALS data demonstrate that OSM-3 purifies as stable dimers (Xie et al., EMBO J, 2024, PMID: 38806659). Thus, dimeric OSM-3 is perhaps the predominant functional species in our assays…”

(5) An alternative explanation for the data is that both PD and PM mutations result in loss-of-function effects, disrupting OSM-3 activity. For instance:

a) In Figure 2C, both mutations cause shorter cilia than the wild type (WT).

b) In Figure 4A, both mutations result in higher ATPase activity than WT.

c) In Figure 4D, both mutations show increased gliding velocity compared to WT. These results suggest the observed effects could stem from loss of function rather than phosphorylation-specific regulation.

Although PD and PM mutations exhibit superficially similar "loss-of-function" phenotypes in certain assays, they mechanistically disrupt motor regulation in distinct ways:

a) Ciliary Length (Figure 2C) PD Mutants: Hyperactivation causes OSM-3-PD to prematurely aggregate into axonal puncta, preventing ciliary entry. Consequently, cilia are built solely by the weaker Kinesin-II motor, which only constructs shorter middle segments.

PM Mutants: OSM-3-PM retains autoinhibition during transport (enabling ciliary entry) but cannot be dephosphorylated in cilia. This blocks activation, leaving OSM-3-PM partially functional and resulting in cilia intermediate in length between WT and PD.

We have discussed this issue in the revised text on page #5, line #30:

“…These findings indicate that OSM-3-PM is in an autoinhibited state capable of ciliary delivery, yet fails to achieve full activation due to defective dephosphorylation. This incomplete activation results in suboptimal motor function and intermediate ciliary length phenotypes (Fig.2 B-C). In contrast, OSM-3-PD exhibits constitutive activation leading to aggregation into axonal puncta, which completely abolishes its ciliary entry capacity (Fig.2 A-B)...”

b) ATPase Activity (Figure 4A)

PD Mutants: Fully autoinhibition-released (98.15% of KHC ATPase activity), consistent with constitutive activation.

PM Mutants: Show partial ATPase activity (34.28% of KHC), reflecting imperfect phosphomimicry. While the DDEE substitution introduces negative charges, it fails to fully replicate the steric/kinetic effects of phosphorylated tyrosine (Y486; phenyl ring absent), resulting in incomplete autoinhibition stabilization. Despite this, the residual inhibition is sufficient to phenocopy shorter cilia in vivo.

We have discussed this issue in the revised text on page #7, line#19:

“…The PM mutant’s partial ATPase activity (34.28% of KHC) might arise from imperfect phosphomimicry—while the DDEE substitution introduces negative charges, it lacks the steric bulk of phosphorylated tyrosine (pY487). And this incomplete mimicry allows residual autoinhibition, sufficient to limit ciliary construction in vivo...”

c) Microtubule Gliding Velocity (Figure 4D)

Gliding Assay Limitation: Tail immobilization artificially releases autoinhibition, masking regulatory differences. Thus, all constructs (PD, PM) exhibit similar velocities (~0.7 µm/s), reflecting conserved motor head activity.

Single-Molecule Assay (Figure 4E): Directly resolves native autoinhibition states:

PD mutants show robust motility (autoinhibition released).

PM mutants remain largely inactive (autoinhibition retained).

We have discussed this issue in the revised text on page #10, line#18:

“…In our gliding assays, OSM-3PM has an increased gliding speed of 0.69 ± 0.07 μm/s (Fig. 4 C-D), similar to PD mutant. PD and PM mutations are confined to the elbow region, leaving the motor head’s mechanochemical properties intact. Upon tail immobilization—which releases autoinhibition—the gliding speeds reflect motor head activity. Single-molecule assays, however, directly resolve their native regulatory states: PD mutants are constitutively active, whereas PM mutants persist in an autoinhibited state (Fig. 4E-G)...”

Minor Suggestions and Concerns

(1) Lines 60-66: References that support these observations are missing from this section.

We have added the relevant references.

(2) Lines 66-67: I would revise this sentence as "It remains unclear how OSM-3 becomes enriched...".

We have made the changes.

(3) Line 85: The authors should describe how they perform these assays (i.e. recombinantly expressed NEKL-3 and OSM-3, are these C. elegans proteins, and which expression system was used...).

We have described them in the main text and methods

Page #4 line #26

“...To determine whether NIMA kinase family members could directly phosphorylate OSM-3, we purified prokaryotic recombinant C. elegans NEKL-3/NEKL-4 and OSM-3 protein in order to perform in vitro phosphorylation assays...”

Page #35 line#12

“...Basically, point mutations was introduced in to pET.M.3C OSM-3-eGFP-His6 plasmid for prokaryotic expression. Plasmid transformed E. coli (BL21) was cultured at 37°C and induced overnight at 23°C with 0.2 mM IPTG. Cells were lysed in lysis buffer (50 mM NaPO4 pH8.0, 250 mM NaCl, 20 mM imidazole, 10 mM bME, 0.5 mM ATP, 1 mM MgCl¬2, Complete Protease Inhibitor Cocktail (Roche)) and Ni-NTA beads were applied for affinity purification. After incubation, beads were washed with wash buffer (50 mM NaPO4 pH6.0, 250 mM NaCl, 10 mM bME, 0.1 mM ATP, 1 mM MgCl¬2) and eluted with elute buffer (50 mM NaPO4 pH7.2, 250 mM NaCl, 500 mM imidazole, 10 mM bME, 0.1 mM ATP, 1 mM MgCl¬2). Protein concentration was determined by standard Bradford assay. C elegans nekl-3 cDNA was cloned in to pGEX-6P GST vector and expressed in E. coli BL21 (DE3) and purified for in vitro phosphorylation assays. Plasmid transformed E. coli (BL21) was cultured at 37°C and induced overnight at 18°C with 0.5 mM IPTG. Cells were lysed in lysis buffer (50 mM NaPO4 pH8.0, 250 mM NaCl, 1 mM DTT, Complete Protease Inhibitor Cocktail (Roche)) and GST beads were applied for affinity purification. After incubation, beads were washed with wash buffer (50 mM NaPO4 pH6.0, 250 mM NaCl, 1 mM DTT) and eluted with elute buffer (50 mM NaPO4 pH7.2, 150 mM NaCl, 10 mM GSH, 1 mM DTT). Purified proteins were dialyzed against storge buffer (50 mM Tris-HCl, pH 8.0, 150 mM NaCl). Protein concentration was determined by standard Bradford assay...”

(4) Line 141: The first sentence of this paragraph lacks motivation. I would start this sentence with "To directly observe the effects of phosphor mutants in the elbow region in microtubule binding and motility of OSM-3, we...".

We have made the change.

(5) Figure 1B: The mass spectrometry data in Figure 1B lacks adequate explanation. The Methods section should detail the experimental protocol, data interpretation, and any databases used. Additionally, the manuscript should list all identified phosphorylation sites on OSM-3 to provide context, including whether Y487_T490 is the major site.

We have provided the detailed experimental protocol, data interpretation, and databases used in methods. We have provided all identified sites as Appendix table S1.

(6) Figure 1C: Is it possible to model the effect of PM and PD mutations using AlphaFold? The authors should also show PAE or pLDDT scores of their model.

AlphaFold cannot well model the effect of mutants, but we conducted the Rosetta relax to capture their possible conformational changes, as shown in the revised Figure 3. We have provided PAE and pLDDT as a new figure, Figure S2.

(7) Figure 2D: The unit for speed should use a lowercase "s" for seconds.

We have fixed it.

(8) Figure 3: I am not sure whether this figure stands for a main text figure on its own, as it is only a Rosetta prediction and is not supported by any experimental data. In addition, it remains unclear what the labels on the x-axis mean.

We have updated the figure and explain the labels on the x-axis in Figure S4 to make it more reader-friendly.

(9) Figure 4: NEKL-3-treated OSM-1 should be included as a positive control in the in vitro experiments.

We suspect that the Reviewer asked for NEKL-3-treated OSM-3. 

In our other study which has just been accepted by the Journal of Cell Biology, NEKL3-treated OSM-3 significantly reduced the affinity between OSM-3 motor and microtubules and showed very low ATPase activity. We have cited and discussed this in the revised text on page #10, line #28: 

“…As demonstrated in our recent study (Huang et al., JCB, 2025, In press, attached), phosphorylation of OSM-3 by NEKL-3 at two distinct regions—Ser96 and the conserved "elbow" motif—differentially regulates its activity and localization. Phosphorylation at Ser96 reduces OSM-3’s ATPase activity and alters its ciliary distribution from the distal segment to a uniform localization, while elbow phosphorylation induces autoinhibition, retaining OSM-3 in the cell body. Strikingly, in vitro phosphorylation of OSM-3 by NEKL-3 significantly reduces its microtubulebinding affinity, likely arising from combined modifications at both sites. We propose a model wherein elbow phosphorylation ensures anterograde ciliary transport, while Ser96 phosphorylation fine-tunes distal segment targeting. This multistep regulation may involve distinct phosphatases to reverse phosphorylation at specific sites, a hypothesis warranting further investigation….”

(10) Figure 4C, D, and F: The unit of velocity is wrong. The authors should use the same units they used in the table shown in Figure 4B.

We have fixed these errors

(11) Figure 4F: The velocity of PD is a lot lower than G444E. Therefore, it would be more appropriate to refer to PD as partially active, rather than hyperactive.

We have made the change. 

(12) Figure 5: There is too much genetics jargon on this figure (EMF, F2, 100%Dyf,...). How are the alleles numbered? Is it OK to refer to them as Alleles 1 and 2 for simplicity?

According to the established C. elegans allele nomenclature, each worm allele has a unique number named after the lab code for identification. We have simplified the labels and updated the figure to make it more reader-friendly.

(13) Figure 5E: A plot would be more reader-friendly than a table. Additionally, the legend for Fig. 5E mistakenly refers to it as "D."

We have changed the table to a plot and fixed the mistakes. We thank the Reviewer for pointing them out.

Reviewer #2 (Recommendations for the authors):

(1) The model appears as if NEKL-3 induces dephosphorylation of OSM-3 (Figure 6). This is not consistent with the conclusions described in the Discussion and is confusing.

We have updated the model figure and fixed the error.

(2) It should be described why the authors hypothesized NEKL-3 phosphorylates OSM3. Was there genetic evidence? Did the authors screened cilia-related kinases? or Did the authors identify it incidentally? Providing this information would help readers to understand the context of the research.

We appreciate both Reviewers for pointing out this issue. 

Our hypothesis that NEKL-3 phosphorylates OSM-3 stems from prior findings in our lab. In a previous study (Yi et al., Traffic, 2018, PMID: 29655266), we identified NEKL-4, a member of the NIMA kinase family, as a suppressor of the OSM-3(G444E) hyperactive mutation. This discovery prompted us to explore the broader role of NIMA kinases in regulating OSM-3. Subsequent genetic screens (Xie et al., EMBO J, 2024, PMID: 38806659) revealed that both NEKL-3 and NEKL-4 suppress multiple OSM-3 mutations, further supporting their functional interaction. Given the established role of NIMA kinases in phosphorylation-dependent processes (Fry et al., JCS, 2012, PMID: 23132929; Chivukula et al., Nat. Med., 2020, PMID: 31959991; Thiel, C. et al. Am. J. Hum. Genet. 2011, PMID: 21211617; Smith, L. A. et al., J. Am. Soc. Nephrol., 2006, PMID: 16928806), we hypothesized that NEKL-3/4 may directly phosphorylate OSM3 to modulate its activity.

To test this hypothesis, we expressed recombinant C. elegans NEKL-3 and OSM-3 proteins and conducted in vitro phosphorylation assays. While we were unable to obtain active recombinant NEKL-4 (limitations noted in the revised text), our experiments with NEKL-3 revealed phosphorylation at residues 487-490 (YSTT motif) in OSM-3’s tail region, as confirmed by mass spectrometry. These findings are now explicitly contextualized in the Introduction and Results sections of the revised manuscript.

Page #4, Line #11:

“... In our previous study (Yi et al., Traffic, 2018, PMID: 29655266), a genetic screen targeting the OSM-3(G444E) hyperactive mutation identified NEKL-4, a member of the NIMA kinase family, as a suppressor of this phenotype. This finding, combined with reports that NIMA kinases regulate ciliary processes independently of their canonical mitotic roles (Fry et al., JCS, 2012, PMID: 23132929; Chivukula et al., Nat. Med., 2020, PMID: 31959991; Thiel, C. et al. Am. J. Hum. Genet. 2011, PMID: 21211617; Smith, L. A. et al., J. Am. Soc. Nephrol., 2006, PMID: 16928806), prompted us to investigate whether NIMA kinases modulate OSM-3-driven intraflagellar transport. We hypothesized that NEKL-3/4, as paralogs within this family, might directly phosphorylate OSM-3 to regulate its motility...”

Page #4, line #26: 

“... To determine whether NIMA kinase family members could directly phosphorylate OSM-3, we purified prokaryotic recombinant C. elegans NEKL-3/NEKL-4 and OSM3 protein in order to perform in vitro phosphorylation assays. We were able to obtain active recombinant NEKL-3 but not NEKL-4. The in vitro phosphorylation assays showed that NEKL-3, directly phosphorylates OSM-3 (Fig. 1A-B, Appendix Table S1). Subsequent mass spectrometric analysis revealed phosphorylation at residues 487-490, which localize to the conserved "YSTT" motif within OSM-3’s C-terminal tail region...”

(3) It is curious the authors have not addressed the cilia phenotype and the localization of OSM-3 in nekl-3 mutant. Regardless of whether these observations agrees with the proposed mechanisms, it is essential for the authors to show and discuss the cilia phenotype and OSM-3 localization in nekl-3 mutants.

We thank the Reviewer for highlighting this critical point. Indeed, nekl-3 null mutants are inviable due to essential mitotic roles (Barstead et al., 2012, PMID: 23173093), precluding direct analysis of ciliary phenotypes. To bypass this limitation, we recently generated nekl-3 conditional knockouts (cKOs) in ciliated neurons (Huang et al., JCB, 2025 in press, attached). In these mutants, OSM-3—which is normally enriched in the ciliary distal segment—becomes uniformly distributed along the cilium. This redistribution correlates with premature activation of OSM-3-driven anterograde motility in the ciliary middle region, consistent with our proposed model where NEKL3 phosphorylation suppresses OSM-3 activity. We have now integrated this result and discussion into the revised manuscript, reinforcing the physiological relevance of NEKL-3-mediated regulation in ciliary transport. 

Page #6 line #10

“… While nekl-3 null mutants are inviable due to essential mitotic roles (Barstead et al., 2012, PMID: 23173093), conditional knockout (cKO) of nekl-3 in ciliated neurons (Huang et al., JCB, 2025 in press, attached) revealed its critical role in regulating OSM3 dynamics. In nekl-3 cKO animals, OSM-3—normally enriched in the ciliary distal segment—redistributed uniformly along the cilium, concomitant with premature activation of anterograde motility in the middle ciliary region. This phenotype aligns with our model wherein NEKL-3 phosphorylation suppresses OSM-3 activity, ensuring spatiotemporal regulation of IFT.…”

(4) The methods section lacks some information, which is critical to reproducing this study.

We have now provided detailed information in the methods section in the revised manuscript.

(a) It is not described how the authors determined phosphorylation of OSM-3 by NEKL-3. In methods, nothing is described about the assay.

We performed in vitro phosphorylation assays using recombinant OSM-3 and NEKL3 purified from bacteria. We then used LC-MS/MS for identification of phosphorylation sites. We have now updated the methods section to include all the information.

Page #4 line #26

“... To determine whether NIMA kinase family members could directly phosphorylate OSM-3, we purified prokaryotic recombinant C. elegans NEKL-3/NEKL-4 and OSM3 protein in order to perform in vitro phosphorylation assays. We were able to obtain active recombinant NEKL-3 but not NEKL-4. The in vitro phosphorylation assays showed that NEKL-3, directly phosphorylates OSM-3 (Fig. 1A-B, Appendix Table S1). Subsequent mass spectrometric analysis revealed phosphorylation at residues 487-490, which localize to the conserved "YSTT" motif within OSM-3’s C-terminal tail region...”

Page #36, line #19

“In vitro phosphorylation assay 20 μM purified OSM-3 was incubated with 1 μM GST-NEKL-3 at 30 °C in 100 μL reaction buffer (50 mM Tris-HCl pH 8.0, 10 mM MgCl2, 150 mM NaCl, and 2 mM ATP) for 30 min. The reaction was terminated by boiling for 5 min with an SDS-sample buffer.

Mass spectrometry

Following NEKL-3 treatment, OSM-3 proteins were resolved by SDS-PAGE and visualized with Coomassie Brilliant Blue staining. Protein bands corresponding to OSM-3 were excised and subjected to digestion using the following protocol: reduction with 5 mM TCEP at 56°C for 30 min; alkylation with 10 mM iodoacetamide in darkness for 45 min at room temperature, and tryptic digestion at 37°C overnight with a 1:20 enzyme-to-protein ratio. The resulting peptides were subjected to mass spectrometry analysis. Briefly, the peptides were analyzed using an UltiMate 3000 RSLCnano system coupled to an Orbitrap Fusion Lumos mass spectrometer (Thermo Fisher Scientific). We applied an in-house proteome discovery searching algorithm to search the MS/MS data against the C. elegans database. Phosphorylation sites were determined using PhosphoRS algorithm with manual validation of MS/MS spectra.”

(b) The method of structural prediction by Alfafold2 and LocalColabFold needs clarification. In general, the prediction gives several candidates. How did the authors choose one of these candidates?

We generated five candidate models and all of them showed similar conformation. We thus chose the model with the highest confidence. We have provided PAE and pLDDT as additional data in Figure S2 and discussed them in the revised text on, Page #4, line #32: 

“...To gain structural insights from this motif, we employed LocalColabFold based on AlphaFold2 to predict the dimeric structure of OSM-3 (Evans et al., 2022; Jumper et al., 2021; Mirdita et al., 2022). The highest-confidence model was selected for further analysis (Fig. 1C, Fig. S2)...”

(c) The methods to predict conformational changes by introducing various point mutations are interesting (Figure 3). However, the methods require more detailed descriptions. In the current form, the manuscript only lists the tools used. The pipelines and parameters need to be described. This information is important because AlphaFoldbased predictions often give folded conformations because the training data are mainly composed of folded proteins. It is surprising that the methods applied here give open conformations induced by point mutations.

We have described the pipelines in the revised Methods section on page#34, line#25: 

“…OSM-3 model was predicted using LocalColabFold (Evans et al., 2022; Jumper et al., 2021; Mirdita et al., 2022). Mutated proteins were designed by Pymol 2.6, choosing the rotamer of the mutated residues in G444E, PM and PD models with the least clash as the initial conformation. To predict mutation-induced conformational changes, the initial models were subjected to Pyrosetta (Chaudhury et al., 2010). The energies of pre-relaxed models were evaluated with Rosetta Energy Function 2015 (Alford et al., 2017), and then the relax procedure were applied to the models with default parameters to obtain the relaxed models visualized by Pymol to minimize the energy of these models. In detail, to obtain the relaxed models visualized by Pymol and minimize the energy of these models, the classic relax mover was used in the procedure mentioned above with default settings. The relax script has been uploaded to Github: https://github.com/young55775/RosettaRelax_for_OSM3...”

(5) The authors have purified proteins. Do they show different properties in gel filtration that are consistent with the structural prediction? It is anticipated that open-form mutants are eluted from earlier than closed forms.

We thank the reviewer for this insightful suggestion. Indeed, our recent study supported that the open-from of the active OSM-3 G444E mutation were eluted earlier than the wild-type closed form (Xie et al., EMBO J., 2024). While the current study did not perform gel filtration chromatography (SEC) to directly compare the hydrodynamic properties of the OSM-3 mutants, our functional assays provide robust evidence for conformational changes predicted by structural modeling. For example: ATPase activity assays revealed that the open-state mutants (e.g., G444E and PD muatnts) exhibited significantly enhanced enzymatic activity (Figure 4A), consistent with structural predictions of an active, destabilized autoinhibitory interface (Figure 3A). These functional readouts collectively validate the predicted structural states. While SEC could further corroborate these findings by distinguishing compact (closed) versus extended (open) conformations, we prioritized assays that directly link structural predictions to in vitro enzymatic activity and in vivo ciliary transport dynamics. Future studies incorporating SEC or cryo-EM will provide additional biophysical validation of these states.

We have revised the text in the manuscript (Page #7, Lines #22): 

“…Notably, the open-state OSM-3 mutants (e.g., G444E) displayed elevated ATPase activity, consistent with structural predictions of autoinhibition release (Fig. 3A, Fig. 4A) (Xie et al., 2024). While hydrodynamic profiling (e.g., SEC) could further resolve conformational states, our functional assays directly connect predicted structural changes to altered biochemical and cellular activity...”

Minor point

(1) Line 85 "MIMA kinase family" should be "NIMA kinase family".

We have corrected the typo and appreciate that the Reviewer for pointing it out. 

(2) M.S. and D.S. need to be defined in Figure 2D.

We have updated the figures.

Author Response

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

1) The main issue relates to Set2, and how STIM1 expression rescues Set2-dependent functions in Set2 KO flies. If Set2 is downstream of STIM1, how would STIM1 over-expression rescue a Set2-dependent effect?

STIM rescue is of Set2 knockdown (RNAi) and NOT Set2 Knockout flies. Over expression of STIM raises SOCE in primary cultures of Drosophila neurons (as demonstrated in previous publications from our group: Agrawal et al., 2010; Chakraborty et al, 2016; Deb et al., 2016). The higher SOCE drives greater expression of Set2 from the endogenous locus thus reducing the efficacy of Set2 RNAi. Hence the rescue by STIM of Set2 KD flies in Figure S2E. We have explained this in lines 227-234.

2) There is still no characterization of SOCE in fpDANs from flies expressing native Orai or the dominant negative OraiE180A mutant.

Measurement of SOCE is not technically feasible in ex-vivo preps due to the presence of extracellular calcium in the brain milieu. In the past we have measured SOCE from primary cultures of central dopaminergic neurons expressing either native Orai OR OraiE180A mutant (Pathak et al., 2015) where we found that all dopaminergic neurons expressing OraiE180A exhibit very low SOCE. This is the reason we have not measured SOCE in the fewer cells of the fpDAN subset marked by THD' GAL4. This point has been specifically mentioned and explained in the section on “limitations of the study” at the end of the manuscript.

3) The revised version does not include an analysis of the STIM:Orai stoichiometry, which has been demonstrated to be essential for SOCE.

To measure such stoichiometry we would need to perform direct measurements of STIM and Orai levels by protein extraction from the fpDANs of all appropriate genotypes. This is not feasible due to the small number of cells available from each brain.

I confirm that there are no changes to the text OR figures from the previous version of the manuscript.

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

[…]

The manuscript by Mitra and coworkers analyses the functional role of Orai in the excitability of central dopaminergic neurons in Drosophila. The authors show that a dominant-negative mutant of Orai (OraiE180A) significantly alters the gene expression profile of flight-promoting dopaminergic neurons (fpDANs). Among them, OraiE180A attenuates the expression of Set2 and enhances that of E(z) shifting the level of epigenetic signatures that modulate gene expression. The present results also demonstrate that Set2 expression via Orai involves the transcription factor Trl. The Orai-Trl-Set1 pathway modulates the expression of VGCC, which, in turn, are involved in dopamine release. The topic investigated is interesting and timely and the study is carefully performed and technically sound; however, there are several major concerns that need to be addressed:

1) In Figure S2E, STIM is overexpressed in the absence of Set2 and this leads to rescue. It is presumed that STIM overexpression causes excess SOCE, yet this is rarely the case. Perhaps the bigger concern, however, is how excess SOCE might overcome the loss of SET2 if SET2 mediates SOCE-induced development of flight. These data are more consistent with something other than SET2 mediating this function.

Our statement that STIM overexpression overcomes deficits in SOCE is based on the following published work, which has been highlighted in the revised version of the manuscript (see Lines 226-233):

1. Studies of SOCE in wildtype cultured larval Drosophila neurons demonstrated that overexpression of STIM raised SOCE to the same extent as co-expression of STIM and Orai in the WT background (Chakraborty et al, 2016; Figure 1D).

2. Both Carbachol-induced IP3-mediated Ca2+ release and SOCE (measured by Ca2+ add back after Thapsigargin-induced store depletion) were rescued in primary cultures of IP3R hypomorphic mutant (itprku) Drosophila neurons by overexpression of STIM (Agrawal et al., 2010; Figure 8A-G).

3. Deb et al., 2016 (Supplementary Figure 2h,i) reaffirmed that overexpression of STIM significantly improves SOCE after Thapsigargin-induced passive store-depletion in Drosophila neurons expressing IP3RRNAi.

4. Consistent with the cellular rescue of SOCE, defects in flight initiation and physiology observed in the heteroallelic IP3R hypomorphic background (itprku) could be rescued by overexpression of STIM (Agrawal et al., 2010; Figure 3A-E) as well as Orai (Venkiteswaran and Hasan, 2009; Figure 3).

5. In Figure S2E, we show that flight deficits arising from THD’> Set2RNAi are rescued upon overexpression of STIM (i.e. THD’>Set2RNAi; STIMOE). Here and in another recent publication (Mitra et al., 2021) we show that neurons expressing Set2RNAi exhibit reduced expression of the IP3R and reduced ER-Ca2+ release presumably leading to reduced SOCE. As mentioned above we have consistently found that STIM overexpression raises both IP3-mediated Ca2+ release and SOCE in Drosophila neurons.

In this study, we propose that Ca2+ release through the IP3R followed by SOCE are part of a positive feedback loop (described in the revised manuscript- see Lines 302-307) driving expression of Set2 which in turn upregulates expression of mAChR and IP3R (Figure 3F) to regulate dopaminergic neuron function. Our observation that loss of Set2 (THD’>Set2RNAi) can be rescued by STIM overexpression is consistent with this model because:

1. Loss of Set2 (THD’>Set2RNAi) results in downregulation of several genes including mAChR and IP3R leading to decreased SOCE.

2. As evident from our previous studies increased STIM expression in the Set2RNAi background (THD’>Set2RNAi; STIMOE) is expected to enhance SOCE which we predict would rescue Set2 expression leading to rescue of other Set2 dependent downstream functions like flight (Figure 2D).

2) In Figure 3, data is provided linking SET2 expression and Cch-induced Ca2+ responses. The presentation of these data is confusing. In addition, the results may be a simple side effect of SET2-dependent expression of IP3R. Given that this article is about SOCE, why isn't SOCE shown here? More generally, there are no measurements of SOCE in this entire article. Measuring SOCE (not what is measured in response to Cch) could help eliminate some of this confusion.

This section has been re-written in the revised version for better clarity and we have explained how Set2-dependent IP3R expression is an important component of Orai-mediated Ca2+ entry in fpDANs (see Lines 302-307). Here, we propose that IP3-mediated Ca2+ release and SOCE, through Orai, are together part of a positive feedback loop (see Lines 286-307) driving transcription of Set2 which in turn upregulates mAChR and IP3R expression (Figure 3F). We hypothesized that the observed loss of CCh-induced Ca2+ response in the Set2RNAi background (Figure 3B-D; THD’>Set2RNAi) results from decreased itpr and mAChR expression and verified this in Figure 3E. This is further validated by the rescue of CCh-induced Ca2+ response and itpr/mAChR expression in the OraiE180A background upon Set2 overexpression (Figure 3B-E; THD’>OraiE180A; Set2OE). We were constrained to measure CCh-induced Ca2+ responses in OraiE180A expressing neurons for the following reasons (highlighted in the revised version of the manuscript- (See Lines 307-313; ‘Limitations of the study’-Lines 719-735):

1. SOCE measurements through Tg mediated store Ca2+ release followed by Ca2+ add back require a 0 Ca2+ environment that can only be achieved in culture. The Drosophila brain is bathed in hemolymph which contains Ca2+ and there do not exist any methods to readily deplete Ca2+ from the tissue to create a 0 Ca2+ environment without also effecting the health of the neurons.

2. Cultures of the subset of dopaminergic neurons (THD’) we have focused on in this study were not feasible due to the small number of neurons being studied from the total number of dopaminergic neurons in the brain (~35/400). In previous studies we have shown that SOCE post-Tg induced store depletion is abrogated in cultured dopaminergic neurons from Drosophila upon expression of OraiE180A (Pathak et al., 2015). Furthermore, Carbachol-induced IP3-mediated Ca2+ release is tightly coupled to SOCE in Drosophila neurons (Venkiteswaran and Hasan, 2009) and Ca2+ release from the IP3R is physiologically relevant for flight behavior in THD’ neurons (Sharma and Hasan, 2020).

3) A significant gap in the study relates to the conclusion that trl is a SOCE-regulated transcription factor. This conclusion is entirely based on genetic analysis of STIMKO heterozygous flies in which a copy of the trl13C hypomorph allele is introduced. While these results suggest a genetic interaction between the expression of the two genes, the evidence that expression translates into a functional interaction that places trl immediately downstream of SOCE is not rigorous or convincing. All that can be said is that the double mutant shows a defect in flight which could arise from an interruption of the circuit. Further, it is not clear whether the trl13C hypomorph is only introduced during the critical 72-96 hour time window when the Orai1E180E phenotype shows up. The same applies to the over-expression of Set2 and the other genes. If the expression is not temporally controlled, then the phenotype could be due to the blockade of an entirely different aspect of flight neuron function.

The idea that Trl functions downstream of Orai-mediated Ca2+ entry in THD’ neurons is based on the following genetic evidence (highlighted in the revised version; see Lines 339-341; 351-367; 647-65; ‘Limitations of the study’: 736-739)

1. In Figure 4D, we show evidence of genetic interaction between trl-STIM and trl-Set2. The rescue of trl13c/STIMKO with STIM overexpression in THD’ neurons indicates that excess SOCE (driven by STIMOE) may activate the residual Trl (there exists a WT Trl copy in this genetic background) to rescue THD’ flight function. This is further supported by the rescue of trl/STIMKO with Set2 overexpression in THD’ neurons, which is consistent with the feedback loop model proposed in Figure 5C (see Lines 390-396) where we propose that reduced SOCE leads to reduced ‘activated’ Trl and thus reduced Set2 expression, and the latter is rescued by SET2OE . The manner in which SOCE ‘activates’ Trl is the subject of ongoing investigations.

2. The trl hypomorphic alleles (including trl13C) exist as genetic mutants and they affect Trl function in all tissues throughout development. While we concede that these mutant alleles would affect multiple functions at other stages of development, which may impinge on the phenotypes noted in Figure S4B, we have used a targeted RNAi approach to validate Trl function specifically in the THD’ neurons (see Figure 4C; Lines 339-341).

3. Overexpression mediated rescues (including Set2) were not induced only during the critical 72-96 hrs APF developmental window. Having established that Orai function drives critical gene expression during this window (Figure 1), it is reasonable to assume that Set2 rescue of loss of flight in OraiE180A occurs in the same time window where flight is disrupted (see Lines 221-224).

4) In Figure 4, data is shown that SOCE compensates for the loss of Trl, the presumed mediator of SOCE-dependent flight. The fact that flight deficits are rescued by raising SOCE in the absence of Trl is very inconsistent with this conclusion.

We apologise for this confusion and have clarified in the revision (see Lines 346-367). trl13c is a recessive allele of Trl and has been written as such throughout the text and in the figures (i.e trl13c and NOT Trl13c). In all cases of Trl mutant rescue by STIMOE and Set2OE there exists residual Trl that can be activated by excess SOCE thus leading to the rescue. This is true for trl13C/ STIMKO where each mutant is present as a heterozygote (the complete genotype of this strain is STIMKO/+; trl13c/+; this has been corrected in the revision). Similarly, for TrlRNAi we expect reduced levels (but not complete loss) of Trl. Thus the SOCE rescue of loss of Trl occurs in conditions where Trl levels are reduced but NOT absent. Homozygous trl null mutants are lethal.

5) In Figure 5 (A-C), data is provided that Trl transcripts are unaffected by loss of SOCE and that overexpression cannot rescue flightlessness. From this, the authors conclude that this gene "must" be calcium responsive. While that is one possibility, it is also possible that these genes are not functionally linked.

The idea that Trl is functionally linked to SOCE is based on the following evidence (included in the revised version- see Lines 339-341; 346-367; 391-396)

1. In Figure 4C we show that flight defects caused by partial loss of Trl (THD’>TrlRNAi) were rescued by STIM overexpression (THD’>TrlRNAi; STIMOE). As mentioned above we have found that STIM overexpression raises SOCE.

2. Heteroalleles of the trl13C hypomorph exhibit a strong genetic interaction with a single copy of the null allele of STIMKO as shown by the flight deficit of trl13c/+; STIMKO/+ (trl13C/STIMKO ) flies (Figure 4D). The genotypes will be corrected in the revision.

3. Flight defects in trl13C/STIMKO flies could be rescued by STIM overexpression in the THD’ neurons (trl13C/STIMKO; THD’>STIMOE)

4. In Figure 4E, we show that partial loss of Trl in THD’ neurons (THD’>TrlRNAi) leads to decreased expression of the Ca2+ responsive genes mAChR, itpr, and Set2 genes indicating that Trl is a constituent of the SOCE-driven transcriptional feedback loop (see Figure 5C).

Since we could not detect a well-defined Ca2+ binding domain in Trl, we hypothesize that it could be activated by a Ca2+ dependent post-translational modification. Phosphoproteome analysis of Trl demonstrated that it does indeed undergo phosphorylation at a Threonine residue (T237; Zhai et al., 2008), which lies within a potential site for CaMKII. Independently, CaMKII has been identified as a binding partner of Trl from a Trl interactome study (Lomaev et al., 2018). Past work from our group (Ravi et al., 2018) identified a role for CaMKII in THD’ neurons in the context of flight. We are currently testing if CaMKII functions downstream of SOCE in THD’ neurons to mediate flight and will update this information in the next version of the manuscript.

Now included in the revised version of the manuscript as Figure S5; Lines 397-424)

6) There is no characterization of SOCE in fpDANs from flies expressing native Orai or the dominant negative OraiE180A mutant. While the authors refer to previous studies, as the manuscript is essentially based on Orai function thapsigargin-induced SOCE should be tested using the Ca2+ add-back protocol in order to assess the release of Ca2+ from the ER in response to thapsigargin as well as the subsequent SOCE.

The fpDANs consist of 16-19 neurons in each hemisphere (PPL1 are 10-12 and PPM3 are 6-7 cells; Pathak et al., 2015). Measuring SOCE from these neurons in vivo is not possible due to the presence of abundant extracellular Ca2+ in the brain. Given their sparse number, it proved technically challenging to isolate the fpDANs in culture to perform SOCE measurements using the Ca2+ add back protocol. Due to these reasons, we have relied upon using Carbachol to elicit IP3-mediated Ca2+ release and SOCE as a proxy for in vivo SOCE. In previous studies we have shown that Carbachol treatment of cultured Drosophila neurons elicits IP3-mediated Ca2+ release and SOCE (Agrawal et al., 2010; Figure 8). Moreover, expression of OraiE180A completely blocks SOCE as measured in primary cultures of dopaminergic neurons (Pathak et al., 2015; Figure 1E). Hence we have not repeated SOCE measurements from all dopaminergic neurons in this work. In the revised version we have explicitly stated this weakness of our study and the reasons for it (See Lines 307-313; ‘Limitations of the study’-Lines 719-735).

7) In the experiments performed to rescue flight duration in Set2RNAi individuals the authors overexpress STIM and attribute the effect to "Excess STIM presumably drives higher SOCE sufficient to rescue flight bout durations caused by deficient Set2 levels.". This should be experimentally tested as the STIM:Orai stoichiometry has been demonstrated as essential for SOCE.

The assumption that STIM overexpression drives higher SOCE is based upon previously published work from Drosophila neurons (Agrawal et al., 2010; Chakraborty et al, 2016; Deb et al., 2016) which demonstrates that excess WT STIM overcomes IP3R deficiencies (RNAi or hypomorphic mutants) to rescue SOCE. We agree that STIM-Orai stoichiometry is essential for SOCE, and propose that the rescue backgrounds possess sufficient WT Orai, which is recruited by the excess STIM to mediate the rescue. We have referenced the earlier work to validate our use of STIMOE for rescue of SOCE (See Lines 226-233).

Here, we propose that Set2 is part of a positive feedback loop (see Lines 286-307) driving transcription of mAChR and IP3R (Figure 3F). In keeping with this hypothesis, we posit that the phenotypes observed in the Set2RNAi background (Figure 2D) result from decreased itpr and mAChR expression (validated in Figure 3E). This is further validated by the Set2 overexpression mediated rescue of OraiE180A (Figure 2D) and rescue of itpr/mAChR expression in the OraiE180A background (Figure 3B-E; THD’>OraiE180A; Set2OE).

8) The authors show that overexpression of OraiE108A results in Stim downregulation at a mRNA level. What about the protein level? And more important, how does OraiE108A downregulate Stim expression? Does it promote Stim degradation? Does it inhibit Stim expression?

We hypothesize that changes in STIM mRNA observed in the THD’ > OraiE180A neurons stems from an overall reduction in IP3-mediated Ca2+ release and SOCE due to loss of Trl-Set2 driven gene expression detailed in our transcriptional feedback loop model (Figure 5C; see Lines 286-307; 581-591). We have attempted to explain this aspect more clearly in the revised version of the manuscript. While we agree that measuring levels of STIM protein would be helpful, estimation of protein levels from a limited number of neurons (~35 cells per brain) is technically challenging. The STIM antibody does not work well in immunohistochemistry. In the absence of any experimental evidence we cannot comment on how expression of OraiE180A might affect STIM protein turnover (see Lines 307-313).

9) Lines 271-273, the authors state "whereas overexpression of a transgene encoding Set2 in THD' neurons either with loss of SOCE (OraiE180A) or with knockdown of the IP3R (itprRNAi), lead to significant rescue of the Ca2+ response". This is attributed to a positive effect of Set2 expression on IP3R expression and the authors show a positive correlation between these two parameters; however, there is no demonstration that Set2 expression can rescue IP3R expression in cells where the IP3R is knocked down (itprRNAi). This should be further demonstrated.

The rescue of IP3R expression by Set2 overexpression in itprRNAi was demonstrated in a different set of Drosophila neurons in an earlier study (Mitra et al., 2021) and has not been repeated specifically in THD’ neurons (see Lines 286-307). Similar to the previous study, here we tested CCh stimulated Ca2+ responses of THD’ neurons with itprRNAi and itprRNAi; SetOE (Fig S3), which are indeed rescued by SET2OE see Lines 280-285)

10) The data presented in Figure 3E should be functionally demonstrated by analyzing the ability of CCh to release Ca2+ from the intracellular stores in the absence of extracellular Ca2+.

CCh-mediated Ca2+ release from the intracellular stores in the absence of extracellular Ca2+ has been described in primary cultures of Drosophila neurons in previously published work (Venkiteswaran and Hasan, 2009; Agrawal et al., 2010) This work focuses on a set of 16-19 dopaminergic neurons in a hemisphere of the Drosophila central brain. It is technically challenging to generate a 0 Ca2+ environment in vivo, which is essential for measuring store Ca2+ release. Given their meagre numbers, primary cultures of these neurons is not readily feasible. (see Lines 307-313; ‘Limitations of the study’-Lines 719-735)

11) The conclusion that SOCE regulates the neuronal excitability threshold is based entirely on either partial behavioral rescue of flight, or measurements of KCl-induced Ca2+ rises monitored by GCaMP6m in DAN neurons. The threshold for neuronal excitability is a precise parameter based on rheobase measurements of action potentials in current-clamp. Measurements of slow calcium signals using a slow dye such as GCaMp6m should not be equated with neuronal excitability. What is measured is a loss of the calcium response in high K depolarization experiments, which occurs due to the loss of expression of Cav channels. Hence, the use of this term is not accurate and will confuse readers. The use of terms referring to neuronal excitability needs to be changed throughout the manuscript. As such, the conclusions regarding neuronal excitability should be strongly tempered and the data reinterpreted as there are no true measurements of neuronal excitability in the manuscript. All that can be said is that expression of certain ion channel genes is suppressed. Since both Na+ channels and K+ channel expression is down-regulated, it is hard to say precisely how membrane excitability is altered without action potential analysis.

The claim that SOCE influences neuronal excitability is based on the following observations:

1. Interruption of the transcriptional feedback loop involving SOCE, Trl, and Set2 through loss of any of its constituents, results in the downregulation of VGCCs (Figure 5G, 6H), which are essential components of action potentials.

2. OraiE180A mediated loss of SOCE in THD’ neurons abrogates the KCl-evoked depolarization response (Figure 6B, C) measured using GCaMP6m. We verified that this response requires VGCC function using pharmacological inhibition of L-type VGCCs (Figure 6E, F).

3. SOCE deficient THD’ neurons, which were presumably compromised in their ability to evoke action potentials could be rescued to undergo KCl-evoked depolarisation by expression of NachBac, which lowers the depolarization threshold (Figure 7C, D) or through optogenetic stimulation using CsChrimson (Figure 7F).

We agree that ‘neuronal excitability threshold’ is a precise electrophysiological parameter that has not been directly investigated here by measurement of action potentials. Therefore, references to neuronal excitability have been tempered throughout the revised manuscript and be replaced with a more generic reference to ‘neuronal activity’. In this context we have included further evidence supporting reduced activity of THD’ neurons upon loss of SOCE in the revision.

Since one of the key functional outcomes of activity during critical developmental periods such as the 72-96 hrs APF developmental window identified in this study, is remodelling of neuronal morphology, we decided to investigate the same in our context. Neuronal activity can drive changes in neurite complexity and axonal arborization (Depetris-Chauvin et al., 2011) especially during critical developmental periods (Sachse et al., 2007). To understand if Orai mediated Ca2+ entry and downstream gene expression through Set2 affects this activity-driven parameter, we investigated the morphology of fpDANs, and specifically measured the complexity of presynaptic terminals within the 2’1 lobe MB using super-resolution microscopy. We found striking changes in the neurite volume upon expression of OraiE180A which could be rescued by restoring either Set2 (OraiE180A; Set2OE) or by inducing hyperactivity through NachBac expression (OraiE180A ; NachBacOE). These data have been included in the revised manuscript (Figure 8 B, C, D; see Lines 481-482; 519-534; 584-591; 701-704).

12) Related, since trl does not contain any molecular domains that could be regulated by Ca2+ signaling, it is unclear whether trl is directly regulated by SOCE or the regulation is highly indirect. Reporter assays evaluating trl activation upon Ca2+ rises would provide much stronger and more direct evidence for the conclusion that trl is a SOCE-regulated TF. As such the evidence is entirely based on RNAi downregulation of trl which indicates that trl is essential but has no bearing on exactly what point of the signaling cascade it is involved.

We agree that luciferase Trl reporters would provide a direct method to test SOCE-mediated activation. Future investigations will be targeted in this direction. Regarding possible mechanisms of Trl activation - since we could not detect a well-defined Ca2+ binding domain in Trl, we hypothesize that it may be phosphorylation by a Ca2+ sensitive kinase. Phosphoproteome analysis of Trl indicates that it does indeed undergo phosphorylation at a Threonine reside (T237; Zhai et al., 2008), which may be mediated by the Ca2+ sensitive kinase-CaMKII based on binding partners identified in the Trl interactome (Lomaev et al., 2018; Past work (Ravi et al., 2018) has indeed demonstrated a requirement for CaMKII in THD’ neurons for flight. We are currently testing whether CaMKII functions downstream of SOCE in these neurons to mediate flight, and will be updating this information in the next version of the manuscript.

New data and analysis has been included - see Figure S5; ‘Limitations of the study’- Lines 397-424; 736-739).

13) Are NFAT levels altered in the Orai1 loss of function mutant? If not, this should be explicitly stated. It would seem based on previous literature that some gene regulation may be related to the downregulation of this established Ca2+-dependent transcription factor. Same for NFkb.

As mentioned in the revised version of the manuscript (see Lines 315-326), Drosophila NFAT lacks a calcineurin binding site and is therefore not sensitive to Ca2+ (Keyser et al., 2007). In the past we tested if knockdown of NF-kB in dopaminergic neurons gave a flight phenotype and did not observe any measurable deficit. From the RNAseq data we find a slight downregulation of NFAT (0.49 fold, p value=0.048) and NF-kb (0.26 fold, p value =0.258) the significance of which is unclear at this point. We did not find any consensus binding sites for these two factors in the regulatory regions of downregulated genes from THD’ neurons.

14) Does over-expression of Set2 restore ion channel expression especially those of the VGCCs? This would provide rigorous, direct evidence that SOCE-mediated regulation of VGCCs through Set2 controls voltage-gated calcium channel signaling.

Set2 overexpression in the OraiE180A background indeed restores the expression of VGCC genes (see Figure 6H; Lines 461-468).

15) All 6 representative panels from Figure 3B are duplicated in Figure 4G. Likewise, 2 representative panels from Figure 5H are duplicated in Figure 6D. Although these panels all represent the results from control experiments, the relevant experiments were likely not conducted at the same time and under the same conditions. Thus, control images from other experiments should not be used simply because they correspond to controls. This situation should be clarified.

We regret the confusion caused by the same representative images for the control experiments. These have been replaced by new representative images for Figure 4G and 6D in the updated version of the manuscript.

16) The figures are unusually busy and difficult to follow. In part this is because they usually have many panels (Fig. 1: A-I; Fig. 2, A-J, etc) but also because the arrangement of the panels is not consistent: sometimes the following panel is found to the right, other times it is below. It would help the reader to make the order of the panels consistent, and, if possible, reduce the number of panels and/or move some of the panels to new figures (eLife does not limit the number of display items).

The image panels have been rearranged for ease of reading in the updated version of the manuscript.

17) As a final recommendation, the reviewers suggest that the authors a- Reword the text that refers to membrane excitability since membrane excitability was not directly measured here. b-Explain why STIM1 rescues the partial loss of flight in Set2 RNAi flies (Fig. S2E); and c- Explain how/why trl is calcium regulated and test using luciferase (or other) reporter assays whether Orai activation leads to trl activation.

a. Textual references to membrane excitability have been appropriately modified and some new data has been included in this regard (see Figure 8 B, C, D; Lines 481-483; 519-534; 584-591; 701-704).

b. We have provided a detailed explanation for how STIM overexpression might rescue the phenotypes caused by Set2RNAi in Point 1 (see Lines 226-233). In short, these phenotypes depend upon IP3R mediated Ca2+ entry driving a transcriptional feedback loop. We relied upon past reports that STIM overexpression upregulates IP3R-mediated Ca2+ release and SOCE in Drosophila itpr mutant neurons (Agrawal et al., 2010; Chakraborty et al, 2016; Deb et al, 2016). We therefore propose that STIM overexpression in the Set2RNAi background rescues IP3R mediated Ca2+ release followed by SOCE, which drives enhanced Set2 transcription, counteracting the effects of the RNAi. We will explain this more clearly with past references in the next revision.

c. We have provided a detailed response to this comment in Point 12. Briefly, we agree that building luciferase reporters for Trl could be an ideal strategy to test for its responsiveness to SOCE and needs to be done in future. As an alternate strategy, we have looked at data from existing studies of interacting partners of Trl (Lomaev et al., 2017) and identified CamKII, which is both Ca2+ responsive (Braun and Schulman, 1995; Yasuda et al., 2022), and thus might activate Trl through a phosphorylation-switch like mechanism (see Figure S5; ‘Limitations of the study’-736-739; Lines 397-424). Moreover, a previous publication identified a requirement for CamKII in THD’ neurons for Drosophila flight (Ravi et al., 2018). We have tested the ability of a dominant active version of CamKII to rescue THD’>E180A flight deficits and have included this information in the next version of the manuscript.

References

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2. Braun AP, Schulman H. A non-selective cation current activated via the multifunctional Ca(2+)-calmodulin-dependent protein kinase in human epithelial cells. J Physiol. 1995. 488:37-55. doi:10.1113/jphysiol.1995.sp020944

3. Chakraborty S, Deb BK, Chorna T, Konieczny V, Taylor CW, Hasan G. Mutant IP3 receptors attenuate store-operated Ca2+ entry by destabilizing STIM-Orai interactions in Drosophila neurons. J Cell Sci. 2016. 129:3903-3910. doi:10.1242/jcs.191585

4. Deb BK, Pathak T, Hasan G. Store-independent modulation of Ca2+ entry through Orai by Septin 7. Nat Commun. 2016. 7:11751. doi:10.1038/ncomms11751

5. Depetris-Chauvin A, Berni J, Aranovich EJ, Muraro NI, Beckwith EJ, Ceriani MF. Adult-specific electrical silencing of pacemaker neurons uncouples molecular clock from circadian outputs. Curr Biol. 2011. 21:1783-1793. doi: 10.1016/j.cub.2011.09.027.

6. Keyser P, Borge-Renberg K, Hultmark D. The Drosophila NFAT homolog is involved in salt stress tolerance. Insect Biochem Mol Biol. 2007. 37:356-362. doi:10.1016/j.ibmb.2006.12.009

7. Kilo L, Stürner T, Tavosanis G, Ziegler AB. Drosophila Dendritic Arborisation Neurons: Fantastic Actin Dynamics and Where to Find Them. Cells. 2021. 10:2777. doi:10.3390/cells10102777

8. Lomaev D, Mikhailova A, Erokhin M, et al. The GAGA factor regulatory network: Identification of GAGA factor associated proteins. PLoS One. 2017. 12:e0173602. doi:10.1371/journal.pone.0173602

9. Mitra R, Richhariya S, Jayakumar S, Notani D, Hasan G. IP3/Ca2+ signals regulate larval to pupal transition under nutrient stress through the H3K36 methyltransferase dSET2. Development. 2021. 148:dev199018. doi:10.1101/2020.11.25.399329

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11. Ravi P, Trivedi D, Hasan G. FMRFa receptor stimulated Ca2+ signals alter the activity of flight modulating central dopaminergic neurons in Drosophila melanogaster. Barsh GS, ed. PLOS Genet. 2018. 14:e1007459. doi:10.1371/journal.pgen.1007459

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Author Response:

Reviewer #1 (Public Review):

Summary:<br /> The global decline of amphibians is primarily attributed to deadly disease outbreaks caused by the chytrid fungus, Batrachochytrium dendrobatidis (Bd). It is unclear whether and how skin-resident immune cells defend against Bd. Although it is well known that mammalian mast cells are crucial immune sentinels in the skin and play a pivotal role in the immune recognition of pathogens and orchestrating subsequent immune responses, the roles of amphibian mast cells during Bd infections are largely unknown. The current study developed a novel way to enrich X. laevis skin mast cells by injecting the skin with recombinant stem cell factor (SCF), a KIT ligand required for mast cell differentiation and survival. The investigators found an enrichment of skin mast cells provides X. laevis substantial protection against Bd and mitigates the inflammation-related skin damage resulting from Bd infection. Additionally, the augmentation of mast cells leads to increased mucin content within cutaneous mucus glands and shields frogs from the alterations to their skin microbiomes caused by Bd.

Strengths:<br /> This study underscores the significance of amphibian skin-resident immune cells in defenses against Bd and introduces a novel approach to examining interactions between amphibian hosts and fungal pathogens.

Weaknesses:<br /> The main weakness of the study is the lack of functional analysis of X. laevis mast cells. Upon activation, mast cells have the characteristic feature of degranulation to release histamine, serotonin, proteases, cytokines, and chemokines, etc. The study should determine whether X. laevis mast cells can be degranulated by two commonly used mast cell activators IgE and compound 48/80 for IgE-dependent and independent pathways. This can be easily done in vitro. It is also important to assess whether in vivo these mast cells are degranulated upon Bd infection using avidin staining to visualize vesicle releases from mast cells. Figure 3 only showed rSCF injection caused an increase in mast cells in naïve skin. They need to present whether Bd infection can induce mast cell increase and rSCF injection under Bd infection causes a mast cell increase in the skin. In addition, it is unclear how the enrichment of mast cells provides protection against Bd infection and alternations to skin microbiomes after infection. It is important to determine whether skin mast cells release any contents mentioned above.

We would like to thank the reviewer for taking the time to review our work and for providing us with valuable feedback.

Please note that amphibians do not possess the IgE antibody isotype1.

To our knowledge there have been no published studies using approaches for studying mammalian mast cell degranulation to examine amphibian mast cells. Notably, several studies suggest that amphibian mast cells lack histamine2, 3, 4, 5 and serotonin2, 6. While there are commercially available kits and reagents for examining mammalian mast cell granule content, most of these reagents may not cross-react with their amphibian counterparts. This is especially true of cytokines and chemokines, which diverged quickly with evolution and thus do not share substantial protein sequence identity across species as divergent as frogs and mammals. Respectfully, while following up on these findings is possible, it would involve considerable additional work to find reagents that would detect amphibian mast cell contents.

We would also like to respectfully point out that while mast cell degranulation is a feature most associated with mammalian mast cells, this is not the only means by which mammalian mast cells confer their immunological effects. While we agree that defining the biology of amphibian mast cell degranulation is important, we anticipate that since the anti-Bd protection conferred by enriching frog mast cells is seen after 21 days of enrichment, it is quite possible that degranulation may not be the central mechanism by which the mast cells are mediating this protection.

As noted in our manuscript, frog mast cells upregulate their expression of interleukin-4 (IL4), which is a hallmark cytokine associated with mammalian mast cells7. We are presently exploring the role of the frog IL4 in the observed mast cell anti-Bd protection. Should we generate meaningful findings in this regard, we will add them to the revised version of this manuscript.

We are also exploring the heparin content of frog mast cells and capacities of these cells to degranulate in vitro in response to compound 48/80. In addition, we are exploring in vivo mast cell degranulation via histology and avidin-staining. Should these studies generate significant findings, we will include them in the revised version of this manuscript.

Per the reviewer’s suggestion, in our revised manuscript we also plan to include data showing whether Bd infections affect skin mast cell numbers and how rSCF injection impacts skin mast cell numbers in the context of Bd infections.

In regard to how mast cells impact Bd infections and skin microbiomes, our data indicate that mast cells are augmenting skin integrity during Bd infections and promoting mucus production, as indicated by the findings presented in Figure 4A-C and Figure 5A-C, respectively. There are several mammalian mast cell products that elicit mucus production. In mammals, this mucus production is mediated by goblet cells while the molecular control of amphibian skin mucus gland content remains incompletely understood. Interleukin-13 (IL13) is the major cytokine associated with mammalian mucus production8, while to our knowledge this cytokine is either not encoded by amphibians or else has yet to be identified and annotated in these animals’ genomes. IL4 signaling also results in mucus production9 and we are presently exploring the possible contribution of the X. laevis IL4 to skin mucus gland filling. Any significant findings on this front will be included in the revised manuscript. Histamine release contributes to mast cell-mediated mucus production10, but as we outline above, several studies indicate that amphibian mast cells may lack histamine2, 3, 4, 5. Mammalian mast cell-produced lipid mediators also play a critical role in eliciting mucus secretion11 and our transcriptomic analysis indicates that frog mast cells express several enzymes associated with production of such mediators. We will highlight this observation in our revised manuscript.

We anticipate that X. laevis mast cells influence skin integrity, microbial composition and Bd susceptibility in a myriad of ways. Considering the substantial differences between amphibian and mammalian evolutionary histories and physiologies, we anticipate that many of the mechanisms by which X. laevis mast cells confer anti-Bd protection will prove to be specific to amphibians and some even unique to X. laevis. We are most interested in deciphering what these mechanisms are but foresee that they will not necessarily reflect what one would expect based on what we know about mammalian mast cells in the context of mammalian physiologies.

Reviewer #2 (Public Review):

Summary:<br /> In this study, Hauser et al investigate the role of amphibian (Xenopus laevis) mast cells in cutaneous immune responses to the ecologically important pathogen Batrachochytrium dendrobatidis (Bd) using novel methods of in vitro differentiation of bone marrow-derived mast cells and in vivo expansion of skin mast cell populations. They find that bone marrow-derived myeloid precursors cultured in the presence of recombinant X. laevis Stem Cell Factor (rSCF) differentiate into cells that display hallmark characteristics of mast cells. They inject their novel (r)SCF reagent into the skin of X. laevis and find that this stimulates the expansion of cutaneous mast cell populations in vivo. They then apply this model of cutaneous mast cell expansion in the setting of Bd infection and find that mast cell expansion attenuates the skin burden of Bd zoospores and pathologic features including epithelial thickness and improves protective mucus production and transcriptional markers of barrier function. Utilizing their prior expertise with expanding neutrophil populations in X. laevis, the authors compare mast cell expansion using (r)SCF to neutrophil expansion using recombinant colony-stimulating factor 3 (rCSF3) and find that neutrophil expansion in Bd infection leads to greater burden of zoospores and worse skin pathology.

Strengths: <br /> The authors report a novel method of expanding amphibian mast cells utilizing their custom-made rSCF reagent. They rigorously characterize expanded mast cells in vitro and in vivo using histologic, morphologic, transcriptional, and functional assays. This establishes solid footing with which to then study the role of rSCF-stimulated mast cell expansion in the Bd infection model. This appears to be the first demonstration of the exogenous use of rSCF in amphibians to expand mast cell populations and may set a foundation for future mechanistic studies of mast cells in the X. laevis model organism. 

We thank the reviewer for recognizing the breadth and extent of the undertaking that culminated in this manuscript. Indeed, this manuscript would not have been possible without considerable reagent development and adaptation of techniques that had previously not been used for amphibian immunity research. In line with the reviewer’s sentiment, to our knowledge this is the first report of using molecular approaches to augment amphibian mast cells, which we hope will pave the way for new areas of research within the fields of comparative immunology and amphibian disease biology.

Weaknesses:<br /> The conclusions regarding the role of mast cell expansion in controlling Bd infection would be stronger with a more rigorous evaluation of the model, as there are some key gaps and remaining questions regarding the data. For example:

1. Granulocyte expansion is carefully quantified in the initial time courses of rSCF and rCSF3 injections, but similar quantification is not provided in the disease models (Figures 3E, 4G, 5D-G). A key implication of the opposing effects of mast cell vs neutrophil expansion is that mast cells may suppress neutrophil recruitment or function. Alternatively, mast cells also express notable levels of csfr3 (Figure 2) and previous work from this group (Hauser et al, Facets 2020) showed rG-CSF-stimulated peritoneal granulocytes express mast cell markers including kit and tpsab1, raising the question of what effect rCSF3 might have on mast cell populations in the skin. Considering these points, it would be helpful if both mast cells and neutrophils were quantified histologically (based on Figure 1, they can be readily distinguished by SE or Giemsa stain) in the Bd infection models.

We thank the reviewer for this insightful suggestion. We are performing a further examination of skin granulocyte content during Bd infections and plan on including any significant findings in our revised manuscript.

We predict that rSCF administration results in the accumulation of mast cells that are polarized such that they ablate the inflammatory response elicited by Bd infection. Mammalian mast cells, including peritonea-resident mast cells, express csf3r12, 13. Although the X. laevis animal model does not permit nearly the degree of immune cell resolution afforded by mammalian animal models, we do know that the adult X. laevis peritonea contain heterogenous leukocyte populations. We anticipate that the high kit expression reported by Hauser et al., 2020 in the rCSF3-recruited peritoneal leukocytes reflects the presence of mast cells therein. As such and in acknowledgement of the reviewer’s suggestion, we also think that the cells recruited by rCSF3 into the skin may include not only neutrophils but also mast cells. Possibly, these mast cells have distinct polarization states from those enriched by rSCF. While the lack of antibodies against frog neutrophils or mast cells has limited our capacity to address this question, we will attempt to reexamine by histology the proportions of skin neutrophils and mast cells in the skins of frogs under the conditions described in our manuscript. Any new findings in this regard will be included in the revised version of this work.

2. Epithelial thickness and inflammation in Bd infection are reported to be reduced by rSCF treatment (Figure 3E, 5A-B) or increased by rCSF3 treatment (Figure 4G) but quantification of these critical readouts is not shown.

We thank the reviewer for this suggestion. We will score epithelial thickness under the distinct conditions described in our manuscript and present the quantified data in the revised paper.

3. Critical time points in the Bd model are incompletely characterized. Mast cell expansion decreases zoospore burden at 21 dpi, while there is no difference at 7 dpi (Figure 3E). Conversely, neutrophil expansion increases zoospore burden at 7 dpi, but no corresponding 21 dpi data is shown for comparison (Figure 4G). Microbiota analysis is performed at a third time point,10 dpi (Figure 5D-G), making it difficult to compare with the data from the 7 dpi and 21 dpi time points. Reporting consistent readouts at these three time points is important to draw solid conclusions about the relationship of mast cell expansion to Bd infection and shifts in microbiota.

Because there were no significant effects of mast cell enrichment at 7 days post Bd infection, we chose to look at the microbiome composition in a subsequent experiment at 10 days and 21 days post Bd infection, with 10 days being a bit more of a midway point between the initial exposure and day 21, when we see the effect on Bd loads. We will clarify this rationale in the revised manuscript.

The enrichment of neutrophils in frog skins resulted in prompt (12 hours post enrichment) skin thickening (in absence of Bd infection) and increased frog Bd susceptibility by 7 days of infection. Conversely, mast cell enrichment stabilized skin mucosal and symbiotic microbial environment, presumably accounting at least in part for the lack of further Bd growth on mast cell-enriched animals by 21 days of infection. Our question regarding the roles of inflammatory granulocytes/neutrophils during Bd infections was that of ‘how’ rather ‘when’ these cells affect Bd infections. Because the central focus of this work was mast cells and not other granulocyte subsets, when we saw that rCSF3-recruited granulocytes adversely affected Bd infections at 7 days post infection, we did not pursue the kinetics of these responses further. We plan to explore the roles of inflammatory mediators and disparate frog immune cell subsets during the course of Bd infections, but we feel that these future studies are more peripheral to the central thesis of the present manuscript regarding the roles of frog mast cells during Bd infections.

4. Although the effect of rSCF treatment on Bd zoospores is significant at 21 dpi (Figure 3E), bacterial microbiota changes at 21 dpi are not (Figure S3B-C). This discrepancy, how it relates to the bacterial microbiota changes at 10 dpi, and why 7, 10, and 21 dpi time points were chosen for these different readouts (Figure 5F-G), is not discussed.

Our results indicate that after 10 days of Bd infection, control Bd-challenged animals exhibited reduced microbial richness, while skin mast cell-enriched Bd-infected frogs were protected from this disruption of their microbiome. The amphibian microbiome serves as a major barrier to these fungal infections14, and we anticipate that Bd-mediated disruption of microbial richness and composition facilitates host skin colonization by this pathogen. Control and mast cell-enriched animals had similar skin Bd loads at 10 days post infection. However, by 21 days of Bd infection the mast cells-enriched animals maintained their Bd loads to levels observed at 10 days post infection, whereas the control animals had significantly greater Bd loads. Thus, we anticipate that frog mast cells are conferring the observed anti-Bd protection in part by preventing microbial disassembly and thus interfering with optimal Bd colonization and growth on frog skins. In other words, maintained microbial composition at 10 days of infection may be preventing additional Bd colonization/growth, as seen when comparing skins of control and mast cell-enriched frogs at 21 days post infection. By 21 days of infection, control animals rebounded from the Bd-mediated reduction in bacterial richness seen at 10 days. Considering that after 21 days of infection control animals also had significantly greater Bd loads than mast-cell enriched animals suggests that there may be a critical earlier window during which microbial composition is able to counteract _Bd_growth. 

While the current draft of our manuscript has a paragraph to this effect (see below), we appreciate the reviewer conveying to us that our perspective on the relationship between skin mast cells and the kinetics of microbial composition and _Bd_loads could be better emphasized. We plan to revise our manuscript to include the above discussion points. 

Bd infections caused major reductions in bacterial taxa richness, changes in composition and substantial increases in the relative abundance of Bd-inhibitory bacteria early in the infection. Similar changes to microbiome structure occur during experimental Bd infections of red-backed salamanders and mountain yellow-legged frogs15, 16. In turn, progressing Bd_infections corresponded with a return to baseline levels of _Bd-inhibitory bacteria abundance and rebounding microbial richness, albeit with dissimilar communities to those seen in control animals. These temporal changes indicate that amphibian microbiomes are dynamic, as are the effects of Bd infections on them. Indeed, Bd infections may have long-lasting impacts on amphibian microbiomes15. While Bd infections manifested in these considerable changes to frog skin microbiome structure, mast cell enrichment appeared to counteract these deleterious effects to their microbial composition. Presumably, the greater skin mucosal integrity and mucus production observed after mast cell enrichment served to stabilize the cutaneous environment during Bd infections, thereby ameliorating the Bd-mediated microbiome changes. While this work explored the changes in established antifungal flora, we anticipate the mast cell-mediated inhibition of Bd may be due to additional, yet unidentified bacterial or fungal taxa. Intriguingly, while mammalian skin mast cell functionality depends on microbiome elicited SCF production by keratinocytes17, our results indicate that frog skin mast cells in turn impact skin microbiome structure and likely their function. It will be interesting to further explore the interdependent nature of amphibian skin microbiomes and resident mast cells.

5. The time course of rSCF or rCSF3 treatments relative to Bd infection in the experiments is not clear. Were the treatments given 12 hours prior to the final analysis point to maximize the effect? For example, in Figure 3E, were rSCF injections given at 6.5 dpi and 20.5 dpi? Or were treatments administered on day 0 of the infection model? If the latter, how do the authors explain the effects at 7 dpi or 21 dpi given mast cell and neutrophil numbers return to baseline within 24 hours after rSCF or rCSF3 treatment, respectively?

Please find the schematic of the immune manipulation, Bd infection, and sample collection times below. We will include a figure like this in our revised manuscript.

The title of the manuscript may be mildly overstated. Although Bd infection can indeed be deadly, mortality was not a readout in this study, and it is not clear from the data reported that expanding skin mast cells would ultimately prevent progression to death in Bd infections.

We acknowledge this point. The revised manuscript will be titled: “Amphibian mast cells: barriers to chytrid fungus infections”.

Reviewer #3 (Public Review):

Summary:<br /> Hauser et al. provide an exceptional study describing the role of resident mast cells in amphibian epidermis that produce anti-inflammatory cytokines that prevent Batrachochytrium dendrobatidis (Bd) infection from causing harmful inflammation, and also protect frogs from changes in skin microbiomes and loss of mucin in glands and loss of mucus integrity that otherwise cause changes to their skin microbiomes. Neutrophils, in contrast, were not protective against Bd infection. Beyond the beautiful cytology and transcriptional profiling, the authors utilized elegant cell enrichment experiments to enrich mast cells by recombinant stem cell factor, or to enrich neutrophils by recombinant colony-stimulating factor-3, and examined respective infection outcomes in Xenopus.

Strengths:<br /> Through the use of recombinant IL4, the authors were able to test and eliminate the hypothesis that mast cell production of IL4 was the mechanism of host protection from Bd infection. Instead, impacts on the mucus glands and interaction with the skin microbiome are implicated as the protective mechanism. These results will press disease ecologists to examine the relative importance of this immune defense among species, the influence of mast cells on the skin microbiome and mucosal function, and open the potential for modulating mucosal defense.

We thank the reviewer for recognizing the significance and utility of the findings presented in our manuscript.

Weaknesses:<br /> A reduction of bacterial diversity upon infection, as described at the end of the results section, may not always be an "adverse effect," particularly given that anti-Bd function of the microbiome increased. Some authors (see Letourneau et al. 2022 ISME, or Woodhams et al. 2023 DCI) consider these short-term alterations as encoding ecological memory, such that continued exposure to a pathogen would encounter an enriched microbial defense. Regardless, mast cell-initiated protection of the mucus layer may negate the need for this microbial memory defense.

We thank the reviewer their insightful comment. We will revise our discussion to include this possible interpretation.

While the description of the mast cell location in the epidermal skin layer in amphibians is novel, it is not known how representative these results are across species ranging in chytridiomycosis susceptibility. No management applications are provided such as methods to increase this defense without the use of recombinant stem cell factor, and more discussion is needed on how the mast cell component (abundance, distribution in the skin) of the epidermis develops or is regulated.

We appreciate the reviewer’s comment and would like to point out that the work presented in our manuscript was driven by comparative immunology questions more than by conservation biology.

We thank the reviewer for suggesting expanding our discussion to include potential management applications and potential mechanisms for regulating frog skin mast cells. While any content to these effects would be highly speculative, we agree that it may spark new interest and pave new avenues for research. To this end, our revised manuscript will include a paragraph to this effect.

References:

1. Flajnik, M.F. A cold-blooded view of adaptive immunity. Nat Rev Immunol 18, 438-453 (2018).

2. Mulero, I., Sepulcre, M.P., Meseguer, J., Garcia-Ayala, A. & Mulero, V. Histamine is stored in mast cells of most evolutionarily advanced fish and regulates the fish inflammatory response. Proc Natl Acad Sci U S A 104, 19434-19439 (2007).

3. Reite, O.B. A phylogenetical approach to the functional significance of tissue mast cell histamine. Nature 206, 1334-1336 (1965).

4. Reite, O.B. Comparative physiology of histamine. Physiol Rev 52, 778-819 (1972).

5. Takaya, K., Fujita, T. & Endo, K. Mast cells free of histamine in Rana catasbiana. Nature 215, 776-777 (1967).

6. Galli, S.J. New insights into "the riddle of the mast cells": microenvironmental regulation of mast cell development and phenotypic heterogeneity. Lab Invest 62, 5-33 (1990).

7. Babina, M., Guhl, S., Artuc, M. & Zuberbier, T. IL-4 and human skin mast cells revisited: reinforcement of a pro-allergic phenotype upon prolonged exposure. Archives of dermatological research 308, 665-670 (2016).

8. Lai, H. & Rogers, D.F. New pharmacotherapy for airway mucus hypersecretion in asthma and COPD: targeting intracellular signaling pathways. J Aerosol Med Pulm Drug Deliv 23, 219-231 (2010).

9. Rankin, J.A. et al. Phenotypic and physiologic characterization of transgenic mice expressing interleukin 4 in the lung: lymphocytic and eosinophilic inflammation without airway hyperreactivity. Proc Natl Acad Sci U S A 93, 7821-7825 (1996).

10. Church, M.K. Allergy, Histamine and Antihistamines. Handb Exp Pharmacol 241, 321-331 (2017).

11. Nakamura, T. The roles of lipid mediators in type I hypersensitivity. J Pharmacol Sci 147, 126-131 (2021).

12. Aponte-Lopez, A., Enciso, J., Munoz-Cruz, S. & Fuentes-Panana, E.M. An In Vitro Model of Mast Cell Recruitment and Activation by Breast Cancer Cells Supports Anti-Tumoral Responses. Int J Mol Sci 21 (2020).

13. Jamur, M.C. et al. Mast cell repopulation of the peritoneal cavity: contribution of mast cell progenitors versus bone marrow derived committed mast cell precursors. BMC Immunol 11, 32 (2010).

14. Walke, J.B. & Belden, L.K. Harnessing the Microbiome to Prevent Fungal Infections: Lessons from Amphibians. PLoS Pathog 12, e1005796 (2016).

15. Jani, A.J. et al. The amphibian microbiome exhibits poor resilience following pathogen-induced disturbance. ISME J 15, 1628-1640 (2021).

16. Muletz-Wolz, C.R., Fleischer, R.C. & Lips, K.R. Fungal disease and temperature alter skin microbiome structure in an experimental salamander system. Mol Ecol 28, 2917-2931 (2019).

17. Wang, Z. et al. Skin microbiome promotes mast cell maturation by triggering stem cell factor production in keratinocytes. J Allergy Clin Immunol 139, 1205-1216 e1206 (2017).

Author response:

The following is the authors’ response to the previous reviews

eLife Assessment

For decades it has been accepted that only the growth-arrested "stumpy" form of Trypanosoma brucei can infect the arthropod vector, the Tsetse fly, but this was recently challenged by a demonstration that - under artificial conditions that are known to enhance infectivity - the proliferative "slender" form can also establish Tsetse infections. The infectiousness of the two forms is a fundamental question in trypanosome biology and epidemiology, concerning both infection dynamics and parasite differentiation. The authors of the current study provide compelling evidence that without artificial enhancement, the "stumpy" form is indeed much more infective for Tsetse than the slender form; they suggest that this is probably also true in the wild.

Since the authors of this paper did not themselves test the effect of enhancing conditions, the precise reason for the discrepancy in results between the two laboratories has not been demonstrated conclusively.

This specific comment was addressed in the revision and illustrated with new data.

Differences between the strain clones, the cell culture conditions and/or the fly colony maintenance conditions could explain part of the differences in infection rates observed here as compared to the Schuster et al. study (1). However, the use of the lectin-inhibitory sugar N-acetyl-glucosamine to enhance infection rates in the latter study could be a more likely explanation. To assess this hypothesis, an additional experimental challenge was performed to compare infection rates in teneral versus adult flies, with or without N-acetyl-glucosamine supplement in an infective meal containing 10⁵ slender parasites / ml (Figure 2). Whereas no infection was detected in adult flies, the N-acetyl-glucosamine supplementation of the infective meal led to an increase of the infection rates from 2,4% to 13,3% in teneral flies (Figure 2).

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Ngoune et al. present compelling evidence that Slender cells are challenged to infect tsetse flies. They explore the experimental context of a recent important paper in the field, Schuster et al., that presents evidence suggesting the proliferative Slender bloodstream T.brucei can infect juvenile tsetse flies. Schuster et al. was disruptive to the widely accepted paradigm that the Stumpy bloodstream form is solely responsible for tsetse infection and T.brucei transmission potential. Evidence presented here shows that in all cases, Stumpy form parasites are exponentially more capable of infecting tsetse flies. They further show that Slender cells do not infect mature flies.

However, they raise questions of immature tsetse immunological potential and field transmission potential that their experiments do not address. Specifically, they do not show that teneral tsetse flies are immunocompromised, that tsetse flies must be immunocompromised for Slender infection nor that younger teneral tsetse infection is not pertinent to field transmission.

All these specific comments were addressed in the revision and illustrated with new data and references.

- The limited immunocompetence of teneral flies has been extensively studied by the labs of S. Aksoy at Yale and M. Lehane at Liverpool. In the discussion, we provide key references from these two labs 19-22.

- Differences between the strain clones, the cell culture conditions and/or the fly colony maintenance conditions could explain part of the differences in infection rates observed here as compared to the Schuster et al. study (1). However, the use of the lectin-inhibitory sugar N-acetyl-glucosamine to enhance infection rates in the latter study could be a more likely explanation. To assess this hypothesis, an additional experimental challenge was performed to compare infection rates in teneral versus adult flies, with or without N-acetyl-glucosamine supplement in an infective meal containing 10⁵ slender parasites / ml (Figure 2). Whereas no infection was detected in adult flies, the N-acetyl-glucosamine supplementation of the infective meal led to an increase of the infection rates from 2,4% to 13,3% in teneral flies (Figure 2).

- Our comment on the relevance to field transmission is simply based on field observations of the fly biology. For example, according to the capture-recapture experiments described in HARGROVE JW insect sci applic 1990 (new ref 23), wild female mortality was reported 6.8% shortly after emergence, <1% for ages 20-50 days and rose to 5% by 130 day (a pattern similar to that for laboratory reared tsetse), while wild male daily mortality was 8.3% after emergence, fell to 5.5% by 9 days, then rose continuously to more than 10% by 30 days. This means that adult flies represent the majority of individuals in a wild tsetse population. Hence, knowing that both males and females are strictly hematophagous and that they can live up to nine months, the impact of teneral flies (up to 4 days after emergence) on trypanosome transmission appears limited, if not incidental.

Strengths:

Experimental Design is precise and elegant, outcomes are convincing. Discussion is compelling and important to the field. This is a timely piece that adds important data to a critical discussion of host:parasite interactions, of relevance to all parasite transmission.

Thank you

Weaknesses:

As above, the authors dispute the biological relevance of teneral tsetse infection in the wild, without offering evidence to the contrary. Statements need to be softened for claims regarding immunological competence or relevance to field transmission.

All these specific comments were addressed in the revision and illustrated with new data and references.

- The limited immunocompetence of teneral flies has been extensively studied by the labs of S. Aksoy at Yale and M. Lehane at Liverpool. In the discussion, we provide key references from these two labs 19-22.

- Differences between the strain clones, the cell culture conditions and/or the fly colony maintenance conditions could explain part of the differences in infection rates observed here as compared to the Schuster et al. study (1). However, the use of the lectin-inhibitory sugar N-acetyl-glucosamine to enhance infection rates in the latter study could be a more likely explanation. To assess this hypothesis, an additional experimental challenge was performed to compare infection rates in teneral versus adult flies, with or without N-acetyl-glucosamine supplement in an infective meal containing 10⁵ slender parasites / ml (Figure 2). Whereas no infection was detected in adult flies, the N-acetyl-glucosamine supplementation of the infective meal led to an increase of the infection rates from 2,4% to 13,3% in teneral flies (Figure 2).

- Our comment on the relevance to field transmission is simply based on field observations of the fly biology. For example, according to the capture-recapture experiments described in HARGROVE JW insect sci applic 1990 (new ref 23), wild female mortality was reported 6.8% shortly after emergence, <1% for ages 20-50 days and rose to 5% by 130 day (a pattern similar to that for laboratory reared tsetse), while wild male daily mortality was 8.3% after emergence, fell to 5.5% by 9 days, then rose continuously to more than 10% by 30 days. This means that adult flies represent the majority of individuals in a wild tsetse population. Hence, knowing that both males and females are strictly hematophagous and that they can live up to nine months, the impact of teneral flies (up to 4 days after emergence) on trypanosome transmission appears limited, if not incidental.

Reviewer #2 (Public Review):

Summary:

In contrast to the recent findings reported by Schuster S et al., this brief paper presents evidence suggesting that the stumpy form of T. brucei is likely the most pre-adapted form to progress through the life cycle of this parasite in the tsetse vector.

Strengths:

One significant experimental point is that all fly infection experiments are conducted in the absence of "boosting" metabolites like GlcNAc or S-glutathione. As a result, flies infected with slender trypanosomes present very low or nonexistent infection rates. This provides important experimental evidence that the findings of Schuster S and colleagues may need to be revisited.

Thank you

Weaknesses:

However, I believe the authors should have included their own set of experiments demonstrating that the presence of these metabolites in the infectious bloodmeal enhances infection rates in flies receiving blood meals containing slender trypanosomes. Considering the well-known physiological variabilities among flies from different facilities, including infection rates, this would have strengthened the experimental evidence presented by the authors.

This specific comment was addressed in the revision and illustrated with new data.

Differences between the strain clones, the cell culture conditions and/or the fly colony maintenance conditions could explain part of the differences in infection rates observed here as compared to the Schuster et al. study (1). However, the use of the lectin-inhibitory sugar N-acetyl-glucosamine to enhance infection rates in the latter study could be a more likely explanation. To assess this hypothesis, an additional experimental challenge was performed to compare infection rates in teneral versus adult flies, with or without N-acetyl-glucosamine supplement in an infective meal containing 10⁵ slender parasites / ml (Figure 2). Whereas no infection was detected in adult flies, the N-acetyl-glucosamine supplementation of the infective meal led to an increase of the infection rates from 2,4% to 13,3% in teneral flies (Figure 2).

Reviewer #3 (Public Review):

The dogma in the Trypanosome field is that transmission by Tsetse flies is ensured by stumpy forms. This has been recently challenged by the Engstler lab (Schuster et al.), who showed that slender forms can also be transmitted by teneral flies. In this work, the authors aimed to test whether transmission by slender forms is possible and frequent. The authors observed that most stumpy forms infections with teneral and adult flies were successful while only 1 out of 24 slender form infections were successful.

In this revised version of the manuscript, the authors made some text changes and included statistical testing as a new section of the Materials and Methods. It seems the comparison of midgut infection in adult vs teneral flies was significant in most of the conditions. However, the critical comparison is still missing: within each type of fly (adult or teneral), was the MG infection significantly different between slender and stumpy forms?

An ANOVA statistical analysis was performed and a dedicated section added to the revised version. MG infection rate comparisons were statistically significant between teneral and adult flies infected with ST in each amount (p<0.02 with 10 parasites; p<0.0001 with 100 and 1,000 parasites) and with 1,000 SL (p<0.0001). MG infection rate comparisons were statistically significant (p<0.0001) between parasite stages (SL and ST) in each amount (10, 100 and 1,000) and for each fly group (teneral and adult), excepted in teneral flies infected with 1,000 parasites (p=0.2356).

Given no additional experiments were performed, it remains unknown why this work and Schuster et al. reached different conclusions. As a result it remains unclear in which conditions slender forms could be important for transmission. Several variables could explain differences between the two groups: the strain used, the presence or absence of N-acetylglucosamine and/or glutathione, how Tsetse colonies were maintained, thorough molecular and cellular characterisation of slender and stumpy forms (to avoid using intermediate forms as slender forms), comparison to recent field parasite strains.

This specific comment was addressed in the revision and illustrated with new data.

Differences between the strain clones, the cell culture conditions and/or the fly colony maintenance conditions could explain part of the differences in infection rates observed here as compared to the Schuster et al. study (1). However, the use of the lectin-inhibitory sugar N-acetyl-glucosamine to enhance infection rates in the latter study could be a more likely explanation. To assess this hypothesis, an additional experimental challenge was performed to compare infection rates in teneral versus adult flies, with or without N-acetyl-glucosamine supplement in an infective meal containing 10⁵ slender parasites / ml (Figure 2). Whereas no infection was detected in adult flies, the N-acetyl-glucosamine supplementation of the infective meal led to an increase of the infection rates from 2,4% to 13,3% in teneral flies (Figure 2).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

The manuscript is improved, but the author has not addressed much of the constructive criticism offered that would benefit the manuscript.

To clarify, evidence from Schuster et al did not demonstrate, rather it suggested. That is a major point of this paper - that the previous evidence presented had caveats. Terms such as demonstrate or prove are inappropriate in most biological contexts, unless evidence is without caveat.

This specific comment was addressed in the revision and illustrated with new data.

Differences between the strain clones, the cell culture conditions and/or the fly colony maintenance conditions could explain part of the differences in infection rates observed here as compared to the Schuster et al. study (1). However, the use of the lectin-inhibitory sugar N-acetyl-glucosamine to enhance infection rates in the latter study could be a more likely explanation. To assess this hypothesis, an additional experimental challenge was performed to compare infection rates in teneral versus adult flies, with or without N-acetyl-glucosamine supplement in an infective meal containing 10⁵ slender parasites / ml (Figure 2). Whereas no infection was detected in adult flies, the N-acetyl-glucosamine supplementation of the infective meal led to an increase of the infection rates from 2,4% to 13,3% in teneral flies (Figure 2).

Statements regarding teneral flies in the field are softened. Yet the referenced papers pertain more to commensurate coinfections rather than reduced immunocapacity of immature teneral flies in the field. This should be clarified.

The limited immunocompetence of teneral flies has been extensively studied by the labs of S. Aksoy at Yale and M. Lehane at Liverpool. In the discussion, we provide key references from these two labs 19-22.

The text remains convoluted to read with grammatical errors in places. For example, it is incorrect to begin a sentence with However. There are far too many run-on sentences in the manuscript that confuse this straightforward story.

The revised text was improved as much as possible.

All text requires grammatical refinement and softer claims unless additional experiments are undertaken.

Reviewer #2 (Recommendations For The Authors):

I continue to endorse the publication of this manuscript; however, I am somewhat disappointed by the authors' justifications for not conducting additional experiments or exploring other factors that might influence the infection phenotypes in the fly.

This specific comment was addressed in the revision and illustrated with new data.

Differences between the strain clones, the cell culture conditions and/or the fly colony maintenance conditions could explain part of the differences in infection rates observed here as compared to the Schuster et al. study (1). However, the use of the lectin-inhibitory sugar N-acetyl-glucosamine to enhance infection rates in the latter study could be a more likely explanation. To assess this hypothesis, an additional experimental challenge was performed to compare infection rates in teneral versus adult flies, with or without N-acetyl-glucosamine supplement in an infective meal containing 10⁵ slender parasites / ml (Figure 2). Whereas no infection was detected in adult flies, the N-acetyl-glucosamine supplementation of the infective meal led to an increase of the infection rates from 2,4% to 13,3% in teneral flies (Figure 2).

Author response:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors performed an integration of 48 scRNA-seq public datasets and created a single-cell transcriptomic atlas for AML (222 samples comprising 748,679 cells). This is important since most AML scRNA-seq studies suffer from small sample size coupled with high heterogeneity. They used this atlas to further dissect AML with t(8;21) (AML-ETO/RUNX1-RUNX1T1), which is one of the most frequent AML subtypes in young people. In particular, they were able to predict Gene Regulatory Networks in this AML subtype using pySCENIC, which identified the paediatric regulon defined by a distinct group of hematopoietic transcription factors (TFs) and the adult regulon for t(8;21). They further validated this in bulk RNA-seq with AUCell algorithm and inferred prenatal signature to 5 key TFs (KDM5A, REST, BCLAF1, YY1, and RAD21), and the postnatal signature to 9 TFs (ENO1, TFDP1, MYBL2, KLF1, TAGLN2, KLF2, IRF7, SPI1, and YXB1). They also used SCENIC+ to identify enhancer-driven regulons (eRegulons), forming an eGRN, and found that prenatal origin shows a specific HSC eRegulon profile, while a postnatal origin shows a GMP profile. They also did an in silico perturbation and found AP-1 complex (JUN, ATF4, FOSL2), P300, and BCLAF1 as important TFs to induce differentiation. Overall, I found this study very important in creating a comprehensive resource for AML research.

Strengths:

(1) The generation of an AML atlas integrating multiple datasets with almost 750K cells will further support the community working on AML.

(2) Characterisation of t(8;21) AML proposes new interesting leads.

We thank the reviewer for a succinct summary of our work and highlighting its strengths.

Weaknesses:

Were these t(8;21) TFs/regulons identified from any of the single datasets? For example, if the authors apply pySCENIC to any dataset, would they find the same TFs, or is it the increase in the number of cells that allows identification of these?

The purpose of our study was to gain biological insights by integrating multiple datasets, to overcome limitations from small sample size. We expect that the larger dataset would improve network inference, which is what we implemented in the manuscript, hence we have not looked at individual datasets. However, we will investigate this further in the revised manuscript by running pySCENIC on individual datasets and comparing to the results drawn from the whole atlas.

Reviewer #2 (Public review):

Summary:

The authors assemble 222 publicly available bone marrow single-cell RNA sequencing samples from healthy donors and primary AML, including pediatric, adolescent, and adult patients at diagnosis. Focusing on one specific subtype, t(8;21), which, despite affecting all age classes, is associated with better prognosis and drug response for younger patients, the authors investigate if this difference is reflected also in the transcriptomic signal. Specifically, they hypothesize that the pediatric and part of the young population acquires leukemic mutations in utero, which leads to a different leukemogenic transformation and ultimately to differently regulated leukemic stem cells with respect to the adult counterpart. The analysis in this work heavily relies on regulatory network inference and clustering (via SCENIC tools), which identifies regulatory modules believed to distinguish the pre-, respectively, post-natal leukemic transformation. Bulk RNA-seq and scATAC-seq datasets displaying the same signatures are subsequently used for extending the pool of putative signature-specific TFs and enhancer elements. Through gene set enrichment, ontology, and perturbation simulation, the authors aim to interpret the regulatory signatures and translate them into potential onset-specific therapeutic targets. The putative pre-natal signature is associated with increased chemosensitivity, RNA splicing, histone modification, stem-ness marker SMARCA2, and potentially maintained by EP300 and BCLAF1.

Strengths:

The main strength of this work is the compilation of a pediatric AML atlas using the efficient Cellxgene interface. Also, the idea of identifying markers for different disease onsets, interpreting them from a developmental angle, and connecting this to the different therapy and relapse observations, is interesting. The results obtained, the set of putative up-regulated TFs, are biologically coherent with the mechanisms and the conclusions drawn. I also appreciate that the analysis code was made available and is well documented.

We thank the reviewer for reviewing our work, and highlighting its key features, including creation of AML atlas, downstream analysis and interpretation for t(8;21) subtype.

We also appreciate useful critique of our paper provided below.

Weaknesses:

There were fundamental flaws in how methods and samples were applied, a general lack of critical examination of both the results and the appropriateness of the methods for the data at hand, and in how results were presented. In particular:

(1) Cell type annotation:

a) The 2-phase cell type annotation process employed for the scRNA-seq sample collection raised concerns. Initially annotated cells are re-labeled after a second round with the same cell types from the initial label pool (Figure 1E). The automatic annotation tools were used without specifying the database and tissue atlases used as a reference, and no information was shown regarding the consensus across these tools.

We believe that most of the reviewer’s criticisms stem from a misunderstanding, and we apologize for not explaining certain aspects of our work more clearly.

The two types of cell type annotation applied were different and served distinct purposes:

• One was using general bone marrow/blood reference datasets to annotate blood subtype lineage clusters.

• The other was using a CD34 purified AML specific reference dataset which included leukaemia-associated annotations, to identify HSPC subpopulations. We also implemented this on a single-cell level to allow more robust identification of these rare populations in a large dataset.

This is probably not well explained in the methods and figure presentation. We will clearly indicate in the revised manuscript that different HSPC annotations represent separate analysis and will update the figures to highlight this. We will provide a comprehensive review of the annotation strategies implemented, including the automated tool outputs, which may be useful for the single-cell community.

b) Expression of the CD34 marker is only reported as a selection method for HSPCs, which is not in line with common practice. The use of only is admitted as a surface marker, while robust annotation of HSPCs should be done on the basis of expression of gene sets.

We used CD34 expression in conjunction with other cell type annotations and marker sets to identify LSCs, although results are same when we use HSPC annotated cells without condition on CD34 expression.  In the revised manuscript, we will simplify this analysis to use HSPC clusters as suggested by the reviewer.

c) During several analyses, the cell types used were either not well defined or contradictory, such as in Figure 2D, where it is not clear if pySCENIC and AUC scores were computed on HSPCs alone or merged with CMPs. In other cases, different cell type populations are compared and used interchangeably: comparing the HSPC-derived regulons with bulk (probably not enriched for CD34+ cells) RNA samples could be an issue if there are no valid assumptions on the cell composition of the bulk sample.

As mentioned in the Methods, we only excluded lymphoid cell types from the pySCENIC analysis to overcome the bias that some samples were enriched using CD34 selection when preparing them for scRNA-seq. We will make this clearer in the text and figures of the revised manuscript. It is difficult to overcome this bias when using bulk RNA samples, which may explain why some of our samples do not fit into our defined signature groups. However, as we do not have access to primary samples ourselves, we cannot provide a better matched experimental cohort for validation.

(2) Method selection:

a) The authors should explain why they use pySCENIC and not any other approach. They should briefly explain how pySCENIC works and what they get out in the main text. In addition they should explain the AUCell algorithm and motivate its usage.

pySCENIC is state-of-the-art method for network inference from scRNA data and is widely used within the single-cell community (over 5000 citations for both versions of the SCENIC pipeline). The pipeline has been benchmarked as one of the top performers for GRN analysis (Nguyen et al, 2021. Briefings in Bioinformatics). AUCELL is a module within the pySCENIC pipeline to summarise the activity of a set of genes (a regulon) into a single number which helps compare and visualise different regulons. We agree with reviewer that this could have been more clearly explained within the manuscript. We will update text in the revised manuscript to add more explanation.

b) The obtained GRN signatures were not critically challenged on an external dataset. Therefore, the evidence that supports these signatures to be reliable and significant to the investigated setting is weak.

These signatures were inferred from the best suitable AML single-cell RNA datasets available to date, and we used two independent datasets to validate our findings (the TARGET AML bulk RNA sequencing cohort, and the Lambo et al. scRNA-seq dataset). To our knowledge, there are no other better suited datasets for validation. Experimental validations on patient samples are beyond the scope of this study.

(3) There are some issues with the analysis & visualization of the data.

We will provide new statistical tests to improve robustness of the analysis as well as presentation and visualization of the data in the revised manuscript.

(4) Discussion:

a) What exactly is the 'regulon signature' that the authors infer? How can it be useful for insights into disease mechanisms?

The ’regulon signature’ here refers to a gene regulatory program (multiple gene modules, each defined by a transcription factor and its targets) which are specific to different age groups. Further investigation into this can be useful for understanding why patients of different ages confer a different clinical course. We will add more text on the utility of our discovered 'regulon signature' in the discussion section of revised manuscript.

b) The authors write 'Together this indicates that EP300 inhibition may be particularly effective in t(8;21) AML, and that BCLAF1 may present a new therapeutic target for t(8;21) AML, particularly in children with inferred pre-natal origin of the driver translocation.' I am missing a critical discussion of what is needed to further test the two targets. Put differently: Would the authors take the risk of a clinical study given the evidence from their analysis?

Of course, many extensive studies would be required before these findings are clinically translatable. We can include some perspectives on what further work is required in terms of further experimental validation and potential subsequent clinical study.

Author response:

The following is the authors’ response to the original reviews

Thank you for your valuable comments, which helped us improve our manuscript. We will make the following modifications in the revised manuscript:

(1) In the first paragraph of the Result section, we will provide a summary of trimeric G proteins in Ciona and explain how we focused on Gαs and Gαq in the initial phase of this study.

We added a summary of trimeric G proteins in Ciona in the initial part of the Results section (page 6, line 23 to page 8, line 5). In this summary, we added the following sentence explaining the reason we focused on Gas and Gaq in the initial phase of this study: "Among them, we prioritized examining the Gα proteins having an excitatory function (Gαq and Gαs) rather than inhibitory roles since previous studies suggested that excitatory events like Ca²⁺ transient and neuropeptide secretion occur when Ciona metamorphose."

(2) As the reviewer 1 suggests, the polymodal roles of papilla neurons are interesting. Although we could not address this through functional analyses in this study, we will add a discussion regarding this aspect. The sentences will be something like the following:

“The recent study (Hoyer et al., 2024) provided several lines of evidence suggesting that PSNs can serve as the sensors of several chemicals in addition to the mechanical stimuli. This finding and our model could be mutually related because these chemicals could modify Ca²⁺ and cAMP production. The use of G protein signaling allows Ciona to reflect various environmental stimuli to initiate metamorphosis in the appropriate situation, both mechanically and chemically.”

We added a discussion related to the recent publication by Hoyer and colleagues on page 23, lines 13-18: " A recent study[19] provided several lines of evidence suggesting that PNs can serve as the sensors of several chemicals in addition to mechanical stimuli. This finding and our model could be mutually related because these chemicals could modify Ca²⁺ and cAMP production. G protein signaling allows Ciona to reflect various environmental stimuli to initiate metamorphosis either mechanically or chemically according to the situation."

(3) As both reviewers suggested, imaging cAMP on the backgrounds of some G protein knockdowns is essential, and we will conduct the experiments.

We added the data on cAMP imaging in Gas, Gaq, and dvGai_Chr2 knockdown larvae in Supplementary Figure S4C-D and Figure 6E.

(4) We carefully modify the text throughout the manuscript so that the descriptions suitably reflect the results.

We modified the descriptions of experimental results so that the text reflects the results more precisely.

Reviewer #1:

Pg1 - need to add an additional '6' to the author list to clarify which two or more authors contributed equally.

We added a 6 as suggested. Thank you for pointing this out.

Pg3 - note that larval adhesive organ applies to not all benthic adults, but to benthic sessile adults this makes it sound like the adhesive organ can trigger metamorphosis but has that been shown? In Ciona or others? Need to specify the role of cells secreting adhesive, vs sensory cells that trigger metamorphosis?

We divided the corresponding sentence into two to clearly state that adhesion and triggering metamorphosis are related but could be different events. Moreover, we modified the sentence to state that physical contact is one example of a cue triggering metamorphosis. We then added another example of a factor triggering metamorphosis—i.e., chemicals from the organisms surrounding the adherence site (page 3, lines 16-20 of the revised version):

"Many marine invertebrates exhibit a benthic lifestyle at the adult stage[4]. Their planktonic larvae have an adhesive organ that secretes adhesives and adheres to a substratum. The cues associated with the adhesion, such as the physical contact with the substratum and a chemical from organisms surrounding the adherence site, can trigger their metamorphosis."

Pg 4 - although mechanosensation is the focus here, could there also be chemoreception/chemoreceptors involved in Ciona metamorphosis? For example, Hoyer et al. 2024 (Current Biology 34(6):1168-1182) concluded that some palp sensory neurons were multimodal and could be both chemo- and mechano-sensory.

We added statements about this recent finding in the Introduction and Discussion sections. In the Introduction (page 4, lines 16-18), however, we also stated that a mechanical stimulus can trigger metamorphosis in the lab without the need to supply these chemicals. This is to emphasize that the mechanical stimulus is the focus of this study. In the Discussion, we added a statement that G-protein signaling could also be used to receive the chemical stimuli (page 23, lines 13-18).

Pg 6 - Before starting functional characterizations, it would be useful to give an overview (table?) of the G proteins found in papillae, and what receptor they are suspected of binding to, or if this is completely unknown, and which downstream pathways they likely activate. That is, to show some results about which G proteins are found in Ciona, and which are found in papillae. In this way, it will make more sense for readers when the Gai is suddenly introduced later, following the sections of Gaq and Gas.

Thank you for your idea to improve the readability of this manuscript. In the initial part of the Results section (page 6, line 22 to page 8, line 5), we added descriptions of the repertoire of trimeric G-proteins in Ciona, including phylogenetic analyses, and expression in the papillae based on RNA-seq data, followed by the reason why we initially focused on Gaq and Gas. The data are displayed in Supplementary Figure S1. The phylogenetic analyses were modified from those shown in Supplementary Figure S5 of the previous version. We also added the general downstream activities of Gas, Gai and Gaq in the Introduction section (page 6, lines 10-12). Considering the contents, the general function of Ga12/13 was stated in the Results section (page 8, lines 2-3).

We did not add the information about their partner receptors in this early section. This is because there are many candidates, and we could not pick some of them. Instead, we described our current suppositions about their possible partners in the Discussion (page 23, line 22 to page 24, line 19). However, we suspect that there are more candidates, and we wish to promote unbiased research in the future.

Pg 9 - would be good to know the timing of this PF fluorescence increase and the timing of stimulation in the text here, relevant to the 30-min gap before metamorphosis initiation

We added the start times for the cAMP reduction and re-upregulation in the following sentence (page 11, lines 17-18): "The cAMP reduction and increase respectively started at 35 seconds and 4 min 40 seconds after stimulation on average."

Pg 28 - Phylogenetic analysis: Given that the results may be of interest to metamorphosis in other marine invertebrates as discussed in the last paragraph of the paper, it would be useful to include G proteins from these other animal phyla where available in the phylogenetic tree. Similarly, in Figure S5A it would be useful to highlight further all the different Ciona G proteins, and the different protein families, through the use of additional colour/labelling (regardless of whether this remains Fig S5A, or becomes part of the main figures)

We drew a phylogenetic tree of G-proteins including those in some sessile and benthic animals (barnacle, sea anemone, hydra, sponge, sea urchin and shell). However, we decided not to add the tree in the revised version because, unfortunately, the bootstrap values of many branches were not high enough to have confidence in the results. We hope you understand our decision. Ciona divergent G-proteins are likely to be specific to Ciona.

According to your comment, we highlighted all Ciona G alpha proteins in red in Figure S5A, which is now Figure S1A in the revised version.

Figure 3E and Figure S3 - is the data shown as an average of all larvae measured (n=5 and n=4) or is it data from one representative larva out of the 4-5 measured? This needs clarification.

The original graphs in Figure 3E and Figure S3 are typical examples. We added the graphs summarizing data of all larvae in each experimental condition in Supplementary Figure S4 (corresponding to Supplementary Figure S3 of the original version). Figure 3E remains as a typical example of the result of a single larva to explain our data analysis in detail.

Experimental suggestion - As mentioned above, one missing detail seems to be the need for evidence that cAMP is elevated in the papillae directly as a result of Gs activation- this could be shown with measurement of cAMP via PF in Gs knockdown larvae that are mechanically stimulated compared to wildtype stimulated and non-stimulated?

Thank you for your suggestion. The experiments are indeed important. We added the data of Pink Flamindo imaging in the Gas, Gaq and dvGai_Chr2 knockdown conditions. The results of Gas and Gaq knockdowns are described in page 11, line 24 to page 12, line 5, and are displayed in Supplementary Figure S4C-D. The result of dvGai_Chr2 knockdown is given on page 16, lines 20-22 and shown in Figure 6E.

In order to insert the data of cAMP imaging of dvGai_Chr2 knockdown larvae, we transferred some panels of Figure 6 to Supplementary Figure S6. In addition, the knockdown data of dvGαi_Chr4 and double knockdowns of Gai genes are also included in Supplementary Figure S6.

Reviewer #2:

Page 6, line 3-4 in the first paragraph of the "Results"; the authors state "Neither morphant showed any signature of metamorphosis even though both were allowed to adhere to the base of culture dishes...". However, judging from Fig. 1E, "the percentage of metamorphosis initiation" (indicated by the initiation of tail regression) in Gαq morphans is not close to 0 (average about 40%), thus I am not convinced this observation can be described as "Neither morphant showed any signature of metamorphosis..." in this sentence.

Thank you for your suggestion. In writing the original text, we oversimplified some of the descriptions when trying to improve the readability. We agree this resulted in imprecision in places. We have revised all these passages in our revision. In this particular case, we softened the overly emphatic statement to better reflect the results, changing “... any signature of metamorphosis...” to “... reduced rate of metamorphosis initiation...” In addition, we stated that the effect of G_α_q MO was weaker than that of G_α_s MO on page 8, lines 10-12. The weaker effect of Gaq MO was due to the redundant role of the Gi pathway, which is shown on page 17, lines 10-17, and in Figure 6G-H.

Similarly, in the next paragraph describing the knockdown of PLCβ1/2/3, PLCβ4, and IP3R genes, the authors appear to neglect there is a weaker effect of the PLCβ4 MO, and simply described the results as "The knockdown larvae of these three genes failed to start metamorphosis". Based on Fig. 1H, about 30% of the PLCβ4 MO-injected animals still initiated tail regeneration. This difference may have some biological meanings and thus should be described more precisely.

We added the following sentence on page 8, lines 18-19 of the revised version: “The effect of PLCβ4 MO was weaker than those of the other MOs, suggesting that this PLC plays an auxiliary role.”

Page 7, second paragraph, on the description of GCaMP8 fluorescence and also at the end of Fig. 1O legend, the citation to "Figure S1" is confusing; Fig. S1 is the phylogenetic tree of PLCβ proteins. Is there additional data regarding this Gαq MO plus GCaMP8 mRNA injection experiment?

Figure S1 of the original version corresponds to Figure S2 of the revised version. To avoid confusion, we deleted this citation from the legend of Figure 1O. By this modification, the sentence stating the repertoire of PLCb and IP3R in Ciona (page 8, lines 15-16) is the only sentence citing Figure S2 in the revised version.

Page 8, first sentence; The purpose of theophylline treatment is not to prevent larvae from adhesion, thus I would suggest modifying this sentence to: "We treated wild-type larvae with theophylline after tail amputation, and we observed that most theophylline-treated larvae completed tail regression without adhesion (Figure 2D-F)".

We modified the sentence according to your comment. Thank you for your suggestion.

Page 9, second paragraph; judging from the data presented in Fig. 3C, I think this description: "when papillae were removed from larvae, theophylline failed to induce metamorphosis" is not accurate, because about ~30% of the Papilla cut +Theophylline-treated larvae still initiated their tail regression. This needs to be explained clearly.

We modified the sentence (page 11, lines 2-3) as follows: “...the average rate of metamorphosis induction by theophylline was reduced from 100% to 30%...”

Similarly in the next few sentences regarding the results presented in Fig, 3D, the effects of overexpressing those genes are not uniform. While amputation of papillae in larvae overexpressing caPLCβ1/2/3 could inhibit metamorphosis almost completely, papilla cut seems to have a weaker effect on caGαq, caGαs, and bPAC-overexpressing larvae.

We added a description explaining that caPLCβ1/2/3 was the most sensitive to papilla amputation, and the possibility that PLCβ1/2/3 works specifically in the papillae (page 11, lines 9-11): “Among these experiments, caPLCβ1/2/3 overexpression was the most sensitive to papilla amputation, suggesting that PLCβ1/2/3 acts specifically in the papillae during metamorphosis.”

Page 9, the paragraph on using the fluorescent cAMP indicator; there is a discrepancy between the described developmental time when the authors conducted this experiment and the metamorphosis competent timing (after 24hpf) described on page 7. On page 26, the authors describe "The Pink Flamindo mRNA-injected larvae were immobilized on Poly L lysine-coated glass bottom dishes at 20-21 hpf...". Did the authors start stimulating the larvae to observe the fluorescent signal soon after immobilization, or wait several hours until the larvae passed 24hpf and then conduct the experiment?

The latter is the case. The immobilized larvae were kept until they acquired the competence for metamorphosis and then stimulation/recording was carried out. This point is described in the Materials and Methods section of the revised version (page 29, lines 16-18):

"The Pink Flamindo mRNA-injected larvae were immobilized on Poly L lysine-coated glass-bottom dishes at 20-21 hpf, and stimulated their adhesive papillae around 25 hpf."

Page 10, the description "...Gαq morphants initiated metamorphosis when caGαs was overexpressed in the nervous system (Figure 4F)". It should be noted that the result is only a partial rescue. To be precise, this description needs to be modified.

We changed the sentence to reflect the results more precisely (page 14, lines 2-3): “Moreover, caGαs overexpression in the nervous system significantly, although not perfectly, ameliorated the effect of Gαq MO (Figure 4F).”

Page 12-13, This description and the figure 5E presented is a bit confusing to me. The figure legend for 5E: "GABA is necessary for Ca2+ transient in the adhesive papillae (arrow)" But the arrow in this image points to a place with no fluorescent signal, and on the upper corner it labeled as "29% (n=17)". Does that mean the proportion of "no Ca2+ increase after stimulation" was 29% among the 17 samples examined? Or actually, is the other way around that 81% of the examined larvae did not show Ca2+ signal increase after stimulation?

The latter is the case. We added a caption explaining this clearly in the Figure legend: “The percentage and number exhibit the rate of animals showing Ca²⁺ transient in the papillae.”

Page 13, second paragraph; I do not agree with the overly simplified description that "GABA significantly ameliorated the metamorphosis-failed phenocopies of Gαq, PLCβ, and Gαs morphants". As shown in Fig. 5F-H, adding GABA exerts different levels of partial rescue effect on each morphant, and thus should be described clearly.

When the outliers are neglected, the effect of GABA is most evident in Gαs knockdowns. This suggests that the target(s) of GABA signaling is more likely to be Gq pathway components. We added the following sentence to the revised version (page 15, lines 14-16):

“Among the three morphants, GABA exhibited the most effective rescues in Gαs knockdowns than Gαq and PLCβ.”

In addition, we think this sentence establishes a more logical connection with the sentence that follows it: “These results could be explained by assuming enhancement of the Gq pathway by GABA through PLCβ and another GABA-mediated metamorphic pathway bypassing Gq components.” Thank you for your suggestion.

The section "Contribution of Gi to metamorphosis" confirmed the possibility that GABA signaling targets Gq pathway components.

Page 13, the first paragraph on "Contribution of Gi to metamorphosis"; the description that "The knockdown of this gene (Gαi) exhibited a significantly reduced rate of metamorphosis;..." is misleading. I would suggest modifying the entire sentence as "The knockdown of this gene (Gαi) exhibited a moderate (although statistically significant) reduction of metamorphosis rate, suggesting the presence of another Gαi regulating metamorphosis".

Thank you for your suggestion. We modified the sentence (page 16, lines 2-4 in the revised version) as recommended. We believe the description is much improved.

Page 20, the last sentence about Ciona papilla neurons expressing transcription factor Islet; the authors seem to attempt to make some comparison with the vertebrate pancreatic beta cells in this paragraph, but the comparison and the argument are not fully developed in this current format.

To deepen this discussion, we added the following sentence (page 23, lines 10-12): “The atypical secretion of GABA might depend on the transcription factor like Islet shared between Ciona papilla neurons and vertebrate beta cells.”

However, we would like to limit the depth of our discussion on this point, as we hope to expand on it further in future studies.

Other suggestions:

Page 3, second paragraph: as they become unable to "move" after metamorphosis -> "relocate"

We corrected the word as suggested.

Page 4, second paragraph: In the first sentence, the author states the current understanding of chordate phylogeny and cites Delsuc et al. 2006 Nature paper at the end of this sentence. However, in this paper cephalochordates were erroneously grouped with echinoderms, and thus chordates did not form a monophyletic clade. A later paper by Bourlat et al, (Nature 444:85-88, 2006) corrected this problem, and subsequently Dulsuc et al. also published another paper (genesis, 46:592-604, 2008) with broader sampling to overcome this problem. These later publications need to be included for the sake of correctness.

We added this reference.

Page 14, regarding the redundant function of the typical Gαi protein in the papillae; the authors may try double KD of Gαi and dvGαi_Chr2 in their experimental system to test this idea.

We carried out double knockdown of typical Gai and dvGαi_Chr2. However, we could not address their redundant role sufficiently because most of the double knockdown larvae exhibited severe shape malformation.

dvGαi_Chr4 is also expressed in the papillae. We carried out knockdown of this gene, to find that the knockdown resulted in very minor but statistically significant reduction of the metamorphosis rate, suggesting that this Gai also plays a supportive role in metamorphosis. We also carried out double knockdown of dvGαi_Chr2 and dvGαi_Chr4. The double KD larvae exhibited responsiveness to GABA, probably because of the presence of typical Gai.

These results are described on page 16, lines 2-18, and the data are shown in Supplementary Figure S6A-D of the revised version.

Responses to the Reviewing editor's comments:

"Larvae of the ascidian Ciona initiate metamorphosis tens of minutes after adhesion to a substratum via its adhesive organ." - Larvae is plural so change to 'via their adhesive organ'

The sentence was corrected as suggested.

"Metamorphosis is a widespread feature of animal development that allows them" - revise the sentence, e.g. "Metamorphosis is a widespread feature of development that allows animals"

The sentence was corrected as suggested.

"GABA synthase (GAD)" GAD is not called GABA synthase but glutamate decarboxylase - clarify, e.g. encoding the enzyme synthesizing GABA called glutamate decarboxylase (GAD)

This part was corrected exactly as suggested. Thank you.

"IP3 is received by its receptor on the endoplasmic reticulum (ER) and releases calcium ion (Ca2+ )" revise to "IP3 is received by its receptor on the endoplasmic reticulum (ER) that releases calcium ion (Ca2+ )"

The sentence was corrected as suggested.

"Moreover, GPCR is implicated as the mediator of settlement" - GPCRs are implicated

This sentence was modified as suggested.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1(Public review):

Summary:

This manuscript details the results of a small pilot study of neoadjuvant radiotherapy followed by combination treatment with hormone therapy and dalpiciclib for early-stage HR+/HER2-negative breast cancer.

Strengths:

The strengths of the manuscript include the scientific rationale behind the approach and the inclusion of some simple translational studies.

Weaknesses:

The main weakness of the manuscript is that overly strong conclusions are made by the authors based on a very small study of twelve patients. A study this small is not powered to fully characterize the efficacy or safety of a treatment approach, and can, at best, demonstrate feasibility. These data need validation in a larger cohort before they can have any implications for clinical practice, and the treatment approach outlined should not yet be considered a true alternative to standard evidence-based approaches.

I would urge the authors and readers to exercise caution when comparing results of this 12-patient pilot study to historical studies, many of which were much larger, and had different treatment protocols and baseline patient characteristics. Cross-trial comparisons like this are prone to mislead, even when comparing well powered studies. With such a small sample size, the risk of statistical error is very high, and comparisons like this have little meaning.

We greatly appreciate your evaluation of our study and fully agree with the limitations you have pointed out. We have clearly stated the limitations of the small sample size and emphasized the need for a larger population to validate our preliminary findings in the discussion section (Lines 311-316).

We acknowledge that this small sample size is not powered to characterize this regimen as a promising alternative regimen in the treatment of patients with HR-positive, HER2-negative breast cancer. Therefore, we have revised the description of this regimen to serve as a feasible option for neoadjuvant therapy in HR-positive, HER2-negative breast cancers both in the discussion (Lines 317-320) and the abstract (Lines 71-72).

We agree with you that cross-trial comparisons should be approached with caution due to differences in study designs and patient populations. In our discussion section, we acknowledge that small sample size limited the comparison of our data with historical data in the literature due to the potential bias (Lines 312-313). We clearly state that such comparisons hold limited significance (Lines 313-314) and suggest a larger population to validate our preliminary findings.

• Why was dalpiciclib chosen, as opposed to another CDK4/6 inhibitor?

Thank you for your comments. The rationale for selecting dalpiciclib over other CDK4/6 inhibitors in our study is primarily based on the following considerations:

(1) Clinical Efficacy: In several clinical trials, including DAWNA-1 and DAWNA-2, the combination of dalpiciclib with endocrine therapies such as fulvestrant, letrozole, or anastrozole has been shown to significantly extend the progression-free survival (PFS) in patients with hormone receptor-positive, HER2-negative advanced breast cancer [1-2].

(2) Tolerability and Management of Adverse Reactions: The primary adverse reactions associated with dalpiciclib are neutropenia, leukopenia, and anemia. Despite these potential side effects, the majority of patients are able to tolerate them, and with proper monitoring and management, these reactions can be effectively mitigated [1-2].

(3) Comparable pharmacodynamic with other CDK4/6 inhibitors: The combination of CDK4/6 inhibitors, including palbociclib, ribociclib, and abemaciclib, with aromatase inhibitors has demonstrated an enhanced ability to suppress tumor proliferation and increase the rate of clinical response in neoadjuvant therapy for HR-positive, HER2-negative breast cancer [3-5]. Furthermore, preclinical studies have shown that dalpiciclib has comparable in vivo and in vitro pharmacodynamic activity to palbociclib, suggesting its potential effectiveness in similar treatment regimens [6].

(4) Accessibility and Regulatory Approval: Dalpiciclib has gained marketing approval in China on December 31, 2021, which facilitates the accessibility of this medication, making it a more convenient option when considering treatment plans.

References:

(1) Zhang P, Zhang Q, Tong Z, et al. Dalpiciclib plus letrozole or anastrozole versus placebo plus letrozole or anastrozole as first-line treatment in patients with hormone receptor-positive, HER2-negative advanced breast cancer (DAWNA-2): a multicentre, randomised, double-blind, placebo-controlled, phase 3 trial[J]. The Lancet Oncology, 2023, 24(6): 646-657.

(2) Xu B, Zhang Q, Zhang P, et al. Dalpiciclib or placebo plus fulvestrant in hormone receptor-positive and HER2-negative advanced breast cancer: a randomized, phase 3 trial[J]. Nature medicine, 2021, 27(11): 1904-1909.

(3) Hurvitz S A, Martin M, Press M F, et al. Potent cell-cycle inhibition and upregulation of immune response with abemaciclib and anastrozole in neoMONARCH, phase II neoadjuvant study in HR+/HER2− breast cancer[J]. Clinical Cancer Research, 2020, 26(3): 566-580.

(4) Prat A, Saura C, Pascual T, et al. Ribociclib plus letrozole versus chemotherapy for postmenopausal women with hormone receptor-positive, HER2-negative, luminal B breast cancer (CORALLEEN): an open-label, multicentre, randomised, phase 2 trial[J]. The lancet oncology, 2020, 21(1): 33-43.

(5) Ma C X, Gao F, Luo J, et al. NeoPalAna: neoadjuvant palbociclib, a cyclin-dependent kinase 4/6 inhibitor, and anastrozole for clinical stage 2 or 3 estrogen receptor–positive breast cancer[J]. Clinical Cancer Research, 2017, 23(15): 4055-4065.

(6) Long F, He Y, Fu H, et al. Preclinical characterization of SHR6390, a novel CDK 4/6 inhibitor, in vitro and in human tumor xenograft models[J]. Cancer science, 2019, 110(4): 1420-1430.

• The eligibility criteria are not consistent throughout the manuscript, sometimes saying early breast cancer, other times saying stage II/III by MRI criteria.

Thank you for pointing out the inconsistencies in the description of the eligibility criteria in our manuscript. We deeply apologize for any confusion caused by these inconsistencies. We have revised the term from “early-stage HR-positive, HER2-negative breast cancer” to “early or locally advanced HR-positive, HER2-negative breast cancer” (Lines 128 and 150). The term “early or locally advanced” encompasses two different stages of breast cancer, whereas “Stage II/III by MRI criteria” refers to specific stages within the TNM staging system.

• The authors should emphasize the 25% rate of conversion from mastectomy to breast conservation and also report the type and nature of axillary lymph node surgery performed. As the authors note in the discussion section, rates of pathologic complete response/RCB scores are less prognostic for hormone-receptor-positive breast cancer than other subtypes, so one of the main rationales for neoadjuvant medical therapy is for surgical downstaging. This is a clinically relevant outcome.

We appreciate your constructive comments. Based on your suggestions, we have made the following revisions and additions to the article.

The breast conservation rate serves as a secondary endpoint in our study (Line 62 and 179). We have highlighted the significant 25% conversion rate from mastectomy to breast conservation in both the results (Lines 229-230) and discussion sections (Lines 290-292).

In our study, all patients underwent lymph node surgery, including sentinel lymph node biopsy or axillary lymph node dissection. Among them, 58.3% of patients (7/12) underwent sentinel lymph node biopsies.

We agree with your point that the prognostic value of pathologic complete response/RCB score is lower for hormone receptor-positive breast cancer compared to other subtypes, we have revised the discussion section to clarify that one of the principal objectives for neoadjuvant therapy in this patient population is to facilitate downstaging and enhance the rate of breast conservation (Lines 289-290). And also emphasized that this neoadjuvant therapeutic regiment appeared to improve the likelihood of pathological downstaging and achieve a margin-free resection, particularly for those with locally advanced and high-risk breast cancer (Lines 293-295).

Reviewer #2 (Public review):

Firstly, as this is a single-arm preliminary study, we are curious about the order of radiotherapy and the endocrine therapy. Besides, considering the radiotherapy, we also concern about the recovery of the wound after the surgery and whether related data were collected.

Thanks for the comments. The treatment sequence in this study is to first administer radiotherapy, followed by endocrine therapy. A meta-analysis has indicated that concurrent radiotherapy with endocrine therapy does not significantly impact the incidence of radiation-induced toxicity or survival rates compared to a sequential approach [1]. In light of preclinical research suggesting enhanced therapeutic efficacy when radiotherapy is delivered prior to CDK4/6 inhibitors, we have opted to administer radiotherapy before the combination therapy of CDK4/6 inhibitors and hormone therapy [2].

In our study, we collected data on surgical wound recovery. All 12 patients had Class I incisions, which healed by primary intention. The wounds exhibited no signs of redness, swelling, exudate, or fat necrosis.

References:

(1) Li Y F, Chang L, Li W H, et al. Radiotherapy concurrent versus sequential with endocrine therapy in breast cancer: A meta-analysis[J]. The Breast, 2016, 27: 93-98.

(2) Petroni G, Buqué A, Yamazaki T, et al. Radiotherapy delivered before CDK4/6 inhibitors mediates superior therapeutic effects in ER+ breast cancer[J]. Clinical Cancer Research, 2021, 27(7): 1855-1863.

Secondly, in the methodology, please describe the sample size estimation of this study and follow up details.

Thanks for pointing out this crucial omission. Sample size estimation for this study and follow-up details have been added in the methodology section. The section on sample size estimation has been revised to state in Statistical analysis: “This exploratory study involves 12 patients, with the sample size determined based on clinical considerations, not statistical factors (Lines 210-211).” The section on follow up has been revised to state in Procedures section “A 5-year follow-up is conducted every 3 months during the first 2 years, and every 6 months for the subsequent 3 years. Additionally, safety data are collected within 90 days after surgery for subjects who discontinue study treatment (Lines 169-172).”

Thirdly, in Table 1, the item HER2 expression, it's better to categorise HER2 into 0, 1+, 2+ and FISH-.

Thank you very much for pointing out this issue. The item HER2 expression in Table 1 has been revised from “negative, 1+, 2+ and FISH-” to “0, 1+, 2+ and FISH-”.

Author response:

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

Reviewer #1 (Recommendations For The Authors):

I can find no problems with the experiments performed in this study, but there are several results that are not easily explained. I would like to see more consideration of possible explanations. For example, one of the major differences between the the CESA structure from primary and secondary cell walls is the displacement of TM7 in the primary cell wall CESAs that leads to the formation of lipid exposed channel. Why does this vary between primary and secondary cell wall CESA proteins? Could it explain differences in the properties, such as crystallinity between primary and secondary cell wall cellulose?

At this time, the different position of TM helix 7 observed in our GmCesA structures is just an observation. We have some emerging evidence that this helix is also flexible in POCesA8 under certain conditions; however, we do not know whether this affects catalytic activity or cellulose coalescence. We have revised the text to avoid the interpretation that TM 7 repositioning is a characteristic feature of primary cell wall CesAs only.

Similarly, regarding the formation of the larger structures from mixtures of different CESA trimers. Why do they not form roseOes? Par;cularly as these appear to be forming 2-dimensional structures.

We have included additional data on the interaction between different CesA isoform trimers (Figure 6). To answer the reviewer’s ques;on, the most likely reasons for not observing closely packed roseOe-like structures are (a) steric interferences between the micelles harboring the individual CesA trimers, and (b) the lack of a stabilizing cellulose fiber.  This interpretation is supported by 2D class averages of dimers of CesA1 and CesA3 trimers (now shown in Fig. 6). The class averages show an ‘upside-down and side-by-side’ orientation of the two trimers, consistent with interferences between the solubilizing detergent micelles. The implica;ons of this non-physiological arrangement are discussed in the revised manuscript. In a biological membrane, the CesA trimers are confined to the same plane in the same orientation, which is likely necessary to form ordered arrangements.

What role does the NTD play in trimer formation given its apparent very high class specificity?

We have no data suggesting any contribution of the NTD to trimer formation. Recent work on moss CesA5 and similar AlphaFold predic;ons suggest that, for some CesAs, an extreme Nterminal region can interact with the beta sheet of the catalytic domain via beta-strand augmentation. Whether this interaction can contribute to CesA-CesA interactions remains unknown.

Reviewer #2 (Recommendations For The Authors):

The authors provide PDB codes but not EMDB codes for the EM maps, also I would encourage the authors to upload the raw micrographs to the EMPIAR database.

The EMDB codes are shown in Table 1 and data transfer to EMPIAR is ongoing.  

Page 6 line 144, the statement "All CesA isoforms show greatest catalytic activity at neutral pH" seems to contradict the data in Figure 1e and the subsequent statements. This sentence should be removed.

The text has been revised to indicate that CesA1 and CesA6 show highest activity under mild alkaline conditions.  

Page 6, line 150, the authors state "The affinities for substrate binding range from 1.4 mM for CesA1 to 0.6 and 2.4 mM for CesA3 and CesA6, respectively." How were the affinities determined? Is this the affinities or the Michaelis constants? Is it known whether CesAs are rapid equilibrium enzymes? This should be clarified.

The text now states that we performed Michaelis Menten kine;cs using the ‘UDP-Glo’ glycosyltransferase assay kit. We are uncertain about whether CesAs can be classified as rapid equilibrium enzymes. The rate-limiting step of cellulose biosynthesis has been proposed to be glycosyl transfer, rather than cellulose transloca;on.  To avoid any confusion, we changed the text from '…reveals Michaelis Menten constants for substrate binding of CesA1 and CesA3' to '…reveals Michaelis Menten constants for CesA1 and CesA3 with respect to UDP-Glc'.

Page 6, line 153, the authors state "CesA1's apparent Ki for UDP is roughly 0.8 mM, whereas this concentration is increased to about 1.2 to 1.5 mM for CesA6 and CesA3, respectively." From the Figure 1g legend, it appears that the authors performed additional experiments at different UDP-Glc concentrations in order to determine Ki that are not shown. This data should be included as a figure supplement as the data presented are insufficient to determine Ki (only IC50).

The UDP inhibition data show apparent IC50 values, and this has been corrected in the text. For each CesA isoform, the titration was done at one UDP-Glc concentration only.    

Page 8, line 202, the authors state that TM helix 7 of the primary cell wall CesAs is more flexible "as evidenced by weaker density." The density for the TM helix 7 should be shown. If the density shown in Supplementary Figure 3 corresponds to TM helices the number of the helices should be indicated as it is not immediately obvious from the amino acid residue numbers.

The densities for TM helix 7 of all CesA isoforms are shown in Supplemental Figure 3. The helices are now labeled to orient the reader.  

Reviewer #2 (Public Review)

The authors demonstrate via truncation that the N-terminus of the CesA is not involved in the interactions between the isoforms and propose that the CSR hook-like extensions are the primary mediator of trimer-trimer interactions. This argument would be strengthened by equivalent truncation experiments in which the CSR region is removed.

We performed the suggested experiment. We replaced the CSR in N-terminally truncated GmCesA1 and GmCesA3 with a 20-residue long linker. The resulting constructs assemble into homotrimeric complexes as observed for the wild type and only N-terminally truncated versions. However, the CSR-truncated constructs of the different isoforms do not interact with each other in vitro. Further, CSR-deleted GmCesA3 also does not interact with full-length CesA1, suggesting that two CSR domains of different isoforms are necessary for homotrimer interaction. This data is now shown as Fig. 5.  

Reviewer #3 (Recommendations For The Authors):

Major Points

(1) The authors state on Line 354 that they were unable to isolate heterotrimers, but they need to provide the data to support this claim; for example, it is important for readers to understand whether co-expression of all three CESAs leads to only homotrimers or only monomers. This information is essential to exclude model C in Figure 6.

We have revised the corresponding discussion and toned down the statement that heterotrimeric complexes did not form in our recombinant expression system. Co-expression of differently tagged secondary or primary cell wall CesAs in Sf9 cells has consistently resulted in negligible amounts of material that can be purified sequentially over different affinity matrices (corresponding to the tags on the recombinantly expressed CesAs – His, Strep, Flag). While this does not exclude the formation of a small fraction of hetero-oligomeric complexes (which could be trimers as observed in the structures or monomers interacting via their CSR regions), it demonstrates that CesAs favor the same isoform for trimer formation, rather than partnering with other isoforms. An example of such a purification is now shown as Supplemental Figure 8.

Determining whether heterotrimers are formed upon co-expression of different CesA isoforms requires high resolution structural analysis because co-purification of different isoforms can also be due to interactions between different homo-trimeric complexes, as demonstrated in this study.

While we cannot exclude that factors exist in planta that may prevent the formation of homotrimers and favor the formation of hetero-trimers, it is important to keep in mind that currently no experimental data supports the formation of hetero-trimeric complexes. Instead, our work demonstrates that existing data on CesA isoform interactions can be explained by the interaction of homotrimers of different isoforms.

(2) The evidence that the products of GmCEA1, GmCESA3, and GmCESA6 homotrimers are cellulose is that they consume UDP-glucose and produce a beta-glucanase-sensitive product. Other beta-glucans synthesized by similar GT2 family proteins (e.g. CSLDs, Yang et al., 2020 Plant Cell or CSLCs, Kim et al., 2020 PNAS) would be sensitive to this enzyme, and the product cannot truly be called cellulose unless it forms microfibrils. Previous reports of CESA activity in vitro have demonstrated that the products form genuine cellulose microfibrils rather than amorphous beta-glucan (via electron microscopy); extensively documented that the product is sensitive to beta-glucanase, but not other enzymes (e.g., callose or MLG degrading enzymes); provided linkage analysis of the product to conclusively demonstrate that it is a beta1,4-linked glucan; and documented a loss of activity when key catalytic residues were mutated (Purushotham et al., 2016 PNAS; Cho et al., 2017 Plant Phys; Purushotham et al., 2020 Science).

Other GT2 characterization efforts have documented activity to similar standards (e.g. CSLDs, Yang et al., 2020 Plant Cell or CSLFs, Purushotham et al., 2022 Science Advances). At least one independent method should be provided, and the TEM of the product is necessary for readers to appreciate whether the product forms true cellulose microfibrils.

There may be some confusion regarding the nomenclature. Therefore, we revised the second sentence of the Introduction to define ‘cellulose’ as a beta-1,4 linked glucose polymer, in accordance with the ‘Essentials of Glycobiology’. This is also consistent with enzyme nomenclature as the primary product of cellulose synthase is a single glucose polymer, and not a fibril. For example, most bacterial cellulose synthases only produce amorphous (single chain) cellulose. 

We show that the GmCesA products can be degraded with a beta-1,4 specific glucanase (cellulase), which demonstrates the formation of authentic cellulose. This study does not focus on the formation of fibrillar cellulose apart from suggesting a revised model for a microfibrilforming CSC.       

(3) The position of isoxaben-resistant mutations implies that primary cell wall CESAs form heterotrimers (Shim et al., 2018 Frontiers in Plant Biology). Indeed, in their previous description of the POCESA8 structure (Purushotham et al., 2020 Science), the authors discussed the position of isoxaben-resistant mutations as a way to justify the way that TM7 of one CESA can contribute to forming the cellulose translocation pore in the neighbouring CESA within a heterotrimer. However, in this manuscript, the authors document a different location for TM7 in the GmCEA1, GmCESA3, and GmCESA6 homotrimers, which would change the position of these resistance mutations. Please discuss.

As stated in the manuscript, we do not know what the functional implication of the TM7 flexibility may be, but we speculate that it could affect the alignment of the synthesized cellulose polymers. Regarding the previously reported POCesA8 structure, the mapping of one of the reported isoxaben resistance mutants to the C-terminus of TM7 was not used to justify the structure; the structure with its position of TM7 stands on its own.  Considering recent observations suggesting that isoxaben may affect cellulose biosynthesis via secondary effects, we prefer not to speculate on the mechanism by which these mutations cause the apparent resistance to isoxaben (PMID: 37823413).

(4) The authors present no evidence that GmCESA1/3/6 are involved in primary cell wall synthesis. Please include gene expression information (documenting widespread expression consistent with primary CESAs) and rigorous molecular phylogenetic analysis (or references to these published data) to clarify that these are indeed primary cell wall CESAs.

This has been addressed. We have included additional figures (Fig. 1 and S1B) that show the strong and wide distribution of the selected CesAs in soybean leaves, their co-expression with primary cell wall markers, and their phylogenetic clustering with Arabidopsis primary cell wall CesAs.  

(5) Several small changes need to be made to the abstract to ensure that it aligns with the data: Line 28: add "in vitro" arer "their assembly into homotrimeric complexes" Line 28: change "stabilized by the PCR" to "presumably stabilized by the PCR".

We inserted ‘in vitro’ as requested. We did not insert the second modification as requested since CesA trimers are stabilized by the PCR. This is a fact arising from several experimentally determined CesA trimer structures.  

(6) In all graphs in all figures it is unclear what the sample size is and what the bars represent. These must be stated in the figure legends. It is best practice to plot individual data points so that readers can easily interpret both the sample size and the variation.

The sample sizes and error bars are now defined in the relevant figure legends.

(7) The methods need to unambiguously define GmCESA1, GmCESA3, GmCESA6 protein identities using appropriate accession numbers.

The accession codes are now provided in the Methods.

Minor Points

(1) Does CESA1 have higher activity in Figure 1D because of the pH at which the assay was conducted (see Figure 1E)? Could this difference in activity or pH preference have also affected their capacity to resolve TM7 of CESA1?

We consistently observe higher in vitro catalytic activity of CesA1, compared to CesA3 and CesA6. Activity assays are performed at a pH of 7.5, roughly halfway between the activity maxima of CesA3 and CesA1/6. At this pH, we expect activity differences to arise from factors other than the buffer pH. As detailed above, we do not know whether the conformational flexibility of TM helix 7 affects catalytic activity.

(2) Line 55: The authors should cite additional papers that also provide insight into CESA structure (e.g. Qiao et al 2021 PNAS).

A recent publication on moss CesA5 has been included. Qiao et al unfortunately report on a dimeric assembly of a fragment of Arabidopsis thaliana’s CesA3 catalytic domain, which we consider non-physiological. We added a brief statement in the Discussion explaining that our GmCesA3 structure is inconsistent with the dimeric arrangement reported by Qiao et al.

(3) Line 95: these references are about secondary cell wall CESA isoforms, but there are more appropriate references for the primary CESAs that should be included in place of these papers.

Fagard et al report on growth defects in roots and dark-grown hypocotyls linked to Arabidopsis CesA 1 and CesA6, which are primary cell wall CesAs. Nevertheless, we have included two additional recent publications from the Meyerowitz and Persson labs.

(4) Line 121-122: Please cite a specific figure that supports this claim, since the (Purushotham et al., 2020) reference refers to POCESA8 enrichment results, but the claims are about the GmCESA1/3/6 enrichment.

The POCesA8 reference has been removed. The classification into monomers and trimers arises from the data processing described in this manuscript and is consistent with similar results obtained for POCesA8.

(5) Line 314: It is more appropriate to use "enzyme activity" rather than "cellulose synthesis".

We prefer to use cellulose biosynthesis since the enzyme produces cellulose.

(6) Figure 1: please add colour to the graphs to clarify which trend lines belong to which data series (especially Figure 1G).

The figure (now Fig. 2) has been revised as suggested.  

(7) Figure 2D: It's not clear which parts are GmCESA and which are POCESA8; please clarify the figure legend.

Thank you, the legend has been revised accordingly (now Fig. 3).

(8) In Figure 5, It's not clear that the one CESA is maintained at a steady concentration throughout the assay since there is only a bar for that CESA at the highest concentration (e.g. in Figure 5A, the blue bar for CESA1 only appears on the right-most assay, but there was CESA1 in all assays, so this should be indicated).

In the panel the reviewer is referring to, the blue bar corresponds to the activity measured for only CesA1 at a concentration of 20 µM. The red columns (indicated as ‘Mix’) represent the activities measured in the presence of 20 µM of CesA1 plus increasing concentrations of CesA3. The purple columns represent activities obtained for only CesA3 at the indicated concentrations. Numerical addition of the activities of CesA1 alone at 20 µM (blue column) and CesA 3 alone (purple columns) gives rise to the gray columns, now indicated by a capital ‘sigma’ sign. We are unclear on how the figure could be improved, but we have revised the legend to avoid confusion.    

(9) Figure 5 legend needs to be clarified to indicate whether monomers or homotrimers were used in the assays.

This is now shown as Fig. 7 and the legend has been revised as requested. The experiments were performed with the trimeric CesA fractions.

(10) There seem to be some random dots near the top of Figures 6B & 6C

Removed. Thank you.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Recommendations for the authors):

We appreciate the reviewers' thoughtful comments and suggestions. Below, we provide point-by-point responses to the recommendations and outline the updates made to the manuscript.

(1) Discussion, "the obvious experiment is to manipulate a neuron's anatomical embedding while leaving stimulus information intact."] The epiphenomenon can arise from the placement and types of a neuron's neurotransmitters and neuromodulators, too.

The content of vesicles released by a neuron is obviously of great importance in determining postsynaptic impact. However, we’re suggesting that (assuming vesicular content is held constant) the anatomically-relevant patterning of spiking might additionally affect the postsynaptic neuron’s integration of the presynaptic input. To avoid confusion, we updated the text accordingly: “the obvious experiment is to manipulate a neuron's anatomical embedding while minimally impacting external and internal variables, such as stimulus information and levels of neurotransmitters or neuromodulators” (Line 594 - 596).

(2) “In all conditions, the slope of the input duration versus sensitivity line was still positive at 1,800 seconds (Fig. 3B)". This may suggest that the estimate of the calculated statistics (ISI, PSTH) is more reliable with more data, rather than (or in addition to) specific information being extracted from faraway time points. Another potential confound is the training statistics were calculated from all training data, so the test data is a better match to training data when test statistics are calculated from more data. Overall, the validity of the conclusions following this observation is not clear to me.

This is a great point. Accordingly, we revised the text to include this possibility: “Because the training data were of similar duration, this could be explained by either of two possibilities. First, the signal is relatively short, but noisy—in this case, extended sampling will increase reliability. Second, the anatomical signal is, itself, distributed over time scales of tens to hundreds of seconds.” (Line 252 - 255).

(3) "This further suggests that there is a latent neural code for anatomical location embedded within the spike train, a feature that could be practically applied to determining the brain region of a recording electrode without the need for post-hoc histology". The performance of the model at the subregion level, which is a typical level of desired precision in locating cells, does not seem to support such a practical application. Please clarify to avoid confusion.

The current model should not be considered a replacement for traditional methods, such as histology. Our intention is to convey that, with the inclusion of multimodal data and additional samples, a computational approach to anatomical localization has great promise. We updated the manuscript to clarify this point: “While significantly above chance, the structure-level model still lacks the accuracy for immediate practical application. However, it is highly likely that the incorporation of datasets with diverse multi-modal features and alternative regions from other research groups will increase the accuracy of such a model. In addition, a computational approach can be combined with other methods of anatomical reconstruction.” (Line 355 - 359).

Additionally, we directly addressed this point in our original manuscript (Discussion section: Line 498 - 505 in the current version). Furthermore, following the release of our preprint, independent efforts have adopted a multimodal strategy with qualitatively similar results (Yu et al., 2024). Other recent work expands on the idea of utilizing single-neuron features for brain region/structure characterization (La Merre et al., 2024).

Yu, H., Lyu, H., Xu, E. Y., Windolf, C., Lee, E. K., Yang, F., ... & Hurwitz, C. (2024). In vivo cell-type and brain region classification via multimodal contrastive learning. bioRxiv, 2024-11.

Le Merre, P., Heining, K., Slashcheva, M., Jung, F., Moysiadou, E., Guyon, N., ... & Carlén, M. (2024). A Prefrontal Cortex Map based on Single Neuron Activity. bioRxiv, 2024-11.

(4) "These results support the notion the meaningful computational division in murine visuocortical regions is at the level of VISp versus secondary areas.". The use of the word "meaningful" is vague and this conclusion is not well justified because it is possible that subregions serve different functional roles without having different spiking statistics.

Precisely! It is well established that different subregions serve different functional purposes - but they do not necessitate different regional embeddings. It is important to note the difference between stimulus encoding and the embedding that we are describing. As a rough analogy, the regional embedding might be considered a language, while the stimulus is the content of the spoken words. However, to avoid vague words, we revised the sentence to “These results suggest that the computational differentiability of murine visuocortical regions is at the level of VISp versus secondary areas.” (Line 380 - 381)

(5) Figure 3D left/right halves look similar. A measure of the effect size needs to accompany these p-values.

We assume the reviewer is referring to Figure 3E. Although some of the violin plots in Figure 3E look similar, they are not identical. In the revision, we include effect sizes in the caption.

(6) Figure 3A, 3F: Could uncertainty estimates be provided?

Yes. We added uncertainty estimates to the text (Line 272 - 294) and to the caption of Figure S2, which displays confusion matrices corresponding to Figure 3A. The inclusion of similar estimates for 3F would be so unwieldy as to be a disservice to the reader—there are 240 unique combinations of stimulus parameters and structures. In the context of the larger figure, 3F serves to illustrate a relationship between stimulus, region, and the anatomical embedding.

(7) Page 21. "semi-orthogonal". Please reword or explain if this usage is technical.

We replaced “semi-orthogonal” with “dissociable” (Line 549).

(8) Page 11, "This approach tested whether..."] Unclear sentence. Please reword.

We changed “This approach tested whether the MLP’s performance depended on viewing the entire ISI distribution or was enriched in a subset of patterns” to “This approach identified regions of the ISI distribution informative for classification” (Line 261).

Reviewer #2 (Recommendations for the authors):

We appreciate the reviewer’s comments and summary of the results. We agree that the introductory results (Figs. 1-3) are not particularly compelling when considered in isolation. They provide a baseline of comparison for the subsequent results. Our intention was to approach the problem systematically, progressing from well-established, basic methods to more advanced approaches. This allows us to clearly test a baseline and avoid analytical leaps or untested assumptions. Specifically:

● Figure 1 provides an evaluation of the standard dimensionality reduction methods. As expected, these methods yield minimal results, serving as a clear baseline. This is consistent, for example, with an understanding of single units as rate-varying Poisson processes.

● Figures 2 and 3 then build upon these results with spiking features frequent in neuroscience literature such as firing rate, coefficient of variation, etc using linear supervised and more detailed spiking features such as ISI distribution using nonlinear supervised machine learning methods.

By starting from the standpoint of the status quo, we are better able to contextualize the significance of our later findings in Figures 4–6.

Response to Specific Points in the Summary

(6) Separability of VISp vs. Secondary Visual Areas

I found the entire argument about visual areas somewhat messy and unclear. The stimuli used might not drive the secondary visual areas particularly well and might necessitate task engagement.

We appreciate your feedback that the dissection of visual cortical structures is unclear. To summarize, as shown in the bottom three rows of Figure 6, there is a notable lack of diagonality in visuocortical structures. This means that our model was unable to learn signatures to reliably predict these classes. In contrast, visuocortical layer is returned well above chance, and superstructures (primary and secondary areas) are moderately well identified, albeit still well above chance.

Consider a thought experiment, if Charlie Gross had not shown faces to monkeys to find IT, or Newsome and others shown motion to find MT and Zeki and others color stimuli to find V4, we would conclude that there are no differences.

The thought experiment is misleading. The results specifically do not arise from stimulus selectivity—much of Newsome’s own work suggests that the selectivity of neurons in IT etc. is explained by little more than rate varying Poisson processes. In this case, there should be no fundamental anatomical difference in the “language” of the neurons in V4 and IT, only a difference in the inputs driving those neurons. In contrast, our work suggests that the “language” of neurons varies as a function of some anatomical divisions. In other words, in contrast to a Poisson rate code, our results predict that single neuron spike patterns might be remarkably different in MT and IT— and that this is not a function of stimulus selectivity. Notably, the anatomical (and functional) division between V1 and secondary visual areas does not appear to manifest in a different “language”, thus constituting an interesting result in and of itself.

We regret a failure to communicate this in a tight and compelling fashion on the first submission, but hope that the revision is limpid and accessible.

Barberini, C. L., Horwitz, G. D., & Newsome, W. T. (2001). A comparison of spiking statistics in motion sensing neurones of flies and monkeys. Motion Vision: Computational, Neural, and Ecological Constraints, 307-320.

Bair, W., Zohary, E., & Newsome, W. T. (2001). Correlated firing in macaque visual area MT: time scales and relationship to behavior. Journal of Neuroscience, 21(5), 1676-1697.

Similarly, why would drifting gratings be a good example of a stimulus for the hippocampus, an area thought to be involved in memory/place fields?

The results suggest that anatomical “language” is not tied to stimuli. It is imperative to recall that neurons are highly active absent experimentally imposed stimuli, such as when an animal is at rest, when an animal is asleep, and when an animal is in the dark (relevant to visual cortices). With this in mind, also recall that, despite the lack of stimuli tailored to the hippocampus, neurons therein were still reliably separable from neurons in seven nuclei in the thalamus, 6 of which are not classically considered visual regions. Should these regions (including hippocampus) have been inert during the presentation of visual stimuli, there would have been very little separability.

(7) Generalization across laboratories

“[C]omparison across laboratories was somewhat underwhelming. It does okay but none of the results are particularly compelling in terms of performance.

Any result above chance is a rejection of the null hypothesis: that a model trained on a set of animals in Laboratory A will be ineffective in identifying brain regions when tested on recordings collected in Laboratory B (in different animals and under different experimental conditions). As an existence proof, the results suggest conserved principles (however modest) that constrain neuronal activity as a function of anatomy. That models fail to achieve high accuracy (in this context) is not surprising (given the limitations of available recordings)---that models achieve anything above chance, however, is.

Thus, after reading the paper many times, I think part of the problem is that the study is not cohesive, and the authors need to either come up with a tool or demonstrate a scientific finding.

We demonstrate that neuronal spike trains carry robust anatomical information. We developed an ML architecture for this and that architecture is publicly available.

They try to split the middle and I am left somewhat perplexed about what exact scientific problem they or other researchers are solving.

We humbly suggest that the question of a neurons “language” is highly important and central to an understanding of how brains work. From a computational perspective, there is no reason for a vast diversity of cell types, nor a differentiation of the rules that dictate neuronal activity in one region versus another. A Turing Complete system can be trivially constructed from a small number of simple components, such as an excitatory and inhibitory cell type. This is the basis of many machine learning tools.

Please do not confuse stimulus specificity with the concept of a neuron’s language. Neurons in VISp might fire more in response to light, while those in auditory cortex respond to sound. This does not mean that these neurons are different - only that their inputs are. Given the lack of a literature describing our main effect—that single neuron spiking carries information about anatomical location—it is difficult to conclude that our results are either commonplace or to be expected.

I am also unsure why the authors think some of these results are particularly important.

See above.

For instance, has anyone ever argued that brain areas do not have different spike patterns?

Yes. In effect, by two avenues. The first is a lack of any argument otherwise (please do not conflate spike patterns with stimulus tuning), and the second is the preponderance of, e.g., rate codes across many functionally distinct regions and circuits.

Is that not the premise for all systems neuroscience?

No. The premise for all systems neuroscience (from our perspective) is that the brain is a) a collection of interacting neurons and b) the collective system of neurons gives rise to behavior, cognition, sensation, and perception. As stated above, these axiomatic first principles fundamentally do not require that neurons, as individual entities, obey different rules in different parts of the brain.

I could see how one could argue no one has said ISIs matter but the premise that the areas are different is a fundamental part of neuroscience.

Based on logic and the literature, we fundamentally disagree. Consider: while systems neuroscience operates on the principle that brain regions have specialized functions, there is no a priori reason to assume that these functions must be reflected in different underlying computational rules. The simplest explanation is that a single language of spiking exists across regions, with functional differences arising from processing distinct inputs rather than fundamentally different spiking rules. For example, an identical spike train in the amygdala and Layer 5 of M1 would have profoundly different functional impacts, yet the spike timing itself could be identical (even as stimulus response). Until now, evidence for region-specific spiking patterns has been lacking, and our work attempts to begin addressing this gap. There is extensive further work to be conducted in this space, and it is certain that models will improve, rules will be clarified, and mechanisms will be identified.

Detailed major comments

(1) Exploratory trends in spiking by region and structure across the population:

The argument in this section is that unsupervised analyses might reveal subtle trends in the organization of spiking patterns by area. The authors show 4 plots from t-SNE and claim to see subtle organization. I have concerns. For Figure 1C, it is nearly impossible to see if a significant structure exists that differentiates regions and structures. So this leads certain readers to conclude that the authors are looking at the artifactual structure (see Chari et al. 2024) - likely to contribute to large Twitter battles. Contributing to this issue is that the hyperparameter for tSNE was incorrectly chosen. I do think that a different perplexity should be used for the visualization in order to better show the underlying structure; the current visualization just looks like a single "blob". The UMAP visualizations in the supplement make this point more clearly. I also think the authors should include a better plot with appropriate perplexity or not include this at all. The color map of subtle shades of green and yellow is hard to see as well in both Figure S1 and Figure 1.

In response to the feedback, we replaced t-SNE/UMAP with LDA, while keeping PCA for dimensionality reduction.

As stated in the original methods, t-SNE/UMAP hyperparameters were chosen based on the combination that led to the greatest classifiable separability of the regions/structures in the space (across a broad range of possible combinations). It just so happens that the maximally separable structure from a regions/structures perspective is the “blob”. This suggests that perhaps the predominant structure the t-SNE finds in the data is not driven by anatomy. If we selected hyperparameters in some other way that was not based specifically on regions/structures (e.g. simple visual inspection of the plots) the conformation would of course be different and not blob-like. However, we removed the t-SNE and UMAP to avoid further confusion.

The “muddy appearance” is not an issue with the color map. As seen in Figure 1B, the chosen colors are visibly distinct. Figure 1C (previous version) appeared muddy yellow/green because of points that overlap with transparency, resulting in a mix of clearly defined classes (e.g., a yellow point on top of a blue point creating green). This overlap is a meaningful representation of the separability observed in this analysis. We also tried using 2D KDE for visualization, but it did not improve the impression of visual separability.

We are removing p-values from the figures because they lead to the impression that we over-interpret these results quantitatively. However, we calculated p-values based on label permutation similar to the way R2 suggests (see previous methods). The conflation with the Wasserstein distances is an understandable misunderstanding. These are unrelated to p-values and used for the heatmaps in S1 only (see previous methods).

Instead of p-values, we now use the adjusted rand index, which measures how accurately neurons within the same region are clustered together (see Line 670 - 671, Figure 1C, and Figure S1) (Hubert & Arabie 1985). This quantifies the extent to which the distribution of points in dimensionally-reduced space is shaped by region/structure.

Hubert, L., & Arabie, P. (1985). Comparing partitions. Journal of Classification, 2(1), 193–218. https://doi.org/10.1007/BF01908075

(2) Logistic classifiers:

The results in this section are somewhat underwhelming. Accuracy is around 40% and yes above chance but I would be very surprised if someone is worried about separating visual structures from the thalamus. Such coarse brain targeting is not difficult. If the authors want to include this data, I recommend they show it as a control in the ISI distribution section. The entire argument here is that perhaps one should not use derived metrics and a nonlinear classifier on more data is better, which is essentially the thrust of the next section.

As outlined above, our work systematically increases in model complexity. The logistic result is an intermediate model, and it returns intermediate results. This is an important stepping stone between the lack of a result based on unsupervised linear dimensionality reduction and the performance of supervised nonlinear models.

From a purely utilitarian perspective, the argument could be framed as “one should not use derived metrics, and a nonlinear classifier on more data is better.” However, please see all of our notes above.

(3) MLP classifiers:

Even in this section, I was left somewhat underwhelmed that a nonlinear classifier with large amounts of data outperforms a linear classifier with small amounts of data. I found the analysis of the ISIs and which timescales are driving the classifier interesting but I think the classifier with smoothing is more interesting. So with a modest chance level decodability of different brain areas in the visual system, I found it somewhat grandiose to claim a "conserved" code for anatomy in the brain. If there is conservation, it seems to be at the level of the coarse brain organization, which in my opinion is not particularly compelling.

The sample size used for both the linear and nonlinear classifiers is the same; however, the nonlinear classifier leverages the detailed spiking time information from ISIs. Our goal here was to systematically evaluate how classical spike metrics compare to more detailed temporal features in their ability to decode brain areas. We chose a linear classifier for spike metrics because, with fewer features, nonlinear methods like neural networks often offer very modest advantages over linear methods, less interpretability, and are prone to overfitting.

Respectfully, we stand by our word choice. The term “conserved” is appropriate given that our results hold appreciably, i.e., statistically above chance, across animals.

(4) Generalization section:

The authors suggest that a classifier learned from one set of data could be used for new data. I was unsure if this was a scientific point or the fact that they could use it as a tool.

It can be both. We are more driven by the scientific implications of a rejection of the null.

Is the scientific argument that ISIs are similar across areas even in different tasks?

It appears so - despite heterogeneity in the tuning of single neurons, their presynaptic inputs, and stimuli, there is identifiable information about anatomical location in the spike train.

Why would one not learn a classifier from every piece of available data: like LFP bands, ISI distributions, and average firing rates, and use that to predict the brain area as a comparison?

Because this would obfuscate the ability to conclude that spike trains embed information about anatomy.

Considering all features simultaneously and adding additional data modalities—such as LFP bands and spike waveforms—has potential to improve classification accuracy at the cost of understanding the contribution of each feature. The spike train as a time series is the most fundamental component of neuronal communication. As a result, this is the only feature of neuronal activity of concern for the present investigation.

Or is the argument that the ISIs are a conserved code for anatomy? Unfortunately, even in this section, the data are underwhelming.

We appreciate the reviewer’s comments, but arrive at a very different conclusion. We were quite surprised to find any generalizability whatsoever.

Moreover, for use as a tool, I think the authors need to seriously consider a control that is either waveforms from different brain areas or the local field potentials. Without that, I am struggling to understand how good this tool is. The authors said "because information transmission in the brain arises primarily from the timing of spiking and not waveforms (etc)., our studies involve only the timestamps of individual spikes from well-isolated units ". However, we are not talking about information transmission and actually trying to identify and assess brain areas from electrophysiological data.

While we are not blind to the “tool” potential that is suggested by our work, this is not the primary motivation or content in any section of the paper. As stated clearly in the abstract, our motivation is to ask “whether individual neurons [...] embed information about their own anatomical location within their spike patterns”. We go on to say “This discovery provides new insights into the relationship between brain structure and function, with broad implications for neurodevelopment, multimodal integration, and the interpretation of large-scale neuronal recordings. Immediately, it has potential as a strategy for in-vivo electrode localization.” Crucially, the last point we make is a nod to application. Indeed, our results suggest that in-vivo electrode localization protocols may benefit from the incorporation of such a model.

In light of the reviewer’s concerns, we have further dampened the weight of statements about our model as a consumer-ready tool.

Example 1: The final sentence of the abstract now reads: “Computational approximations of anatomy have potential to support in-vivo electrode localization.”

Example 2: The results sections now contains the following text: “While significantly above chance, the structure-level model still lacks the accuracy for immediate practical application. However, it is highly likely that the incorporation of datasets with diverse multi-modal features and alternative regions from other research groups will increase the accuracy of such a model. In addition, a computational approach can be combined with other methods of anatomical reconstruction.” (Line 355 - 359).

Example 3: We replaced the phrase "because information transmission in the brain arises primarily from the timing of spiking and not waveforms (etc) " with the phrase “because information is primarily encoded by the firing rate or the timing of spiking and not waveforms (etc)” (Line 116 - 118).

(5) Discussion section:

In the discussion, beginning with "It is reasonable to consider . . ." all the way to the penultimate paragraph, I found the argumentation here extremely hard to follow. Furthermore, the parts of the discussion here I did feel I understood, I heavily disagreed with. They state that "recordings are random in their local sampling" which is almost certainly untrue when it comes to electrophysiology which tends to oversample task-modulated excitatory neurons (https://elifesciences.org/articles/69068). I also disagree that "each neuron's connectivity is unique, and vertebrate brains lack 'identified neurons' characteristic of simple organisms. While brains are only eutelic and "nameable" in only the simplest organisms (C. elegans), cell types are exceedingly stereotyped in their connectivity even in mammals and such connectivity defines their computational properties. Thus I don't find the premise the authors state in the next sentence to be undermined ("it seems unlikely that a single neuron's happenstance imprinting of its unique connectivity should generalize across stimuli and animals"). Overall, I found this subsection to rely on false premises and in my opinion it should be removed.

At the suggestion of R2, we removed the paragraph in question. However, we would like to address some points of disagreement:

We agree that electrophysiology, along with spike-sorting, quality metrics, and filtering of low-firing neurons, leads to oversampling of task-modulated neurons. However, when we stated that recordings are random in their local sampling, we were referring to structural (anatomical) randomness, not functional randomness. In other words, the recorded neurons were not specifically targeted (see below).

Electrode arrays, such as Neuropixels, record from hundreds of neurons within a small volume relative to the total number of neurons and the volume of a given brain region. For instance, the paper R2 referenced includes a statement supporting this: “... assuming a 50-μm ‘listening radius’ for the probes (radius of half-cylinder around the probe where the neurons’ spike amplitude is sufficiently above noise to trigger detection) …, the average yield of 116 regular-spiking units/probe (prior to QC filtering) would imply a density of 42,000 neurons/mm³, much lower than the known density of ~90,000 neurons/mm³ for excitatory cells in mouse visual cortex….”

If we take the estimated volume of V1 to be approximately 3 mm³, this region could theoretically be subdivided into multiple cylinders with a 100-μm diameter. While stereotaxic implantation of the probe mitigates some variability, the natural anatomical variability across individual animals introduces spatially random sampling. This was the randomness we were referring to, and thus, we disagree with the assertion that our claim is “almost certainly untrue.”

Additionally, each cortical pyramidal neuron is understood to have ~ 10,000 presynaptic partners. It is highly unlikely that these connections are entirely pre-specified, perfectly replicated within the same animal, and identical across all members of species. Further, there is enormous diversity in the activity properties of even neighboring cells of the same type. Consider pyramidal neurons in V1. Single neuron firing rates are log normally distributed, there are many of combinations of tuning properties (i.e., direction, orientation) that must occupy each point in retinotopic space, and there is powerful experience dependent change in the connectivity of these cells. We suggest that it is inconceivable that any two neurons, even within a small region of V1, have identical connectivity.

Minor Comments:

(1) Although the description of confusion matrices is good from a didactic perspective, some of this could be moved to methods to simplify the paper.

We thank the reviewer for the suggestion. However, given the broad readership of eLife, we gently suggest that confusion matrices are not a trivial and universally appreciated plotting format. For the purpose of accessibility, a brief and didactic 2-sentence description will make the paper far more comprehensible to many readers at little cost to experts.

(2) Figure 3A: It is concluded in their subsequent figure that the longer the measured amount of time, the better the decoding performance. Thus it makes sense why the average PSTHs do not show significant decoding of areas or structures

That is a good observation. However, all features were calculated from the same duration of data, except in Figure 3B, where we tested the effect of duration. The averaged PSTH was calculated from the same length of data as the ISI distribution and binned to have the same number of feature lengths as the ISI distribution (refer to Methods section). Therefore, we interpreted this as an indication of information degradation through averaging, rather than an effect of data length (Line 234 - 237).

(3) Figure 3D: A Gaussian is used to fit the ISI distributions here but ISI distributions do not follow a normal distribution, they follow an inverse gamma distribution.

We agree with the reviewer and we are familiar with the literature that the ISI distribution is best fitted by a gamma family distribution (as a recent, but not earliest example: Li et al. 2018). However, we did not fit a gaussian (or any distribution) to the data, we just calculated the sample mean and variance. Reporting sample mean and variance (or standard deviation) is not something that is only done for Gaussian distributions. They are broadly used metrics that simply have additional intrinsic meaning for Gaussian distributions. We used the schematic illustration in Fig 3D because mean and variance are much more familiar in Gaussian distribution context, but ultimately that does not affect our analyses in Fig 3 E-F. Alternatively, the alpha and beta intrinsic parameters of a gamma distribution could have been used, but they are known by a much smaller portion of neuroscientists.

Li, M., Xie, K., Kuang, H., Liu, J., Wang, D., Fox, G. E., ... & Tsien, J. Z. (2018). Spike-timing pattern operates as gamma-distribution across cell types, regions and animal species and is essential for naturally-occurring cognitive states. Biorxiv, 145813(10.1101), 145813.

(4) Figure 3G: Something is wrong with this figure as each vertical bar is supposed to represent a drifting grating onset but yet, they are all at 5 hz despite the PSTH being purportedly shown at many different frequencies from 1 to 15 hz.

We appreciate your attention to detail, but we are not representing the onset of individual drifting gratings in this. We just meant to represent the overall start\end of the drifting grating session. We did not intend to signal the temporal frequency of the drifting gratings (or the spatial frequency, orientation, or contrast).

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

The mechanism, as I understand it, is different from what the authors described before in the RNN with tonic gain changes. As uncertainty increases, the network enters a regime in which the two excitatory populations start to oscillate. My intuition is that this oscillation arises from the feedback loop created by the new gain control mechanism. If my intuition is correct, I think it would be worth to explain this mechanism in the paper more explicitly.

While interesting, this intuition is not correct. The oscillations are generated by the interaction between excitatory and inhibitory nodes in the network and occur in the model even with stationary gain. All of the plots in figure 3 exploring the dynamical regime of the network at different input x gain combinations (i.e., where the oscillatory regime is characterised) are simulations run with stationary gain.

To ensure that this intuition is more clearly presented in the manuscript, we have edited the description in the text.

P. 12: “Because of the large size of the network, we could not solve for the fixed points or study their stability analytically. Instead, we opted for a numerical approach and characterised the dynamical regime (i.e. the location and existence of approximate fixed-point attractors) across all combinations of (static) gain and  visited by the network.”

Reviewer #2 (Public review):

- The demonstration of the causal role of gain modulation in perceptual switches is partial. This causality is clearly demonstrated in the simulation work with the RNN. However, it is not fully demonstrated in the pupil analysis and the fMRI analysis. One reason is that this work is correlative (which is already very informative). An analysis of the timing of the effect might have overcome this limitation. For example, in a previous study, the same group showed that fMRI activity in the LC region precedes changes in the energy landscape of fMRI dynamics, which is a step towards investigating causal links between gain modulation, changes in the energy landscape and perceptual switches.

Thank you for the suggestion, which we considered in detail. Unfortunately, the  temporal and spatial resolution of the fMRI data collected for this study precluded the same analyses we’ve run in previous work, however this is an important question for future work.

- Some effects may reflect the expectation of a perceptual switch rather than the perceptual switch itself. To mitigate this risk, the design of the fMRI task included catch trials, in which no switch occurs, to reduce the expectation of a switch. The pupil study, however, did not include such catch trials.

We agree that this is a limitation of the current study, which we previously highlighted in the methods section.

- The paper uses RNN-based modelling to provide mechanistic insight into the role of gain modulation in perceptual switches. However, the RNN solves a task that differs markedly from that performed by human participants, which may limit the explanatory value of the model. The RNN is provided with two inputs characterising the sensory evidence supporting the first and last image category in the sequence (e.g. plane and shark). In contrast, observers in the task were naïve as to the identity of the last image at the beginning of the sequence. The brain first receives sensory evidence about the image category (e.g. plane) with which the sequence begins, which is very easy to recognise, then it sees a sequence of morphed images and has to discover what the final image category will be. To discover the final image category, the brain has to search a vast space of possible second images (it is a shark?, a frog?, a bird?, etc.), rather than comparing the likelihood of just two categories. This search process and the perceptual switch in the task appear to be mechanistically different from the competition between two inputs in the RNN.

We appreciate the critical analysis of the experimental paradigm but disagree with the reviewers conclusions for two keys reasons: 1) Participants prior exposure to the images, such that they could create an expectation about what stimulus category a particular image would transition into (i.e., the image could not switch into any possible category); and 2) even if the reviewers’ concern was founded, models of K winner-take-all decision making are structured identically irrespective of whether the options are 2 or K options all that changes is the simulated reaction times which depend linearly on the K (for an example model see Hugh Wilson’s textbook Spikes, Decisions, and Actions, 1999, p.89-91). For these reasons, we maintain that the RNN is a sensible representation of the behavioural task.

- Another aspect of the motivation for the RNN model remains unclear. The authors introduce dynamic gain modulation in the RNN, but it is not clear what the added value of dynamic gain modulation is. Both static (Fig. S1) and dynamic (Fig. 2F) gain modulation lead to the predicted effect: faster switching when the gain is larger.

While we agree that the effect is observable with both static and dynamic gain, the stronger construct validity associated with the dynamic approach, including a stronger link with the observed pupil dynamics and a rich literature associated with modelling the behavioural consequences of surprise/uncertainty led us to the conclusion that the dynamical approach was a better representation of our hypothesis.

- Fig 1C: I don't see a "top grey bar" indicating significance.

Thank you for catching this, the caption has been amended. The text was from an older version of the manuscript.

- p. 10, reference to fig 3F seems incorrect: there is Fig 3F upper and Fig 3F lower, and nothing on Fig 3 and its legend mention the lesion of units

This has been amended. We meant to refer to 2F.

- In the response letter you mention a MATLAB tutorial, but I could not find it.

This has been amended. Github repository can be found at https://github.com/ShineLabUSYD/AmbiguousFigures

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript reports that expression of the E. coli operon topAI/yjhQ/yjhP is controlled by the translation status of a small open reading frame, that authors have discovered and named toiL, located in the leader region upstream of the operon. Authors propose the following model for topAI activation: Under normal conditions, toiL is translated but topAI is not expressed because of Rho-dependent transcription termination within the topAI ORF and because its ribosome binding site and start codon are trapped in an mRNA hairpin. Ribosome stalling at various codons of the toiL ORF, prompted in this work by some ribosome-targeting antibiotics, triggers an mRNA conformational switch which allows translation of topAI and, in addition, activation of the operon's transcription because presence of translating ribosomes at the topAI ORF blocks Rho from terminating transcription. The model is appealing and several of the experimental data mainly support it. However, it remains unanswered what is the true trigger of the translation arrest at toiL and what is the physiological role of the induced expression of the topAI/yjhQ/yjhP operon.

Reviewer #2 (Public review):

Summary:

Baniulyte and Wade describe how translation of an 8-codon uORF denoted toiL upstream of the topAI-yjhQP operon is responsive to different ribosome-targeting antibiotics, consequently controlling translation of the TopAI toxin as well as Rho-dependent termination with the gene.

Strengths:

The authors used multiple different approaches such as a genetic screen to identify factors such as 23S rRNA mutations that affect topA1 expression and ribosome profiling to examine the consequences of various antibiotics on toiL-mediated regulation.

Weaknesses:

Future experiments will be needed to better understand the physiological role of the toiL-mediated regulation and elucidate the mechanism of specific antibiotic sensing.

The results are clearly described, and the revisions have helped to improve the presentation of the data.

Reviewer #3 (Public review):

In this revised manuscript, the authors provide convincing data to support an elegant model in which ribosome stalling by ToiL promotes downstream topAI translation and prevents premature Rho-dependent transcription termination. However, the physiological consequences of activating topAI-yjhQP expression upon exposure to various ribosome-targeting antibiotics remain unresolved. The authors have satisfactorily addressed all major concerns raised by the reviewers, particularly regarding the SHAPE-seq data. Overall, this study underscores the diversity of regulatory ribosome-stalling peptides in nature, highlighting ToiL's uniqueness in sensing multiple antibiotics and offering significant insights into bacterial gene regulation coordinated by transcription and translation.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

- Showing the ribosome density profiles of topAI/yjhQP and toiL in control and tetracycline treated cells is necessary to support that ribosome arrest at toiL increases translation of topAI/yjhQP.

Figure 7B shows ribosome density around the start of toiL. Ribosome density increases across topAI in the presence of tetracycline, but we have opted not to show this region because we cannot say whether the increase in ribosome occupancy (represented in Figure 7A) is due to an increase in translation efficiency, RNA level, or both.

- The subinhibitory antibiotic concentrations used in the reporter assays were based on MICs reported in the literature. This is not appropriate since MICs can greatly vary between strains, antibiotic solution stocks, and experimental conditions.

Reported MICs were used as an initial guide for selecting antibiotic concentrations to test in our reporter assays. We have added text to indicate this, and to highlight that MICs vary considerably between strains.

- toiL sequence may have evolved to maintain base-pairing with the topAI upstream region rather than, as authors suggest in Discussion, to respond to antibiotic-mediated arrest in an amino acid sequence specific manner.

We have chosen to frame this as speculation.

- Authors may consider commenting on the possibility that chloramphenicol does not induce because ToiL lacks alanine residues, whose presence at specific places of a nascent protein have been shown to promote chloramphenicol action (2016 PNAS 113:12150; 2022 NSMB 29:152).

This is a great point as none of our stalling reporters included an ORF with alanine. We now include a short paragraph in the Discussion section to raise this possibility.

- Tetracycline was added at the "subinhibitory concentration" of 8 ug/mL for the reporter assays but at 1 ug/mL for the ribosome profiling experiments. Authors should explain what was the rational for this.

We think the reviewer is mixing up the epidemiological cut-off value of 8 ug/mL with the concentration used in experiments (0.5-1 ug/mL for reporter assays and ribosome profiling). The text was confusing, so we have added a sentence to the Methods section to indicate that epidemiological cut-off values and MICs were only a guide for selecting antibiotic concentrations to test.

Reviewer #2 (Recommendations for the authors):

I wish the authors had been slightly less dismissive of the reviewers' comments. At a minimum, it would be nice if the authors could be consistent about the ribosome representation throughout the manuscript;

We apologize if our previous responses gave the impression of being dismissive. That was certainly not our intention. We greatly value the reviewers' feedback, and we appreciate the opportunity to clarify any misunderstandings. We believe the reviewer is referring to the different shape and color of the ribosome in Figures 8 and 9, and Figure 8 figure supplement 2, which we have now corrected.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #2 (Public Review):

Comments on revisions:

Although the authors have revealed the sulfane sulfur content in native MT-3, my question, namely, whether canonical MT-1 and MT-2 contained sulfane sulfur after the induction has been left.

The authors argue that the biological significance of sulfane sulfur in MTs lies in its ability to contribute to metal binding affinity, provide a sensing mechanism against oxidative stress, and aid in the regulation of the protein. Due to their biological roles, induced MT-1 and MT-2 could contain sulfane sulfur in their molecules. Thus, I expect the authors to evaluate or explain the sulfane sulfur content in induced MT-1 and MT-2.

Thank you for your valuable comments. In this study, we were not able to examine the role of sulfane sulfur in the induced forms of MT-1 and MT-2. However, this topic is undoubtedly important and intriguing; therefore, we will continue to explore it in future studies.

Reviewer #3 (Public Review):

Comments on revisions:

The revised manuscript is only slightly changed from the original, with the inclusion of a supplementary figure (Fig. S2) and minor changes in the text. The authors did not choose to carry out the quantitative Zn binding experiment (which I really wanted to see), but given the complexities of the experiment, I'll let it go.

Fig. 9: the authors imply in the mechanistic "redox-switch" figure that Trx/TR can not reduce persulfide linkages. A number of groups have shown this to be the case. I recommend modifying the figure legend or text to make this clear to the reader.

Thank you for your understanding. Regarding the "redox-switch" figure, although some groups have demonstrated the ability of Trx to reduce persulfide moieties, as you pointed out, we have addressed this discrepancy in the Discussion section as follows (lines 357-361): “In contrast, Trx has been proposed to reduce the persulfide moiety of PTP1B (37) and albumin (38, 39). A possible explanation for this discrepancy is that apo-GIF/MT-3-persulfide is rapidly changed into a different conformation that is topologically resistant to Trx reduction. In other words, Trx may exhibit substrate specificity.” Additionally, we have inserted the following sentence just before the above discussion to further clarify this point:“This suggests that the persulfide moiety in GIF/MT-3 appears to be relatively stable against Trx reduction.”

Author response:

Reviewer 1:

We thank the reviewer for his/her very positive comments.

Reviewer 2:

We thank the reviewer for his/her positive evaluation. We plan to add RNAseq data of yeast wild-type and JDP mutant strains as more direct readout for the role of Apj1 in controlling Hsf1 activity. We agree with the reviewer that our study includes one major finding: the central role of Apj1 in controlling the attenuation phase of the heat shock response. In accordance with the reviewer we consider this finding highly relevant and interesting for a broad readership. We agree that additional studies are now necessary to mechanistically dissect how the diverse JDPs support Hsp70 in controlling Hsf1 activity. We believe that such analysis should be part of an independent study but we will indicate this aspect as part of an outlook in the discussion section of a revised manuscript.

Reviewer 3:

We thank the reviewer for his/her suggestions. We agree that it is sometimes difficult to distinguish direct effects of JDP mutants on heat shock regulation from indirect ones, which can result from the accumulation of misfolded proteins that titrate Hsp70 capacity. We also agree that an in vitro reconstitution of Hsf1 displacement from DNA by Apj1/Hsp70 will be important, also to dissect Apj1 function mechanistically. We will add this point as outlook to the revised manuscript.

Author response:

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

eLife Assessment

This important and creative study finds that the uplift of the Qinghai-Tibet Plateau-via its resultant monsoon system rather than solely its high elevation-has shifted avian migratory directions from a latitudinal to a longitudinal orientation. However, the main claims are incomplete and only partially supported, as the reliance on eBird data-which lacks the resolution to capture population-specific teleconnections-combined with a limited tracking dataset covering only seven species leaves key aspects of the argument underdetermined, and the critical assumption of niche conservatism is not sufficiently foregrounded in the manuscript. More clearly communicating these limitations would significantly enhance the interpretability of the results, ensuring that the major conclusions are presented in the context of these essential caveats.

We appreciate your positive comments and constructive suggestions. We fully acknowledge your concerns about clearly communicating the limitations associated with the data used and analytical assumptions. We will try to get more satellite tracking data of birds migrating across the plateau. We will carefully consider the insights that our paper can deliver and make sure the limitations of our datasets and the critical assumption of niche conservatism are clearly presented. By explicitly clarifying these caveats, we believe the transparency and interpretability of the findings will be much improved.

Public Reviews:

Reviewer #1 (Public review):

The authors have done a good job of responding to the reviewer's comments, and the paper is now much improved.

Again, we thank the reviewer for constructive comments during review.

Reviewer #2 (Public review):

I would like to thank the authors for the revision and the input they invested in this study.

We are grateful for your thoughtful feedback and enthusiasms, which will help us improve our manuscript.

With the revised text of the study, my earlier criticism holds, and your arguments about the counterfactual approach are irrelevant to that. The recent rise of the counterfactual approach might likely mirror the fact that there are too many scientists behind their computers, and few go into the field to collect in situ data. Studies like the one presented here are a good intellectual exercise but the real impact is questionable.

We understand your question about the relevance of the counterfactual approach used in our study. Our intent in using a counterfactual scenario (reconstructing migration patterns assuming pre-uplift conditions on the QTP) was to isolate the potential influence of the plateau’s geological history on current migration routes. We agree that such an approach must be used properly. In the revision, we will explicitly clarify why this counterfactual comparison is useful – namely, it provides a theoretical baseline to test how much the QTP’s uplift (and the associated monsoon system) might have redirected migration paths. We acknowledge that the counterfactual results are theoretical and will explicitly emphasise the assumptions involved (e.g. species–environment relationships hold between pre- and post- lift environments) in the main text. Nonetheless, we defend the approach as a valuable study design: it helps generate testable hypotheses about migration (for instance, that the plateau’s monsoon-driven climate, rather than just its elevation, introduces an east–west shift en route). We will also tone down the language around this analysis to avoid overstating its real-world relevance. In summary, we will clarify that the counterfactual analysis is meant to complement, not replace, empirical observations, and we will discuss its limitations so that its role is appropriately bounded in the paper.

All your main conclusions are inferred from published studies on 7! bird species. In addition, spatial sampling in those seven species was not ideal in relation to your target questions. Thus, no matter how fancy your findings look, the basic fact remains that your input data were for 7 bird species only! Your conclusion, “our study provides a novel understanding of how QTP shapes migration patterns of birds” is simply overstretching.

Thank you for your comments. We apologise for any confusion regarding the scope of our dataset. Our main conclusions are not solely derived from seven bird species. Rather, we integrated a full list of 50 bird species that migrate across the QTP and analysed their migratory patterns with eBird data. We studied the factors influencing their choices of migratory routes with seven species that were among the few with available tracking data across the QTP. In this revision, we will clarify the role of these seven species and the rationale for their selection. Additionally, we attempt to include more satellite tracking data to improve spatial coverage, as recommended by the reviewer and editor. Based on discussions with potential collaborators, we will hopefully include a number of at least 10 more species with available tracking data.

The way you respond to my criticism on L 81-93 is something different than what you admit in the rebuttal letter. The text of the ms is silent about the drawbacks and instead highlights your perspective. I understand you; you are trying to sell the story in a nice wrapper. In the rebuttal you state: “we assume species' responses to environments are conservative and their evolution should not discount our findings.” But I do not see that clearly stated in the main text.

Thanks, as suggested we will clearly state the assumptions of niche conservatism in the Introduction.

In your rebuttal, you respond to my criticism of "No matter how good the data eBird provides is, you do not know population-specific connections between wintering and breeding sites" when you responded: ... "we can track the movement of species every week, and capture the breeding and wintering areas for specific populations" I am having a feeling that you either play with words with me or do not understand that from eBird data nobody will be ever able to estimate population-specific teleconnections between breeding and wintering areas. It is simply impossible as you do not track individuals. eBird gives you a global picture per species but not for particular populations. You cannot resolve this critical drawback of your study.

We agree that inferring population-specific migratory connections (teleconnections) from eBird data is challenging and inherently limited. eBird provides occurrence records for species, but it generally cannot distinguish which breeding population an individual bird came from or exactly where it goes for winter. However, in this study we intend to infer broad-scale movement patterns (e.g. general directions and stopover regions) rather than precise one-to-one population linkages. In the revision, we will carefully rephrase those sections to make clear that our inferences are at the species level and at large spatial scales. We will also explicitly state in the Discussion that confirming population connectivity would require targeted tracking or genetic studies, and that our eBird-based analysis can only suggest plausible routes and region-to-region linkages. We will contrast migratory routes identified by using eBird data and satellite tracking for the same species to check their similarity. We argue that, even with its limits, the eBird dataset can still yield useful insights (such as identifying major flyway corridors over the QTP).

I am sorry that you invested so much energy into this study, but I see it as a very limited contribution to understanding the role of a major barrier in shaping migration.

Thank you for recognising our efforts in the study. By integrating both satellite tracking and community-contributed data, we explored how the uplift of the QTP could shape avian migration across the area. We believe our findings provide important insights of how birds balance their responses to large-scale climate change and geological barrier, which yields the most comprehensive picture to date of how the QTP uplift shapes migratory patterns of birds. We will also acknowledge the study’s limitations to ensure that readers understand the context and constraints of our findings.

My modest suggestion for you is: go into the field. Ideally use bird radars along the plateau to document whether the birds shift the directions when facing the barrier.

We appreciate your suggestions to incorporate field tracking or radar studies to strengthen our results. All coauthors have years of field experiences, even on the QTP and Arctic. For example, the tracking data of peregrine falcons (Falco peregrinus) that we will incorporate in the revision are collected with during our own fieldwork in the Arctic for more than six years. We agree that more direct tracking (through GPS tagging or radar) would be an ideal way to validate migration pathways and population connectivity. In this revision, as stated above we will try to more species with satellite tracking data. We will also note that future studies should build on our findings by using dedicated tracking of more individual birds and radar monitoring of migration over the QTP. We will cite recent advances in these techniques and suggest that incorporating more tracking data could further test the hypotheses generated by our analyses.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

L55 "an important animal movement behaviour is.." Is there any unimportant animal movement? I mean this sentence is floppy, empty.

We will rewrite this sentence to remove any ambiguous phrasing.

L 152-154 This sentence is full of nonsense or you misinterpretation. First of all, the issue of inflexible initiation of migration was related to long-distance migrants only! The way you present it mixes apples and oranges (long- and short-distance migrants). It is not "owing to insufficient responses" but due to inherited patterns of when to take off, photoperiod and local conditions.

We will remove the sentence to avoid misinterpretation.

L 158 what is a migration circle? I do not know such a term.

We will amend it as “annual migration cycle”, which is a more common way to describe the yearly round-trip journey between breeding and wintering grounds of birds.

L 193 The way you present and mix capital and income breeding theory with your simulation study is quite tricky and super speculative.

We will present this idea as an inference rather than a conclusion: “This pattern could be consistent with a ‘capital breeding’ strategy — where birds rely on energy reserves acquired before breeding — rather than an ‘income’ strategy that depends on food acquired during breeding. However, we note that this interpretation would require further study.” By adding this caution, we will make it clear that we are not asserting this link as proven fact, only suggesting it as one possible explanation. We will also double-check that the rest of the discussion around this point is framed appropriately.

The following is the authors’ response to the previous reviews

eLife Assessment

This study addresses a novel and interesting question about how the rise of the Qinghai-Tibet Plateau influenced patterns of bird migration, employing a multi-faceted approach that combines species distribution data with environmental modeling. The findings are valuable for understanding avian migration within a subfield, but the strength of evidence is incomplete due to critical methodological assumptions about historical species-environment correlations, limited tracking data, and insufficient clarity in species selection criteria. Addressing these weaknesses would significantly enhance the reliability and interpretability of the results.

We would like to thank you and two anonymous reviewers for your careful, thoughtful, and constructive feedback on our manuscript. These reviews made us revisit a lot of our assumptions and we believe the paper is much improved as a result. In addition to minor points, we have made three main changes to our manuscript in response to the reviews. First, we addressed the concerns on the assumptions of historical species-environment correlations from perspectives of both theoretical and empirical evidence. Second, we discussed the benefits and limitations of using tracking data in our study and demonstrate how the findings of our study are consolidated with results of previous studies. Third, we clarified our criteria for selecting species in terms of both eBird and tracking data.

Below, we respond to each comment in turn. Once again, we thank you all for your feedback.

Public Reviews:

Reviewer #1 (Public review):

Strengths:

This is an interesting topic and a novel theme. The visualisations and presentation are to a very high standard. The Introduction is very well-written and introduces the main concepts well, with a clear logical structure and good use of the literature. The methods are detailed and well described and written in such a fashion that they are transparent and repeatable.

We are appreciative of the reviewer’s careful reading of our manuscript, encouraging comments and constructive suggestions.

Weaknesses:

I only have one major issue, which is possibly a product of the structure requirements of the paper/journal. This relates to the Results and Discussion, line 91 onwards. I understand the structure of the paper necessitates delving immediately into the results, but it is quite hard to follow due to a lack of background information. In comparison to the Methods, which are incredibly detailed, the Results in the main section reads as quite superficial. They provide broad overviews of broad findings but I found it very hard to actually get a picture of the main results in its current form. For example, how the different species factor in, etc.

Yes, it is the journal request to format in this way (Methods follows the Results and Discussion) for the article type of short reports. As suggested, in the revision we have elaborated on details of our findings, in terms of (i) shifts of distribution of avian breeding and wintering areas under the influence of the uplift of the Qinghai-Tibet Plateau (Lines 102-116), and (ii) major factors that shape current migration patterns of birds in the plateau (Lines 118-138). We have also better referenced the approaches we used in the study.

Reviewer #2 (Public review):

Summary:

The study tries to assess how the rise of the Qinghai-Tibet Plateau affected patterns of bird migration between their breeding and wintering sites. They do so by correlating the present distribution of the species with a set of environmental variables. The data on species distributions come from eBird. The main issue lies in the problematic assumption that species correlations between their current distribution and environment were about the same before the rise of the Plateau. There is no ground truthing and the study relies on Movebank data of only 7 species which are not even listed in the study. Similarly, the study does not outline the boundaries of breeding sites NE of the Plateau. Thus it is absolutely unclear potentially which breeding populations it covers.

We are very grateful for the careful review and helpful suggestions. We have revised the manuscript carefully in response to the reviewer’s comments and believe that it is much improved as a result. Below are our point-by-point replies to the comments.

Strengths:

I like the approach for how you combined various environmental datasets for the modelling part.

We appreciate the reviewer’s encouragement.

Weaknesses:

The major weakness of the study lies in the assumption that species correlations between their current distribution and environments found today are back-projected to the far past before the rise of the Q-T Plateau. This would mean that species responses to the environmental cues do not evolve which is clearly not true. Thus, your study is a very nice intellectual exercise of too many ifs.

This is a valid concern. We have addressed this from both the perspectives of the theoretical design of our study and empirical evidence.

First, we agree with the reviewer that species responses to environmental cues might vary over time. Nonetheless, the simulated environments before the uplift of the plateau serve as a counterfactual state in our study. Counterfactual is an important concept to support causation claims by comparing what happened to what would have happened in a hypothetical situation: “If event X had not occurred, event Y would not have occurred” (Lewis 1973). Recent years have seen an increasing application of the counterfactual approach to detect biodiversity change, i.e., comparing diversity between the counterfactual state and real estimates to attribute the factors causing such changes (e.g., Gonzalez et al. 2023). Whilst we do not aim to provide causal inferences for avian distributional change, using the counterfactual approach, we are able to estimate the influence of the plateau uplift by detecting the changes of avian distributions, i.e., by comparing where the birds would have distributed without the plateau to where they currently distributed. We regard the counterfactual environments as a powerful tool for eliminating, to the extent possible, vagueness, as opposed to simply description of current distributions of birds. Therefore, we assume species’ responses to environments are conservative and their evolution should not discount our findings. We have clarified this in the Introduction (Lines 81-93).

Second, we used species distribution modelling to contrast the distributions of birds before and after the uplift of the plateau under the assumption that species tend to keep their ancestral ecological traits over time (i.e., niche conservatism). This indicates a high probability for species to distribute in similar environments wherever suitable. Particularly, considering bird distributions are more likely to be influenced by food resources and vegetation distributions (Qu et al. 2010, Li et al. 2021, Martins et al. 2024), and the available food and vegetation before the uplift can provide suitable habitats for birds (Jia et al. 2020), we believe the findings can provide valuable insights into the influence of the plateau rise on avian migratory patterns. Having said that, we acknowledge other factors, e.g., carbon dioxide concentrations (Zhang et al. 2022), can influence the simulations of environments and our prediction of avian distribution. We have clarified the assumptions and evidence we have for the modelling in Methods (Lines 362-370).

The second major drawback lies in the way you estimate the migratory routes of particular birds. No matter how good the data eBird provides is, you do not know population-specific connections between wintering and breeding sites. Some might overwinter in India, some populations in Africa and you will never know the teleconnections between breeding and wintering sites of particular species. The few available tracking studies (seven!) are too coarse and with limited aspects of migratory connectivity to give answer on the target questions of your study.

We agree with the reviewer that establishing interconnections for birds is important for estimating the migration patterns of birds. We employed a dynamic model to assess their weekly distributions. Thus, we can track the movement of species every week, and capture the breeding and wintering areas for specific populations. That being said, we acknowledge that our approach can be subjected to the patchy sampling of eBird data. In contrast, tracking data can provide detailed information of the movement patterns of species but are limited to small numbers of species due to the considerable costs and time needed. We aimed to adopt the tracking data to examine the influence of focal factors on avian migration patterns, but only seven species, to the best of our ability, were acquired. Moreover, similar results were found in studies that used tracking data to estimate the distribution of breeding and wintering areas of birds in the plateau (e.g., Prosser et al. 2011, Zhang et al. 2011, Zhang et al. 2014, Liu et al. 2018, Kumar et al. 2020, Wang et al. 2020, Pu and Guo 2023, Yu et al. 2024, Zhao et al. 2024). We believe the conclusions based on seven species are rigour, but their implications could be restricted by the number of tracking species we obtained. We have better demonstrated how our findings on breeding and wintering areas of birds are reinforced by other studies reporting the locations of those areas. We have also added a separate caveat section to discuss the limitations stated above (Lines 202-215).

Your set of species is unclear, selection criteria for the 50 species are unknown and variability in their migratory strategies is likely to affect the direction of the effects.

In this revision, we have clarified the selection criteria for the 50 species and outlined the boundaries of the breeding areas of all birds (Lines 243-249). Briefly, we first obtained a full list of birds in the plateau from Prins and Namgail (2017). We then extracted species identified as full migrants in Birdlife International (https://datazone.birdlife.org/species/spcdistPOS) from the full list. Migratory birds may follow a capital or income migratory strategy depending on how much birds ingest endogenous reserved energy gained prior to reproduction. We have added discussions on how these migratory strategies might influence the effects of environment on migratory direction (Lines 183-200).

In addition, the position of the breeding sites relative to the Q-T plate will affect the azimuths and resulting migratory flyways. So in fact, we have no idea what your estimates mean in Figure 2.

We calculated the azimuths not only by the angles between breeding sites and wintering sites but also based on the angles between the stopovers of birds. Therefore, the azimuths are influenced by the relative positions of breeding, wintering and stopover sites. This would minimize the possible errors by just using breeding areas such as the biases caused by relative locations of breeding areas to the QTP as the reviewer pointed. We have better explained this both in the Introduction, Methods and legend of Figure 2.

There is no way one can assess the performance of your statistical exercises, e.g. performances of the models.

As suggested, we have reported Area Under the Curve (AUC) of the Receiver Operator Characteristic (ROC)assess the performances of the models (Table S1). AUC is a threshold-independent measurement for discrimination ability between presence and random points (Phillips et al. 2006). When the AUC value is higher than 0.75, the model was considered to be good (Elith et al. 2006). (Lines 379-383).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

This is an interesting topic and a novel theme. The visualisations and presentation are to a very high standard. The Introduction is very well-written and introduces the main concepts well, with a clear logical structure and good use of the literature. The Methods are detailed and well described and written in such a fashion that they are transparent and repeatable.

I only have one major issue, which is possibly a product of the structure requirements of the paper/journal. With the Results and Discussion, line 91 onwards. I understand the structure of the paper necessitates delving immediately into the results, but it is quite hard to follow due to a lack of background information. In comparison to the Methods, which are incredibly detailed, the Results in the main section read quite superficial. They provide broad overviews of broad findings but I found it very hard to actually get a picture of the main results in its current form. For example, how the different species factor in, etc.

Please see our responses above.

Reviewer #2 (Recommendations for the authors):

Methodological issues:

Line 219 Why have you selected only 64 species and what were the selection criteria?

We have clarified the selection criteria (Lines 243-248). Briefly, we first obtained a full list of birds in the plateau from Prins and Namgail (2017). We then extracted species identified as full migrants in Birdlife International (https://datazone.birdlife.org/species/spcdistPOS) from the full list.

Minor:

Line 219 eBird has very uneven distribution, especially in vast areas of Russia. How can your exercise on Lines 232-238 overcome this issue?

Yes, eBird data can be biased due to patchy sampling and variation of observers’ skills in identifying species. To address this issue, we have developed an adaptive spatial-temporal modelling (stemflow; Chen et al. 2024) to correct the imbalance distribution of data and modelled the observer experience to address the bias in recognising species. The stemflow was developed based on a machine learning modelling framework (AdaSTEM) which leverages the spatio-temporal adjacency information of sample points to model occurrence or abundance of species at different scales. It has been frequently used in modelling eBird data (Fink et al. 2013, Johnston et al. 2015, Fink et al. 2020) and has been proven to be efficient and advanced in multi-scale spatiotemporal data modelling. We have better explained this (Lines 251-270; Lines 307-321).

Line 54 This sentence sounds very empty and in fact does not tell us much.

We have adjusted this sentenced to “Animal movement underpins species’ spatial distributions and ecosystem processes”.

Line 55 Again a sentence that implies a causality of the annual cycle to make the species migrate. It does not make sense.

We have revised this sentence as “An important animal movement behaviour is migrating between breeding and wintering grounds”.

Line 58 How is our fascination with migratory journeys related to the present article? I think this line is empty.

We have changed this sentence to “Those migratory journeys have intrigued a body of different approaches and indicators to describe and model migration, including migratory direction, speed, timing, distance, and staging periods”.

Figure 1 - ABC insets are OK, but a combination of lati- and longitudinal patterns is possible, e.g. in species with conservative strategies or for whatever other reason.

Thank you for the suggestion. We kept the ABC insets rather than combining them together as we believe this can deliver a clear structure of influence of QTP uplift under different scenarios.

The legend to Figure 2 is not self-explanatory. Please make it clear what the response variable is and its units. The first line of the legend should read something like The influence of environmental factors on the direction of avian migration.

Thank you. We have amended the legends of Figure 2 as suggested:

“Figure 2. The influence of environmental factors on the direction of avian migration.  Migratory directions are calculated based on the azimuths between each adjacent stopover, breeding and wintering areas for each species. We employ multivariate linear regression models under the Bayesian framework to measure the correlation between environmental factors and avian migratory directions. Wind represents the wind cost calculated by wind connectivity. Vegetation is measured by the proportion of average vegetation cover in each pixel (~1.9° in latitude by 2.5° in longitude). Temperature is the average annual temperature. Precipitation is the average yearly precipitation. All environmental layers are obtained using the Community Earth System Model. West QTP, central QTP, and East QTP denote areas in the areas west (longitude < 73°E), central (73°E ≤ longitude < 105°E), and east of (longitude ≥ 105°E) the Qinghai-Tibet Plateau, respectively.”

References

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Author response:

Reviewer #1 (Public Review):

Overall, I find only two minor weaknesses. First, the insights of this study are, first and foremost, of feed-forward nature, and a feed-forward network would have been enough (and the more parsimonious model) to illustrate the results. While using a recurrent neural network (RNN) shows that the results are, in general, compatible with recurrent dynamics, the specific limitations imposed by RNNs (e.g., dynamical stability, low-dimensional internal dynamics) are not the focus of this study. Indeed, the additional RNN models in the supplementary material show that under more constrained conditions for the RNN (low-dimensional dynamics), using the input control alone runs into difficulties.

We thank the reviewer for raising this important point. While we agree that recurrent dynamics were not the focus of this study, we would like to point out that 1) dynamics, of some kind, are necessary to simulate the decoder fitting process and 2) recurrent neural networks (RNNs) are valuable for obtaining general insights on how biological constraints shape the reachable manifold:

(1) To simulate the decoder fitting process, we had to simulate neural activity during the so-called “calibration task”. Some dynamics to these responses are necessary to produce a population response with dimensionality resembling what was found in experiments (10 dimensions). Moreover, dynamics are necessary to create a common direction of high variance across population responses to the calibration task stimuli (see Supplementary Figure 2a and surrounding discussion), which is necessary to reproduce the biases in readouts demonstrated in Figure 4 (as many within-manifold decoder perturbations are aligned with it; Supplementary Figure 2b).

Because feed-forward networks lack dynamics, reproducing our results with a feed-forward network would require using an input with dynamics. Rather than making an arbitrary choice for these input dynamics, we chose to keep the input static and instead generate the dynamics with a RNN, which is in line with recent models of motor cortex.

We agree, however, that this is an important point worth clarifying in the manuscript. In our revision we will aim to add a demonstration of how to reproduce a subset of our results with a feed-forward network and a dynamic input.

(2) While we agree that RNNs impose certain limitations over feed-forward networks, we see these limitations as an advantage because they provide a framework for understanding the structure of the reachable manifold in terms of biological constraints. For example, our simulations in Supplementary Figure 1 show that the dimensionality of the reachable manifold is highly dependent on recurrent connectivity: inhibition-stabilized connectivity makes it higher-dimensional whereas task-specific optimized connectivity makes it lower-dimensional. Such insights are valuable to understand the broader implications and experimental predictions of the re-aiming strategy.

Because feed-forward networks are untied from the reality of recurrent cortical circuitry, they cannot be characterized in terms of such biological constraints. For instance, as the reviewer points out, dynamical stability is not a well-defined property of feed-forward networks. Such models therefore cannot provide any insight into how the biological constraint of dynamical stability could influence the reachable manifold (which we show it does in Figure 5b). Relatedly, feed-forward networks cannot be optimized to solve complex spatiotemporal tasks like the ballistic reaching task we used for our task-optimized RNN (Supplementary Figure 1, right column), so cannot be used to understand how such behavioral constraints would influence the reachable manifold.

We agree that these reasons for using RNNs are subtle and left implicit in how they are currently exposed in the text. We will add a discussion point clarifying these in our revision.

Second, explaining the quantitative differences between the model and data for shifts in tuning curves seems to take the model a bit too literally. The model serves greatly for qualitative observations. I assume, however, that many of the unconstrained aspects of the model would yield quantitatively different results.

We completely agree: our model is best used to provide a qualitative description of the capabilities of the re-aiming strategy. We will be sure to revise our manuscript to keep such quantitative comparisons at a minimum.

Reviewer #2 (Public Review):

The authors mention alternative models (eg, based on synaptic plasticity in the RNN and/or input weights) that can explain the same experimental data that they do, they do not provide any direct comparisons to those models. Thus, the main argument that the authors have in favor of their model is the fact that it is more plausible because it relies on performing the optimization in a low-dimensional space. It would be nice to see more quantitative arguments for why the re-aiming strategy may be more plausible than synaptic plasticity (either by showing that it explains data better, or explaining why it may be more optimal in the context of fast learning).

We agree this remains a limitation of our study. To contrast our re-aiming model with models of synaptic plasticity (in the input and/or recurrent weights), we have included substantial discussion of these alternative models in two sections of the manuscript:

• Introduction, where we elaborate on the argument that synaptic plasticity requires solving an exceptionally difficult optimization problem in high dimensions

• Discussion section “The role of synaptic plasticity in BCI learning”, where we review a number of synaptic plasticity models and experimental results they can account for

We fully agree that more quantitative comparisons remain an important follow-up to this line of research. However, it is worth noting that there are many such models out there. Moreover, as is the case with many computational models, the results one can achieve with any given model can be highly sensitive to a number of different hyperparameters (e.g. learning rates). We therefore feel that a more rigorous comparison requires deeper study and is out of scope of this manuscript.

In particular, the authors model the adaptation to outside-manifold perturbations (OMPs) through a "generalized re-aiming strategy". This assumes the existence of additional command variables, which are not used in the original decoding task, but can then be exploited to adapt to these OMPs. While this model is meant to capture the fact that optimization is occurring in a low-dimensional subspace, the fact that animals take longer to adapt to OMPs suggests that WMPs and OMPs may rely on different learning mechanisms, and that synaptic plasticity may actually be a better model of adaptation to OMPs. 

We thank the reviewer for raising this question. We agree that the fact that animals take longer to adapt to OMPs suggests that the underlying learning strategy is somehow different. But the argument we try to make in this section of the paper is that it in fact does not require an entirely different mechanism. Our simulations show that the same mechanism of re-aiming can suffice to learn OMPs, but it simply requires re-aiming in the larger space of all command variables available to the motor system (rather than just the two command variables evoked by the calibration task). Because this is a much higher-dimensional search space (10-20 vs. 2 dimensions, which is a substantial difference due to the curse of dimensionality), we argue that learning should be slower, even though the mechanism (i.e. re-aiming) is the same.

This is an important and somewhat surprising takeaway from these simulations, which we will try to bring up more explicitly and clearly in the revision.

It would be important to discuss how exactly generalized re-aiming would differ from allowing plasticity in the input weights, or in all weights in the network. Do those models make different predictions, and could they be differentiated in future experiments?

They do in fact make different predictions, and we thank the reviewer for asking and pointing out the lack of discussion of this point. The key difference between these two learning mechanisms is demonstrated in Figure 5b: under generalized re-aiming, there is a fundamental limit to the set of activity patterns one can learn to produce in the brain-computer interface (BCI) learning task. This is quantified in that analysis by the asymptotic participation ratio of the reachable manifold as K increases, which indicates that there is a limited ~12-dimensional subspace that the reachable manifold can occupy. The specific orientation of this subspace is determined by the (recurrent and input) connectivity of the recurrent neural network. With synaptic plasticity in any of the weight matrices (Wrec,Win,U), this subspace could be re-oriented in any arbitrary direction. Our theory of “generalized re-aiming” therefore predicts that the reachable manifold is 1) constrained to a low-d subspace and 2) is not modified when learning BCIs with outside-manifold perturbations.

Experimentally testing this would require a within-/outside- manifold perturbation BCI learning task akin to that of Sadtler et al, but where the “intrinsic manifold” is measured from population responses evoked by every possible motor command so as to entirely contain the full reachable manifold at max K. This would require measuring motor cortical activity during naturalistic behavior under a wide range of conditions, rather than just in response to the 2D cursor movements on the screen used in the calibration task of the original study. In this case, learning outside-manifold perturbations would require re-orienting the reachable manifold, so a pure generalized re-aiming strategy would fail to learn them. Synaptic plasticity, on the other hand, would not.

We will be sure to elaborate further on this claim in the revised manuscript.

Author response:

Reviewer #1 (Public review):

Weaknesses:

(1) The manuscript's logical flow is challenging and hard to follow, and key arguments could be more clearly structured, particularly in transitions between mechanistic components.

We will revise our manuscript so as to make it easy to follow the logical flow in transitions between mechanistic components.

(2) The causality between stress-induced α2A-AR internalization and the enhanced MAO-A remains unclear. Direct experimental evidence is needed to determine whether α2A-AR internalization itself or Ca²⁺ drives MAO-A activation, and how they activate MAO-A should be considered.

We believe that the causality between stress-induced α2A-AR internalization and the enhancement of MAO-A is clearly demonstrated by our current experiments, while our explanations may be improved by making them easier to understand especially for those who are not expert on electrophysiology.

Firstly, it is well established that autoinhibition in LC neurons is mediated by α2A-AR coupled-GIRK (Arima et al., 1998, J Physiol; Williams et al., 1985, Neuroscience). We found that spike frequency adaptation in LC neurons was also mediated by α2A-AR coupled GIRK-I (Fig. 1A-I), and that α2A-AR coupled GIRK-I underwent [Ca²⁺]_i-dependent rundown (Figs. 2, S1, S2), leading to an abolishment of spike-frequency adaptation (Figs. S4). [Ca²⁺]_i-dependent rundown of α2A-AR coupled GIRK-I was prevented by barbadin (Fig 2G-J), which prevents the internalization of G-protein coupled receptor (GPCR) channels.

Abolishment of spike frequency adaptation itself, i.e., “increased spike activity” can increase [Ca²⁺]_i because [Ca²⁺]_i is entirely dependent on the spike activity as shown by Ca²⁺ imaging method in Figure S3.

Thus, α2A-AR internalization can increase [Ca²⁺]_i through the abolishment of autoinhibition or spike frequency adaptation, and a [Ca²⁺]_i increase drives MAO-A activation as reported previously (Cao et al., 2007, BMC Neurosci). The mechanism how Ca²⁺ activates MAO-A is beyond the scope of the current study.

Our study just focused on the mechanism how chronic or sever stress can cause persistent overexcitation and how it results in LC degeneration.

(3) The connection between α2A-AR internalization and increased cytosolic NA levels lacks direct quantification, which is necessary to validate the proposed mechanism.

Direct quantification of the relationship between α2A-AR internalization and increased cytosolic NA levels may not be possible, and may not be necessarily needed to be demonstrated as explained below.

The internalization of α2A-AR can increase [Ca²⁺]_i through the abolishment of autoinhibition or spike frequency adaptation, and [Ca²⁺]_i increases can facilitate NA autocrine (Huang et al., 2007), similar to the transmitter release from nerve terminals (Kaeser & Regehr, 2014, Annu Rev Physiol).

Autocrine released NA must be re-uptaken by NAT (NA transporter), which is firmly established (Torres et al., 2003, Nat Rev Neurosci). Re-uptake of NA by NAT is the only source of intracellular NA, and NA re-uptake by NAT should be increased as the internalization of NA biding site (α2A-AR) progresses in association with [Ca²⁺]_i increases (see page 11, lines 334-336).

Thus, the connection between α2A-AR internalization and increased cytosolic NA levels is logically compelling, and the quantification of such connection may not be possible at present (see the response to the comment made by the Reviewer #1 as Recommendations for the authors (2) and beyond the scope of our current study.

(4) The chronic stress model needs further validation, including measurements of stress-induced physiological changes (e.g., corticosterone levels) to rule out systemic effects that may influence LC activity. Additional behavioral assays for spatial memory impairment should also be included, as a single behavioral test is insufficient to confirm memory dysfunction.

It is well established that restraint stress (RS) increases corticosterone levels depending on the period of RS (García-Iglesias et al., 2014, Neuropharmacology), although we are not reluctant to measure the corticosterone levels. In addition, there are numerous reports that showed the increased activity of LC neurons in response to various stresses (Valentino et al., 1983; Valentino and Foote, 1988; Valentino et al., 2001; McCall et al., 2015), as described in the text (page 4, lines 96-98). Measurement of cortisol levels may not be able to rule out systemic effects of CRS on the whole brain.

We had already done another behavioral test using elevated plus maze (EPM) test.

By combining the two tests, it may be possible to more accurately evaluate the results of Y-maze test by differentiating the memory impairment from anxiety. However, the results obtained by these behavioral tests are just supplementary to our current aim to elucidate the cellular mechanisms for the accumulation of cytosolic free NA. Its subsequent anxiety and memory impairment are just supplementary to our current study. We will soften the implication of anxiety and memory impairment.

(5) Beyond b-arrestin binding, the role of alternative internalization pathways (e.g., phosphorylation, ubiquitination) in α2A-AR desensitization should be considered, as current evidence is insufficient to establish a purely Ca²⁺-dependent mechanism.

We can hardly agree with this comment.

It was clearly demonstrated that repeated application of NA itself did not cause desensitization of α2A-AR (Figure S1A-D), and that the blockade of b-arrestin binding by barbadin completely suppressed the Ca²⁺-dependent downregulation of GIRK (Fig. 2G-K). These observations can clearly rule out the possible involvement of phosphorylation or ubiquitination for the desensitization.

Not only the barbadin experiment, but also the immunohistochemistry and western blot method clearly demonstrated the decrease of α2A-AR expression on the cell membrane (Fig. 3).

Ca²⁺-dependent mechanism of the rundown of GIRK was convincingly demonstrated by a set of different protocols of voltage-clamp study, in which Ca²⁺ influx was differentially increased. The rundown of GIRK-I was orderly potentiated or accelerated by increasing the number of positive command pulses each of which induces Ca²⁺ influx (compare Figure S1E-J, Figure S2A-E and Figure S2F-K along with Fig. 2A-F). The presence or absence of Ca²⁺ currents and the amount of Ca²⁺ currents determined the trend of the rundown of GIRK-I (Figs. 2, S1 and S2). Because the same voltage protocol hardly caused the rundown when it did not induce Ca²⁺ currents in the absence of TEA (Fig. S1F; compare with Fig. 2B), blockade of Ca²⁺ currents by nifedipine would not be so beneficial.

We believe the series of voltage-clamp protocols convincingly demonstrated the orderly involvement of [Ca²⁺]_i in accelerating the rundown of GIRK-I.

(6) NA leakage for free NA accumulation is also influenced by NAT or VMAT2. Please discuss the potential role of VMAT2 in NA accumulation within the LC in AD.

We will discuss the role of VMAT2 in NA accumulation, especially when VMAT2 was impaired. Indeed, it has been demonstrated that reduced VMAT2 levels increased susceptibility to neuronal damage: VMAT2 heterozygote mice displayed increased vulnerability to MPTP as evidenced by reductions in nigral dopamine cell counts (Takahashi et al, 1997, PNAS). Thus, when the activity of VMAT2 in LC neurons were impaired by chronic restraint stress, cytosolic NA levels in LC neurons would increase. We will add such discussion in the revised manuscript.

(7) Since the LC is a small brain region, proper staining is required to differentiate it from surrounding areas. Please provide a detailed explanation of the methodology used to define LC regions and how LC neurons were selected among different cell types in brain slices for whole-cell recordings.

LC neurons were identified immunohistochemically and electrophysiologically as we previously reported (see Fig. 2 in Front. Cell. Neurosci. 16:841239. doi: 10.3389/fncel.2022.841239). A delayed spiking pattern in response to depolarizing pulses (Figure S9) applied at a hyperpolarized membrane potential was commonly observed in LC neurons in many studies (Masuko et al., 1986; van den Pol et al., 2002; Wagner-Altendorf et al., 2019).

Reviewer #2 (Public review):

Weaknesses:

(1) The manuscript reports that chronic stress for 5 days increases MAO-A levels in LC neurons, leading to the production of DOPEGAL, activation of AEP, and subsequent tau cleavage into the tau N368 fragment, ultimately contributing to neuronal damage. However, the authors used wild-type C57BL/6 mice, and previous literature has indicated that AEP-mediated tau cleavage in wild-type mice is minimal and generally insufficient to cause significant behavioral alterations. Please clarify and discuss this apparent discrepancy.

In our study, normalized relative value of AEP-mediated tau cleavage (Tau N368) was much higher in CRS mice than non-stress wild-type mice. It is not possible to compare AEP-mediated tau cleavage between our non-stress wild type mice and those observed in previous study (Zhang et al., 2014, Nat Med), because band intensity is largely dependent on the exposure time and its numerical value is the normalized relative value. In view of such differences, our apparent band expression might have been intensified to detect small changes.

(2) It is recommended that the authors include additional experiments to examine the effects of different durations and intensities of stress on MAO-A expression and AEP activity. This would strengthen the understanding of stress-induced biochemical changes and their thresholds.

GIRK rundown was almost saturated after 3-day RS and remained the same in 5-day RS mice (Fig. 4A-G), which is consistent with the downregulation of α2A-AR and GIRK1 expression by 3-day RS (Fig. 3C, F and G; Fig. 4J and K). However, we examine the protein levels of MAO-A, pro/active-AEP and Tau N368 only in 5-day RS mice without examining in 3-day RS mice. This is because we considered the possibility that 3-day RS may be insufficient to induce changes in MAO-A, AEP and Tau N368 and some period of high [Ca²⁺]_i condition may be necessary to induce such changes. We will discuss this in the revised manuscript.

(3) Please clarify the rationale for the inconsistent stress durations used across Figures 3, 4, and 5. In some cases, a 3-day stress protocol is used, while in others, a 5-day protocol is applied. This discrepancy should be addressed to ensure clarity and experimental consistency.

Please see our response to the comment (2).

(4) The abbreviation "vMAT2" is incorrectly formatted. It should be "VMAT2," and the full name (vesicular monoamine transporter 2) should be provided at first mention.

Thank you for your suggestion. We will revise accordingly.

Author response:

We thank the referees for finding our work well written and systematic. We are planning a revision of the manuscript based on the public review and the confidential recommendations of the referees.

The role of axons:

Indeed, radial axon projections appear before mature epithelial stripes in the cornea (Iannaccone et al., 2012). Our claim is, however, not that guidance cues are absent, but that global cues are unnecessary. The alignment term in our model, together with evidence that corneal epithelial cells follow contact-mediated substrate cues (Walczysko et al., 2016), show that corneal cells migration is responsive to external forces, and the underlying patterns of axonal projections could be one of those cues.

Experiments (Collinson et al., 2002) and simulations in this work show that a rapid spiral epithelial flow forms first, with cells migrating radially for ~2 weeks before stripes become visible. Axons seeking the path of least resistance within this moving basal layer would therefore appear radial early on. By contrast, establishing visible stripes requires an entire cohort of epithelial cells to travel from the limbus to the central cornea (Fig. 7). Extensive in-vivo studies (Song et al., 2004; Leiper et al., 2009) find no evidence that axons direct epithelial migration; if anything, epithelial flow dictates axonal trajectories.

Geometry and boundaries:

The spiral also forms on a flat disc, but its exact shape changes with curvature and cap angle; this variation is seen across mammals, including humans (Dua et al., 1993) and in diseases such as keratoconus. On a spherical cap the boundary winding number fixes the interior index, so ongoing limbal influx keeps the total index = 1. 

In the revised version, we will therefore simulate a range of curvatures, cap angles, a prolate ellipsoid, and cases without limbal division, then compare with published data and disease states.

In-vitro data and parameter fits:

Although our dataset is limited, the inferred parameters match three independent invitro estimates (Kostanjevec et al. 2020; Saraswathibhatla et al. 2021; Kammeraat et al. in prep.). Spatial correlations exceed those expected from persistence alone, implying some polar alignment - consistent with Saraswathibhatla et al. 2021.  Slide-scanner images that we will include in the revision show cells are neither elongated nor nematically ordered. In the revision we will detail our parameter extraction, highlight evidence for alignment, stress the substrate-based activity mechanism, and draw attention to the supplementary videos.

Topological clarification:

Stagnation points can be seen as topological defects because classification depends only on vector directions. Boundary conditions can remove such defects in fluids, yet two sources/sinks still interact via the same logarithmic Green’s function that governs disclinations, despite di^erent physics. The Euler characteristic is a property of the surface; while the boundary winding number fixes the field index, it does not alter the surface’s Euler characteristic. 

In the revision, we will add a concise primer on the di^erential-geometric concepts to make these points explicit.

Author response:

We thank the reviewers for their thoughtful and generous assessment of our work. Overall, the reviewers found our work to be novel and relevant. In particular: reviewer #1 found that our manuscript “It is timely and highly valuable for the telomere field” reviewer #2 stated, “Overall, I find this manuscript worthy of publication, as the optimized END-seq methods described here will likely be widely utilized in the telomere field.” Reviewer #3 stated that “The study is original, the experiments were well-controlled and excellently executed.”

We are extremely grateful for these comments and want to thank all the reviewers and the editors for their time and effort in reviewing our work.

The reviewers had a number of suggestions to improve our work. We have addressed all the points as highlighted in the point-by-point responses below.

Reviewer 1:

One minor question would be whether the authors could expand more on the application of END-Seq to examine the processive steps of the ALT mechanism? Can they speculate if the ssDNA detected in ALT cells might be an intermediate generated during BIR (i.e., is the ssDNA displaced strand during BIR) or a lesion? Furthermore, have the authors assessed whether ssDNA lesions are due to the loss of ATRX or DAXX, either of which can be mutated in the ALT setting?

We appreciate the reviewer’s insightful questions regarding the application of our assays to investigate the nature of the ssDNA detected in ALT telomeres. Our primary aim in this study was to establish the utility of END-seq and S1-END-seq in telomere biology and to demonstrate their applicability across both ALT-positive and -negative contexts. We agree that exploring the mechanistic origins of ssDNA would be highly informative, and we anticipate that END-seq–based approaches will be well suited for such future studies. However, it remains unclear whether the resolution of S1-END-seq is sufficient to capture transient intermediates such as those generated during BIR. We have now included a brief speculative statement in the revised discussion addressing the potential nature of ssDNA at telomeres in ALT cells.

Reviewer #2:

How can we be sure that all telomeres are equally represented? The authors seem to assume that END-seq captures all chromosome ends equally, but can we be certain of this? While I do not see an obvious way to resolve this experimentally, I recommend discussing this potential bias more extensively in the manuscript.

We thank the reviewer for raising this important point. END-seq and S1-END-seq are unbiased methods designed to capture either double-stranded or single-stranded DNA that can be converted into blunt-ended double-stranded DNA and ligated to a capture oligo. As such, if a subset of telomeres cannot be processed using this approach, it is possible that these telomeres may be underrepresented or lost. However, to our knowledge, there are no proposed telomeric structures that would prevent capture using this method. For example, even if a subset of telomeres possesses a 5′ overhang, it would still be captured by END-seq. Indeed, we observed the consistent presence of the 5′-ATC motif across multiple cell lines and species (human, mouse, and dog). More importantly, we detected predictable and significant changes in sequence composition when telomere ends were experimentally altered, either in vivo (via POT1 depletion) or in vitro (via T7 exonuclease treatment). Together, these findings support the robustness of the method in capturing a representative and dynamic view of telomeres across different systems.

That said, we have now included a brief statement in the revised discussion acknowledging that we cannot fully exclude the possibility that a subset of telomeres may be missed due to unusual or uncharacterized structures

I believe Figures 1 and 2 should be merged.

We appreciate the reviewer’s suggestion to merge Figures 1 and 2. However, we feel that keeping them as separate figures better preserves the logical flow of the manuscript and allows the validation of END-seq and its application to be presented with appropriate clarity and focus. We hope the reviewer agrees that this layout enhances the clarity and interpretability of the data.

Scale bars should be added to all microscopy figures.

We thank the reviewer for pointing this out. We have now added scale bars to all the microscopy panels in the figures and included the scale details in the figure legends.

Reviewer #3:

Overall, the discussion section is lacking depth and should be expanded and a few additional experiments should be performed to clarify the results.

We thank the reviewer for the suggestions. Based on this reviewer’s comments and comments for the other reviewers, we incorporated several points into the discussion. As a result, we hope that we provide additional depth to our conclusions.

(1) The finding that the abundance of variant telomeric repeats (VTRs) within the final 30 nucleotides of the telomeric 5' ends is similar in both telomerase-expressing and ALT cells is intriguing, but the authors do not address this result. Could the authors provide more insight into this observation and suggest potential explanations? As the frequency of VTRs does not seem to be upregulated in POT1-depleted cells, what then drives the appearance of VTRs on the C-strand at the very end of telomeres? Is CST-Pola complex responsible?

The reviewer raises a very interesting and relevant point. We are hesitant at this point to speculate on why we do not see a difference in variant repeats in ALT versus non-ALT cells, since additional data would be needed. One possibility is that variant repeats in ALT cells accumulate stochastically within telomeres but are selected against when they are present at the terminal portion of chromosome ends. However, to prove this hypothesis, we would need error-free long-read technology combined with END-seq. We feel that developing this approach would be beyond the scope of this manuscript.

(2) The authors also note that, in ALT cells, the frequency of VTRs in the first 30 nucleotides of the S1-END-SEQ reads is higher compared to END-SEQ, but this finding is not discussed either. Do the authors think that the presence of ssDNA regions is associated with the VTRs? Along this line, what is the frequency of VTRs in the END-SEQ analysis of TRF1-FokI-expressing ALT cells? Is it also increased? Has TRF1-FokI been applied to telomerase-expressing cells to compare VTR frequencies at internal sites between ALT and telomerase-expressing cells?

Similarly to what is discussed above, short reads have the advantage of being very accurate but do not provide sufficient length to establish the relative frequency of VTRs across the whole telomere sequence. The TRF1-FokI experiment is a good suggestion, but it would still be biased toward non-variant repeats due to the TRF1-binding properties. We plan to address these questions in a future study involving long-read sequencing and END-seq capture of telomeres.

Finally, in these experiments (S1-END-SEQ or END-SEQ in TRF1-Fok1), is the frequency of VTRs the same on both the C- and the G-rich strands? It is possible that the sequences are not fully complementary in regions where G4 structures form.

We thank the reviewer for this observation. While we do observe a higher frequency of variant telomeric repeats (VTRs) in the first 30 nucleotides of S1-END-seq reads compared to END-seq in ALT cells, we are currently unable to determine whether this difference is significant, as an appropriate control or matched normalization strategy for this comparison is lacking. Therefore, we refrain from overinterpreting the biological relevance of this observation.

The reviewer is absolutely correct. Our calculation did not exclude the possibility of extrachromosomal DNA as a source of telomeric ssDNA. We have now addressed this point in our discussion.

The reviewer is correct in pointing out that we still do not know what causes ssDNA at telomeres in ALT cells. Replication stress seems the most logical explanation based on the work of many labs in the field. However, our data did not reveal any significant difference in the levels of ssDNA at telomeres in non-ALT cells based on telomere length. We used the HeLa1.2.11 cell line (now clarified in the Materials section), which is the parental line of HeLa1.3 and has similarly long telomeres (~20 kb vs. ~23 kb). Despite their long telomeres and potential for replication-associated challenges such as G-quadruplex formation, HeLa1.2.11 cells did not exhibit the elevated levels of telomeric ssDNA that we observed in ALT cells (Figure 4B). Additional experiments are needed to map the occurrence of ssDNA at telomeres in relation to progression toward ALT.

(3) Based on the ratio of C-rich to G-rich reads in the S1-END-SEQ experiment, the authors estimate that ALT cells contain at least 3-5 ssDNA regions per chromosome end. While the calculation is understandable, this number could be discussed further to consider the possibility that the observed ratios (of roughly 0.5) might result from the presence of extrachromosomal DNA species, such as C-circles. The observed increase in the ratio of C-rich to G-rich reads in BLM-depleted cells supports this hypothesis, as BLM depletion suppresses C-circle formation in U2OS cells. To test this, the authors should examine the impact of POLD3 depletion on the C-rich/G-rich read ratio. Alternatively, they could separate high-molecular-weight (HMW) DNA from low-molecular-weight DNA in ALT cells and repeat the S1-END-SEQ in the HMW fraction.

The reviewer is absolutely correct. Our calculation did not exclude the possibility of extrachromosomal DNA as a source of telomeric ssDNA. We have now addressed this point in our discussion.

(4) What is the authors' perspective on the presence of ssDNA at ALT telomeres? Do they attribute this to replication stress? It would be helpful for the authors to repeat the S1-END-SEQ in telomerase-expressing cells with very long telomeres, such as HeLa1.3 cells, to determine if ssDNA is a specific feature of ALT cells or a result of replication stress. The increased abundance of G4 structures at telomeres in HeLa1.3 cells (as shown in J. Wong's lab) may indicate that replication stress is a factor. Similar to Wong's work, it would be valuable to compare the C-rich/G-rich read ratios in HeLa1.3 cells to those in ALT cells with similar telomeric DNA content.

The reviewer is correct in pointing out that we still do not know what causes ssDNA at telomeres in ALT cells. Replication stress seems the most logical explanation based on the work of many labs in the field. However, our data did not reveal any significant difference in the levels of ssDNA at telomeres in non-ALT cells based on telomere length. We used the HeLa1.2.11 cell line (now clarified in the Materials section), which is the parental line of HeLa1.3 and has similarly long telomeres (~20 kb vs. ~23 kb). Despite their long telomeres and potential for replication-associated challenges such as G-quadruplex formation, HeLa1.2.11 cells did not exhibit the elevated levels of telomeric ssDNA that we observed in ALT cells (Figure 4B). Additional experiments are needed to map the occurrence of ssDNA at telomeres in relation to progression toward ALT.

Finally, Reviewer #3 raises a list of minor points:

(1) The Y-axes of Figure 4 have been relabeled to account for the G-strand reads.

(2) Statistical analyses have been added to the figures where applicable.

(3) The manuscript has been carefully proofread to improve clarity and consistency throughout the text and figure legends.

(4) We have revised the text to address issues related to the lack of cross-referencing between the supplementary figures and their corresponding legends.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

Summary:

In this manuscript, authors have tried to repurpose cipargamin (CIP), a known drug against Plasmodium and Toxoplasma against Babesia. They proved the efficacy of CIP on Babesia in nanomolar range. In silico analyses revealed the drug resistance mechanism through a single amino acid mutation at amino acid position 921 on the ATP4 gene of Babesia. Overall, the conclusions drawn by the authors are well justified by their data. I believe this study opens up a novel therapeutic strategy against babesiosis.

Strengths:

Authors have carried out a comprehensive study. All the experiments performed were carried out methodically and logically.

We appreciate your positive feedback. Your acknowledgment reinforces our commitment to rigor and thoroughness in our research.

Reviewer #3 (Public review):

Summary:

The authors aim to establish that cipargamin can be used for the treatment of infection caused by Babesia organisms.

Strengths:

The study provides strong evidence that cipargamin is effective against various Babesia species. In vitro growth assays were used to establish that cipargamin is effective against Babesia bovis and Babesia gibsoni. Infection of mice with Babesia microti demonstrated that cipargamin is as effective as the combination of atovaquone plus azithromycin. Cipargamin protected mice from lethal infection with Babesia rodhaini. Mutations that confer resistance to cipargamin were identified in the gene encoding ATP4, a P-type Na+ ATPase that is found in other apicomplexan parasites, thereby validating ATP4 as the target of cipargamin. A 7-day treatment of cipagarmin, when combined with a single dose of tafenoquine, was sufficient to eradicate Babesia microti in a mouse model of severe babesiosis caused by lack of adaptive immunity.

Thank you for the comments and for your time to review our manuscript.

Weaknesses:

Cipargamin was tested in vivo at a single dose administered daily for 7 days. Despite the prospect of using cipargamin for the treatment of human babesiosis, there was no attempt to identify the lowest dose of cipagarmin that protects mice from Babesia microti infection. In the SCID mouse model, cipargamin was tested in combination with tafenoquine but not with atovaquone and/or azithromycin, although the latter combination is often used as first-line therapy for human babesiosis caused by Babesia microti.

Thank you for your insightful comments. We agree that using a single daily dose over 7 days is one of the limitations in the in vivo trial. Our main goals were to demonstrate cipargamin's efficacy and understand its antibabesial agent mechanism. For future work, we plan to conduct dose‐optimization studies to determine the lowest effective dose in vivo. Regarding the drug combination in the SCID mouse model, although atovaquone and/or azithromycin are frequently used as first-line therapies for human babesiosis, resistance to these traditional drugs is emerging. Based on this challenge, we opted to evaluate a combination with tafenoquine as a novel partner, aiming to overcome resistance issues and improve therapeutic outcomes.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

None other than some minor grammatical mistakes.

We have corrected the grammatical mistakes.

Reviewer #3 (Recommendations for the authors):

The revised manuscript is much improved. I have the following comments.

Comment 1: Atovaquone plus azithromycin is effective against Babesia microti (Figure 1C) but not against Babesia rodhaini (Figure 1E). It would be valuable to provide a possible explanation.

Thank you for highlighting this issue. One potential explanation is that B. microti and B. rodhaini might have intrinsic differences in drug sensitivity and susceptibility. A previous study reported that both species possess a unique linear monomeric mitochondrial genome with a dual flip-flop inversion system, which generates four distinct genome structures (Hikosaka et al., 2012). In addition, previous studies have shown that mitochondria-associated energy production is greater in B. microti than in B. rodhaini (Shikano et al., 1998). This suggests that B. microti, whose metabolism is largely driven by mitochondrial function, may be more susceptible to drugs (like atovaquone) that induce parasite death by disrupting mitochondrial targets such as cytochrome b (Wormser et al., 2010). Moreover, B. rodhaini tends to proliferate more rapidly and causes acute infections, which may outpace any drug effects. Further, the rapid proliferation of apicomplexan parasites, as is the case in Plasmodium (Salcedo-Sora et al., 2014), Theileria (Metheni et al., 2015), and B. rodhaini (Rickard, 1970; Shikano et al., 1995), has been ascribed to glycolysis as the primary energy source. This may have contributed to the reduced efficacy of atovaquone and azithromycin in B. rodhaini-infected mice in the current study. Nonetheless, we plan to explore these interspecies differences in our future work.

Comment 2: The relapse that follows a 7-day treatment with cipargamin is transient in BALB/ mice infected with Babesia rodhaini (Figure 1E) but persistent in SCID mice infected with Babesia microti (Figure 5C). It would be valuable to provide a possible explanation.

Thank you for your insightful comment. One possible explanation is the difference in immune status between the two mouse models. BALB/c mice have a fully functional immune system that can likely clear residual parasites following a transient relapse after cipargamin treatment. In contrast, SCID mice lack an adaptive immune response, which might allow residual B. microti parasites to persist and cause a sustained relapse. Additionally, intrinsic differences between B. rodhaini and B. microti, such as growth rate or drug susceptibility, could also play a role. We plan to explore these factors in future studies.

Comment 3: The effect of cipargamin on parasite pH is the greatest when assessed 4 to 8 min after exposure is initiated (Figure 3E). Yet, resistance of parasites that carry a mutation in ATP4, the target of cipargamin, was assessed 20 min after cipargamin addition. At this time point, cipargamin has very little effect (Figure 3E). Accordingly, data reported in Figure 3G are of limited value.

Thank you for your comment. The initial pH increase we see around 4 to 8 minutes likely reflects the rapid inhibition of ATP4-mediated Na⁺/H⁺ exchange by cipargamin, which quickly alkalinizes the cell. However, after the initial increase, compensatory processes, such as proton influx or metabolic acid production, gradually restored the pH, resulting in a later decline. Although assessing the pH level at 20 minutes may have recorded less dramatic changes, it still allowed us to compare the sustained differences between wild-type and mutant strains. We agree that including earlier time points for the mutants might provide further insight and we will consider this in our future work.

Comment 4: In Figure 3H, please report the lack of statistical significance between wild-type parasites and parasites that carry the mutation L921V.

In Figure 3H, the ATPase activity in erythrocytes infected with wild-type parasites (6.31 ± 1.20 nmol Pi/mg protein/min) is higher than that of the L921V mutation (5.11 ± 0.50 nmol Pi/mg protein/min), but the difference is not statistically significant (P = 0.095), so no asterisk was added.

Comment 5: Tafenoquine was administered as a single 20 mg/kg dose. Please specify whether this dose is for tafenoquine succinate or tafenoquine base.

Thank you for raising this point. In our study, the single 20 mg/kg dose refers to tafenoquine succinate. We have clarified this detail in the revised manuscript (Line 40).

Comment 6: A single dose of 20 mg/kg tafenoquine succinate was first tested in the SCID mouse model of severe babesiosis by Mordue et al (JID 2019), not by Liu et al. (JID 2024). Please amend discussion accordingly (line 311). As correctly stated in the discussion, the single 20 mg/kg dose was not sufficient to prevent relapse of Babesia microti in the study by Mordue et al. Please provide a possible explanation for why no parasitemia was detected for 90 days in your SCID model (Figure 5C).

Thank you for your comment. We have modified the suggested citation (Line 309). As noted by Mordue et al. (JID 2019), a single 20 mg/kg dose of tafenoquine succinate was insufficient to prevent relapse in their SCID mouse model using B. microti (ATCC 30221 Gray strain). In our study, however, no parasitemia was detected for 90 days (Figure 5C) using the B. microti Peabody mjr strain (ATCC PRA-99). Differences in the parasite strain and the timing of treatment relative to infection may have contributed to the extended suppression of parasitemia observed in our study. We plan to explore these aspects in future work.

Comment 7: Real-time PCR was used to confirm eradication of Babesia microti infection (Figure 5D). Please specify the blood volume from which genomic DNA was extracted for each mouse. Please specify the amount of genomic DNA (i.e., not the volume) used in each reaction. Please explain how/why the cut-off was set at 35 cycles. What were the Ct values when blood was obtained from uninfected mice? For infected mice treated with cipargamin plus tafenoquine, there was no amplification. Was each reaction subjected to a maximum of 40 cycles (as suggested by Figure 5D)?

In our qPCR assay, genomic DNA was extracted from 200 µL of blood per mouse (Line 458). In each reaction, we used 100 ng of genomic DNA (Line 464), and the thermocycling conditions were set at 40 cycles. We set the cut-off at 35 cycles based on our optimization experiments: samples with Ct values ≤ 35 consistently indicated the presence of parasite DNA, while samples without parasite DNA (distilled water and DNA from uninfected mice) had CT values > 35 cycles or undetectable. Although each reaction was run for 40 cycles, for our analysis, we defined samples as negative if no signal was observed beyond cycle 35. In mice treated with cipargamin plus tafenoquine, no signal was detected until 40 cycles, indicating the absence of parasite DNA in the samples.

Comment 8:  Persistence of parasite DNA in blood of tafenoquine treated mice highlights the limitation of PCR to assess persistence of infection. That is, PCR cannot distinguish between viable parasites and non-viable (or dead) parasites. An adoptive transfer of blood to immunocompromised mice can help determine whether persistence of DNA is due to persistence of viable parasites. Because the experiment was carried out in SCID mice, no adoptive transfer is needed. Few parasites are required for a successful infection of immunocompromised mice (SCID mice included). Given that parasitemia never rose following treatment of SCID mice with a single dose of tafenoquine, it is highly likely that parasite DNA detected on day 90 post-infection in these tafenoquine treated mice came from persistent non-viable/dead parasites.

We appreciate your comment and acknowledge that the use of PCR has limitations in differentiating between live and dead parasites. It is possible that the residual DNA may represent a small population of dormant parasites that are not actively replicating and thus remain below the detection threshold of parasitemia. Even in highly immunocompromised SCID mice, such dormant parasites might persist without causing overt infection under our experimental conditions. An adoptive transfer experiment in SCID mice, although not strictly necessary, could validate whether the detection of low levels of DNA comes from viable parasites capable of reactivating under different circumstances. Future studies using more sensitive viability assays or adoptive transfer approaches could provide further insights into this possibility.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

This study examined the interaction between two key cortical regions in the mouse brain involved in goal-directed movements, the rostral forelimb area (RFA) - considered a premotor region involved in movement planning, and the caudal forelimb area (CFA) - considered a primary motor region that more directly influences movement execution. The authors ask whether there exists a hierarchical interaction between these regions, as previously hypothesized, and focus on a specific definition of hierarchy - examining whether the neural activity in the premotor region exerts a larger functional influence on the activity in the primary motor area than vice versa. They examine this question using advanced experimental and analytical methods, including localized optogenetic manipulation of neural activity in either region while measuring both the neural activity in the other region and EMG signals from several muscles involved in the reaching movement, as well as simultaneous electrophysiology recordings from both regions in a separate cohort of animals.

The findings presented show that localized optogenetic manipulation of neural activity in either RFA or CFA resulted in similarly short-latency changes in the muscle output and in firing rate changes in the other region. However, perturbation of RFA led to a larger absolute change in the neural activity of CFA neurons. The authors interpret these findings as evidence for reciprocal, but asymmetrical, influence between the regions, suggesting some degree of hierarchy in which RFA has a greater effect on the neural activity in CFA. They go on to examine whether this asymmetry can also be observed in simultaneously recorded neural activity patterns from both regions. They use multiple advanced analysis methods that either identify latent components at the population level or measure the predictability of firing rates of single neurons in one region using firing rates of single neurons in the other region. Interestingly, the main finding across these analyses seems to be that both regions share highly similar components that capture a high degree of variability of the neural activity patterns in each region. Single units' activity from either region could be predicted to a similar degree from the activity of single units in the other region, without a clear division into a leading area and a lagging area, as one might expect to find in a simple hierarchical interaction. However, the authors find some evidence showing a slight bias towards leading activity in RFA. Using a two-region neural network model that is fit to the summed neural activity recorded in the different experiments and to the summed muscle output, the authors show that a network with constrained (balanced) weights between the regions can still output the observed measured activities and the observed asymmetrical effects of the optogenetic manipulations, by having different within-region local weights. These results put into question whether previous and current findings that demonstrate asymmetry in the output of regions can be interpreted as evidence for asymmetrical (and thus hierarchical) inputs between regions, emphasizing the challenges in studying interactions between any brain regions.

Strengths:

The experiments and analyses performed in this study are comprehensive and provide a detailed examination and comparison of neural activity recorded simultaneously using dense electrophysiology probes from two main motor regions that have been the focus of studies examining goal-directed movements. The findings showing reciprocal effects from each region to the other, similar short-latency modulation of muscle output by both regions, and similarity of neural activity patterns without a clear lead/lag interaction, are convincing and add to the growing body of evidence that highlight the complexity of the interactions between multiple regions in the motor system and go against a simple feedforward-like network and dynamics. The neural network model complements these findings and adds an important demonstration that the observed asymmetry can, in theory, also arise from differences in local recurrent connections and not necessarily from different input projections from one region to the other. This sheds an important light on the multiple factors that should be considered when studying the interaction between any two brain regions, with a specific emphasis on the role of local recurrent connections, that should be of interest to the general neuroscience community.

Weaknesses:

While the similarity of the activity patterns across regions and lack of a clear leading/lagging interaction are interesting observations that are mostly supported by the findings presented (however, see comment below for lack of clarity in CCA/PLS analyses), the main question posed by the authors - whether there exists an endogenous hierarchical interaction between RFA and CFA - seems to be left largely open. 

The authors note that there is currently no clear evidence of asymmetrical reciprocal influence between naturally occurring neural activity patterns of the two regions, as previous attempts have used non-natural electrical stimulation, lesions, or pharmacological inactivation. The use of acute optogenetic perturbations does not seem to be vastly different in that aspect, as it is a non-natural stimulation of inhibitory interneurons that abruptly perturbs the ongoing dynamics.

We do believe that our optogenetic inactivation identifies a causal interaction between the endogenous activity patterns in the excitatory projection neurons, which we have largely silenced, and the downstream endogenous activity that is perturbed. The effect in the downstream region results directly from the silencing of activity in the excitatory projection neurons that mediate each region’s interaction with other regions. Here we have performed a causal intervention common in biology: a loss-of-function experiment. Such experiments generally reveal that a causal interaction of some sort is present, but often do not clarify much about the nature of the interaction, as is true in our case. By showing that a silencing of endogenous activity in one motor cortical region causes a significant change to the endogenous activity in another, we establish a causal relationship between these activity patterns. This is analogous to knocking out the gene for a transcription factor and observing causal effects on the expression of other genes that depend on it. 

Moreover, our experiments are, to our knowledge, the first that localize a causal relationship to endogenous activity in motor cortex at a particular point during a motor behavior. Lesion and pharmacological or chemogenetic inactivation have long-lasting effects, and so their consequences on firing in other regions cannot be attributed to a short-latency influence of activity at a particular point during movement. Moreover, the involvement of motor cortex in motor learning and movement preparation/initiation complicates the interpretation of these consequences in relation to movement execution, as disturbance to processes on which execution depends can impede execution itself. Stimulation experiments generate spiking in excitatory projection neurons that is not endogenous.

That said, we would agree that the form of the causal interaction between RFA and CFA remains unaddressed by our results. These results do not expose how the silenced activity patterns affect activity in the downstream region, just as knocking out a transcription factor gene does not expose how the transcription factor influences the expression of other genes. To show evidence for a specific type of interaction dynamics between RFA and CFA, a different sort of experiment would be necessary. See Jazayeri and Afraz, Neuron, 2017 for more on this issue.

Furthermore, the main finding that supports a hierarchical interaction is a difference in the absolute change of firing rates as a result of the optogenetic perturbation, a finding that is based on a small number of animals (N = 3 in each experimental group), and one which may be difficult to interpret. 

Though N = 3, we do show statistical significance. Moreover, using three replicates is not uncommon in biological experiments that require a large technical investment.

As the authors nicely demonstrate in their neural network model, the two regions may differ in the strength of local within-region inhibitory connections. Could this theoretically also lead to a difference in the effect of the artificial light stimulation of the inhibitory interneurons on the local population of excitatory projection neurons, driving an asymmetrical effect on the downstream region? 

We (Miri et al., Neuron, 2017) and others (Guo et al., Neuron, 2014) have shown that the effect of this inactivation on excitatory neurons in CFA is a near-complete silencing (90-95% within 20 ms). There thus is not much room for the effects on projection neurons in RFA to be much larger. We have measured these local effects in RFA as part of other work (Kristl et al., biorxiv, 2025), verifying that the effects on RFA projection neuron firing are not larger.

Moreover, the manipulation was performed upon the beginning of the reaching movement, while the premotor region is often hypothesized to exert its main control during movement preparation, and thus possibly show greater modulation during that movement epoch. It is not clear if the observed difference in absolute change is dependent on the chosen time of optogenetic stimulation and if this effect is a general effect that will hold if the stimulation is delivered during different movement epochs, such as during movement preparation.

We agree that the dependence of RFA-CFA interactions on movement phase would be interesting to address in subsequent experiments. While a strong interpretation of lesion results might lead to a hypothesis that premotor influence on primary motor cortex is local to, or stronger during, movement preparation as opposed to execution, at present there is to our knowledge no empirical support from interventional experiments for this hypothesis. Moreover, existing results from analysis of activity in these two regions have produced conflicting results on the strength of interaction between these regions during preparation. Compare for example BachschmidRomano et al., eLife, 2023 to Kaufman et al., Nature Neuroscience, 2014.

That said, this lesion interpretation would predict the same asymmetry we have observed from perturbations at the beginning of a reach - a larger effect of RFA on CFA than vice versa.

Another finding that is not clearly interpretable is in the analysis of the population activity using CCA and PLS. The authors show that shifting the activity of one region compared to the other, in an attempt to find the optimal leading/lagging interaction, does not affect the results of these analyses. Assuming the activities of both regions are better aligned at some unknown groundtruth lead/lag time, I would expect to see a peak somewhere in the range examined, as is nicely shown when running the same analyses on a single region's activity. If the activities are indeed aligned at zero, without a clear leading/lagging interaction, but the results remain similar when shifting the activities of one region compared to the other, the interpretation of these analyses is not clear.

Our results in this case were definitely surprising. Many share the intuition that there should be a lag at which the correlations in activity between regions may be strongest. The similarity in alignment across lags we observed might be expected if communication between regions occurs over a range of latencies as a result of dependence on a broad diversity of synaptic paths that connect neurons. In the Discussion, we offer an explanation of how to reconcile these findings with the seemingly different picture presented by DLAG.

Reviewer #2 (Public review):

Summary:

While technical advances have enabled large-scale, multi-site neural recordings, characterizing inter-regional communication and its behavioral relevance remains challenging due to intrinsic properties of the brain such as shared inputs, network complexity, and external noise. This work by Saiki-Ishkawa et al. examines the functional hierarchy between premotor (PM) and primary motor (M1) cortices in mice during a directional reaching task. The authors find some evidence consistent with an asymmetric reciprocal influence between the regions, but overall, activity patterns were highly similar and equally predictive of one another. These results suggest that motor cortical hierarchy, though present, is not fully reflected in firing patterns alone.

Strengths:

Inferring functional hierarchies between brain regions, given the complexity of reciprocal and local connectivity, dynamic interactions, and the influence of both shared and independent external inputs, is a challenging task. It requires careful analysis of simultaneous recording data, combined with cross-validation across multiple metrics, to accurately assess the functional relationships between regions. The authors have generated a valuable dataset simultaneously recording from both regions at scale from mice performing a cortex-dependent directional reaching task.

Using electrophysiological and silencing data, the authors found evidence supporting the traditionally assumed asymmetric influence from PM to M1. While earlier studies inferred a functional hierarchy based on partial temporal relationships in firing patterns, the authors applied a series of complementary analyses to rigorously test this hierarchy at both individual neuron and population levels, with robust statistical validation of significance.

In addition, recording combined with brief optogenetic silencing of the other region allowed authors to infer the asymmetric functional influence in a more causal manner. This experiment is well designed to focus on the effect of inactivation manifesting through oligosynaptic connections to support the existence of a premotor to primary motor functional hierarchy.

Subsequent analyses revealed a more complex picture. CCA, PLS, and three measures of predictivity (Granger causality, transfer entropy, and convergent cross-mapping) emphasized similarities in firing patterns and cross-region predictability. However, DLAG suggested an imbalance, with RFA capturing CFA variance at a negative time lag, indicating that RFA 'leads' CFA. Taken together these results provide useful insights for current studies of functional hierarchy about potential limitations in inferring hierarchy solely based on firing rates.

While I would detail some questions and issues on specifics of data analyses and modeling below, I appreciate the authors' effort in training RNNs that match some behavioral and recorded neural activity patterns including the inactivation result. The authors point out two components that can determine the across-region influence - 1) the amount of inputs received and 2) the dependence on across-region input, i.e., the relative importance of local dynamics, providing useful insights in inferring functional relationships across regions.

Weaknesses:

(1) Trial-averaging was applied in CCA and PLS analyses. While trial-averaging can be appropriate in certain cases, it leads to the loss of trial-to-trial variance, potentially inflating the perceived similarities between the activity in the two regions (Figure 4). Do authors observe comparable degrees of similarity, e.g., variance explained by canonical variables? Also, the authors report conflicting findings regarding the temporal relationship between RFA and CFA when using CCA/PLS versus DLAG. Could this discrepancy be due to the use of trial-averaging in former analyses but not in the latter?

We certainly agree that the similarity in firing patterns is higher in trial averages than on single trials, given the variation in single-neuron firing patterns across trials. Here, we were trying to examine the similarity of activity variance that is clearly movement dependent, as trial averages are, and to use an approach aligned with those applied in the existing literature. We would also agree that there is more that can be learned about interactions from trial-by-trial analysis. It is possible that the activity components identified by DLAG as being asymmetric somehow are not reflected strongly in trial averages. In our Discussion we offer another potential explanation that is based on other differences in what is calculated by DLAG and CCA/PLS.

We also note here that all of the firing pattern predictivity analysis we report (Figure 6) was done on single trial data, and in all cases the predictivity was symmetric. Thus, our results in aggregate are not consistent with symmetry purely being an artifact of trial averaging.

(2) A key strength of the current study is the precise tracking of forelimb muscle activity during a complex motor task involving reaching for four different targets. This rich behavioral data is rarely collected in mice and offers a valuable opportunity to investigate the behavioral relevance of the PM-M1 functional interaction, yet little has been done to explore this aspect in depth. For example, single-trial time courses of inter-regional latent variables acquired from DLAG analysis can be correlated with single-trial muscle activity and/or reach trajectories to examine the behavioral relevance of inter-regional dynamics. Namely, can trial-by-trial change in inter-regional dynamics explain behavioral variability across trials and/or targets? Does the inter-areal interaction change in error trials? Furthermore, the authors could quantify the relative contribution of across-area versus within-area dynamics to behavioral variability. It would also be interesting to assess the degree to which across-area and within-area dynamics are correlated. Specifically, can acrossarea dynamics vary independently from within-area dynamics across trials, potentially operating through a distinct communication subspace?

These are all very interesting questions. Our study does not attempt to parse activity into components predictive of muscle activity and others that may reflect other functions. Distinct components of RFA and CFA activity may very well rely on distinct interactions between them.

(3) While network modeling of RFA and CFA activity captured some aspects of behavioral and neural data, I wonder if certain findings such as the connection weight distribution (Figure 7C), across-region input (Figure 7F), and the within-region weights (Figure 7G), primarily resulted from fitting the different overall firing rates between the two regions with CFA exhibiting higher average firing rates. Did the authors account for this firing rate disparity when training the RNNs?

The key comparison in Figure 7 is shown in 7F, where the firing rates are accounted for in calculating the across-region input strength. Equalizing the firing rates in RFA and CFA would effectively increase RFA rates. If the mean firing rates in each region were appreciably dependent on across-region inputs, we would then expect an off-setting change in the RFA→CFA weights, such that the RFA→CFA distributions in 7F would stay the same. We would also expect the CFA→RFA weights would increase, since RFA neurons would need more input. This would shift the CFA→RFA (blue) distributions up. Thus, if anything, the key difference in this panel would only get larger. 

We also generally feel that it is a better approach to fit the actual firing rates, rather than normalizing, since normalizing the firing rates would take us further from the actual biology, not closer.

(4) Another way to assess the functional hierarchy is by comparing the time courses of movement representation between the two regions. For example, a linear decoder could be used to compare the amount of information about muscle activity and/or target location as well as time courses thereof between the two regions. This approach is advantageous because it incorporates behavior rather than focusing solely on neural activity. Since one of the main claims of this study is the limitation of inferring functional hierarchy from firing rate data alone, the authors should use the behavior as a lens for examining inter-areal interactions.

As we state above, we agree that examining interactions specific to movement-related activity components could reveal interesting structure in interregional interactions. Since it remains a challenge to rigorously identify a subset of neural activity patterns specifically related to driving muscle activity, any such analysis would involve an additional assumption. It remains unclear how well the activity that decoders use for predicting muscle activity matches the activity that actually drives muscle activity in situ.

To address this issue, which related to one raised by Reviewer #3 below, we have added an additional paragraph to the Discussion (see “Manifestations of hierarchy in firing patterns”).

Reviewer #3 (Public review):

This study investigates how two cortical regions that are central to the study of rodent motor control (rostral forelimb area, RFA, and caudal forelimb area, CFA) interact during directional forelimb reaching in mice. The authors investigate this interaction using

(1) optogenetic manipulations in one area while recording extracellularly from the other, (2) statistical analyses of simultaneous CFA/RFA extracellular recordings, and (3) network modeling.

The authors provide solid evidence that asymmetry between RFA and CFA can be observed, although such asymmetry is only observed in certain experimental and analytical contexts.

The authors find asymmetry when applying optogenetic perturbations, reporting a greater impact of RFA inactivation on CFA activity than vice-versa. The authors then investigate asymmetry in endogenous activity during forelimb movements and find asymmetry with some analytical methods but not others. Asymmetry was observed in the onset timing of movement-related deviations of local latent components with RFA leading CFA (computed with PCA) and in a relatively higher proportion and importance of cross-area latent components with RFA leading than CFA leading (computed with DLAG). However, no asymmetry was observed using several other methods that compute cross-area latent dynamics, nor with methods computed on individual neuron pairs across regions. The authors follow up this experimental work by developing a twoarea model with asymmetric dependence on cross-area input. This model is used to show that differences in local connectivity can drive asymmetry between two areas with equal amounts of across-region input.

Overall, this work provides a useful demonstration that different cross-area analysis methods result in different conclusions regarding asymmetric interactions between brain areas and suggests careful consideration of methods when analyzing such networks is critical. A deeper examination of why different analytical methods result in observed asymmetry or no asymmetry, analyses that specifically examine neural dynamics informative about details of the movement, or a biological investigation of the hypothesis provided by the model would provide greater clarity regarding the interaction between RFA and CFA.

Strengths:

The authors are rigorous in their experimental and analytical methods, carefully monitoring the impact of their perturbations with simultaneous recordings, and providing valid controls for their analytical methods. They cite relevant previous literature that largely agrees with the current work, highlighting the continued ambiguity regarding the extent to which there exists an asymmetry in endogenous activity between RFA and CFA.

A strength of the paper is the evidence for asymmetry provided by optogenetic manipulation. They show that RFA inactivation causes a greater absolute difference in muscle activity than CFA interaction (deviations begin 25-50 ms after laser onset, Figure 1) and that RFA inactivation causes a relatively larger decrease in CFA firing rate than CFA inactivation causes in RFA (deviations begin <25ms after laser onset, Figure 3). The timescales of these changes provide solid evidence for an asymmetry in the impact of inactivating RFA/CFA on the other region that could not be driven by differences in feedback from disrupted movement (which would appear with a ~50ms delay).

The authors also utilize a range of different analytical methods, showing an interesting difference between some population-based methods (PCA, DLAG) that observe asymmetry, and single neuron pair methods (granger causality, transfer entropy, and convergent cross mapping) that do not. Moreover, the modeling work presents an interesting potential cause of "hierarchy" or "asymmetry" between brain areas: local connectivity that impacts dependence on across-region input, rather than the amount of across-region input actually present.

Weaknesses:

There is no attempt to examine neural dynamics that are specifically relevant/informative about the details of the ongoing forelimb movement (e.g., kinematics, reach direction). Thus, it may be preemptive to claim that firing patterns alone do not reflect functional influence between RFA/CFA. For example, given evidence that the largest component of motor cortical activity doesn't reflect details of ongoing movement (reach direction or path; Kaufman, et al. PMID: 27761519) and that the analytical tools the authors use likely isolate this component (PCA, CCA), it may not be surprising that CFA and RFA do not show asymmetry if such asymmetry is related to the control of movement details. 

An asymmetry may still exist in the components of neural activity that encode information about movement details, and thus it may be necessary to isolate and examine the interaction of behaviorally-relevant dynamics (e.g., Sani, et al. PMID: 33169030).

To clarify, we are not claiming that firing patterns in no way reflect the asymmetric functional influence that we demonstrate with optogenetic inactivation. Instead, we show that certain types of analysis that we might expect to reflect such influence, in fact, do not. Indeed, DLAG did exhibit asymmetries that matched those seen in functional influence (at least qualitatively), though other methods we applied did not.

As we state above, we do think that there is more that can be gleaned by looking at influence specifically in terms of activity related to movement. However, if we did find that movement-related activity exhibited an asymmetry following functional influence, our results imply that the remaining activity components would exhibit an opposite asymmetry, such that the overall balance is symmetric. This would itself be surprising. We also note that the components identified by CCA and PLS do show substantial variation across reach targets, indicating that they are not only reflecting condition-invariant components. These analyses were performed on components accounting for well over 90% of the total activity variance, suggesting that both conditiondependent and condition-invariant components should be included.

To address the concern about condition-dependent and condition-invariant components, we have added a sentence to the Results section reporting our CCA and PLS results: “Because our results here involve the vast majority of trial-averaged activity variance, we expect that they encompass both components of activity that vary for different movement conditions (condition-dependent), and those that do not (condition-invariant).” To address the general concerns about potential differences in activity components specifically related to muscle activity, we have also added an additional paragraph to the Discussion (see “Manifestations of hierarchy in firing patterns”).

The idea that local circuit dynamics play a central role in determining the asymmetry between RFA and CFA is not supported by experimental data in this paper. The plausibility of this hypothesis is supported by the model but is not explored in any analyses of the experimental data collected. Given the focus on this idea in the discussion, further experimental investigation is warranted.

While we do not provide experimental support for this hypothesis, the data we present also do not contradict this hypothesis. Here we used modeling as it is often used - to capture experimental results and generate hypotheses about potential explanation. We do feel that our Discussion makes clear where the hypothesis derives from and does not misrepresent the lack of experimental support. We expect readers will take our engagement with this hypothesis with the appropriate grain of salt. The imaginable experiments to support such a hypothesis would constitute another substantial study, requiring numerous controls - a whole other paper in itself.

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors):

(1) There are a few small text/figure caption modifications that can be made for clarity of reading:

(2) Unclear sentence in the second paragraph of the introduction: "For example, stimulation applied in PM has been shown to alter the effects on muscles of stimulation in M1 under anesthesia, both in monkeys and rodents."

This sentence has been rephrased for clarity: “For example, in anesthetized monkeys34 and rodents35, stimulation in PM alters the effects of stimulation in M1 on muscles.”

(3) The first section of the results presents the optogenetic manipulation. However, the critical control that tests whether this was strictly a local manipulation that did not affect cells in the other region is introduced only much later. It may be helpful to add a comment in this section noting that such a control was performed, even if it is explained in detail later when introducing the recordings.

We have added the following to the first Results section: “we show below that direct optogenetic effects were only seen in the targeted forelimb area and not the other.”

(4) Figure 1D - I imagine these averages are from a single animal, but this is not stated in the figure caption.

“For one example mouse,” has been added to the beginning of the Figure 1D legend.

(5) Figure 2F - N=6 is not stated in the panel's caption (though it can make it clearer), while it is stated in the caption of 2H.

“n = 6 mice” has been added to the Figure 2F legend.

(6) There's some inconsistency with the order of RFA/CFA in the figures, sometimes RFA is presented first (e.g., Figure 1D and 1F), and sometimes CFA is presented first (e.g., panels of Figure 2).

We do not foresee this leading to confusion.

(7) "As expected, the majority of recorded neurons in each region exhibited an elevated average firing rate during movement as compared to periods when forelimb muscles were quiescent (Figure 2D,E; Figure S1A,B)" - Figure S1A,B show histograms of narrow vs. wide waveforms, is this the relevant figure here?

We apologize for the cryptic reference. The waveform width histograms were referred to here because they enabled the separation of narrow- and wide-waveform cells shown in Figure 2D,E. We have added the following clause to the referenced sentence to make this explicit:  “, both for narrow-waveform, putative interneurons and wide-waveform putative pyramidal neurons.”

(8) Figure 2I caption - "The fraction of activity variance from 150 ms before reach onset to 150 ms after it that occurs before reach onset" - this sentence is not clear.

The Figure 2I legend has been updated to “The activity variance in the 150 ms before muscle activity onset, defined as a fraction of the total activity variance from 150 ms before to 150 ms after muscle activity onset, for each animal (circles) and the mean across animals (black bars, n = 6 mice).”

(9) Figure 4B-G - is this showing results across the 6 animals? Not stated clearly.

Yes - the 21 sessions we had referred to are drawn from all six mice. We have updated the legend here to make this explicit.

(10) DLAG analysis - is there any particular reasoning behind choosing four across-region and four within-region components?

In actuality, we completed this analysis for a broad range of component numbers and obtained similar results in all cases. Four fell in the center of our range, and so we focused the illustrations shown in the figure on this value. In general, the number of components is arbitrary. The original paper from Gokcen et al. describes a method for identifying a lower bound on the number of distinct components the method can identify. However, this method yields different results for each individual recording session. For the comparisons we performed, we needed to use the same range of values for each session.

(11) Figure 5A seems to show 11 across-session components, it's unclear from the caption but I imagine this should show 12 (4 components times 3 sessions?)

As we state in the Methods, any across-region latent variable with a lag that failed to converge between the boundary values of ±200 ms was removed from the analysis. In the case illustrated in this panel, the lag for one of the components failed to converge and is not shown. We have now clarified this both in the relevant Results paragraph and in the figure legend.

(12) Figure 5B - is each marker here the average variance explained by all across/within components that were within the specified lag criteria across sessions per mouse? In other words, what does a single marker here stand for?

We apologize for the lack of clarity here. These values reflect the average across sessions for each mouse. We have updated the legend to make this explicit.

Reviewer #2 (Recommendations for the authors):

As I have addressed most of my major recommendations in the public review, I will use this section to include relatively minor points for the authors to consider.

(1) The EMG data in Figure 1C shows distinct patterns across spouts, both in the magnitude and complexity of muscle activations. It would be interesting to investigate whether these differences in muscle activity lead to behavioral variations (e.g., reaction time, reach duration) and how they relate to the relative involvement of the two areas.

We agree that it would be interesting to examine how the interactions between areas vary as behavior varies. While the differences between reaches here are limited, we have addressed this question for two substantially different motor behaviors (reaching and climbing) in a follow-up study that was recently preprinted (Kristl et al., biorxiv, 2025).

(2) How do the authors account for the lingering impact of RFA inactivation on muscle activity, which persists for tens of milliseconds after laser offset? Could this effect be due to compensatory motor activity following the perturbation? A further illustration of how the raw limb trajectories and/or muscle activity are perturbed and recovered would help readers better understand the impact of motor cortical inactivation.

To clarify the effects of inactivation on a longer timescale, we have added a new supplemental figure showing the plots from Figure 1D over a longer time window extending to 500 ms after trial onset (new Figure S1). Lingering effects do persist, at least in certain cases. In general, we find it hard to ascertain the source of optogenetic effects on longer timescales like this. On the shortest timescales, effects will be mediated by relatively direct connections between regions. However, on these longer timescales, effects could be due to broader changes in brain and behavioral state that can influence muscle activity. For example, attempts to compensate for the initial disturbance to muscle activity could cause divergence from controls on these longer timescales. Muscle tissue itself is also known to have long timescale relaxation dynamics, and it would not be surprising if the relevant control circuits here also had long timescales dynamics, such that we would not expect an immediate return to control when the light pulse ends. Because of this ambiguity, we generally avoid interpretation of optogenetic effects on these longer timescales.

Reviewer #3 (Recommendations for the authors):

(1) Page 9: ". We measured the time at which the activity state deviated from baseline preceding reach onset," - I cannot find how this deviation was defined (neither the baseline nor the threshold).

We have added text to the Figure 2G legend that explicitly states how the baseline and activity onset time were defined.

(2) Given the shape of the curves in Figure 2G, the significance of this result seems susceptible to slight modifications of what defines a baseline or a deviation threshold. For example, it looks like the circle for CFA has a higher y-axis value, suggesting the baseline deviance is higher, but it is unclear why that would be from the plot. If the threshold for deviation in neural activity state were held uniform between CFA and RFA is the difference still significant across animals?

We have repeated the analysis using the same absolute threshold for each region. We used the higher of the two thresholds from each region. The difference remains significant. This is now described in the last paragraph of the Results section for Figure 2.

(3) Since summed deviation of the top 3 PCs is used to show a difference in activity onset between CFA/RFA, but only a small proportion of variance is explained pre-movement (<2% in most animals), it seems relevant to understand what percentage of CFA/RFA neuron activity actually is modulated and deviates from baseline prior to movement and to show the distribution of activity onsets at the single neuron level in CFA/RFA. Can an onset difference only be observed using PCA? 

Because many neurons have low firing rates, estimating the time at which their firing rate begins to rise near reach onset is difficult to do reliably. It is also true that not all neurons show an increase around onset - some show a decrease and others show no discernible change. Using PCs to measure onset avoids both of these problems, since they capture both increases and decreases in individual neuron firing rates and are much less noisy than individual neuron firing rates. 

However, based on this comment, we have repeated this analysis on a single-neuron level using only neurons with relatively high average firing rates. Specifically, we analyzed neurons with mean firing rates above the 90th percentile across all sessions within an animal. Neurons whose activity never crossed threshold were excluded. Results matched those using PCs, with RFA neurons showing an earlier average activity onset time. This is now described in the last paragraph of the Results section for Figure 2.

(4) It is stated that to study the impact of inactivation on CFA/RFA activity, only the 50 highest average firing rate neurons were used (and maybe elsewhere too, e.g., convergent cross mapping). It is unclear why this subselection is necessary. It is justified by stating that higher firing rate neurons have better firing rate estimates. This may be supportable for very low firing rate units that spike sorting tools have a hard time tracking, but I don't think this is supported by data for most of the distribution of firing rates. It therefore seems like the results might be biased by a subselection of certain high firing rate neuron populations. It would be useful to also compute and mention if the results for all neurons/neuron pairs are the same. If there is worry about low-quality units being those with low firing rates, a threshold for firing rate as used elsewhere in the paper (at least 1 spike / 2 trials) seems justified.

The issue here is that as firing rates decrease and firing rate estimates get noisier, estimates of the change in firing rate get more variable. Here we are trying to estimate the fraction of neurons for which firing rates decreased upon inactivation of the other region. Variability in estimates of the firing rate change will bias this estimate toward 50%, since in the limit when the change estimates are entirely based on noise, we expect 50% to be decreases. As expected, when we use increasingly liberal thresholds for this analysis, the fraction of decreases trends closer to 50%. 

As a consequence of this, we cannot easily distinguish whether higher firing rate neurons might for some reason have a greater tendency to exhibit decreases in firing compared to lower firing rate neurons. However, we see no positive reason to expect such a difference. We have added a sentence noting this caveat in interpreting our findings to the relevant paragraph of the Results.

The lack of min/max axis values in Figure 3B-F makes it hard to interpret - are these neurons almost silent when near the bottom of the plot or are they still firing a substantial # of spikes?

To aid interpretation of the relative magnitude of firing rate changes, we have added minimum firing rates for the averages depicted in Figure 3B,C,E and F to the legend. Our original thinking was that the plots in Figure 3G and H would provide an indication of the relative changes in firing.

It would be interesting to know if the impact of optogenetic stimulation changed with exposure to the manipulation. Are all results presented only from the first X number of sessions in each animal? Or is the effect robust over time and (within the same animal) you can get the same results of optogenetic inactivation over time? This information seems critical for reproducibility.

We have now performed brief optogenetic inactivations in several brain areas in several different behavioral paradigms, and have found that inactivation effects are stable both within and across sessions, almost surprisingly so. This includes cases where the inactivations were more frequent (every ~1.25 s on average) and more numerous (>15,000 trials per animal) than in the present manuscript. Thus we did not restrict our analysis here to the first X sessions or trials within a session. We have added additional plots as Figure S3T-AA showing the stability of optogenetic effects both within and across sessions.

Given that it can be difficult to record from interneurons (as the proportion of putative interneurons in Figure S1 attests), the SALT analyses would be more convincing if a few recordings had been performed in the same region as optogenetic stimulation to show a "positive control" of what direct interneuron stimulation looks like. Could also use this to validate the narrow/wide waveform classification.

We have verified that using SALT as we have in the present manuscript does detect vGAT+ interneurons directly responding to light. This is included in a recent preprint from the lab (Kristl et al., biorxiv, 2025). We (Warriner et al., Cell Reports, 2022) and others (Guo et al., Neuron, 2014) have previously used direct ChR2 activation to validate waveform-based classification.

Simultaneous CFA/RFA recordings during optogenetic perturbation would also allow for time courses of inhibition to be compared in RFA/CFA. Does it take 25ms to inhibit locally, and the cross-area impact is fast, or does it inactivate very fast locally and takes ~25ms to impact the other region?

Latencies of this sort are difficult to precisely measure given the statistical limits of this sort of data, but there does appear to be some degree of delay between local and downstream effects. We do not have a statistical foundation as of yet for concluding that this is the case. It will be interesting to examine this issue more rigorously in the future.

Given the difference in the analytical methods, the authors should share data in a relatively unprocessed format (e.g., spike times from sorted units relative to video tracking + behavioral data), along with analysis code, to allow others to investigate these differences.

We plan to post the data and code to our lab’s Github site once the Version of Record is online.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

In this paper, the authors reveal that the MK2 inhibitor CMPD1 can inhibit the growth, migration, and invasion of breast cancer cells both in vitro and in vivo by inducing microtubule depolymerization, preferentially at the microtubule plus-end, leading to cell division arrest, mitotic defects, and apoptotic cell death. They also showed that CMPD1 treatment upregulates genes associated with cell migration and cell death, and downregulates genes related to mitosis and chromosome segregation in breast cancer cells, suggesting a potential mechanism of CMPD1 inhibition in breast cancer. Besides, they used the combination of an MK2-specific inhibitor, MK2-IN-3, with the microtubule depolymerizer vinblastine to simultaneously disrupt both the MK2 signaling pathway and microtubule dynamics, and they claim that inhibiting the p38-MK2 pathway may help to enhance the efficacy of MTAs in the treatment of breast cancer. However, there are a few concerns, including:

(1) What is the effect of CMPD1 on breast cancer metastasis?

In this study, we hypothesized that the MK2 signaling pathway could synergize with microtubule-targeting agents (MTAs) to enhance anti-cancer efficacy. We utilized CMPD1 as a potent dual-function inhibitor, targeting both MK2 and microtubule dynamics. By simultaneously inhibiting these pathways, CMPD1 not only shows the therapeutic impact of MTAs, but also significantly suppresses breast cancer cell migration and invasion. Therefore, we propose that CMPD1, through its dual inhibition of MK2 activity and microtubule dynamics, may offer enhanced specificity and efficacy in preventing breast cancer metastasis and limiting tumor progression.

(2) The mechanism is lacking as to how MK2 inhibitors enhance the efficacy of MTAs.

Thank you for the valuable suggestion. We agree that our current findings do not fully elucidate the underlying mechanism by which MK2 inhibition synergistically enhances the efficacy of MTAs. We recognize this as an important area for further investigation and are committed to exploring the molecular interplay between MK2 signaling and microtubule dynamics in future studies. A deeper mechanistic understanding will be critical to establishing a strong rationale for the potential co-treatment of MK2 inhibitors and MTAs in clinical breast cancer therapy.

Reviewer #2 (Public review):

Summary:

This study explores the potential of inhibiting the p38-MK2 signaling pathway to enhance the efficacy of microtubule-targeting agents (MTAs) in breast cancer treatment using a dual-target inhibitor.

Strengths:

The study identifies the p38-MK2 pathway as a promising target to enhance the efficacy of microtubule-targeting agents (MTAs), offering a novel therapeutic strategy for breast cancer treatment. In addition, the study employs a wide range of techniques, especially live-cell imaging, to assess the microtubule dynamics in TNBC cells.

We sincerely appreciate your recognition of the significance and impact of our work.

Weaknesses:

The study primarily uses RPE1 cells as the control for normal cells, which may not fully capture the response of normal mammary epithelial cells. While CMPD1 is shown to be effective in suppressing tumor growth in MDA-MB-231 xenograft, the study lacks detailed toxicity data to confirm its safety profile in vivo.

Thank you for your valuable suggestions. In the revised manuscript, we have included CMPD1 treatment in MCF10A cells, a more appropriate non-transformed control line commonly used in breast cancer research. Notably, MCF10A cells exhibited results similar to those observed in RPE1 cells, further reinforcing our conclusion that breast cancer cells display increased sensitivity to CMPD1 treatment. These new findings are presented in Figure 2-Supplement 1A-C. Additionally, we performed further xenograft experiments using CAL-51 and MDA-MB-231 cells. We collected data on tumor growth, mouse body weight, survival rates, and other relevant parameters to comprehensively assess toxicity. The newly obtained results are presented in Figure 3F-G and Figure 3-Supplement 1-3.

Reviewer #3 (Public review):

Summary:

The authors demonstrated MK2i could enhance the therapeutic efficacy of MTAs. With Tumor xenograft and migration assay, the author suggested that the p38-MK2 pathway may serve as a promising therapeutic target in combination with MTAs in cancer treatment.

Strengths:

The authors provided a potential treatment for breast cancer.

Thank you for recognizing the importance and significance of our work.

Weaknesses:

(1) In Figure 2, the authors used a human retinal pigment epithelial-1 (RPE1) cell line to show that breast cancer cells are more sensitive to CMPD1 treatment. MCF10A cells would be suggested here as a suitable control. Besides, to compare the sensitivity, IC50 indifferent cell lines should be measured.

In the revised manuscript, we have addressed these points by determining the IC50 values for CMPD1 in MDA-MB-231, CAL-51, MCF10A, and CAL-51 p53 knockout cells. These new results are presented in Figure 2-Supplement Figure 3.

(2) The data of MDA-MB-231 in Figure 1D is not consistent with CAL-51 and T47D, also not consistent with the data in Figures 2B-C.

In the revised manuscript, we have included all relevant statistical analyses in Figure 1D. In MDA-MB-231 cells, there are no statistically significant differences in mitotic duration between 1 µM and 5 µM, 5 µM and 10 µM, or 1 µM and 10 µM CMPD1 treatments. Similarly, no significant differences are observed between 1 µM and 5 µM or 5 µM and 10 µM CMPD1 treatments in CAL-51 cells, and between 5 µM and 10 µM in T-47D cells. These results suggest that mitotic duration does not exhibit a clear dose-dependent relationship within the 1–10 µM range, likely because mitotic arrest has reached a near-plateau effect at these concentrations.

It is also important to note that the experimental conditions in Figures 1 and 2 are fundamentally different. Figure 1 investigates the effects of higher concentrations of CMPD1 (≥1 µM), which severely disrupt microtubule organization and result in robust mitotic arrest, with cells arrested in mitosis for over 8 hours. In contrast, the conditions in Figure 2 utilize much lower concentrations of CMPD1 (10–50 nM), which are insufficient to cause complete microtubule depolymerization, but are capable of inducing a subtle yet statistically significant mitotic delay, particularly in breast cancer cell lines. These lower concentrations were chosen to mimic clinically relevant intratumoral drug levels. Previous studies have reported that paclitaxel (PTX) concentrations in patient tumors approximate ~50 nM when modeled in vitro. At these physiologically relevant levels, PTX does not induce strong mitotic arrest but instead causes moderate delays that result in division errors and chromosomal instability, ultimately contributing to cancer cell death. In this study, the conditions used in Figure 2 emulate these clinically relevant concentrations for CMPD1. We found that, similar to PTX, low-dose CMPD1 induces a slight but significant mitotic delay without triggering a full mitotic arrest. Notably, unlike PTX, CMPD1 appears to exert this effect selectively in breast cancer cells, contributing to mitotic errors and potentially enhancing therapeutic efficacy through targeted chromosomal instability.

(3) To support the authors' conclusion in Figure 5, an additional animal experiment performed by tail vein injection would be helpful.

While current technical limitations have precluded us from conducting this suggested experiment in this study, we have performed complementary xenograft studies using CAL-51 cells treated with CMPD1. These experiments included a comprehensive toxicity analysis. Furthermore, we carried out an in vitro migration assay using CAL-51 cells under combined treatment with the MK2 inhibitor and vinblastine. These additional findings are presented in Figure 3–Supplement 1–3 and Figure 6–Supplement 3. We recognize the importance of the suggested tail vein injection approach and are actively pursuing further mechanistic studies, including this experiment, in our ongoing and future work.

(4) Page 14, to evaluate the combination result of MK2i and vinblastine, an in vivo animal assay must be performed.

We appreciate the reviewer’s valuable suggestion. We are actively investigating the synergistic mechanisms between the MK2 inhibitor and microtubule-targeting agents (MTAs). In future studies, we plan to extend our findings by conducting xenograft experiments to further evaluate their therapeutic potential in vivo.

(5) The authors used RNA-seq to show some pathways affected by CMPD1. What are the key/top genes that were affected? How about the mechanism?

In the revised manuscript, we have included the top 20 upregulated and downregulated genes identified from RNA-seq analysis using MDA-MB-231 cells. This new data is presented in Figure 6-Supplement Figure 4. Gene Ontology (GO) Biological Process (BP) pathway enrichment analysis revealed that the most significantly enriched pathways among upregulated genes are associated with cell migration, whereas the downregulated genes are primarily involved in mitosis and chromosome segregation. These transcriptional changes are consistent with the phenotypic outcomes observed in our experiments, supporting the functional relevance of CMPD1 treatment. However, further investigation will be necessary to elucidate the detailed molecular mechanisms underlying these effects.

(6) Line 127, more experiments should be involved to support the conclusion.

In the revised manuscript, we have addressed this point by performing additional experiments, including determination of the IC₅₀ values of CMPD1 in MDA-MB-231, CAL-51, MCF10A, and CAL-51 p53 knockout cells. We also conducted live-cell imaging analyses using MCF10A cells. These new results further reinforce our conclusion that breast cancer cells are more sensitive to CMPD1 treatment than normal breast epithelial cells, and that this sensitivity is independent of p53 status. The new data are presented in Figure 2-Supplement Figures 1 and 3.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Figure 1D: As the concentration of CMPD1 increased, the mitotic duration of MDA-MB-231 cells decreased, why was that?

Although there appears to be a slight decrease in mitotic duration with increasing concentrations of CMPD1, our quantitative analysis reveals no statistically significant differences among the 1 to 10 µM treatment groups in MDA-MB-231 cells. In the revised manuscript, we have included all relevant statistical analyses in Figure 1D for clarity. Importantly, all CMPD1-treated groups exhibit a pronounced and statistically significant prolongation of mitosis compared to the DMSO-treated control. While the average mitotic duration in control cells is approximately 30 minutes, cells exposed to 1–10 µM CMPD1 consistently display mitotic durations exceeding 8 hours, indicating a strong and sustained mitotic arrest across this concentration range.

Reviewer #2 (Recommendations for the authors):

(1) The rationale for using RPE1 as normal cell control instead of normal mammary epithelial cells as control is unclear. Using normal mammary epithelial cells such as MCF10A for the study is recommended.

Thank you for this valuable suggestion. In the revised manuscript, we have included additional experiments using non-transformed mammary epithelial MCF10A cells. The new data, presented in Figure 2-Supplement Figures 1 and 3, include both IC50 measurements and live-cell imaging analyses. These results further support our conclusion that breast cancer cells are significantly more sensitive to CMPD1 treatment compared to normal mammary epithelial cells.

(2) It is intriguing that CAL-51 cells are more sensitive to CMPD1 than MDA-MB-231 cells; examining how p53 signaling changes in these cells would be worthwhile.

We appreciate this insightful comment. In the revised manuscript, we have measured the IC₅₀ values for both CAL-51 and CAL-51 p53 knockout (p53KO) cells. The results show no significant difference in CMPD1 sensitivity between the two, suggesting that the enhanced sensitivity of CAL-51 cells is independent of p53 status. These new findings are presented in Figure 2—Supplement Figure 3.

(3) Figures S1A and B are not described and cited in the main text.

We apologize for this oversight. In the revised manuscript, we have correctly cited and described Figures S1A and B (Figure 2-Supplement Figure 2 A-B in revised manuscript) in the main text.

(4) I'm not that convinced by the conclusion made from Lines 201-204. First, Figure S2C, which is the growth of tumor volume, does not reflect the toxicity of the drug treatment. No additional data evaluating the toxicity (such as body weight change) under the regimen was shown. Second, although the tumor weight by the endpoint indicated some anti-tumor effect in the MDA-MB-231 xenograft model, the tumor volume does not show the same pattern (the dot lines do not well distinguish which group from which). I would suggest repeating the in vivo experiment using CAL-51 cells since it is more sensitive to CMPD1 according to the previous data.

Thank you for this thoughtful and constructive feedback. In the revised manuscript, we have addressed these concerns through several additional experiments. We performed new xenograft studies using CAL-51 TNBC cells, in parallel with further toxicity-focused analyses in the MDA-MB-231 model. Consistent with previous results, CMPD1 treatment significantly suppressed tumor growth in CAL-51 xenografts (Figure 3F-G), further supporting its efficacy in a more sensitive cell line. To evaluate drug-associated toxicity, we measured body weight changes throughout the course of treatment. CMPD1-treated mice maintained a comparable weight gain to the control group, whereas mice treated with paclitaxel (PTX) showed significantly reduced body weight (Figure 3-Supplement Figure 2A). Notably, animal deaths occurred only in the PTX-treated groups in both MDA-MB-231 and CAL-51 models (Figure 3-Supplement Figure 2B). We also assessed organ toxicity, including both anatomical and functional evaluations of the kidney and liver, and observed no significant damage in CMPD1-treated mice (Figure 3-Supplement Figures 3A-B and 3D). Furthermore, white blood cell (WBC) counts remained stable in the CMPD1 group, while PTX treatment led to a significant reduction (Figure 3-Supplement Figures 3C-D). These additional data provide strong evidence for the anti-tumor efficacy and lower toxicity of CMPD1 in vivo.

(5) While I appreciate the combination effect of treating cells with the MK2 inhibitor with vinblastine. I would consider using genetic knockdown as a complementary approach to demonstrate that inhibiting the p38-MK2 pathway synergized with microtubule depolymerizing agents. In addition, could inhibition of the p38-MK2 pathway alone induce the cell growth inhibition observed with CMPD1 treatment?

Thank you for these important suggestions. In the revised manuscript, we have incorporated siRNA-mediated knockdown of MK2 in combination with vinblastine treatment. This genetic approach revealed synergistic effects on mitotic index and mitotic errors, closely mirroring the phenotypes observed with pharmacological co-treatment using the MK2 inhibitor and vinblastine (Figure 6-Supplement Figure 2A-C). These results further validate the role of the p38-MK2 pathway in modulating mitotic progression in the presence of MTAs. To address whether MK2 inhibition alone is sufficient to impair cell growth, we performed validation experiments using the MK2 inhibitor at 10 µM. At this concentration, the inhibitor effectively blocked phosphorylation of Hsp27, a major downstream substrate of MK2, under H2O2-induced ROS stress conditions (Figure 6-Supplement Figure 1A-B), confirming MK2 signaling pathway inhibition. However, treatment with the MK2 inhibitor alone did not significantly affect cell proliferation, as shown by a 4-day growth curve analysis in CAL-51 cells (Figure 6-Supplement Figure 1C). These findings suggest that inhibition of the p38-MK2 pathway alone is not sufficient to suppress cancer cell growth, and that its synergistic interaction with MTAs, such as vinblastine, is essential for the observed anti-proliferative effects.

(6) Phenotypic studies (such as anchorage-independent growth and cell migration and invasion assay) of combining MK2 inhibitor with vinblastine in TNBC cells are recommended.

Thank you for this valuable suggestion. In the revised manuscript, we have conducted cancer cell migration assays using CAL-51 TNBC cells treated with control, MK2 inhibitor alone, vinblastine alone, or the combination of both. Our results demonstrate that the combination treatment significantly enhances the inhibition of cell migration compared to either agent alone (Figure 6-Supplement Figure 3A-C). These findings provide additional phenotypic evidence supporting the synergistic interaction between MK2 inhibition and microtubule-targeting agents in TNBC cells.

Reviewer #3 (Recommendations for the authors):

The authors can utilize diverse experiments to support their conclusions.

Thank you for this important suggestion. In the revised manuscript, we have conducted a series of additional experiments to robustly support our conclusions.

These include:

(1) Xenograft studies using CAL-51 TNBC cells, along with comprehensive toxicity evaluations.

(2) CMPD1 sensitivity analysis in non-transformed MCF10A mammary epithelial cells.

(3) IC50 measurements in MDA-MB-231, CAL-51, CAL-51 p53 knockout, and MCF10A cells.

(4) Cell migration assays assessing the combination effects of MK2 inhibitor and vinblastine

(5) siRNA-mediated genetic knockdown of MK2 to complement pharmacological findings

Collectively, these additional data sets substantially strengthen the evidence base for our conclusions and provide a more comprehensive mechanistic understanding.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors use the teleost medaka as an animal model to study the effect of seasonal changes in day-length on feeding behaviour and oocyte production. They report a careful analysis of how day-length affects female medakas and a thorough molecular genetic analysis of genes potentially involved in this process. They show a detailed analysis of two genes and include a mutant analysis of one gene to support their conclusions

Strengths:

The authors pick their animal model well and exploit the possibilities to examine in this laboratory model the effect of a key environmental influence, namely the seasonal changes of day-length. The phenotypic changes are carefully analysed and well-controlled. The mutational analysis of the agrp1 by a ko-mutant provides important evidence to support the conclusions. Thus this report exceeds previous findings on the function of agrp1 and npyb as regulators of food-intake and shows how in medaka these genes are involved in regulating the organismal response to an environmental change. It thus furthers our understanding of how animals react to key exogenous stimuli for adaptation.

Weaknesses:

The authors are too modest when it comes to underscoring the importance of their findings. Previous animal models used to study the effect of these neuropeptides on feeding behaviour have either lost or were most likely never sensitive to seasonal changes of day length. Considering the key importance of this parameter on many aspects of plant and animal life it could be better emphasised that a suitable animal model is at hand that permits this. The molecular characterization of the agrp1 ko-mutant that the authors have generated lacks some details that would help to appreciate the validity of the mutant phenotype. Additional data would help in this respect.

We would like to thank Reviewer #1 for the really constructive advice. In the revised manuscript, we provided more information on the molecular characterization of the agrp1 KO-mutant and to emphasize the importance of our present animal model that permits the analysis of neuropeptide effects on feeding behavior in response to seasonal changes of day length.

Reviewer #2 (Public review):

Summary:

The authors investigated the mechanisms behind breeding season-dependent feeding behavior using medaka, a well-known photoperiodic species, as a model. Through a combination of molecular, cellular, and behavioral analyses, including tests with mutants, they concluded that AgRP1 plays a central role in feeding behavior, mediated by ovarian estrogenic signals.

Strengths:

This study offers valuable insights into the neuroendocrine mechanisms that govern breeding season-dependent feeding behavior in medaka. The multidisciplinary approach, which includes molecular and physiological analyses, enhances the scientific contribution of the research.

Weaknesses:

While medaka is an appropriate model for studying seasonal breeding, the results presented are insufficient to fully support the authors' conclusions.

Specifically, methods and data analyses are incomplete in justifying the primary claims:<br /> - the procedure for the food intake assay is unclear;

- the sample size is very small;

- the statistical analysis is not always adequate.

Additionally, the discussion fails to consider the possible role of other hormones that may be involved in the feeding mechanism.

We would like to thank Reviewer #2 for the helpful comments. As the reviewer suggested, we revised the paragraph describing the procedure for the food intake assay to make it much easier for the readers to understand in the revised manuscript. In Figure 1-Supplementary figure 2, RNAseq was performed to search for the candidate neuropeptides, and that’s why the sample size was the minimum. On the other hand, each group in the other experiments consist of n ≥ 5 samples, which is usually accepted to be adequate sample size in various studies (cf. Kanda et al., Gen Comp Endocrinol., 2011, Spicer et al., Biol Reprod., 2017). As for the statistical analyses, we revised our manuscript so that the readers may be convinced with the validity of our statistical analyses.

Reviewer #3 (Public review):

Summary:

Understanding the mechanisms whereby animals restrict the timing of their reproduction according to day length is a critical challenge given that many of the most relevant species for agriculture are strongly photoperiodic. However, the principal animal models capable of detailed genetic analysis do not respond to photoperiod so this has inevitably limited progress in this field. The fish model medaka occupies a uniquely powerful position since its reproduction is strictly restricted to long days and it also offers a wide range of genetic tools for exploring, in depth, various molecular and cellular control mechanisms.

For these reasons, this manuscript by Tagui and colleagues is particularly valuable. It uses the medaka to explore links bridging photoperiod, feeding behaviour, and reproduction. The authors demonstrate that in female, but not male medaka, photoperiod-induced reproduction is associated with an increase in feeding, presumably explained by the high metabolic cost of producing eggs on a daily basis during the reproductive period. Using RNAseq analysis of the brain, they reveal that the expression of the neuropeptides agrp and npy that have been previously implicated in the regulation of feeding behaviour in mice are upregulated in the medaka brain during exposure to long photoperiod conditions. Unlike the situation in mice, these two neuropeptides are not co-expressed in medaka neurons, and food deprivation in medaka led to increases in agrp but also a decrease in npy expression. Furthermore, the situation in fish may be more complicated than in mice due to the presence of multiple gene paralogs for each neuropeptide. Exposure to long-day conditions increases agrp1 expression in medaka as the result of increases in the number of neurons expressing this neuropeptide, while the increase in npyb levels results from increased levels of expression in the same population of cells. Using ovariectomized medaka and in situ hybridization assays, the authors reveal that the regulation of agrp1 involves estrogen acting via the estrogen receptor esr2a. Finally, a loss of agrp1 function mutant is generated where the female mutants fail to show the characteristic increase in feeding associated with long-day enhanced reproduction as well as yielding reduced numbers of eggs during spawning.

Strengths:

This manuscript provides important foundational work for future investigations aiming to elucidate the coordination of photoperiod sensing, feeding activity, and reproduction function. The authors have used a combination of approaches with a genetic model that is particularly well suited to studying photoperiodic-dependent physiology and behaviour. The data are clear and the results are convincing and support the main conclusions drawn. The findings are relevant not only for understanding photopriodic responses but also provide more general insight into links between reproduction and feeding behaviour control.

Weaknesses:

Some experimental models used in this study, namely ovariectomized female fish and juvenile fish have not been analysed in terms of their feeding behaviour and so do not give a complete view of the position of this feeding regulatory mechanism in the context of reproduction status. Furthermore, the scope of the discussion section should be expanded to speculate on the functional significance of linking feeding behaviour control with reproductive function.

We would like to thank Reviewer #3 for the insightful advice. We added several pertinent sentences describing the ovariectomized female fish and juvenile fish, and our revised manuscript will give more complete view of their feeding regulatory mechanism in the context of reproduction status. In addition, we revised the discussion section to incorporate the valuable suggestion of the Reviewer #3.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

General: the text could profit from a careful editing of errors, including adjusting singular and plural status of nouns and verbs: examples are line 107 noun, line 96 verb suitable text editing software is available to do this task

Thank you for your suggestion. We thoroughly read the entire manuscript and corrected such errors in the revised manuscript.

As medaka is a unique genetic vertebrate model to study seasonal effects, it would be interesting to know whether the authors found novel or rather unexpected genes with a differential expression between LD and SD. It is understandable that the authors focused on argrp1 and npyb, as these have already been well studied in mammalian models although not in this context. Novel insights with genes previously not implicated in feeding regulation could underscore the unique nature of medaka as a model.

We appreciate your kind comments, which we found really encouraging to us. Since we focused on feeding-related peptides, we did not find any novel genes that have not been reported.

ISH is unreliable as a methodology to quantify expression levels. Yet the authors use this to compare fed and starved females to compare expression levels of agrp1. They use a temporal staining comparison and compare 90-minute and 300-minute staining reactions. However, they do not explain why they use the 90-minute staining time point and why 300 minutes of staining is the "saturation point of staining". They should provide compelling data for their claim and the selection of time points or else refrain from using these (at best) semi-quantitative ISH and provide more detailed (using serial sections) data to quantify the number of expressing cells.

Anyhow, the quantification of mRNA expression levels may not be that significant when trying to compare different states of gene function, as translational and post-translational steps can have large effects on gene function. This should be discussed adequately.

Thank you very much for your comments. We conducted ISH by using medaka under LD or SD, not using those under fed or starved conditions. In addition, our previous study demonstrated that the slopes of the increase in the number of cells stained by ISH are also different if there is a difference in the expression level (Mitani et al., 2010). Although we do not have quantitative data of cell numbers, we confirmed that the number of cells expressing agrp1 was saturated around 300 mins in our preliminary experiments, and therefore we terminated the chemogenic reactions at 300 mins. Based on these, we compared the cell ratio of 90 min (beginning of coloring) /300 min (saturation). However, since this analysis may not be worth discussing in detail, we moved this part to the supplementary figure as the reviewer suggested.

The molecular characterization of the agrp1 ko mutant is a bit thin.

Line 221: "We obtained agrp1^−/− medaka, which has lots of amino acid changes in functional site for AgRP1" is a bit vague as a description for the ko-mutation. It would be really helpful if the authors could provide a scheme showing the wt protein with the relevant functional sites alongside the presumptive mutant protein.

How did the authors verify the molecular nature of their mutation? They should use suitable antibodies and western-blot analysis (maybe reagents from Shainer et al., 2019 work in medaka); in case this is not possible they could isolate & clone the mutant transcript and use in-vitro translation systems to show that the presumptive mutant protein can actually be translated from this transcript. Another strategy could be to use a second non-allelic and (hopefully) non-complementing mutation (ko1/ko2 heterozygots for example) to show that ko-mutation acts the way the authors presume. The authors mention agrp1 ko medaka lines (plural!) in line 520, thus they may have an additional ko allele at hand.

Thank you very much for your comments. We explained the mutation site in Figure 6-Supplementary Figure 1 (A: DNA sequences and B: predicted amino acid sequence, of WT and mutants). In addition, we added immunohistochemistry data of WT and mutant using anti-AgRP antibody (Figure 6-Supplementary Figure 1C). While AgRP-immunoreactive signals were observed in WT, those were not in agrp1^−/−. This result suggests that AgRP1 is not functional in agrp1^−/−.

Presumably, the authors analysed heterozygous agrp1^+/− females and found they are as wt. If so the authors should say so.

Yes, we analyzed food intake of agrp1^+/−. We added a supplementary figure (Figure 6-Supplementary Figure 2) and a sentence in L. 233-234.

How about agrp1^−/− medaka males: do they show a discernible phenotype?

We analyzed the phenotypes of agrp1^−/− males but did not describe the results, since the present paper only focused on female-specific feeding behavior.

agrp1^−/− females show no significant sensitivity of food intake to day length (Figure 6C). Does their (reduced) oocyte production react to day length? With other words: how much of the seasonal sensitivity is left in agrp1^−/− females. The authors suggest that E2 acts upstream of agrp1 and therefore some seasonality may still be left in agrp1^−/− females.

Although agrp1^−/− female is suggested to display abnormal seasonality of food intake, agrp1^−/− female in LD spawns and that in SD does not, indicating that seasonality of gonadal maturation still remains in agrp1^−/− female.

The authors show that fshb and lhb are downregulated in agrp1^−/− females. Is this also the case in wt females at SD?

Thank you very much for your comment. As described above, agrp1^−/− can spawn, which indicates that mechanisms for the downregulation of gonadotropins in agrp1^−/− may be different from that in SD female.

Figure 1_Supplementary Figure 2: the trends are visible in B and C, however, there is quite some variance between LD1, 2, and 3; the same for SD 1, 2, and 3. Can the authors give an explanation for this?

Since the data for LD1, 2, and 3 (SD1, 2, and 3) were obtained from different individual fish, the variance may be reasonable. We conducted expression analyses by using RNA-seq to find candidate genes that show larger differences than individual ones.

Figure 7E: the ovaries are difficult to see and the size bar in the wt picture is missing.

Thank you very much for your comments. We added a scale bar in the wt picture.

509 ff: the authors do not describe what exactly the "sham operation" encompasses: were the females just anesthetised or was there an actual operation without removing the ovaries?

The sham operation group was anesthetized, received an abdominal incision without removing the ovaries, and received skin suture by using a silk thread. We added this explanation in the Method section.

519 ff: was the agrp1^−/− ko induced in the d-rR strain to have the same genetic background as the wt fish?

Exactly. As the reviewer pointed out, the genetic background of agrp1 -/- was the same as that of WT.

Minor points (Text edits):

Line 42: change "when" into "where".

Line: 54 "under the fixed appropriate ambient temperature" change into "while keeping an appropriate temperature constant".

Line 55: here it would be good to briefly explain what long-day and short-day is so that the reader has an idea about the changes required without having to scroll down to the M&M section. For example LD 14/10 light-dark cycle, SD 10/14 light-dark cycle.

Line 88: change "measurement" into "measuring".

Line 96 change eats -> eat.

Line 107 change female -> females.

We deeply appreciate the reviewer’s suggestions described above. We corrected them as the reviewer suggested (L. 42, L. 54, L. 55, L. 89, L. 96, L. 107).

Line 144-145: the sentence "since hypothalamic npy control..." does not make sense. Please correct.

Thank you very much for your suggestion. We corrected the sentence so that it makes sense (L. 145-146).

Line 180 and 185: the term here should be "LD induced sexual activity" rather than maturity. Age is the main determinant of maturity whereas light (LD) determines activity, in other words SD females are sexually mature if they are post-puberty stage.

Thank you very much for your suggestion. Since the sentence “LD-induced sexual maturity” made the reviewer confused, we corrected the sentence “substance(s) from LD-induced mature ovary” or “ovarian maturity”. Even though SD females are at post-puberty stage, their ovaries are immature and do not possess mature oocytes (L. 181).

Line 222: the authors should include the relevant information about the females: presumably agrp1.

In Line 226-228, we explained the phenotypes of agrp1 knockout and added information for AgRP1 protein in Figure 6-Supplementary figure 1C.

Lines 449 ff: authors should state that the analysis was done in females, instead of just writing "medaka". This is also in line with the preceding paragraph of the M&M section.

Thank you very much for your suggestions. We corrected the sentence as the reviewer suggested (L.469)

Line 305: change like other mammals -> like in mammals.

Thank you very much for your suggestion. We corrected the sentence as the reviewer suggested (L. 320)

Reviewer #2 (Recommendations for the authors):

(1) The procedure of the food intake assay is not clear.

- Habituation Period: Medaka were placed into a white cup containing 100 mL of water and allowed to habituate for 5 minutes. However, is 5 minutes sufficient to reduce stress in the fish? A stressed fish does not exhibit the same feeding behavior as an unstressed one.

Thank you for your comment. We confirmed that 5 minutes is enough for habituation in medaka, since medaka can swim freely in a few minutes after replacement from the tank and show normal feeding behavior.

- Feeding Protocol: Medaka were fed with 200 μL aliquots of brine shrimp-containing water. This procedure was repeated multiple times. How many times was this feeding procedure repeated? Was it 3, 10, or 100 times?

Although there was a small variation in each trial, we usually applied tubes about 5 times or so.

- Brine Shrimp Counting: You collected 10 mL of the breeding water to count the number of uneaten brine shrimp. Can you confirm that sampling 10% of the total volume is representative? Were any tests conducted to validate this? Given that you developed an automated tool to count the brine shrimp, why didn't you count them in all 100 mL?

The reason for collecting 10 mL is to collect the leftover shrimp as soon as possible. Ten mins after the start of the experiment, we quickly placed a magnetic bar to stir the breeding water so that the shrimp concentration will be constant. Then we collected 10 mL aliquot from the experimental cup by using a micro pipette. In preliminary trials, we applied shrimps, the amount of which is almost the same as that applied to WT medaka in LD, to a white cup containing 100 mL water, and we divided it into 10 mL and 90 mL aliquots and separately counted the number of shrimps in each aliquot. Here, we confirmed that the variance between the numbers calculated by counting the shrimps in 10 mL aliquot and the total volume of 100 mL falls within the range of the variance of total applied shrimp. Thus, our present counting method can be considered reasonable.

- Brine Shrimp Aliquot Measurement: You mentioned counting the number of brine shrimp in the 200 μL solution three times before and after the experiments. What does this mean? Did you use this procedure to calculate the mean number of brine shrimp in each 200 μL aliquot?

Thank you for your comment. As the reviewer commented, to calculate the mean number of brine shrimp in each 200 µL aliquot, we counted the number of brine shrimp in the 200 µL solution three times before and after the experiments.

- How did you normalize the food intake data? This procedure is not detailed in the methods section.

Thank you very much for pointing it out. We normalized food intake by subtracting the amount of shrimp by the average of those in LD or WT fish. This explanation was added in the Method section (L. 439).

(2) Sample Size. Various tests were conducted with a low number of medaka (e.g., 2 brains for RNA-seq, 8 females for ovariectomy). Are these sample sizes sufficient to draw reliable conclusions?

In Figure 1-Supplementary figure 2, RNAseq was performed to search for the candidate neuropeptides, and that’s why the sample size was the minimum; we pooled two brains as one sample and used three samples per group. On the other hand, each group in the other experiments consist of n ≥ 5 samples, which is usually accepted to be adequate sample size in various studies (cf. Kanda et al., Gen Comp Endocrinol., 2011, Spicer et al., Biol Reprod., 2017).

(3) Statistical Analysis.

- The authors used both parametric and non-parametric tests but did not specify how they assessed the normal distribution of the data. For example, if I understood correctly, a t-test was used to compare a small dataset (n=3). In such cases, a U-test would be more appropriate.

Thank you for your comment. As for Figure 1 -Supplementary Figure 2C, we showed the graphs just to show you candidates. To avoid misunderstanding, we deleted statistical statements in that panel.

- It is unclear why the Steel-Dwass test was used instead of the Kruskal-Wallis test for comparing agrp1 and npyb expressions in control, OVX, and E2-administered medaka.

While the authors mentioned using non-parametric tests, they did not specify in which contexts or conditions they were applied.

Thank you very much for your comment. Kruskal-Wallis test statistically shows whether or not there are differences among any of three groups. To perform multiple comparisons among the three groups, we used Steel-Dwass test.

- The results section lacks details on the statistical tests used, including the specific test (e.g., Z, U, or W values) and degrees of freedom.

Thank you for your comment. As the reviewer pointed out, we added such statements in all the figure legends containing statistics.

(4) Previous studies have shown that photoperiod treatments alter the production of various hormones in medaka (e.g., Lucon-Xiccato et al., 2022; Shimmura et al., 2017), some of which, like growth hormone (GH), have been shown to influence feeding behavior (Canosa et al., 2007).

In your RNA-seq analysis, did you observe any changes in the expression of genes involved in other hormone synthesis pathways, such as pituitary hormones (GH and TSH), leptin, or ghrelin (e.g., see Volkoff, 2016; Blanco, 2020; Bertolucci et al., 2019)?

Including such evidence in the discussion would provide a broader perspective on the hormonal regulation of food intake in medaka.

We appreciate your constructive comments. Unfortunately, since we performed RNA-seq using the whole brain after removal of the pituitary, we could not check such changes in the expression of pituitary hormone-related genes. As additional information about the feeding-related hormones, leptin did not show significant difference in our RNA-seq analysis, and we could not analyze ghrelin because ghrelin has not been annotated in medaka (NCBI and ensembl).

Reviewer #3 (Recommendations for the authors):

There are some parts of the study that need to be developed further in order to provide a more comprehensive analysis.

(1) In the juvenile as well as ovariectomized female fish, the authors should confirm experimentally whether day length influences feeding activity.

Thank you very much for your suggestion. We analyzed feeding behavior of juvenile (Figure 4-Supplementary Figure 1) and OVX female (Figure 5-Supplementary Figure 1). As shown in these figures, food intake in juvenile and OVX were not significantly different between LD and SD.

(2) More discussion as to the relevance of increasing feeding activity to support reproductive functions such as sustained egg production would be valuable. One assumes the metabolic costs of producing eggs on a daily basis in this species would inevitably require increased food intake. Is this a reasonable prediction?

We deeply appreciate your suggestion. We strongly agree with this argument, and we added such discussion in “Discussion” section (L. 406-408).

Editor's note:

Should you choose to revise your manuscript, if you have not already done so, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05 in the main manuscript.

We appreciate the editor’s suggestion. We added P-value in the main manuscript, where statistical analyses were performed. In addition, we described test statics in the figure legends. We did not use df values for the statistics used in the present analyses, and therefore did not describe it in the main text.

Author response:

We will revise the statements of novelty in the introduction by more clearly emphasizing how our model addresses gaps in the existing literature. In addition, we will clarify the description of the dispersal process. Briefly, we use the same dispersal gene β to represent the likelihood an individual will either leave or join a group, thereby quantifying both dispersal and immigration using the same parameter. Specifically, individuals with higher β are more likely to remain as floaters (i.e., disperse from their natal group to become a breeder elsewhere), whereas those with lower β are either more likely to remain in their natal group as subordinates (i.e., queue in a group for the breeding position) or join another group if they dispersed. Immigrants that join a group as a subordinate help and queue for a breeding position, as does any natal subordinate born into the group. To follow the suggestion of the referee and more fully explore the impact of competition between subordinates born in the group and subordinate immigrants, we will explore extending our model to allow dispersers to leave their natal group and join another as subordinates, by incorporating a reaction norm based on their age or rank (D = 1 / (1 + exp (β_t * t – β₀)) . This approach will allow individuals to adjust also their dispersal strategy to their competitiveness and to avoid kin competition by remaining as a subordinate in another group.

We apologize that there was some confusion with terminology. We use the term “disperser” to describe individuals that disperse from their natal group. Dispersers can assume one of three roles: (1) they can migrate to another group as "subordinates"; (2) they can join another group as "breeders" if they successfully outcompete other candidates; or (3) they can remain as "floaters" if they fail to join a group. "Floaters" are individuals who persist in a transient state without access to a breeding territory, waiting for opportunities to join a group in an established territory. Therefore, dispersers do not work when they are floaters, but they may later help if they immigrate to a group as a subordinate. Consequently, immigrant subordinates have no inherent competitive advantage over natal subordinates (as step 2.2. “Join a group” is followed by step 3. “Help”, which occurs before step 5. “Become a breeder”). Nevertheless, floaters can potentially outcompete subordinates of the same age if they attempt to breed without first queuing as a subordinate (step 5) when subordinates are engaged in work tasks. We believe that this assumption is realistic and constitutes part of the costs associated with work tasks. However, floaters are at a disadvantage for becoming a breeder because: (1) floaters incur higher mortality than individuals within groups (eq. 3); and (2) floaters may only attempt to become breeders in some breeding cycles (versus subordinate groups members, who are automatically candidates for an open breeding position in the group in each cycle). Therefore, due to their higher mortality, floaters are rarely older than individuals within groups, which heavily influences dominance value and competitiveness. Additionally, any competitive advantage that floaters might have over other subordinate group members is unlikely to drive the kin selection-only results because subordinates would preferably choose defense tasks instead of work tasks so as not to be at a competitive disadvantage compared to floaters.

We note that reviewers also mention that floaters often aren't usually high resource holding potential (RHP) individuals and, therefore, our assumptions might be unrealistic. As we explain above, floaters are not inherently at a competitive advantage in our model. In any case, empirical work in a number of species has shown that dispersers are not necessarily those of lower RHP or of lower quality. In fact, according to the ecological constraints hypothesis, one might predict that high quality individuals are the ones that disperse because only individuals in good condition (e.g., larger body size, better energy reserves) can afford the costs associated with dispersal (Cote et al., 2022). By adding a reaction norm approach to explore the role of age or rank in the revised version, we can also determine whether higher or lower quality individuals are the ones dispersing. We will address the issues of terminology and clarity of the relative competitive advantage of floaters versus subordinates, and also include more information in the Supplementary Tables (e.g., the number of floaters). As a side note, the “scramble context” we mention was an additional implementation that we decided to remove from the final manuscript, but we forgot to remove from Table 1 before submission.

The reviewers also raised a question about asexual reproduction and relatedness more generally. As we showed in the Supplementary Tables and the section on relatedness in the SI (“Kin selection and the evolution of division of labor"), high relatedness does not appear to explain our results. In evolutionary biology generally and in game theory specifically (with the exception of models on sexual selection or sex-specific traits), asexual reproduction is often modelled because it reduces unnecessary complexity. To further study the effect of relatedness on kin structures more closely resembling those of vertebrates, however, we will create an additional “relatedness structure level”, where we will shuffle half of the philopatric offspring using the same method used to remove relatedness completely. This approach will effectively reduce relatedness structure by half and overcome the concerns with our decision to model asexual reproduction.

Briefly, we will elaborate on the concept of division of labor and the tasks that cooperative breeders perform. In nature, multiple tasks are often necessary to successfully rear offspring. For example, in many cooperatively breeding birds, the primary reasons that individuals fail to produce offspring are (1) starvation, which is mitigated by the feeding of offspring, and (2) nest depredation, which is countered by defensive behavior. Consequently, both types of tasks are necessary to successfully produce offspring, and focusing solely on one while neglecting the other is likely to result in lower reproductive success than if both tasks are performed by individuals within the group. We simplify this principle in the model by maximizing reproductive output when both tasks are carried out to a similar extent, allowing for some flexibility from the mean. In response to the reviewer suggestion about making fecundity a function of work tasks and offspring survival as a function of defensive tasks, these are actually equivalent in model terms, as it’s the same whether breeders produce three offspring and two die, or if they only produce one. This represents, of course, a simplification of the natural context, where breeding unsuccessfully is more costly (in terms of time and energy investment) than not breeding at all, but this is approach is typically used in models of this sort.

The scope of this paper was to study division of labor in cooperatively breeding species with fertile workers, in which help is exclusively directed towards breeders to enhance offspring production (i.e., alloparental care). Our focus is in line with previous work in most other social animals, including eusocial insects and humans, which emphasizes how division of labor maximizes group productivity. Other forms of “general” help are not considered in the paper, and such forms of help are rarely considered in cooperatively breeding vertebrates or in the division of labor literature, as they do not result in task partitioning to enhance productivity.

How do we model help? Help provided is an interaction between H (total effort) and T (proportion of total effort invested in each type of task). We will make this definition clearer in the revised manuscript. Thank you for pointing out an error in Eq. 1. This inequality was indeed written incorrectly in the paper (but is correct in the model code); it is dominance rank instead of age (see code in Individual.cpp lines 99-119). We will correct this mistake in the revision.

There was also a question about bounded and unbounded helping costs. The difference in costs is inherent to the nature of the different task (work or defense): while survival is naturally bounded, with death as the lower bound, dominance costs are potentially unbounded, as they are influenced by dynamic social contexts and potential competitors. Therefore, we believe that the model’s cost structure is not too different to that in nature.

Thank you for your comments about the parameter landscape. It is important to point out that variations in the mutation rate do not qualitatively affect our results, as this is something we explored in previous versions of the model (not shown). Briefly, we find that variations in the mutation rates only alter the time required to reach equilibrium. Increasing the step size of mutation diminishes the strength of selection by adding stochasticity and reducing the genetic correlation between offspring and their parents. Population size could, in theory, affect our results, as small populations are more prone to extinction. Since this was not something we planned to explore in the paper directly, we specifically chose a large population size, or better said, a large number of territories (i.e. 5000) that can potentially host a large population.

During the exploratory phase of the model development, various parameters and values were also assessed. However, the manuscript only details the ranges of values and parameters where changes in the behaviors of interest were observed, enhancing clarity and conciseness. For instance, variation in y_h (the cost of help on dominance when performing “work tasks”) led to behavioral changes similar to those caused by changes in x_h (the cost of help in survival when performing “defensive tasks”), as both are proportional to each other. Specifically, since an increase in defense costs raises the proportion of work relative to defense tasks, while an increase in the costs of work task has the opposite effect, only results for the variation of x_h were included in the manuscript to avoid redundancy. We will make this clearer in the revision.

Finally, following the advice from the reviewers, we will add the symbols of the variables to the figure axes, and clarify whether the values shown represent a genetic or phenotypic trait. In Figure 2, the x-axis is H and the y-axis is T. In Figure 3A, the subindex t in x-axis is incorrect; it should be subindex R (reaction norm to dominance rank instead of age), the y-axis is T. In Figure 3B, the x-axis is R, and the y-axis is T. All values of T, H and R are phenotypic expressed values (see Table 1). For instance, T values are the phenotypic expressed values from the individuals in the population according to their genetic gamma values and their current dominance rank at a given time point.

References

Cote, J., Dahirel, M., Schtickzelle, N., Altermatt, F., Ansart, A., Blanchet, S., Chaine, A. S., De Laender, F., De Raedt, J., & Haegeman, B. (2022). Dispersal syndromes in challenging environments: A cross‐species experiment. Ecology Letters, 25(12), 2675–2687.

Author response:

Reviewer #1 (Public review):

Summary:

This manuscript presents a practical modification of the orthogonal hybridization chain reaction (HCR) technique, a promising yet underutilized method with broad potential for future applications across various fields. The authors advance this technique by integrating peptide ligation technology and nanobody-based antibody mimetics - cost-effective and scalable alternatives to conventional antibodies - into a DNA-immunoassay framework that merges oligonucleotide-based detection with immunoassay methodologies. Notably, they demonstrate that this approach facilitates a modified ELISA platform capable of simultaneously quantifying multiple target protein expression levels within a single protein mixture sample.

Strengths:

The hybridization chain reaction (HCR) technique was initially developed to enable the simultaneous detection of multiple mRNA expression levels within the same tissue. This method has since evolved into immuno-HCR, which extends its application to protein detection by utilizing antibodies. A key requirement of immuno-HCR is the coupling of oligonucleotides to antibodies, a process that can be challenging due to the inherent difficulties in expressing and purifying conventional antibodies.

In this study, the authors present an innovative approach that circumvents these limitations by employing nanobody-based antibody mimetics, which recognize antibodies, instead of directly coupling oligonucleotides to conventional antibodies. This strategy facilitates oligonucleotide conjugation - designed to target the initiator hairpin oligonucleotide of HCR -through peptide ligation and click chemistry.

Weaknesses:

The sandwich-format technique presented in this study, which employs a nanobody that recognizes primary IgG antibodies, may have limited scalability compared to existing methods that directly couple oligonucleotides to primary antibodies. This limitation arises because the C-region types of primary antibodies are relatively restricted, meaning that the use of nanobody-based detection may constrain the number of target proteins that can be analyzed simultaneously. In contrast, the conventional approach of directly conjugating oligonucleotides to primary antibodies allows for a broader range of protein targets to be analyzed in parallel.

We would like to clarify that MaMBA was specifically designed to address and overcome the limitations imposed by relying on primary antibodies’ Fc types for multiplexing. MaMBA utilizes DNA oligo-conjugated nanobodies that selectively and monovalently bind to the Fc region of IgG. This key feature allows us to barcode primary IgGs targeting different antigens independently. These barcoded IgGs can then be pooled together after barcoding, effectively minimizing the potential for cross-reactivity or crossover. Therefore, IgGs barcoded using MaMBA are functionally equivalent to those barcoded via conventional direct conjugation approaches with respect to multiplexing capability.

Additionally, in the context of HCR-based protein detection, the number of proteins that can be analyzed simultaneously is inherently constrained by fluorescence wavelength overlap in microscopy, which limits its multiplexing capability. By comparison, direct coupling of oligonucleotides to primary antibodies can facilitate the simultaneous measurement of a significantly greater number of protein targets than the sandwich-based nanobody approach in the barcode-ELISA/NGS-based technique.

As we have responded above, MaMBA barcoding of primary IgGs that target various antigens can be conducted separately. Once barcoded, these IgGs can then be combined into a single pool. Therefore, for BLISA (i.e., the barcode-ELISA/NGS-based technique), IgGs barcoded through MaMBA offer the same multiplexing capability as those barcoded using traditional direct conjugation methods.

In in situ protein imaging, spectral overlap can indeed limit the throughput of multiplexed HCR fluorescent imaging. There are two strategies to address this challenge. As demonstrated in this work with misHCR and misHCRn, removing the HCR amplifiers allows for multiplexed detection using a limited number of fluorescence wavelengths. This is achieved through sequential rounds of HCR amplification and imaging. Alternatively, recent computational approaches offer promising solutions for “one-shot” multiplexed imaging. These include combinatorial multiplexing (PMID: 40133518) and spectral unmixing (PMID: 35513404), which can be applied to misHCR to deconvolute overlapping spectra and increase multiplexing capacity in a single imaging acquisition.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Nuclear depletion and cytoplasmic mislocalization/aggregation of the DNA and RNA binding protein TDP-43 are pathological hallmarks of multiple neurodegenerative diseases. Prior work has demonstrated that depletion of TDP-43 from the nucleus leads to alterations in transcription and splicing. Conversely, cytoplasmic mislocalization/aggregation can contribute to toxicity by impairing mRNA transport and translation as well as miRNA dysregulation. However, to date, models of TDP-43 proteinopathy rely on artificial knockdown- or overexpression-based systems to evaluate either nuclear loss or cytoplasmic gain of function events independently. Few model systems authentically reproduce both nuclear depletion and cytoplasmic miscloalization/aggregation events. In this manuscript, the authors generate novel iPSC-based reagents to manipulate the localization of endogenous TDP-43. This is a valuable resource for the field to study pathological consequences of TDP-43 proteinopathy in a more endogenous and authentic setting. However, in the current manuscript, there are a number of weaknesses that should be addressed to further validate the ability of this model to replicate human disease pathology and demonstrate utility for future studies.

Strengths:

The primary strength of this paper is the development of a novel in vitro tool.

Weaknesses:

There are a number of weaknesses detailed below that should be addressed to thoroughly validate these new reagents as more authentic models of TDP-43 proteinopathy and demonstrate their utility for future investigations.

(1) The authors should include images of their engineered TDP-43-GFP iPSC line to demonstrate TDP-43 localization without the addition of any nanobodies (perhaps immediately prior to addition of nanobodies). Additionally, it is unclear whether simply adding a GFP tag to endogenous TDP-43 impact its normal function (nuclear-cytoplasmic shuttling, regulation of transcription and splicing, mRNA transport etc).

We have included images of the untransduced day 20 MNs derived from the engineered TDP43-GFP iPSC lines and the unedited line (Supplementary Fig. 1B).

We acknowledge the reviewer’s concern about the potential impact of the GFP tag on TDP43's normal function. To address this, we have validated the functionality of TDP43 by assessing the inclusion of cryptic exons in highly sensitive targets such as UNC13A and STMN2, both of which are known to be directly regulated by TDP43.

We compared MNs derived from the unedited parent line with the TDP43-GFP MNs prior to nanobody addition. As measured by qPCR, cryptic exon inclusion in UNC13A and STMN2 was not observed in the unedited or edited TDP43-GFP MNs (Supplementary Fig.1C), confirming that the tagging does not induce splicing defects by itself. The cryptic exon inclusion in UNC13A and STMN2 were only observed in TDP43-GFP MNs expressing the NES nanobody (Supplementary Fig. 2D). These findings were further supported by our next-generation sequencing data, which also showed that cryptic exon inclusion was specific to the TDP43 mislocalization condition (Supplementary Fig.3 and 4).

Thus, we have strong evidence that the GFP-tagged TDP43 behaves similarly to the wild-type protein and does not interfere with its function in our model.

(2) Can the authors explain why there is a significant discrepancy in time points selected for nanobody transduction and immunostaining or cell lysis throughout Figure 1 and 2? This makes interpretation and overall assessment of the model challenging.

For the phenotypic data shown in Fig.1, we added the AAVs at day 18 or 20 and analyzed the cells at day 40. For the phosphorylated TDP43 western blot (revised Fig. 3D), cells were treated with doxycycline at day 20 to induce nanobody expression and samples were harvested at day 40. Thus, cells were harvested between days 20 or 22 after adding the nanobodies. The onset of transgene expression when using AAVs in neurons typically display slow kinetics. We observed TDP43 mislocalization in less than 50% of the neurons after 7 days post-transduction that peaked at 10-12 days after addition of the nanobodies, when more than 80% of the cells displayed TDP43 mislocalization. Hence, we do not believe that a two-day difference significantly alters the interpretation of the data.

The decision to harvest neurons at day 30 for the qPCR data was taken to investigate whether the splicing changes seen at day 40 from the transcriptomics analysis can be detected well before the phenotypes observed at day 40.

(3) The authors should further characterize their TDP-43 puncta. TDP-43 immunostaining is typically punctate so it is unclear if the puncta observed are physiologic or pathologic based on the analyses carried out in the current version of this manuscript. Additionally, do these puncta co-localize with stress granule markers or RNA transport granule markers? Are these puncta phosphorylated (which may be more reminiscent of end-stage pathologic observations in humans)?

We have tried immunostaining neurons for phosphorylated TDP43. However, our immunostaining attempts were unsuccessful. Depending on the antibody, we either saw no signal (antibody from Cosmo Bio, TIP-PTD-M01A) or even the control neurons displayed detectable phosphorylation within the nucleus (antibody from Proteintech 22309-1-AP). Consequently, we performed western blot analysis using an antibody from Cosmo Bio, (TIP-PTD-M01A) that clearly shows hyperphosphorylation of TDP43 in whole cell lysates (Fig. 3D, E). Hence, we have referred to these structures as puncta and not aggregates (Page 4).

To assess co-localization of the puncta with stress granules, we immunostained for the stress granule marker G3BP1. This was done in MNs that were treated with sodium arsenite (SA) or PBS as a control. In the PBS treated control MN cultures, TDP43 mislocalization alone did not induce stress granule formation. G3BP1+ stress granules were only observed following SA stress (0.5 mM, 60 minutes). Further, only a subset of TDP43 puncta overlapped with these stress granules (Supplementary Fig. 7) (Page 6).

(4) The authors should include multiple time points in their evaluation of TDP-43 loss of function events and aggregation. Does loss of function get worse over time? Is there a time course by which RNA misprocessing events emerge or does everything happen all at once? Does aggregation get worse over time? Do these neurons die at any point as a result of TDP-43 proteinopathy?

We agree that a time course to analyze TDP43 mislocalization and its consequences would be ideal. However, the mislocalization of TDP43 across neurons is not a coordinated process. At each given time instance, neurons display varying levels of TDP43 mislocalization. Answering the questions raised by the reviewer would require tracking individual neurons in real time in a controlled environment over weeks. Unfortunately, we currently do not have the hardware to run these experiments. However, we do observe increased levels of cleaved caspase 3 in MNs expressing the NES nanobody, indicating that these neurons indeed undergo apoptosis by day 40 (Fig.1).

We have, however, analyzed changes in splicing using qPCR for 12 genes over a time course starting as early as 4 hours after inducing mislocalization. We detect time-dependent cryptic splicing events in all genes as early as 8 hours after doxycycline addition, coinciding with the appearance TDP43 mislocalization (Fig. 4A, B).

(5) Can the authors please comment on whether or not their model is "tunable"? In real human disease, not every neuron displays complete nuclear depletion of TDP-43. Instead there is often a gradient of neurons with differing magnitudes of nuclear TDP-43 loss. Additionally, very few neurons (5-10%) harbor cytoplasmic TDP-43 aggregates at end-stage disease. These are all important considerations when developing a novel authentic and endogenous model of TDP-43 proteinopathy which the current manuscript fails to address.

As shown in Fig .1, the neurons expressing the NES-nanobody display a wide range of mislocalization as assessed by the % of nuclear TDP43 present. By titrating the amount of AAVs added to the culture, the model can be tuned to achieve a wide gradient of TDP43 mislocalization.

We calculated the size and percentage of neurons displaying TDP43 puncta. The size and the number of aggregates varies across the neurons that display TDP43 mislocalization. Around 50% of the neurons displayed small (1  um²) puncta while large puncta (> 5  um²) were observed in <10% of the cells, similar to observations in patient tissue (Fig. 1F).

Reviewer #2 (Public Review):

Summary:

TDP-43 mislocalization occurs in nearly all of ALS, roughly half of FTD, and as a co-pathology in roughly half of AD cases. Both gain-of-function and loss-of-function mechanisms associated with this mislocalization likely contribute to disease pathogeneisis.

Here, the authors describe a new method to induce TDP-43 mislocalization in cellular models. They endogenously tagged TDP-43 with a C-terminal GFP tag in human iPSCs. They then expressed an intrabody - fused with a nuclear export signal (NES) - that targeted GFP to the cytosol. Expression of this intrabody-NES in human iPSC-derived neurons induced nuclear depletion of homozygous TDP-43-GFP, caused its mislocalization to the cytosol, and at least in some cells appeared to cause cytosolic aggregates. This mislocalization was accompanied by induction of cryptic exons in well characterized transcripts known to be regulated by TDP-43, a hallmark of functional TDP-43 loss and consistent with pathological nuclear TDP-43 depletion. Interestingly, in heterozygous TDP-43-GFP neurons, expression of intrabody-NES appeared to also induce the mislocalization of untagged TDP-43 in roughly half of the neurons, suggesting that this system can also be used to study effects on untagged endogenous TDP-43 as well as TDP-43-GFP fusion protein.

Strengths:

A clearer understanding of how TDP-43 mislocalization alters cellular function, as well as pathways that mitigate clearance of TDP-43 aggregates, is critical. But modeling TDP-43 mislocalization in disease-relevant cellular systems has proven to be challenging. High levels of overexpression of TDP-43 lacking an NES can drive endogenous TDP-43 mislocalization, but such overexpression has direct and artificial consequences on certain cellular features (e.g. altered exon skipping) not seen in diseased patients. Toxic small molecules such as MG132 and arsenite can induce TDP-43 mislocalization, but co-induce myriad additional cellular dysfunctions unrelated to TDP-43 or ALS. TDP-43 binding oligonucleotides can cause cytosolic mislocalization as well. Each system has pros and cons, and additional ways to induce TDP-43 mislocalization would be useful for the field. The method described in this manuscript could provide researchers with a powerful way to study the combined biology of cytosolic TDP-43 mislocalization and nuclear TDP-43 depletion, with additional temporal control that is lacking in current method. Indeed, the authors see some evidence of differences in RNA splicing caused by pure TDP-43 depletion versus their induced mislocalization model. Finally, their method may be especially useful in determining how TDP-43 aggregates are cleared by cells, potentially revealing new biological pathways that could be therapeutically targeted.

Weaknesses:

The method and supporting data have limitations in its current form, outlined below, and in its current form the findings are rather preliminary.

(1) Tagging of TDP-43 with a bulky GFP tag may alter its normal physiological functions, for example phase separation properties and functions within complex ribonucleoprotein complexes. In addition, alternative isoforms of TDP-43 (e.g. "short" TDP-43, would not be GFP tagged and therefore these species would not be directly manipulatable or visualizable with the tools currently employed in the manuscript.

With reference to our answer above, we have confirmed using qPCR and RNA-seq analysis that adding a GFP tag to the C-terminus of TDP43 does not result in an appreciable loss of functionality. We do not observe any cryptic exon inclusion in STMN2 and UNC13A. Cryptic exon inclusion in these genes, especially STMN2, has been recognized as a very sensitive indicator of TDP43 loss of function (Supplementary Fig 1C, Supplementary 2D, Fig. 3, Fig.4)

We acknowledge that truncated alternatively spliced versions of TDP43 will lose the GFP-tag and cannot be manipulated with our system. Since our GFP tag is positioned on the C-terminus, our system cannot manipulate these truncated fragments as the tag is lost in these isoforms. But these isoforms, if present, should be detectable using the Proteintech antibody against total TDP43, which recognizes N-terminal TDP43 epitopes. However, western blot analysis, even 20 days after inducing TDP43 mislocalization, showed no truncated fragments. This suggests that TDP43 mislocalization alone is insufficient to generate significant levels of truncated isoforms. We have added this section to the Limitations paragraph (page 9).

(2) The data regarding potential mislocalization of endogenous TDP-43 in the heterozygous TDP-43-GFP lines is especially intriguing and important, yet very little characterization was done. Does untagged TDP-43 co-aggregate with the tagged TDP-43? Is localization of TDP-43 immunostaining the same as the GFP signal in these cells?

The purpose of the heterozygous experiments was to see whether mislocalized TDP43 could potentially trap the untagged TDP43. If this was not the case, we would have seen a maximum of 50% of the TDP43 signal mislocalized to the cytoplasm. The fact that a sizeable proportion of cells had significantly higher levels of TDP43 loss from the nucleus, indicates that mislocalized TDP43 can indeed trap the untagged protein fraction. We used GFP immunostaining to identify the tagged TDP43 while an antibody against the endogenous TDP43 protein was used to detect total TDP43 levels. In the cells that show near complete loss of nuclear TDP43, the total TDP43 signal coincides with the GFP (tagged TDP43) signal. We are unable to distinguish the untagged fraction selectively as we do not have an antibody that can detect this directly.  

But we agree with the reviewer that these observations need further detailed follow-up that we are unable to provide currently. Hence, we have removed this figure from the manuscript.

(3) The experiments in which dox was used to induce the nanobody-NES, then dox withdrawn to study potential longer-lasting or self-perpetuating inductions of aggregation is potentially interesting. However, the nanobody was only measured at the RNA level. We know that protein half lives can be very long in neurons, and therefore residual nanobody could be present at these delayed time points. The key measurement to make would be at the protein level of the nanobody if any conclusions are be made from this experiment.

The reviewer has highlighted an important point. To address this issue, we tagged the nanobodies with a V5 tag that allowed us to directly measure nanobody levels within cells. After Dox withdrawal, we indeed observed significant expression of the nanobody within cells even after two weeks of Dox withdrawal. Extending the time point to three weeks allowed complete loss of the nanobody in most neurons. However, in contrast to our observations at two weeks, this was accompanied by a reversal of TDP43 mislocalization in these neurons at three weeks (Fig. 5).

Surprisingly, in less than 10% of the neurons, we observed >80% of the total TDP43 still mislocalized to the cytoplasm, despite nearly undetectable levels of the nanobody. Super-resolution microscopy further revealed persistent cytoplasmic TDP43 in these neurons that did not overlap with residual nanobody signal. This suggests that in these neurons, the nanobody was no longer required to maintain TDP43 mislocalization (Fig. 5, page 7)

(4) Potential differences in splicing and microRNAs between TDP-43 knockdown and TDP-43 mislocalization are potentially interesting. However, different patterns of dysregulated RNA splicing can occur at different levels of TDP-knockdown, thus it is difficult to assess whether the changes observed in this paper are due to mislocalization per se, or rather just reflect differences in nuclear TDP-43 abundance.

This a fair point. It is possible that microRNA dysregulation might require a greater loss of nuclear TDP43 and maybe more resilient to TDP43 loss as compared to splicing. We have acknowledged this in the discussion section (page 9).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) It would be helpful to include nuclear vs cytoplasmic ratios of TDP-43 instead of simply "% nuclear TDP-43"

We have used % nuclear TDP43 as these values have biologically meaningful upper and lower bounds, which makes it easier to compare across experiments. We found that using a ratio of nuclear vs cytoplasmic TDP43 intensities displayed higher variability and a wider range.

We have re-labelled the y-axis as “% Nuclear TD43 / soma TDP43” to make our quantification clearer. The conversion from % nuclear TDP43 to N/C is straightforward. If the % nuclear TDP43 is X, then the N/C ratio can be calculated as X / (100-X). For example, a % nuclear TDP43 of 80% would amount to an N/C ratio of 80/20 = 4.

(2) The axis descriptions in Figure 1D are very unclear. While this is described better in the figure legend, it would be beneficial to have a more descriptive y-axis title in the figure (which may mean increasing the number of graphs).

Axis descriptions and figures changed as recommended.

(3) In Figure 1, the time points at which iPSNs were transduced with nanobody and/or fixed for immunostaining is somewhat inconsistent across all panels. This hinders interpretation of the figure as a whole. The authors should use same transduction and immunostaining time points for consistency or demonstrate that the same phenotype is observed regardless of transduction and immunostaining day as long as the time in between (time of nano body expression) is consistent. Subsequently, in Figure 2, a different set of time points is used.

Please see our response in the public comments above

(4) In Figure 1, please show individual data points for each independent differentiation to demonstrate the level of reproducibility from batch to batch.

Data points have been shown per replicate (Supplementary Fig. 2)

We have refined our approach for phenotypic analysis to improve consistency across different clones. Previously, we set thresholds on % nuclear TDP43 to distinguish MNs with nuclear versus mislocalized TDP43. This was done by ranking all cells based on % nuclear TDP43 and applying quantile-based thresholds—designating the top 25% as control and the bottom 25% as mislocalized, ensuring equal number of cells per category. However, we observed significant variability in thresholds across clones. For instance, the E8 clone had thresholds of 96% and 29%, while the E5 clone had 93% and 40%.

To address this, we reanalysed the data using a standardized three-bin approach:

(1) Control: MNs expressing the control nanobody.

(2) Low-Moderate Mislocalization: MNs expressing the NES nanobody with > 40% nuclear TDP43.

(3) Severe Mislocalization: MNs expressing the NES nanobody with < 40% nuclear TDP43.

This approach ensured a more reliable comparison of TDP43 mislocalization effects across experiments. The conclusions remain the same.

(5) In Figure 2, please show individual data points.

Data points for all the qPCR analyses in the paper have been included as a supplementary text file.

(6) In Figure 3, please show individual data points.

Data points for the western blot data have been included as a supplementary data file.

All other comments are within the public review.

Reviewer #2 (Recommendations For The Authors):

(1) In general more robust quantification of many of the described phenotypes are necessary. In particular, no apparent quantification of cytosolic mislocalization was performed in Figure 1, or quantification of mislocalization of Figure 3F. It is unclear in the western blot in Fig 1G if TDP-43 signal were normalized to total protein, and of note it seems that expression of the intrabody-NES reduced total proteins in the western blots that were shown. No quantification or measurement of the insoluble material was done or shown.

We have quantified cytosolic mislocalization of TDP43 (Fig. 1C). The y-axis indicates the total TDP43 signal observed in the nucleus as a percentage of the total signal observed in the soma (including the nucleus). This value has the advantage of ranging between 100% (perfectly nuclear) to 0% (complete nuclear loss). The boxplots indicate that expression of the NES-nanobody results in a range of cytosolic mislocalization with a median value around 40% of the TDP43 remaining in the nucleus.

Western blot data in previous Fig. 1G was normalized to alpha-tubulin. We were unable to get a good signal for the insoluble fraction. From the alpha-tubulin alone, it cannot be concluded that NES-nanobody results in a decrease in total protein levels. In the revised western blot for phosphorylated TDP43 (Fig. 3D, E), we have quantified total and phosphorylated TDP43. Here, we observe a six-fold increase in the levels of phosphorylated TDP43 without a significant change in total TDP43 protein levels.

To avoid potential mis-interpretation of our results, we have now removed the previous Fig. 1G.

(2) Additional images of nearly all microscopy data at higher magnifications would be required to better evaluate TDP-43 localization. Ideally including images for each channel in addition to merged images, and especially for key figures such as Figure 1B, 3B, 3F.

Better images have been provided.

(3) No control images were shown for Figure 1F and 3F. It is unclear what the bright punctate spots of cytoplasmic TDP-43 GFP signal represent. Are these true aggregates? If so, additional characterization would be required before such conclusions can be made, beyond the relatively superficial western blot analysis that was done in Figure 1.

Control images have now been provided (Figure 1E). As we mentioned above, immunostaining analysis to characterize whether the aggregates are phosphorylated failed to provide a clear signal. However, we have now confirmed that the mislocalized TDP43 is indeed hyper-phosphorylated (Figure 3D, E). We have acknowledged this in the main text, and have referred to these as puncta reminiscent of aggregates (Page 4, Page 6).

Author response:

The following is the authors’ response to the original reviews

Public Reviews:  

Reviewer #1 (Public Review):

Summary:

This paper reports an intracranial SEEG study of speech coordination, where participants synchronize their speech output with a virtual partner that is designed to vary its synchronization behavior. This allows the authors to identify electrodes throughout the left hemisphere of the brain that have activity (both power and phase) that correlates with the degree of synchronization behavior. They find that high-frequency activity in the secondary auditory cortex (superior temporal gyrus) is correlated to synchronization, in contrast to primary auditory regions. Furthermore, activity in the inferior frontal gyrus shows a significant phase-amplitude coupling relationship that is interpreted as compensation for deviation from synchronized behavior with the virtual partner.

Strengths:

(1) The development of a virtual partner model trained for each individual participant, which can dynamically vary its synchronization to the participant's behavior in real-time, is novel and exciting.

(2) Understanding real-time temporal coordination for behaviors like speech is a critical and understudied area.

(3) The use of SEEG provides the spatial and temporal resolution necessary to address the complex dynamics associated with the behavior.

(4) The paper provides some results that suggest a role for regions like IFG and STG in the dynamic temporal coordination of behavior both within an individual speaker and across speakers performing a coordination task.

We thank the Reviewer for their positive comments on our manuscript.

Weaknesses:

(1) The main weakness of the paper is that the results are presented in a largely descriptive and vague manner. For instance, while the interpretation of predictive coding and error correction is interesting, it is not clear how the experimental design or analyses specifically support such a model, or how they differentiate that model from the alternatives. It's possible that some greater specificity could be achieved by a more detailed examination of this rich dataset, for example by characterizing the specific phase relationships (e.g., positive vs negative lags) in areas that show correlations with synchronization behavior. However, as written, it is difficult to understand what these results tell us about how coordination behavior arises.

We understand the reviewer’s comment. It is true that this work, being the first in the field using real-time adapting synchronous speech and intracerebral neural data, is a descriptive work, that hopefully will pave the way for further studies. We have now added more statistical analyses (see point 2) to go beyond a descriptive approach and we have also rewritten the discussion to clarify how this work can possibly contribute to disentangle different models of language interaction. Most importantly we have also run new analyses taking into account the specific phase relationship, as suggested.

We already had an analysis using instantaneous phase difference in the phase-amplitude coupling approach, that bridges phase of behaviour to neural responses (amplitude in the high-frequency range). However, this analysis, as the reviewer noted, does not distinguish between positive and negative lags, but rather uses the continuous fluctuations of coordinative behaviour. Following the reviewer’s suggestion, we have now run a new analysis estimating the average delay (between virtual partner speech and patient speech) in each trial, using a cross-correlation approach. This gives a distribution of delays across trials that can then be “binned” as positive or negative. We have thus rerun the phase-amplitude coupling analyses on positive and negative trials separately, to assess whether the phase amplitude relationship depends upon the anticipatory (negative lags) or compensatory (positive lags) behaviour. Our new analysis (now in the supplementary, see figure below) does not reveal significant differences between positive and negative lags. This lack of difference, although not easy to interpret, is nonetheless interesting because it seems to show that the IFG does not have a stronger coupling for anticipatory trials. Rather the IFG seems to be strongly involved in adjusting behaviour, minimizing the error, independently of whether this is early or late.

We have updated the “Coupling behavioural and neurophysiological data” section in Materials and methods as follows:  

“In the third approach, we assessed whether the phase-amplitude relationship (or coupling) depends upon the anticipatory (negative delays) or compensatory (positive delays) behaviour between the VO and the patients’ speech. We computed the average delay in each trial using a cross-correlation approach on speech signals (between patient and VP) with the MATLAB function xcorr. A median split (patient-specific ; average median split = 0ms, average sd = 24ms) was applied to conserve a sufficient amount of data, classifying trials below the median as “anticipatory behaviour” and trials above the median as “compensatory behaviour”. Then we conducted the phase-amplitude coupling analyses on positive and negative trials separately.”

We also added a paragraph on this finding in the Discussion:

“Our results highlight the involvement of the inferior frontal gyrus (IFG) bilaterally, in particular the BA44 region, in speech coordination. First, trials with a weak verbal coordination (VCI) are accompanied by more prominent high frequency activity (HFa, Fig.4; Fig.S4). Second, when considering the within-trial time-resolved dynamics, the phase-amplitude coupling (PAC) reveals a tight relation between the low frequency behavioural dynamics (phase) and the modulation of high-frequency neural activity (amplitude, Fig.5B ; Fig.S5). This relation is strongest when considering the phase adjustments rather than the phase of speech of the VP per se : larger deviations in verbal coordination are accompanied by increase in HFa. Additionally, we also tested for potential effects of different asynchronies (i.e., temporal delay) between the participant's speech and that of the virtual partner but found no significant differences (Fig.S6). While lack of delay-effect does not permit to conclude about the sensitivity of BA44 to absolute timing of the partner’s speech, its neural dynamics are linked to the ongoing process of resolving phase deviations and maintaining synchrony.”

(2) In the results section, there's a general lack of quantification. While some of the statistics reported in the figures are helpful, there are also claims that are stated without any statistical test. For example, in the paragraph starting on line 342, it is claimed that there is an inverse relationship between rho-value and frequency band, "possibly due to the reversed desynchronization/synchronization process in low and high frequency bands". Based on Figure 3, the first part of this statement appears to be true qualitatively, but is not quantified, and is therefore impossible to assess in relation to the second part of the claim. Similarly, the next paragraph on line 348 describes optimal clustering, but statistics of the clustering algorithm and silhouette metric are not provided. More importantly, it's not entirely clear what is being clustered - is the point to identify activity patterns that are similar within/across brain regions? Or to interpret the meaning of the specific patterns? If the latter, this is not explained or explored in the paper.

The reviewer is right. We have now added statistical analyses showing that:

(1) the ratio between synchronization and desynchronization evolves across frequencies (as often reported in the literature).

(2) the sign of rho values also evolves across frequencies.

(3) the clustering does indeed differ when taking into account behaviour. We have also clarified the use of clustering and the reasoning behind it.

We have updated the Materials and methods section as follows:

“The statistical difference between spatial clustering in global effect and brain-behaviour correlation was estimated with linear model using the R function lm (stat package), post-hoc comparisons were corrected for multiple comparisons using the Tukey test (lsmeans R package ; Lenth, 2016). The statistical difference between clustering in global effect and behaviour correlation across the number of clusters was estimated using permutation tests (N=1000) by computing the silhouette score difference between the two conditions.” We have updated the Results section as follows:

(1) “This modulation between synchronization and desynchronization across frequencies was significant (F(5) = 6.42, p < .001 ; estimated with linear model using the R function lm).”

(2) “The first observation is a gradual transition in the direction of correlations as we move up frequency bands, from positive correlations at low frequencies to negative ones at high frequencies (F(5) = 2.68, p = .02). This effect, present in both hemispheres, mimics the reversed desynchronization/synchronization process in low and high frequency bands reported above.”

(3) “Importantly, compared to the global activity (task vs rest, Fig 3A), the neural spatial profile of the behaviour-related activity (Fig 3B) is more clustered, in the left hemisphere. Indeed, silhouette scores are systematically higher for behaviour-related activity compared to global activity, indicating greater clustering consistency across frequency bands (t(106) = 7.79, p < .001, see Figure S3). Moreover, silhouette scores are maximal, in particular for HFa, for five clusters (p < .001), located in the IFG BA44, the IPL BA 40 and the STG BA 41/42 and BA22 (see Figure S3).”

(3) Given the design of the stimuli, it would be useful to know more about how coordination relates to specific speech units. The authors focus on the syllabic level, which is understandable. But as far as the results relate to speech planning (an explicit point in the paper), the claims could be strengthened by determining whether the coordination signal (whether error correction or otherwise) is specifically timed to e.g., the consonant vs the vowel. If the mechanism is a phase reset, does it tend to occur on one part of the syllable?

Thank you for this thoughtful feedback. We agree that the relationship between speech coordination and specific speech units, such as consonants versus vowels, is an intriguing question. However, in our study, both interlocutors (the participant and the virtual partner) are adapting their speech production in real-time. This interactive coordination makes it difficult to isolate neural signatures corresponding to precise segments like consonants or vowels, as the adjustments occur in a continuous and dynamic context.

The VP's ability to adapt depends on its sensitivity to spectral cues, such as the transition from one phonetic element to another. This is likely influenced by the type of articulation, with certain transitions being more salient (e.g., between a stop consonant like "p" and a vowel like "a") and others being less distinct (e.g., between nasal consonants like "m" and a vowel). Thus, the VP’s spectral adaptation tends to occur at these transitions, which are more prominent in some cases than in others.

For the participants, previous studies have shown a greater sensitivity during the production of stressed vowels (Oschkinat & Hoole, 2022; Li & Lancia, 2024), which may reflect a heightened attentional or motor adjustment to stressed syllables.

Here, we did not specifically address the question of coordination at the level of individual linguistic units. Moreover, even if we attempted to focus on this level, it would be challenging to relate neural dynamics directly to specific speech segments. The question of how synchronization at the level of individual linguistic units might relate to neural data is complex. The lack of clear, unit-specific predictions makes it difficult to parse out distinct neural signatures tied to individual segments, particularly when both interlocutors are continuously adjusting their speech in relation to one another.

Therefore, while we recognize the potential importance of examining synchronization at the level of individual phonetic elements, the design of our task and the nature of the coordination in this interactive context (realtime bidirection adaptation) led us to focus more broadly on the overall dynamics of speech synchronization at the syllabic level, rather than on specific linguistic units.

We now state at the end of the Discussion section:

“It is worth noting that the influence of specific speech units, such as consonants versus vowels, on speech coordination remains to be explored. In non-interactive contexts, participants show greater sensitivity during the production of stressed vowels, possibly reflecting heightened attentional or motor adjustments (Oschkinat & Hoole, 2022; Li & Lancia, 2024). In this study, the VP’s adaptation relies on sensitivity to spectral cues, particularly phonetic transitions, with some (e.g., formant transitions) being more salient than others. However, how these effects manifest in an interactive setting remains an open question, as both interlocutors continuously adjust their speech in real time. Future studies could investigate whether coordination signals, such as phase resets, preferentially align with specific parts of the syllable.” References cited:

– Oschkinat, M., & Hoole, P. (2022). Reactive feedback control and adaptation to perturbed speech timing in stressed and unstressed syllables. Journal of Phonetics, 91, 101133.

– Li, J., & Lancia, L. (2024). A multimodal approach to study the nature of coordinative patterns underlying speech rhythm. In Proc. Interspeech, 397-401.

(4) In the discussion the results are related to a previously-described speech-induced suppression effect. However, it's not clear what the current results have to do with SIS, since the speaker's own voice is present and predictable from the forward model on every trial. Statements such as "Moreover, when the two speech signals come close enough in time, the patient possibly perceives them as its own voice" are highly speculative and apparently not supported by the data.

We thank the reviewer for raising thoughtful concerns about our interpretation of the observed neural suppression as related to speaker-induced suppression (SIS). We agree that our study lacks a passive listening condition, which limits direct comparisons to the original SIS effect, traditionally defined as the suppression of neural responses to self-produced speech compared to externally-generated speech (Meekings & Scott, 2021).

In response, we have reconsidered our terminology and interpretation. In the revised Discussion section, we refer to our findings as a "SIS-related phenomenon specific to the synchronous speech context". Unlike classic SIS paradigms, our interactive task involves simultaneous monitoring of self- and externally-generated speech, introducing additional attentional and coordinative demands.

The revised Discussion also incorporates findings by Ozker et al. (2022, 2024), which link SIS and speech monitoring, suggesting that suppressing responses to self-generated speech facilitates error detection. We propose that the decrease in high-frequency activity (HFa) as verbal coordination increases reflects reduced error signals due to closer alignment between perceived and produced speech. Conversely, HFa increases with reduced coordination may signify greater prediction error.

Additionally, we relate our findings to the "rubber voice" effect (Zheng et al., 2011; Lind et al., 2014; Franken et al., 2021), where temporally and phonetically congruent external speech can be perceived as self-generated. We speculate that this may occur in synchronous speech tasks when the participant's and VP's speech signals closely align. However, this interpretation remains speculative, as no subjective reports were collected to confirm this perception. Future studies could include participant questionnaires to validate this effect and relate subjective experience to neural measures of synchronization.

Overall, our findings extend the study of SIS to dynamic, interactive contexts and contribute to understanding internal forward models of speech production in more naturalistic scenarios.

We have now added these points to the discussion as follows:

“The observed negative correlation between verbal coordination and high-frequency activity (HFa) in STG BA22 suggests a suppression of neural responses as the degree of behavioural synchrony increases. This result is reminiscent of findings on speaker-induced suppression (SIS), where neural activity in auditory cortex decreases during self-generated speech compared to externally-generated speech (Meekings & Scott, 2021; Niziolek et al., 2013). However, our paradigm differs from traditional SIS studies in two critical ways: (1) the speaker's own voice is always present and predictable from the forward model, and (2) no passive listening condition was included. Therefore, our findings cannot be directly equated with the original SIS effect.

Instead, we propose that the suppression observed here reflects a SIS-related phenomenon specific to the synchronous speech context. Synchronous speech requires simultaneous monitoring of self- and externallygenerated speech, a task that is both attentionally demanding and coordinative. This aligns with evidence from Ozker et al. (2024, 2022), showing that the same neural populations in STG exhibit SIS and heightened responses to feedback perturbations. These findings suggest that SIS and speech monitoring are related processes, where suppressing responses to self-generated speech facilitates error detection. In our study, suppression of HFa as coordination increases may reflect reduced prediction errors due to closer alignment between perceived and produced speech signals. Conversely, increased HFa during poor coordination may signify greater mismatch, consistent with prediction error theories (Houde & Nagarajan, 2011; Friston et al., 2020). Furthermore, when self- and externally-generated speech signals are temporally and phonetically congruent, participants may perceive external speech as their own. This echoes the "rubber voice" effect, where external speech resembling self-produced feedback is perceived as self-generated (Zheng et al., 2011; Lind et al., 2014; Franken et al., 2021). While this interpretation remains speculative, future studies could incorporate subjective reports to investigate this phenomenon in more detail.” References cited:

– Franken, M. K., Hartsuiker, R. J., Johansson, P., Hall, L., & Lind, A. (2021). Speaking With an Alien Voice: Flexible Sense of Agency During Vocal Production. Journal of Experimental Psychology-Human perception and performance, 47(4), 479-494. https://doi.org/10.1037/xhp0000799

– Houde, J. F., & Nagarajan, S. S. (2011). Speech production as state feedback control. Frontiers in human neuroscience, 5, 82.

– Lind, A., Hall, L., Breidegard, B., Balkenius, C., & Johansson, P. (2014). Speakers' acceptance of real-time speech exchange indicates that we use auditory feedback to specify the meaning of what we say. Psychological Science, 25(6), 1198-1205. https://doi.org/10.1177/0956797614529797

– Meekings, S., & Scott, S. K. (2021). Error in the Superior Temporal Gyrus? A Systematic Review and Activation Likelihood Estimation Meta-Analysis of Speech Production Studies. Journal of Cognitive Neuroscience, 33(3), 422-444. https://doi.org/10.1162/jocn_a_01661

– Niziolek C. A., Nagarajan S. S., Houde J. F (2013) What does motor efference copy represent? Evidence from speech production Journal of Neuroscience 33:16110–16116Ozker M., Doyle W., Devinsky O., Flinker A (2022) A cortical network processes auditory error signals during human speech production to maintain fluency PLoS Biology 20.

– Ozker, M., Yu, L., Dugan, P., Doyle, W., Friedman, D., Devinsky, O., & Flinker, A. (2024). Speech-induced suppression and vocal feedback sensitivity in human cortex. eLife, 13, RP94198. https://doi.org/10.7554/eLife.94198

– Zheng, Z. Z., MacDonald, E. N., Munhall, K. G., & Johnsrude, I. S. (2011). Perceiving a Stranger's Voice as Being One's Own: A 'Rubber Voice' Illusion? PLOS ONE, 6(4), e18655.

(5) There are some seemingly arbitrary decisions made in the design and analysis that, while likely justified, need to be explained. For example, how were the cutoffs for moderate coupling vs phase-shifted coupling (k ~0.09) determined? This is noted as "rather weak" (line 212), but it's not clear where this comes from. Similarly, the ROI-based analyses are only done on regions "recorded in at least 7 patients" - how was this number chosen? How many electrodes total does this correspond to? Is there heterogeneity within each ROI?

The reviewer is correct, we apologize for this missing information. We now specify that the coupling values were empirically determined on the basis of a pilot experiment in order to induce more or less synchronization, but keeping the phase-shifted coupling at a rather implicit level.  

Concerning the definition of coupling as weak, one should consider that, in the Kuramoto model, the strength of coupling (k) is relative to the spread of the natural frequencies (Δω) in the system. In our study, the natural frequencies of syllables range approximately from 2 Hz to 10Hz, resulting in a frequency spread of Δω = 8 Hz. For coupling to strongly synchronize oscillators across such a wide range, k must be comparable to or exceed Δω. Thus, since k = 0.1 is far much smaller than Δω, it is therefore classified as weak coupling.

We have now modified the Materials and methods section as follows:

“More precisely, for a third of the trials the VP had a neutral behaviour (close to zero coupling: k = +/- 0.01). For a third it had a moderate coupling, meaning that the VP synchronised more to the participant speech (k = -0.09). And for the last third of the trials the VP had a moderate coupling but with a phase shift of pi/2, meaning that it moderately aimed to speak in between the participant syllables (k = + 0.09). The coupling values were empirically determined on the basis of a pilot experiment in order to induce more or less synchronization but keeping the phase-shifted coupling at a rather implicit level. In other terms, while participants knew that the VP would adapt, they did not necessarily know in which direction the coupling went.”

Regarding the criterion of including regions recorded in at least 7 patients, our goal was to balance data completeness with statistical power. Given our total sample of 16 patients, this threshold ensures that each included region is represented in at least ~44% of the cohort, reducing the likelihood of spurious findings due to extremely small sample sizes. This choice also aligns with common neurophysiological analysis practices, where a minimum number of subjects (at least 2 in extreme cases) is required to achieve meaningful interindividual comparisons while avoiding excessive data exclusion. Additionally, this threshold maintains a reasonable tradeoff between maximizing patient inclusion and ensuring that statistical tests remain robust.

We have now added more information in the Results section “Spectral profiles in the language network are nuanced by behaviour” on this point as follows:

“To balance data completeness and statistical power, we included only brain regions recorded in at least 7 patients (~44% of the cohort) for the left hemisphere and at least 5 patients for the right hemisphere (~31% of the cohort), ensuring sufficient representation while minimizing biases due to sparse data.”

Reviewer #2 (Public Review):

Summary:

This paper investigates the neural underpinnings of an interactive speech task requiring verbal coordination with another speaker. To achieve this, the authors recorded intracranial brain activity from the left hemisphere in a group of drug-resistant epilepsy patients while they synchronised their speech with a 'virtual partner'. Crucially, the authors were able to manipulate the degree of success of this synchronisation by programming the virtual partner to either actively synchronise or desynchronise their speech with the participant, or else to not vary its speech in response to the participant (making the synchronisation task purely one-way). Using such a paradigm, the authors identified different brain regions that were either more sensitive to the speech of the virtual partner (primary auditory cortex), or more sensitive to the degree of verbal coordination (i.e. synchronisation success) with the virtual partner (secondary auditory cortex and IFG). Such sensitivity was measured by (1) calculating the correlation between the index of verbal coordination and mean power within a range of frequency bands across trials, and (2) calculating the phase-amplitude coupling between the behavioural and brain signals within single trials (using the power of high-frequency neural activity only). Overall, the findings help to elucidate some of the left hemisphere brain areas involved in interactive speaking behaviours, particularly highlighting the highfrequency activity of the IFG as a potential candidate supporting verbal coordination.

Strengths:

This study provides the field with a convincing demonstration of how to investigate speaking behaviours in more complex situations that share many features with real-world speaking contexts e.g. simultaneous engagement of speech perception and production processes, the presence of an interlocutor, and the need for inter-speaker coordination. The findings thus go beyond previous work that has typically studied solo speech production in isolation, and represent a significant advance in our understanding of speech as a social and communicative behaviour. It is further an impressive feat to develop a paradigm in which the degree of cooperativity of the synchronisation partner can be so tightly controlled; in this way, this study combines the benefits of using prerecorded stimuli (namely, the high degree of experimental control) with the benefits of using a live synchronisation partner (allowing the task to be truly two-way interactive, an important criticism of other work using pre-recorded stimuli). A further key strength of the study lies in its employment of stereotactic EEG to measure brain responses with both high temporal and spatial resolution, an ideal method for studying the unfolding relationship between neural processing and this dynamic coordination behaviour.

We sincerely appreciate the Reviewer's thoughtful and positive feedback on our manuscript.

Weaknesses:

One major limitation of the current study is the lack of coverage of the right hemisphere by the implanted electrodes. Of course, electrode location is solely clinically motivated, and so the authors did not have control over this. However, this means that the current study neglects the potentially important role of the right hemisphere in this task. The right hemisphere has previously been proposed to support feedback control for speech (likely a core process engaged by synchronous speech), as opposed to the left hemisphere which has been argued to underlie feedforward control (Tourville & Guenther, 2011). Indeed, a previous fMRI study of synchronous speech reported the engagement of a network of right hemisphere regions, including STG, IPL, IFG, and the temporal pole (Jasmin et al., 2016). Further, the release from speech-induced suppression during a synchronous speech reported by Jasmin et al. was found in the right temporal pole, which may explain the discrepancy with the current finding of reduced leftward high-frequency activity with increasing verbal coordination (suggesting instead increased speech-induced suppression for successful synchronisation). The findings should therefore be interpreted with the caveat that they are limited to the left hemisphere, and are thus likely missing an important aspect of the neural processing underpinning verbal coordination behaviour.

We have now included, in the supplementary materials, data from the right hemisphere, although the coverage is a bit sparse (Figures S2, S4, S5, see our responses in the ‘Recommendation for the authors’ section, below). We have also revised the Discussion section to add the putative role of right temporal regions (see below as well).

A further limitation of this study is that its findings are purely correlational in nature; that is, the results tell us how neural activity correlates with behaviour, but not whether it is instrumental in that behaviour. Elucidating the latter would require some form of intervention such as electrode stimulation, to disrupt activity in a brain area and measure the resulting effect on behaviour. Any claims therefore as to the specific role of brain areas in verbal coordination (e.g. the role of the IFG in supporting online coordinative adjustments to achieve synchronisation) are therefore speculative.

We appreciate the reviewer’s observation regarding the correlational nature of our findings and agree that this is a common limitation of neuroimaging studies. While elucidating causal relationships would indeed require intervention techniques such as electrical stimulation, our study leverages the unique advantages of intracerebral recordings, offering the best available spatial and temporal resolution alongside a high signal-tonoise ratio. These attributes ensure that our data accurately reflect neural activity and its temporal dynamics, providing a robust foundation for understanding the relationship between neural processes and behaviour. Therefore, while causal claims are beyond the scope of this study, the precision of our methodology allows us to make well-supported observations about the neural correlates of synchronous speech tasks.

Recommendations for the authors:

Reviewing Editor Comment:

After joint consultation, we are seeing the potential for the report to be strengthened and the evidence here to be deemed ultimately at least 'solid': to us (editors and reviewers) it seems that this would require both (1) clarifying/acknowledging the limitations of not having right hemisphere data, and (2) running some of the additional analyses the reviewers suggest, which should allow for richer examination of the data e.g. phase relationships in areas that correlate with synchronisation.

We have now added data on the right hemisphere (RH) that we did not previously report due to a rather sparse sampling of the RH. These results are now reported in the Results section as well as in the Supplementary section, where we put all right hemisphere figures for all analyses (Figure S2, S4, S5). We have also run additional analyses digging into the phase relationship in areas that correlate with synchronisation (Figure S6). These additional analyses allowed us to improve the Discussion section as well.

Reviewer #1 (Recommendations For The Authors):

In some sections, the writing is a bit unclear, with both typos and vague statements that could be fixed with careful proofreading.

We thank the reviewer for pointing out areas where the writing could be improved. We carefully proofread the manuscript to address typos and clarify any vague statements. Specific sections identified as unclear have been rephrased for better precision and readability.

In Figure 1, the colors repeat, making it impossible to tell patients apart.

We have now updated Figure 1 colormap to avoid redundancy and added the right hemisphere.

Line 132: "16 unilateral implantations (9 left, 7 bilateral implantations)". Should this say 7 right hemisphere? If so, the following sentence stating that there was "insufficient cover [sic] of the right hemisphere" is unclear, since the number of patients between LH and RH is similar.

The confusion was due to the fact that the lateralization refers to the presence/absence of electrodes in the Heschl’s gyrus (left : H’ ; right : H) exclusively.

We have thus changed this section as follows:

“16 patients (7 women, mean age 29.8 y, range 17 - 50 y) with pharmacoresistant epilepsy took part in the study. They were included if their implantation map covered at least partially the Heschl's gyrus and had sufficiently intact diction to support relatively sustained language production.” The relevant part (previously line 132) now states:

“Sixteen patients with a total of 236 electrodes (145 in the left hemisphere) and 2395 contacts (1459 in the left hemisphere, see Figure 1). While this gives a rather sparse coverage of the right hemisphere, we decided, due to the rarity of this type of data, to report results for both hemispheres, with figures for the left hemisphere in the main text and figures for the right hemisphere in the supplementary section.”

Reviewer #2 (Recommendations For The Authors):

(1) To address the concern regarding the absence of data from the right hemisphere, I would advise the authors to directly acknowledge this limitation in their Discussion section, citing relevant work suggesting that the right hemisphere has an important role to play in this task (e.g. Jasmin et al., 2016). You should also make this clear in your abstract e.g. you could rewrite the sentence in line 40 to be: "Then, we recorded the intracranial brain activity of the left hemisphere in 16 patients with drug-resistant epilepsy...".

We are grateful to the reviewer for this comment that incited us to look into the right hemisphere data. We have now included results in the right hemisphere, although the coverage is a bit sparse. We have also revised the Discussion section to add the putative role of right temporal regions. Interestingly, our results show, as suggested by the reviewer, a clear involvement of the RH in this task.

First, the full brain analyses show a very similar implication of the RH as compared to the LH (see Figure below). We have now added in the Results section:

“As expected, the whole language network is strongly involved, including both dorsal and ventral pathways (Fig 3A). More precisely, in the left temporal lobe the superior, middle and inferior temporal gyri, in the left parietal lobe the inferior parietal lobule (IPL) and in the left frontal lobe the inferior frontal gyrus (IFG) and the middle frontal gyrus (MFG). Similar results are observed in the right hemisphere, neural responses being present across all six frequency bands with medium to large modulation in activity compared to baseline (Figure S2A) in the same regions. Desynchronizations are present in the theta, alpha and beta bands while the low gamma and HFa bands show power increases.”

As to compared to the left hemisphere, assessing brain-behaviour correlations in the right hemisphere does not provide the same statistical power, because some anatomical regions have very few electrodes. Nonetheless, we observe a strong correlation in the right IFG, similar to the one we previously reported in the left hemisphere, and we now report in the Results section:

“The decrease in HFa along the dorsal pathway is replicated in the right hemisphere (Figure S4). However, while both the right STG BA41/42 and STG BA22 present a power increase (compared to baseline) — with a stronger increase for the STG BA41/42 — neither shows a significant correlation with verbal coordination (t(45)=-1.65, p=.1 ; t(8)=-0.67, p=.5 ; Student’s T test, FDR correction). By contrast, results in the right IFG BA44 are similar to the one observed in the left hemisphere with a significant power increase associated with a negative brainbehaviour correlation (t(17) = -3.11, p = .01 ; Student’s T test, FDR correction).”

Interestingly, the phase-amplitude coupling analysis yields very similar results in both hemispheres (exception made for BA22). We have thus updated the Results section as follows:

“Notably, when comparing – within the regions of interest previously described – the PAC with the virtual partner speech and the PAC with the phase difference, the coupling relationship changes when moving along the dorsal pathway: a stronger coupling in the auditory regions with the speech input, no difference between speech and coordination dynamics in the IPL and a stronger coupling for the coordinative dynamics compared to speech signal in the IFG (Figure 5B ). When looking at the right hemisphere, we observe the same changes in the coupling relationship when moving along the dorsal pathway, except that no difference between speech and coordination dynamics is present in the right secondary auditory regions (STG BA22; Figure S5).”

We also included in the Discussion section the right hemisphere results also mentioning previous work of Guenther and the one of Jasmin. On the section “Left secondary auditory regions are more sensitive to coordinative behaviour” one can read:

“Furthermore, the absence of correlation in the right STG BA22 (Figure S4) seems in first stance to challenge influential speech production models (e.g. Guenther & Hickok, 2016) that propose that the right hemisphere is involved in feedback control. However, one needs to consider the the task at stake heavily relied upon temporal mismatches and adjustments. In this context, the left-lateralized sensitivity to verbal coordination reminds of the works of Floegel and colleagues (2020, 2023) suggesting that both hemispheres are involved depending on the type of error: the right auditory association cortex monitoring preferentially spectral speech features and the left auditory association cortex monitoring preferentially temporal speech features. Nonetheless, the right temporal pole seems to be sensitive to speech coordinative behaviour, confirming previous findings using fMRI (Jasmin et al., 2016) and thus showing that the right hemisphere has an important role to play in this type of tasks (e.g. Jasmin et al., 2016).”

References cited:

– Floegel, M., Fuchs, S., & Kell, C. A. (2020). Differential contributions of the two cerebral hemispheres to temporal and spectral speech feedback control. Nature Communications, 11(1), 2839.

– Floegel, M., Kasper, J., Perrier, P., & Kell, C. A. (2023). How the conception of control influences our understanding of actions. Nature Reviews Neuroscience, 24(5), 313-329.

– Guenther, F. H., & Hickok, G. (2016). Neural models of motor speech control. In Neurobiology of language (pp. 725-740). Academic Press.

(2) When discussing previous work on alignment during synchronous speech, you may wish to include a recently published paper by Bradshaw et al (2024); this manipulated the acoustics of the accompanist's voice during a synchronous speech task to show interactions between speech motor adaptation and phonetic convergence/alignment.

We thank the reviewer for pointing to this recent and interesting paper. We added the article as reference as follows

“Furthermore, synchronous speech favors the emergence of alignment phenomena, for instance of the fundamental frequency or the syllable onset (Assaneo et al., 2019 ; Bradshaw & McGettigan, 2021 ; Bradshaw et al., 2023; Bradshaw et al., 2024).”

(3) Line 80: "Synchronous speech resembles to a certain extent to delayed auditory feedback tasks"- I think you mean "altered auditory feedback tasks" here.

In the case of synchronous speech it is more about timing than altered speech signals, that is why the comparison is done with delayed and not altered auditory feedback. Nonetheless, we understand the Reviewer’s point and we have now changed the sentence as follows:

“Synchronous speech resembles to a certain extent to delayed/altered auditory feedback tasks”

(4) When discussing superior temporal responses during such altered feedback tasks, you may also want to cite a review paper by Meekings and Scott (2021).

We thank the reviewer for this suggestion, indeed this was a big oversight!

The paper is now quoted in the introduction as follows:

“Previous studies have revealed increased responses in the superior temporal regions compared to normal feedback conditions (Hirano et al., 1997 ; Hashimoto & Sakai, 2003 ; Takaso et al., 2010 ; Ozerk et al., 2022 ; Floegel et al., 2020 ; see Meekings & Scott, 2021 for a review of error-monitoring and feedback control in the STG during speech production).”

Furthermore, we updated the discussion part concerning the speaker-induced suppression phenomenon (see below our response to the point 10).

(5) Line 125: "The parameters and sound adjustment were set using an external low-latency sound card (RME Babyface Pro Fs)". Can you please report the total feedback loop latency in your set-up? Or at the least cite the following paper which reports low latencies with this audio device.

Kim, K. S., Wang, H., & Max, L. (2020). It's About Time: Minimizing Hardware and Software Latencies in Speech Research With Real-Time Auditory Feedback. Journal of Speech, Language, and Hearing Research, 63(8), 25222534. https://doi.org/10.1044/2020_JSLHR-19-00419

We now report the total feedback loop latency (~5ms) and also cite the relevant paper (Kim et al., 2020).

(6) Line 127 "A calibration was made to find a comfortable volume and an optimal balance for both the sound of the participant's own voice, which was fed back through the headphones, and the sound of the stimuli." What do you mean here by an 'optimal balance'? Was the participant's own voice always louder than the VP stimuli? Can you report roughly what you consider to be a comfortable volume in dB?

This point was indeed unlcear. We have now changed as follows:

“A calibration was made to find a comfortable volume and an optimal balance for both the sound of the participant's own voice, which was fed back through the headphones, and the sound of the stimuli. The aim of this procedure was that the patient would subjectively perceive their voice and the VP-voice in equal measure. VP voice was delivered at approximately 70dB.”

(7) Relatedly, did you use any noise masking to mask the air-conducted feedback from their own voice (which would have been slightly out of phase with the feedback through the headphones, depending on your latency)?

Considering the low-latency condition allowed with the sound card (RME Babyface Pro Fs), we did not use noise masking to mask the air-conducted feedback from the self-voice of the patients.

(8) Line 141: "four short sentences were pre-recorded by a woman and a man." Did all participants synchronise with both the man and woman or was the VP gender matched to that of the participant/patient?

We thank the reviewer for this important missing detail. We know changed the text as follows:

“Four stimuli corresponding to four short sentences were pre-recorded by both a female and a male speaker. This allowed to adapt to the natural gender differences in fundamental frequency (i.e. so that the VP gender matched that of the patients). All stimuli were normalised in amplitude.”

(9) Can you clarify what instructions participants were given regarding the VP? That is, were they told that this was a recording or a real live speaker? Were they naïve to the manipulation of the VP's coupling to the participant?

We have now added this information to the task description as follows:

“Participants, comfortably seated in a medical chair, were instructed that they would perform a real-time interactive synchronous speech task with an artificial agent (Virtual Partner, henceforth VP, see next section) that can modulate and adapt to the participant’s speech in real time.”

“The third step was the actual experiment. This was identical to the training but consisted of 24 trials (14s long, speech rate ~3Hz, yielding ~1000 syllables). Importantly, the VP varied its coupling behaviour to the participant. More precisely, for a third of the sequences the VP had a neutral behaviour (close to zero coupling : k = +/- 0.01). For a third it had a moderate coupling, meaning that the VP synchronised more to the participant speech (k = - 0.09). And for the last third of the sequences the VP had a moderate coupling but with a phase shift of pi/2, meaning that it moderately aimed to speak in between the participant syllables (k = + 0.09). The coupling values were empirically determined on the basis of a pilot experiment in order to induce more or less synchronization, but keeping the phase-shifted coupling at a rather implicit level. In other terms, while participants knew that the VP would adapt, they did not necessarily know in which direction the coupling went.”  

(10) The paragraph from line 438 entitled "Secondary auditory regions are more sensitive to coordinative behaviour" includes an interesting discussion of the relation of the current findings to the phenomenon of speech-induced suppression (SIS). However, the authors appear to equate the observed decrease in highfrequency activity as speech coordination increases with the phenomenon of SIS (in lines 456-457), which is quite a speculative leap. I would encourage the authors to temper this discussion by referring to SIS as a potentially related phenomenon, with a need for more experimental work to determine if this is indeed the same phenomenon as the decreases in high-frequency power observed here. I believe that the authors are arguing here for an interpretation of SIS as reflecting internal modelling of sensory input regardless of whether this is self-generated or other-generated; if this is indeed the case, I would ask the authors to be more explicit here that these ideas are not a standard part of the traditional account of SIS, which only includes internal modelling of self-produced sensory feedback.

As stated in the public review, we thank both reviewers for raising thoughtful concerns about our interpretation of the observed neural suppression as related to speaker-induced suppression (SIS). We agree that our study lacks a passive listening condition, which limits direct comparisons to the original SIS effect, traditionally defined as the suppression of neural responses to self-produced speech compared to externally-generated speech (Meekings & Scott, 2021).

In response, we have reconsidered our terminology and interpretation. In the revised discussion, we refer to our findings as a "SIS-related phenomenon specific to the synchronous speech context." Unlike classic SIS paradigms, our interactive task involves simultaneous monitoring of self- and externally-generated speech, introducing additional attentional and coordinative demands.

The revised discussion also incorporates findings by Ozker et al. (2024, 2022), which link SIS and speech monitoring, suggesting that suppressing responses to self-generated speech facilitates error detection. We propose that the decrease in high-frequency activity (HFa) as verbal coordination increases reflects reduced error signals due to closer alignment between perceived and produced speech. Conversely, HFa increases with reduced coordination may signify greater prediction error.

Additionally, we relate our findings to the "rubber voice" effect (Zheng et al., 2011; Lind et al., 2014; Franken et al., 2021), where temporally and phonetically congruent external speech can be perceived as self-generated. We speculate that this may occur in synchronous speech tasks when the participant's and VP's speech signals closely align. However, this interpretation remains speculative, as no subjective reports were collected to confirm this perception. Future studies could include participant questionnaires to validate this effect and relate subjective experience to neural measures of synchronization.

Overall, our findings extend the study of SIS to dynamic, interactive contexts and contribute to understanding internal forward models of speech production in more naturalistic scenarios.

We have now added these points to the discussion as follows:

“The observed negative correlation between verbal coordination and high-frequency activity (HFa) in STG BA22 suggests a suppression of neural responses as the degree of synchrony increases. This result aligns with findings on speaker-induced suppression (SIS), where neural activity in auditory cortex decreases during self-generated speech compared to externally-generated speech (Meekings & Scott, 2021; Niziolek et al., 2013). However, our paradigm differs from traditional SIS studies in two critical ways: (1) the speaker's own voice is always present and predictable from the forward model, and (2) no passive listening condition was included. Therefore, our findings cannot be directly equated with the original SIS effect.

Instead, we propose that the suppression observed here reflects a SIS-related phenomenon specific to the synchronous speech context. Synchronous speech requires simultaneous monitoring of self- and externally generated speech, a task that is both attentionally demanding and coordinative. This aligns with evidence from Ozker et al. (2024, 2022), showing that the same neural populations in STG exhibit SIS and heightened responses to feedback perturbations. These findings suggest that SIS and speech monitoring are related processes, where suppressing responses to self-generated speech facilitates error detection.

In our study, suppression of HFa as coordination increases may reflect reduced prediction errors due to closer alignment between perceived and produced speech signals. Conversely, increased HFa during poor coordination may signify greater mismatch, consistent with prediction error theories (Houde & Nagarajan, 2011; Friston et al., 2020).”

(11) Within this section, you also speculate in line 460 that "Moreover, when the two speech signals come close enough in time, the patient possibly perceives them as its own voice." I would recommend citing studies on the 'rubber voice' effect to back up this claim (e.g. Franken et al., 2021; Lind et al., 2014; Zheng et al., 2011).

We are grateful to the Reviewer for this interesting suggestion. Directly following the previous comment, the section now states:

“Furthermore, when self- and externally-generated speech signals are temporally and phonetically congruent, participants may perceive external speech as their own. This echoes the "rubber voice" effect, where external speech resembling self-produced feedback is perceived as self-generated (Zheng et al., 2011; Lind et al., 2014; Franken et al., 2021). While this interpretation remains speculative, future studies could incorporate subjective reports to investigate this phenomenon in more detail.”

(12) As noted in my public review, since your methods are correlational, you need to be careful about inferring the causal role of any brain areas in supporting a specific aspect of functioning e.g. line 501-504: "By contrast, in the inferior frontal gyrus, the coupling in the high-frequency activity is strongest with the input-output phase difference (input of the VP - output of the speaker), a metric that reflects the amount of error in the internal computation to reach optimal coordination, which indicates that this region optimises the predictive and coordinative behaviour required by the task." I would argue that the latter part of this sentence is a conclusion that, although consistent with, goes beyond the current data in this study, and thus needs tempering.

We agree with the Reviewer and changed the sentence as follows:

“By contrast, in the inferior frontal gyrus, the coupling in the high-frequency activity is strongest with the inputoutput phase difference (input of the VP - output of the speaker), a metric that could possibly reflect the amount of error in the internal computation to reach optimal coordination. This indicates that this region could have an implication in the optimisation of the predictive and coordinative behaviour required by the task.”

Author response:

The following is the authors’ response to the original reviews

Recommendations For The Authors:

Reviewer #1 (Recommendations For The Authors): 

Recommendations  Analysis: 

(1) Given that a MER21B/C LTR was not immediately identified at the start site of the Liz lncRNA in the mouse, and its match is only 46%, this raises the question of whether an analogous LTR would be identified at the homologous location in other species on deeper analysis. The authors need to argue that what has been conserved in the LTR alone in mouse is the essential element conferring the ability to initiate transcription of Liz. A transient reporter assay might be sufficient to do this. 

We believe that the 46% identity between the first exon of mouse Liz and the consensus sequence of MER21C is so weak that its traces as MER21C are too attenuated to be detected by standard in silico analyses, such as homology searches. For instance, when pairwise alignments are performed between the first exon of mouse Liz and the consensus sequences of solo-LTRs other than MER21C, MER21C does not emerge as the most similar sequence (Figure 5 – figure supplement 1). This is in stark contrast to similar analyses involving the first exon of human and rabbit GPR1AS (which overlaps with MER21C), where MER21C is identified as the most similar sequence. [pages: 26, 31-32]

The positions of these LTRs were initially annotated using RepeatMasker. To ensure robust analysis, we performed additional searches with RepeatMasker under more sensitive conditions, adjusting search engines (e.g., RMblast to HMMER or Cross-match) and sensitivity settings. Nevertheless, MER21C or closely related LTRs were still undetectable in mouse, rat, and hamster (Figure 4 – figure supplement 1). However, a multiple genome alignment generated by Cactus/UCSC revealed a syntenic region corresponding to the first exon of human GPR1-AS, overlapping with LTR21C, in the genomes of mice, as well as rats and hamsters (Figure 4 – figure supplement 2). Although RepeatMasker did not annotate MER21C at the GPR1 locus in these species, homologous regions were observed across all selected Euarchontoglires. Due to the limitations of the Cactus alignment track in delineating precise homologous boundaries across species, extracting sequences for evolutionary tree construction was not feasible. Nevertheless, these findings support the hypothesis that the first exon of GPR1-AS (Liz in mice) originated from a MER21C insertion in the common ancestor of Euarchontoglires. [pages: 21, 24-25]

A combination of traditional annotation of repetitive elements using RepeatMasker and the reconstruction of ancestral genomes through multiple genome alignment can reveal highly degenerated LTR relics. This approach is likely to point to significant future directions for research. This point is further elaborated in the discussion section. [page 42]

Furthermore, in response to the reviewer's suggestion, we investigated the promoter activity of the GPR1-AS and Liz first exons, which are hypothesized to have originated from the same MER21C insertion. Using a dual reporter assay, we demonstrated that the first exon of mouse Liz exhibits promoter activity in a human cell line comparable to that of the human GPR1-AS promoter. Thus, despite the relatively low sequence similarity between the Liz first exon and the MER21C consensus sequence (46% as determined by pairwise alignment, Figure 5 – figure supplement 2), the promoter activity remains functionally conserved. We further discuss the potential functional motifs within the putative MER21C LTR-derived sequences in Figure 4B-D. Taken together, these findings suggest that despite a high level of degeneracy of the promoter region in rodents, including mice, the most parsimonious explanation for the origin of this regulatory element in rodents is the presence of the same LTR relic detectable in humans/primates, which is essential for robust transcription initiation of Liz and GPR1-AS, respectively. [pages: 27, 32]

(2) Imprinting will depend on an initiating mechanism in the germline, in addition to events in the embryo that induce the secondary DMR at ZDBF2. The authors should therefore examine as far as possible the presence of a gDMR in the species with/without GPR1-AS1 and ZDBF2 imprinting. Whole-genome bisulphite sequencing data from oocytes and sperm should exist for some of the relevant species (e.g., pig, cow: Ivanova et al. 2020 PMID: 32393379; Lu et al. 2012 PMID: 34818044). 

As the reviewer noted, the presence of a gDMR is essential for the establishment of imprinting. Following another reviewer's suggestion, we have now demonstrated that the ZDBF2 gene in rhesus monkeys is also subject to imprinting (see Figure 3C-D). We also acquired whole genome bisulfite sequencing data for rhesus monkey sperm and oocytes, identified DMRs between them, and discovered an oocyte-specifically methylated gDMR in the first exon of GPR1-AS (which overlaps with MER21C)(Figure 3 – figure supplement 1A). This finding is consistent with observations in humans and mice. Conversely, we obtained similar sequencing data for porcine and bovine sperm and oocytes and conducted the same analysis (Figure 3 – figure supplement 1A,B). However, we did not detect any oocyte-specific methylated gDMRs in the GPR1 intragenic region (where GPR1AS is transcribed from an intron of GPR1) in these species of the Laurasiatheria superorder. These results support the hypothesis that ZDBF2 is not imprinted in lineages outside the Euarchontoglires, the superorder which includes both rodents and primates. We have included these important DMR results as a supplement to Figure 3. [pages 16-21]

Presentation: 

(1) The first section of the Introduction would benefit from the inclusion of some additional general references on genomic imprinting. 

We have added two review articles, Tucci et al. (2019) and Kobayashi (2021), as references in the first section of the Introduction. [page 5]

(2) Introduction statement: "....nearly 200 imprinted genes have been identified in mice and humans. However, less than half of these genes overlapped in both species." This was the conclusion of one study (Tucci et al. 2016), so it would be better to provide a caveat to the statement "However, one comparative analysis suggested that fewer than half of these genes overlapped in both species". 

The point being that the actual number of imprinted genes is still a matter of debate (see Edwards et al. 2023 PMID: 36916665), and the extent of overlap will depend on the strength of the evidence for each gene in the human and mouse imprinted gene lists. So, it is very difficult to put an accurate figure on the extent of overlap - but the authors' point is valid that there are species- or lineage-specific imprinted genes. 

We have revised this sentence following reviewer #1's suggestion. [page 5]

(3) Introduction statement: "The establishment of species-specific imprinting.....can be driven by various evolutionary events, including.....differences in the function of DNA methyltransferases". I am not aware that this has been described as an evolutionary event causing species-specific imprinting - without supporting evidence, I recommend to remove this suggestion. 

We thank the reviewer for this comment and realize that we should have been more explicit here. We were referring to DNMT3C, a rodent-specific member of the DNMT3 family, which is responsible for the paternal methylation imprinting of Rasgrf1 in mice (Barau et al., Science, 2016), in association with the piRNA pathway and targeting of a specific retrotransposon within the DMR (Watanabe et al. Science, 2011). The Rasgrf1 gene is imprinted in mice but not considered imprinted in humans (though some conflicting data exist). While it is likely that the emergence of DNMT3C was a pre-requisite to the establishment of Rasgrf1 imprinting in evolutionary terms, clear evidence is lacking. Following the reviewer’s suggestion, we have removed the phrase "differences in the function of DNA methyltransferases" from the text. However, we have reintroduced this point in the Introduction section as a potential mechanism that may contribute to the establishment of species-specific imprinted genes, alongside the roles of ZNF445 and ZFP57, which regulate the maintenance of imprinting with partially divided roles between humans and mice. [page 6]

(4) It would be very useful for readers to have a schema of the Gpr1/Zdbf2 locus that indicates the locations of the germline and somatic DMRs and their relationship to the Liz transcript. 

(5) There is a summary figure amongst the Supplementary Figures (Suppl. Fig. 7) - it would be beneficial to readers to have this summary figure in the main text rather than the supplement. 

Following reviewer #1’s suggestion, we have moved the regulatory system schema at the Gpr1/Zdbf2 locus, originally shown in Supplementary Figure 7, to the main text as Figure 7. In addition, in response to comment 4, we have revised the figure to explicitly depict the relationship between the Liz transcript and the establishment of the somatic DMR (sDMR), enhancing the clarity of the regulatory interactions at this locus. [page 38]

(6) With a focus of the study on LTRs as cis-regulatory elements having been co-opted in genomic imprinting mechanisms - whether in the female germline (as in Bogutz et al. 2019) or in the current study as an activating element post-fertilisation - it is a real omission that the authors do not to refer to the role of tissue-specific LTRs as the candidate regulatory elements in non-canonical imprinting (see Hanna et al. 2019 PMID: 31665063). Please include in Introduction and/or Discussion. 

We added a sentence explaining canonical and non-canonical imprinting and the cases where LTRs act as regulatory elements in non-canonical imprinting, with reference to the study of Hanna et al., as suggested. [page 6]

(7) Discussion statement: "Two paternally expressed imprinted genes, PEG10/SIRH1 and PEG11/RTL1/SIRH2 have been identified in mammals. They encode GAG-POL proteins of sushi-ichi LTR retrotransposons and are essential for mammalian placenta formation and maintenance." 

These sentences should be combined: "Two paternally expressed imprinted genes, PEG10/SIRH1, and PEG11/RTL1/SIRH2, that encode GAG-POL proteins of sushi-ichi LTR retrotransposons have been identified in mammals and are essential for mammalian placenta formation and maintenance." 

We have revised this sentence according to reviewer #1's suggestion. [page 41]

Reviewer #2 (Recommendations For The Authors): 

When showing assembled GPR1-AS transcripts via genome browser tracks, it would be valuable to add normalized counts of reads mapping to each strand, in order to more convincingly demonstrate the existence of these transcripts. I ask for this because in my experience Stringtie will assemble transcripts that are only marginally supported by reads. 

In response to Reviewer #2's suggestion, FPKM and TPM values for all StringTiepredicted GPR1-AS-like transcripts are now included in Figure 6. Each of these transcripts has a TPM value greater than 1, supporting their validity. [pages: 35]

Reviewer #3 (Recommendations For The Authors): 

(1) The tree in Figure 5A is one of the main arguments supporting the divergence of the mouse Liz promoter from a common MER21C element, but this contains only a handful of species, making it difficult to appreciate the full extent of its evolution. Presumably its faster mutation rate in mouse would also be supported by other closely related rodents, which would solidify the conclusion that the Liz promoter is derived from an ancient MER21C insertion. So my suggestion is to expand this tree substantially to other species, comparing sequences syntenic to the GPR1-AS/Liz promoter. 

(2) It may also be worth trying different TE/LTR annotation tools and/or running Repeatmasker with different parameters, to see if an MER21C element is detected in mouse using a more sensitive approach. 

In response to this suggestion, we performed computational analyses with RepeatMasker under various settings (e.g., switching search engines from RMblast to HMMER or Crossmatch, adjusting speed/sensitivity settings from default to slow). Despite these modifications, a MER21C element was not detected near the mouse Liz promoter. However, a multiple genome alignment track generated by Cactus/UCSC revealed a syntenic region, corresponding to the first exon of human GPR1-AS, which overlaps with LTR21C, also present in the genomes of mouse, rat, and hamster (Figure 4 – figure supplement 1). While RepeatMasker did not identify MER21C at the GPR1 locus in these species, homologous regions were observed across all selected Euarchontoglires. Although the Cactus alignment track does not delineate the exact boundaries of homologous regions across species (relative to humans) and thus precludes extracting each homologous sequence to construct an evolutionary tree, these findings support the hypothesis that the first exon of GPR1-AS (referred to as Liz in mice) originated from an ancient MER21C insertion in the common ancestor of Euarchontoglires. [pages: 21, 24-25]

(3) According to Dfam, MER21C is not common to all eutherians, but specific to Boroeutheria, whilst MER21B is presumably specific to Euarchontoglires. To clarify MER21C/B evolution, it would be useful to show the number of elements present in select species from each group (including an outgroup). 

(7) In Figure 4 it is hard to distinguish between red and purple. 

Initially, we referenced Repbase (e.g., MER21C: Origin/Eutheria), but, as Reviewer #3 noted, Dfam should be the primary reference. We have now included the copy numbers of MER21C and MER21B for each genome in Figure 4, providing a clearer understanding of their evolutionary appearance (MER21C appears specific to Boroeutheria, while MER21B is specific to Euarchontoglires). Additionally, we adjusted the MER21B position color from purple to dark purple to improve visibility. Furthermore, we have also underlined the copy number of MER21C or MER21B located within the GPR1 region in each species. For example, in the Treeshrew genome, the LTR overlapping with GPR1-AS is annotated as MER21B, so we underlined the copy number of MER21B (2,305). These changes now clearly indicate whether homologous sequences to the first exon of GPR1-AS are annotated as MER21C or MER21B in each genome. [page 22]

(4) Could the imprinting status of ZDBF2 not be determined in chimpanzees and rabbits? Or is it already known? Either way, a clarification would be useful to further support the concordance between GPR1-AS-like transcripts and ZDBF2 imprinting.

The imprinting status of ZDBF2 had not previously been reported in chimpanzees, rhesus macaques, or rabbits, where GPR1-AS-like transcripts were identified. Therefore, we conducted allele-specific expression analysis of ZDBF2 using blood samples from rhesus macaques and rabbits. As expected, paternal-allele-specific expression of ZDBF2 was observed in both species, consistent with findings in humans and mice. These results have been added to Figure 3. Although we did not analyze the imprinting status in chimpanzees, we believe the existing data sufficiently support our hypothesis. [pages: 16, 19-20]

(5) The authors briefly discuss the role of KRAB-ZFPs in controlling TE expression. An interesting addition would be to analyse the expression of the main KRAB-ZFP that binds to MER21C (ZFP789, according to data from PMID 28273063). This could be linked to the temporal control of MER21C expression. 

In response to Reviewer #3's suggestion, we focused on the expression pattern of ZNF789 (noted by the reviewer as ZFP789), the primary KRAB-ZFP known to bind MER21C, as identified by Didier Trono’s group (PMID 28273063). Strikingly, our analysis reveals that ZNF789 is specifically downregulated at the 4-cell stage, which aligns with the timing of MER21C reactivation. While it remains to be determined whether this downregulation directly influences MER21C reactivation or the initiation of GPR1-AS expression, this finding is significant and consistent with our model. We have incorporated this information in Figure 5 – figure supplement 3. [pages: 33]

(6) The sentence "Liz directs DNA methylation at the somatic DMR, which competes with ZDBF2 to repress the paternal allele" (introduction) was confusing to me. 

This sentence has been revised to be more accurate as follows; Liz transcription counteracts the H3K27me3-mediated repression of Zdbf2 by promoting the deposition of antagonistic DNA methylation at the secondary DMR. [page 7]

(8) In Figure 5 I take it that 'consensus motif' refers to ELF1/2? Maybe change the legend. 

To clarify potential confusion around the term 'consensus motif,' which may have been mistaken for 'consensus MER21C' (the consensus sequence of MER21C-LTR from the Dfam database), we have revised the figure legend. We now refer to the motif as the "common motif," indicating the sequence common to all MER21C-derived sequences and overlapping with the first exon of GPR1-AS. [page 29]

Author response:

The following is the authors’ response to the previous reviews

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Glaser et al present ExA-SPIM, a light-sheet microscope platform with large volumetric coverage (Field of view 85mm^2, working distance 35mm), designed to image expanded mouse brains in their entirety. The authors also present an expansion method optimized for whole mouse brains and an acquisition software suite. The microscope is employed in imaging an expanded mouse brain, the macaque motor cortex, and human brain slices of white matter. 

This is impressive work and represents a leap over existing light-sheet microscopes. As an example, it offers a fivefold higher resolution than mesoSPIM (https://mesospim.org/), a popular platform for imaging large cleared samples. Thus while this work is rooted in optical engineering, it manifests a huge step forward and has the potential to become an important tool in the neurosciences. 

Strengths: 

- ExA-SPIM features an exceptional combination of field of view, working distance, resolution, and throughput. 

- An expanded mouse brain can be acquired with only 15 tiles, lowering the burden on computational stitching. That the brain does not need to be mechanically sectioned is also seen as an important capability. 

- The image data is compelling, and tracing of neurons has been performed. This demonstrates the potential of the microscope platform. 

Weaknesses: 

- There is a general question about the scaling laws of lenses, and expansion microscopy, which in my opinion remained unanswered: In the context of whole brain imaging, a larger expansion factor requires a microscope system with larger volumetric coverage, which in turn will have lower resolution (Figure 1B). So what is optimal? Could one alternatively image a cleared (non-expanded) brain with a high-resolution ASLM system (Chakraborty, Tonmoy, Nature Methods 2019, potentially upgraded with custom objectives) and get a similar effective resolution as the authors get with expansion? This is not meant to diminish the achievement, but it was unclear if the gains in resolution from the expansion factor are traded off by the scaling laws of current optical systems. 

Paraphrasing the reviewer: Expanding the tissue requires imaging larger volumes and allows lower optical resolution. What has been gained?

The answer to the reviewer’s question is nuanced and contains four parts. 

First, optical engineering requirements are more forgiving for lenses with lower resolution. Lower resolution lenses can have much larger fields of view (in real terms: the number of resolvable elements, proportional to ‘etendue’) and much longer working distances. In other words, it is currently more feasible to engineer lower resolution lenses with larger volumetric coverage, even when accounting for the expansion factor. 

Second, these lenses are also much better corrected compared to higher resolution (NA) lenses. They have a flat field of view, negligible pincushion distortions, and constant resolution across the field of view. We are not aware of comparable performance for high NA objectives, even when correcting for expansion.

Third, although clearing and expansion render tissues ‘transparent’, there still exist refractive index inhomogeneities which deteriorate image quality, especially at larger imaging depths. These effects are more severe for higher optical resolutions (NA), because the rays entering the objective at higher angles have longer paths in the tissue and will see more aberrations. For lower NA systems, such as ExaSPIM, the differences in paths between the extreme and axial rays are relatively small and image formation is less sensitive to aberrations. 

Fourth, aberrations are proportional to the index of refraction inhomogeneities (dn/dx). Since the index of refraction is roughly proportional to density, scattering and aberration of light decreases as M^3, where M is the expansion factor. In contrast, the imaging path length through the tissue only increases as M. This produces a huge win for imaging larger samples with lower resolutions. 

To our knowledge there are no convincing demonstrations in the literature of diffraction-limited ASLM imaging at a depth of 1 cm in cleared mouse brain tissue, which would be equivalent to the ExA-SPIM imaging results presented in this manuscript.  

In the discussion of the revised manuscript we discuss these factors in more depth. 

- It was unclear if 300 nm lateral and 800 nm axial resolution is enough for many questions in neuroscience. Segmenting spines, distinguishing pre- and postsynaptic densities, or tracing densely labeled neurons might be challenging. A discussion about the necessary resolution levels in neuroscience would be appreciated. 

We have previously shown good results in tracing the thinnest (100 nm thick) axons over cm scales with 1.5 um axial resolution. It is the contrast (SNR) that matters, and the ExaSPIM contrast exceeds the block-face 2-photon contrast, not to mention imaging speed (> 10x).  

Indeed, for some questions, like distinguishing fluorescence in pre- and postsynaptic structures, higher resolutions will be required (0.2 um isotropic; Rah et al Frontiers Neurosci, 2013). This could be achieved with higher expansion factors.

This is not within the intended scope of the current manuscript. As mentioned in the discussion section, we are working towards ExA-SPIM-based concepts to achieve better resolution through the design and fabrication of a customized imaging lens that maintains a high volumetric coverage with increased numerical aperture.  

- Would it be possible to characterize the aberrations that might be still present after whole brain expansion? One approach could be to image small fluorescent nanospheres behind the expanded brain and recover the pupil function via phase retrieval. But even full width half maximum (FWHM) measurements of the nanospheres' images would give some idea of the magnitude of the aberrations. 

We now included a supplementary figure highlighting images of small axon segments within distal regions of the brain.  

Reviewer #2 (Public Review): 

Summary: 

In this manuscript, Glaser et al. describe a new selective plane illumination microscope designed to image a large field of view that is optimized for expanded and cleared tissue samples. For the most part, the microscope design follows a standard formula that is common among many systems (e.g. Keller PJ et al Science 2008, Pitrone PG et al. Nature Methods 2013, Dean KM et al. Biophys J 2015, and Voigt FF et al. Nature Methods 2019). The primary conceptual and technical novelty is to use a detection objective from the metrology industry that has a large field of view and a large area camera. The authors characterize the system resolution, field curvature, and chromatic focal shift by measuring fluorescent beads in a hydrogel and then show example images of expanded samples from mouse, macaque, and human brain tissue. 

Strengths: 

I commend the authors for making all of the documentation, models, and acquisition software openly accessible and believe that this will help assist others who would like to replicate the instrument. I anticipate that the protocols for imaging large expanded tissues (such as an entire mouse brain) will also be useful to the community. 

Weaknesses: 

The characterization of the instrument needs to be improved to validate the claims. If the manuscript claims that the instrument allows for robust automated neuronal tracing, then this should be included in the data. 

The reviewer raises a valid concern. Our assertion that the resolution and contrast is sufficient for robust automated neuronal tracing is overstated based on the data in the paper. We are hard at work on automated tracing of datasets from the ExA-SPIM microscope. We have demonstrated full reconstruction of axonal arbors encompassing >20 cm of axonal length.  But including these methods and results is out of the scope of the current manuscript. 

The claims of robust automated neuronal tracing have been appropriately modified.  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Smaller questions to the authors: 

- Would a multi-directional illumination and detection architecture help? Was there a particular reason the authors did not go that route?

Despite the clarity of the expanded tissue, and the lower numerical aperture of the ExA-SPIM microscope, image quality still degrades slightly towards the distal regions of the brain relative to both the excitation and detection objective. Therefore, multi-directional illumination and detection would be advantageous. Since the initial submission of the manuscript, we have undertaken re-designing the optics and mechanics of the system. This includes provisions for multi-directional illumination and detection. However, this new design is beyond the scope of this manuscript. We now mention this in L254-255 of the Discussion section.

- Why did the authors not use the same objective for illumination and detection, which would allow isotropic resolution in ASLM? 

The current implementation of ASLM requires an infinity corrected objective (i.e. conjugating the axial sweeping mechanism to the back focal plane). This is not possible due to the finite conjugate design of the ExA-SPIM detection lens.

More fundamentally, pushing the excitation NA higher would result in a shorter light sheet Rayleigh length, which would require a smaller detection slit (shorter exposure time, lower signal to noise ratio). For our purposes an excitation NA of 0.1 is an excellent compromise between axial resolution, signal to noise ratio, and imaging speed. 

For other potentially brighter biological structures, it may be possible to design a custom infinity corrected objective that enables ASLM with NA > 0.1.

- Have the authors made any attempt to characterize distortions of the brain tissue that can occur due to expansion? 

We have not systematically characterized the distortions of the brain tissue pre and post expansion. Imaged mouse brain volumes are registered to the Allen CCF regardless of whether or not the tissue was expanded. It is beyond the scope of this manuscript to include these results and processing methods, but we have confirmed that the ExA-SPIM mouse brain volumes contain only modest deformation that is easily accounted for during registration to the Allen CCF. 

- The authors state that a custom lens with NA 0.5-0.6 lens can be designed, featuring similar specifications. Is there a practical design? Wouldn't such a lens be more prone to Field curvature? 

This custom lens has already been designed and is currently being fabricated. The lens maintains a similar space bandwidth product as the current lens (increased numerical aperture but over a proportionally smaller field of view). Over the designed field of view, field curvature is <1 µm. However, including additional discussion or results of this customized lens is beyond the scope of this manuscript.

Reviewer #2 (Recommendations For The Authors): 

System characterization: 

- Please state what wavelength was used for the resolution measurements in Figure 2.

An excitation wavelength of 561 nm was used. This has been added to the manuscript text.

- The manuscript highlights that a key advance for the microscope is the ability to image over a very large 13 mm diameter field of view. Can the authors clarify why they chose to characterize resolution over an 8diameter mm field rather than the full area? 

The 13 mm diameter field of view refers to the diagonal of the 10.6 x 8.0 mm field of view. The results presented in Figure 1c are with respect to the horizontal x direction and vertical y direction. A note indicating that the 13 mm is with respect to the diagonal of the rectangular imaging field has been added to the manuscript text. The results were presented in this way to present the axial and lateral resolution as a function of y (the axial sweeping direction).

- The resolution estimates seem lower than I would expect for a 0.30 NA lens (which should be closer to ~850 nm for 515 nm emission). Could the authors clarify the discrepancy? Is this predicted by the Zemax model and due to using the lens in immersion media, related to sampling size on the camera, or something else? It would be helpful if the authors could overlay the expected diffraction-limited performance together with the plots in Figure 2C. 

As mentioned previously, the resolution measurements were performed with 561 nm excitation and an emission bandpass of ~573 – 616 nm (595 nm average). Based on this we would expect the full width half maximum resolution to be ~975 nm. The resolution is in fact limited by sampling on the camera. The 3.76 µm pixel size, combined with the 5.0X magnification results in a sampling of 752 nm. Based on the Nyquist the resolution is limited to ~1.5 µm. We have added clarifying statements to the text.

- I'm confused about the characterization of light sheet thickness and how it relates to the measured detection field curvature. The authors state that they "deliver a light sheet with NA = 0.10 which has a width of 12.5 mm (FWHM)." If we estimate that light fills the 0.10 NA, it should have a beam waist (2wo) of ~3 microns (assuming Gaussian beam approximations). Although field curvature is described as "minimal" in the text, it is still ~10-15 microns at the edge of the field for the emission bands for GFP and RFP proteins. Given that this is 5X larger than the light sheet thickness, how do the authors deal with this? 

The generated light sheet is flat, with a thickness of ~ 3 µm. This flat light sheet will be captured in focus over the depth of focus of the detection objective. The stated field curvature is within 2.5X the depth of focus of the detection lens, which is equivalent to the “Plan” specification of standard microscope objectives.

- In Figure 2E, it would be helpful if the authors could list the exposure times as well as the total voxels/second for the two-camera comparison. It's also worth noting that the Sony chip used in the VP151MX camera was released last year whereas the Orca Flash V3 chosen for comparison is over a decade old now. I'm confused as to why the authors chose this camera for comparison when they appear to have a more recent Orca BT-Fusion that they show in a picture in the supplement (indicated as Figure S2 in the text, but I believe this is a typo and should be Figure S3). 

This is a useful addition, and we have added exposure times to the plot. We have also added a note that the Orca Flash V3 is an older generation sCMOS camera and that newer variants exist. Including the Orca BT-Fusion. The BT-Fusion has a read noise of 1.0 e- rms versus 1.6 e- rms, and a peak quantum efficiency of ~95% vs. 85%. Based on the discussion in Supplementary Note S1, we do not expect that these differences in specifications would dramatically change the data presented in the plot. In addition, the typo in Figure S2 has been corrected to Figure S3.

- In Table S1, the authors note that they only compare their work to prior modalities that are capable of providing <= 1 micron resolution. I'm a bit confused by this choice given that Figure 2 seems to show the resolution of ExA-SPIM as ~1.5 microns at 4 mm off center (1/2 their stated radial field of view). It also excludes a comparison with the mesoSPIM project which at least to me seems to be the most relevant prior to this manuscript. This system is designed for imaging large cleared tissues like the ones shown here. While the original publication in 2019 had a substantially lower lateral resolution, a newer variant, Nikita et al bioRxiv (which is cited in general terms in this manuscript, but not explicitly discussed) also provides 1.5-micron lateral resolution over a comparable field of view. 

We have updated the table to include the benchtop mesoSPIM from Nikita et al., Nature Communications, 2024. Based on this published version of the manuscript, the lateral resolution is 1.5 µm and axial resolution is 3.3 µm. Assuming the Iris 15 camera sensor, with the stated 2.5 fps, the volumetric rate (megavoxels/sec) is 37.41.

- The authors state that, "We systematically evaluated dehydration agents, including methanol, ethanol, and tetrahydrofuran (THF), followed by delipidation with commonly used protocols on 1 mm thick brain slices. Slices were expanded and examined for clarity under a macroscope." It would be useful to include some data from this evaluation in the manuscript to make it clear how the authors arrived at their final protocol. 

Additional details on the expansion protocol may be included in another manuscript.

General comments: 

There is a tendency in the manuscript to use negative qualitative terms when describing prior work and positive qualitative terms when describing the work here. Examples include: 

- "Throughput is limited in part by cumbersome and error-prone microscopy methods". While I agree that performing single neuron reconstructions at a large scale is a difficult challenge, the terms cumbersome and error-prone are qualitative and lacking objective metrics.

We have revised this statement to be more precise, stating that throughput is limited in part by the speed and image quality of existing microscopy methods.

- The resolution of the system is described in several places as "near-isotropic" whereas prior methods were described as "highly anisotropic". I agree that the ~1:3 lateral to axial ratio here is more isotropic than the 1:6 ratio of the other cited publications. However, I'm not sure I'd consider 3-fold worse axial resolution than lateral to be considered "near" isotropic.

We agree that the term near-isotropic is ambiguous. We have modified the text accordingly, removing the term near-isotropic and where appropriate stating that the resolution is more isotropic than that of other cited publications.

- In the manuscript, the authors describe the photobleaching in their imaging conditions as "negligible". Figure S5 seems to show a loss of 60% fluorescence after 2000 exposures (which in the caption is described as "modest"). I'd suggest removing these qualitative terms and just stating the values.

We agree and have changed the text accordingly.

- The results section for Figure 5 is titled "Tracing axons in human neocortex and white matter". Although this section states "larger axons (>1 um) are well separated... allowing for robust automated and manual tracing" there is no data for any tracing in the manuscript. Although I agree that the images are visually impressive, I'm not sure that this claim is backed by data.

We have now removed the text in this section referring to automated and manual tracing.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this paper Weber et al. investigate the role of 4 dopaminergic neurons of the Drosophila larva in mediating the association between an aversive high-salt stimulus and a neutral odor. The 4 DANs belong to the DL1 cluster and innervate non-overlapping compartments of the mushroom body, distinct from those involved in appetitive associative learning. Using specific driver lines for individual neurons, the authors show that activation of the DAN-g1 is sufficient to mimic an aversive memory and it is also necessary to form a high-salt memory of full strength, although optogenetic silencing of this neuron has only a partial phenotype. The authors use calcium imaging to show that the DAN-g1 is not the only DAN responding to salt. DAN-c1 and d1 also respond to salt, but they seem to play no role for the associative memory. DAN-f1, which does not respond to salt, is able to lead to the formation of a memory (if optogenetically activated), but it is not necessary for the salt-odor memory formation in normal conditions. However, when silenced together with DAN-g1, it enhances the memory deficit of DAN-g1. Overall, this work brings evidence of a complex interaction between DL1 DANs in both the encoding of salt signals and their teaching role in associative learning, with none of them being individually necessary and sufficient for both functions.

Strengths:

Overall, the manuscript contributes interesting results that are useful to understand the organization and function of the dopaminergic system. The behavioral role of the specific DANs is accessed using specific driver lines which allow to test their function individually and in pairs. Moreover, the authors perform calcium imaging to test whether DANs are activated by salt, a prerequisite for inducing a negative association to it. Proper genetic controls are carried across the manuscript.

Weaknesses:

The authors use two different approaches to silence dopaminergic neurons: optogenetics and induction of apoptosis. The results are not always consistent, but the authors discuss these differences appropriately. In general, the optogenetic approach is more appropriate as developmental compensations are not of major interest for the question investigated.

The physiological data would suggest the role of a certain subset of DANs in salt-odor association, but a different partially overlapping set is necessary in behavioral assays (with a partial phenotype). No manipulation completely abolishes the salt-odor association, leaving important open questions on the identity of the neural circuits involved in this behavior.

The EM data analysis reveals a non-trivial organization of sensory inputs into DANs, but it is difficult to extrapolate a link to the functional data presented in the paper.

We would like to once again thank Reviewer 1 for the positive assessment of our work and for the valuable suggestions provided on the first revision of the manuscript. In this second revision, we have addressed the linguistic issues and most of the minor comments as recommended. We now hope that the current version of our manuscript meets the reviewer’s expectations both in terms of language and content.

Reviewer #2 (Public review):

Summary:

In this work the authors show that dopaminergic neurons (DANs) from the DL1 cluster in Drosophila larvae are required for the formation of aversive memories. DL1 DANs complement pPAM cluster neurons which are required for the formation of attractive memories. This shows the compartmentalized network organization of how an insect learning center (the mushroom body) encodes memory by integrating olfactory stimuli with aversive or attractive teaching signals. Interestingly, the authors found that the 4 main dopaminergic DL1 neurons act partially redundant, and that single cell ablation did not result in aversive memory defects. However, ablation or silencing of a specific DL1 subset (DAN-f1,g1) resulted in reduced salt aversion learning, which was specific to salt but no other aversive teaching stimuli tested. Importantly, activation of these DANs using an optogenetic approach was also sufficient to induce aversive learning in the presence of high salt. Together with the functional imaging of salt and fructose responses of the individual DANs and the implemented connectome analysis of sensory (and other) inputs to DL1/pPAM DANs this represents a very comprehensive study linking the structural, functional and behavioral role of DL1 DANs. This provides fundamental insight into the function of a simple yet efficiently organized learning center which displays highly conserved features of integrating teaching signals with other sensory cues via dopaminergic signaling.

Strengths:

This is a very careful, precise and meticulous study identifying the main larval DANs involved in aversive learning using high salt as a teaching signal. This is highly interesting because it allows to define the cellular substrates and pathways of aversive learning down to the single cell level in a system without much redundancy. It therefore sets the basis to conduct even more sophisticated experiments and together with the neat connectome analysis opens the possibility to unravel different sensory processing pathways within the DL1 cluster and integration with the higher order circuit elements (Kenyon cells and MBONs). The authors' claims are well substantiated by the data and balanced, putting their data in the appropriate context. The authors also implemented neat pathway analyses using the larval connectome data to its full advantage, thus providing network pathways that contribute towards explaining the obtained results.

Weaknesses:

Previous comments were fully addressed by the authors.

We sincerely thank Reviewer 2 for the positive evaluation of our work. We are glad that our responses in the first revision addressed the previous concerns and appreciate the reviewer’s constructive feedback once again.

Reviewer #3 (Public review):

Summary:

The study of Weber et al. provides a thorough investigation of the roles of four individual dopamine neurons for aversive associative learning in the Drosophila larva. They focus on the neurons of the DL-1 cluster which already have been shown to signal aversive teaching signals. But the authors go beyond the previous publications and test whether each of these dopamine neurons responds to salt or sugar, is necessary for learning about salt, bitter, or sugar, and is sufficient to induce a memory when optogenetically activated. In addition, previously published connectomic data is used to analyze the synaptic input to each of these dopamine neurons. The authors conclude that the aversive teaching signal induced by salt is distributed across the four DL-1 dopamine neurons, with two of them, DAN-f1 and DAN-g1, being particularly important. Overall, the experiments are well designed and performed, support the authors' conclusions, and deepen our understanding of the dopaminergic punishment system.

Strengths:

(1) This study provides, at least to my knowledge, the first in vivo imaging of larval dopamine neurons in response to tastants. Although the selection of tastants is limited, the results close an important gap in our understanding of the function of these neurons.

(2) The authors performed a large number of experiments to probe for the necessity of each individual dopamine neuron, as well as combinations of neurons, for associative learning. This includes two different training regimen (1 or 3 trials), three different tastants (salt, quinine and fructose) and two different effectors, one ablating the neuron, the other one acutely silencing it. This thorough work is highly commendable, and the results prove that it was worth it. The authors find that only one neuron, DAN-g1, is partially necessary for salt learning when acutely silenced, whereas a combination of two neurons, DAN-f1 and DAN-g1, are necessary for salt learning when either being ablated or silenced.

(3) In addition, the authors probe whether any of the DL-1 neurons is sufficient for inducing an aversive memory. They found this to be the case for two of the neurons, largely confirming previous results obtained by a different learning paradigm, parameters and effector.

(4) This study also takes into account connectomic data to analyze the sensory input that each of the dopamine neurons receives. This analysis provides a welcome addition to previous studies and helps to gain a more complete understanding. The authors find large differences in inputs that each neuron receives, and little overlap in input that the dopamine neurons of the "aversive" DL-1 cluster and the "appetitive" pPAM cluster seem to receive.

(5) Finally, the authors try to link all the gathered information in order to describe an updated working model of how aversive teaching signals are carried by dopamine neurons to the larva's memory center. This includes important comparisons both between two different aversive stimuli (salt and nociception) and between the larval and adult stages.

We would also like to thank Reviewer 3 for the positive assessment of our work. Many of the constructive comments provided were incorporated into the first revision, contributing significantly to the improved clarity and overall quality of the manuscript.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Here are some minor comments (and some semantics that could be addressed to improve the manuscript)

Title: is the title correct given that c1 and d1 do not really signal punishment?

We think the title is correct and would like to keep it as it is.

L72 striatum misspelled

We have corrected the error.

L74 constitute instead of provide?

We made the suggested modification in the text.

L129: "But can these four individual DANs also process other sensory modalities?" other then what? What was used before?

We have made the required change, which now allows us to contrast somatosensory and chemosensory information.

L172: (Please refer to the discussion regarding the partial reduction of the memory); would be more natural to explain shortly here, or add a sentence before this parenthesis that point to the effect

We made the requested change in the manuscript and added a short sentence before the parenthesis.

L182: "DL1 neurons convey a dopaminergic aversive teaching signal" you cannot make this statement from just TH-GAL4!

We agree - that's why we have completely revised the sentence and now further restricted it and also refer to further larval and adult published data

L264: "possible redundancy among" I don't think you are testing a redundancy here, it is more likely a developmental compensation.

We made the requested change in the sentence and added a potential developmental compensation as an interpretation of our results.

L296: "to determine if the activation of individual DL1 DANs signals aspects of the natural high salt punishment," - how can the optogenetic activation tell something about aspects of the natural salt punishment? I understand the fact that salt is present, but still I find it inaccurate

Our approach is based on the framework established by Bertram Gerber and colleagues over the past two decades in larval Drosophila research. According to this logic, memory recall is dependent on the specific properties of the test context, particularly the type and concentration of the stimulus presented on the test plate. Aversive memory retrieval occurs only when the test conditions closely match those of the training stimulus. Consequently, the larva's behavior on the test plate serves as an indicator of the memory content being recalled. We therefore adhere to this established methodology (Gerber & Hendel, 2006; Schleyer et al., 2011; Schleyer et al., 2015).

L307 "DAN-f1 and DAN-g1 encode aspects of the natural aversive high salt teaching" you cannot conclude that given that f1 does not even respond to salt. I understand the logic of the salt during test, but I think it is still a stretched interpretation

We agree and thus have deleted the sentence.

L310 "Individual DL1 DANs are acutely necessary" this is too general, it seems that only one is

We have changed the title and now clearly state that this is only one DAN of the DL1 cluster.

Reviewer #2 (Recommendations for the authors):

In Fig.6 the text flow could be optimized as the authors first mention Fig. 6E,F before they follow up with Fig. 6A-D.

Thanks for bringing this up – we changed it in the revised version of the manuscript. Now 6A-D is mentioned first.

In Fig.6 the finding that optogenetic inactivation but not ablation of DAN-g1 slightly but significantly reduces aversive salt learning suggests that there is an individual contribution of this DAN in this paradigm. The authors emphasize redundancy of DL1 DANs although the effect size seems comparable between DAN-g1 and DAN-f1,g1 silencing.

In response to this concern and the one of reviewer 2, we have revised the section title and removed the final sentence of the section before to avoid placing emphasis on the potential redundancy of DL1 DANs within this results section.

Reviewer #3 (Recommendations for the authors):

The authors replied to each issue I raised, and revised their manuscript accordingly. In particular, regarding my major concern (the sufficiency of the neurons for salt-"specific" memories), I think the authors found a good solution.

I have no further comments.

We sincerely thank the reviewer for the positive feedback on our revision. We are pleased that the revised manuscript meets the expectations and appreciate the time and effort invested in the review process.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In Causal associations between plasma proteins and prostate cancer: a Proteome-Wide Mendelian Randomization, the authors present a manuscript which seeks to identify novel markers for prostate cancer through analysis of large biobank-based datasets and to extend this analysis to potential therapeutic targets for drugs. This is an area that is already extensively researched, but remains important, due to the high burden and mortality of prostate cancer globally.

Strengths:

The main strengths of the manuscript are the identification and use of large biobank data assets, which provide large numbers of cases and controls, essential for achieving statistical power. The databases used (deCODE, FinnGen, and the UK Biobank) allow for robust numbers of cases and controls. The analytical method chosen, Mendelian Randomization, is appropriate to the problem. Another strength is the integration of multi-omic datasets, here using protein data as well as GWAS sources to integrate genomic and proteomic data.

Thank you for your positive feedback regarding the overall quality of our work and we greatly appreciate you taking time and making effort in reviewing our manuscript.

Weaknesses:

The main weaknesses of the manuscript relate to the following areas:

(1) The failure of the study to analyse the data in the context of other closely related conditions such as benign prostatic hyperplasia (BPH) or lower urinary tract symptoms (LUTS), which have some pathways and biomarkers in common, such as inflammatory pathways (including complement) and specific markers such as KLK3. As a consequence, it is not possible for readers to know whether the findings are specific to prostate cancer or whether they are generic to prostate dysfunction. Given the prevalence of prostate dysfunction (half of men reaching their sixth decade), the potential for false positives and overtreatment from non-specific biomarkers is a major problem, resulting in the evidence presented in this manuscript being weak. Other researchers have addressed this issue using the same data sources as presented here, for example, in this paper, looking at BPH in the UK Biobank population. https://www.nature.com/articles/s41467-018-06920-9

Thank you for your valuable comment. We fully agree that biomarker development must prioritize specificity to avoid overtreatment. While our study is a foundational step toward identifying potential therapeutic targets or complementary biomarkers for prostate cancer (PCa)—not as a direct endorsement of these proteins for standalone clinical diagnosis. Mendelian randomization (MR) analysis strengthens causal inference by design, and we further ensured robustness through sensitivity analyses (e.g. MR-Egger regression for pleiotropy, Bonferroni correction for multiple testing). These methods distinguish true causal effects from nonspecific associations. Importantly, while PSA’s lack of specificity is widely recognized, its role in reducing PCa mortality underscores the value of biomarker-driven screening. Our findings align with the need to integrate multiple markers (e.g. combining a novel protein with PSA) to improve diagnostic precision. Translating these causal insights into clinical tools remains challenging but represents a necessary next step, and we emphasize that this work provides a rigorous starting point for future validation studies.

(2) There is no discussion of Gleason scores with regard to either biomarkers or therapies, and a general lack of discussion around indolent disease as compared with more aggressive variants. These are crucial issues with regard to the triage and identification of genomically aggressive localized prostate cancers. See, for example, the work set out in: https://doi.org/10.1038/nature20788

Thank you for pointing this out. We acknowledge that our original analysis did not directly address this critical issue due to a key data limitation: the publicly available GWAS summary statistics for PCa (from openGWAS and FinnGen) do not provide genetic associations stratified by phenotypic severity or molecular subtypes. This limitation precluded MR analysis of proteins specifically linked to aggressive disease. To partially bridge this gap, we integrate evidence from recent studies in the revised Discussion section to explore the relevance of potential biomarkers to aggressive PCa.

(3) An additional issue is that the field of PCa research is fast-moving. The manuscript cites ~80 references, but too few of these are from recent studies, and many important and relevant papers are not included. The manuscript would be much stronger if it compared and contrasted its findings with more recent studies of PCa biomarkers and targets, especially those concerned with multi-omics and those including BPH.

Thank you for your professional comments. We have rigorously updated the manuscript to include more recent publications and we systematically compare and contrast our findings with these recent studies in the revised Discussion section.

(4) The Methods section provides no information on how the Controls were selected. There is no Table providing cohort data to allow the reader to know whether there were differences in age, BMI, ethnic grouping, social status or deprivation, or smoking status, between the Cases and Controls. These types of data are generally recorded in Biobank data, so this sort of analysis should be possible, or if not, the authors' inability to construct an appropriately matched set of Controls should be discussed as a Limitation.

We thank the reviewer for raising this important methodological concern. We have expanded the Limitations section to state it.

Reviewer #2 (Public review):

This is potentially interesting work, but the analyses are attempted in a rather scattergun way, with little evident critical thought. The structure of the work (Results before Methods) can work in some manuscripts, but it is not ideal here. The authors discuss results before we know anything about the underlying data that the results come from. It gives the impression that the authors regard data as a resource to be exploited, without really caring where the data comes from. The methods can provide meaningful insights if correctly used, but while I don't have reasons to doubt that the analyses were conducted correctly, findings are presented with little discussion or interpretation. No follow-up analyses are performed.

In summary, there are likely some gems here, but the whole manuscript is essentially the output from an analytic pipeline.

We thank the reviewer for the thoughtful evaluation of our work.

Taking the researchers aims in turn:

(1) Meta-GWAS - while combining two datasets together can provide additional insights, the contribution of this analysis above existing GWAS is not clear. The PRACTICAL consortium has already reported the GWAS of 70% of these data. What additional value does this analysis provide? (Likely some, but it's not clear from the text.) Also, the presentation of results is unclear - authors state that only 5 gene regions contained variants at p<5x10-8, but Figure 1 shows dozens of hits above 5x10-8. Also, the red line in Figure 1 (supposedly at 5x10-8) is misplaced.

Thank you very much for your feedback. Although the PRACTICAL consortium constituted the majority of PCa GWAS data, our meta-analysis integrating FinnGen data enhanced statistical power enabling robust detection of low-frequency variants with minor allele frequencies. Moreover, FinnGen's Finnish ancestry (genetic isolate) helps distinguish population-specific effects. The presentation of results showed the top 5 gene regions contained variants at p < 5×10^-8. We apologize for not noticing that the red line was not displayed correctly in the original figures included in the manuscript. We have updated it in the revised manuscript.

(2) Cross-phenotype analysis. It is not really clear what this analysis is, or why it is done. What is the iCPAGdb? A database? A statistical method? Why would we want to know cross-phenotype associations? What even are these? It seems that the authors have taken data from an online resource and have written a paragraph based on this existing data with little added value.

We thank you for raising this issue. The iCPAGdb (interactive Cross-Phenotype Analysis of GWAS database) is an integrative platform that systematically identifies cross-phenotype associations and evaluates genetic pleiotropy by leveraging LD-proxy associations from the NHGRI-EBI GWAS Catalog. The pathogenesis and progression of prostate cancer constitute a complex pathophysiological continuum characterized by dynamic multisystem interactions, extending beyond singular molecular pathway dysregulation to encompass coordinated disruptions across endocrine regulation, immune microenvironment remodeling, and metabolic reprogramming. Therefore, it is indispensable for discriminating primary pathogenic drivers from secondary compensatory responses, ultimately informing the development of precision therapeutic strategies.

(3) PW-MR. I can see the value of this work, but many details are unclear. Was this a two-sample MR using PRACTICAL + FinnGen data for the outcome? How many variants were used in key analyses? Again, the description of results is sparse and gives little added value.

We thank you for raising this issue. Two-sample MR refers to an analytical design where genetic instruments for the exposure (plasma proteins) and genetic associations with the outcome (PCa) are derived from non-overlapping populations. This ensures complete sample independence between exposure and outcome datasets to avoid confounding biases, regardless of whether the outcome data originate from single or multiple cohorts. The meta-analysis of PRACTICAL and FinnGen GWAS generates 27,210 quality-controlled variants (p < 5×10^-8, MAF ≥ 1%, LD-clumped r² < 0.1) used in key analyses.

(4) Colocalization - seems clear to me.

(5) Additional post-GWAS analyses (pathway + druggability) - again, the analyses seem to be performed appropriately, although little additional insight other than the reporting of output from the methods.

The post-MR druggability and pathway analyses serve two primary scientific purposes: (1) therapeutic prioritization - systematically evaluating which MR-identified proteins represent tractable drug targets (either through existing FDA-approved agents or compounds in clinical development) with direct relevance to cancer or PCa management, and (2) mechanistic hypothesis generation - mapping these candidate proteins to coherent biological pathways to guide future functional validation studies investigating their causal roles in prostate carcinogenesis.

Minor points:

(6) The stated motivation for this work is "early detection". But causality isn't necessary for early detection. If the authors are interested in early detection, other analysis approaches are more appropriate.

We appreciate your insightful feedback. While early detection is one motivation for this work, our primary goal extends to identifying causally implicated proteins that may serve as intervention targets for PCa prevention or therapy.  Establishing causality is critical for distinguishing biomarkers that drive disease pathogenesis from those that are secondary to disease progression, as the former holds greater specificity for early detection and prioritization of therapeutic targets. While we acknowledge that validation for early detection may require additional methodologies, MR analysis provides a foundational step by prioritizing candidate proteins with causal links to disease. This approach ensures that downstream efforts focus on biomarkers and targets with the greatest potential to alter disease trajectories, rather than merely correlative markers.

(7) The authors state "193 proteins were associated with PCa risk", but they are looking at MR results - these analyses test for disease associations of genetically-predicted levels of proteins, not proteins themselves.

In MR, the exposure of interest is the lifelong effect of genetically predicted protein levels. This approach is designed to infer causality while avoiding confounding and reverse causation, as genetic variants are fixed at conception and unaffected by disease processes. When we state “193 proteins were associated with PCa risk,” we specifically refer to proteins whose genetically predicted levels (based on instrument SNPs from protein QTLs) show causal links to PCa. Importantly, MR does not measure the direct association between observed protein concentrations and disease. Instead, it estimates the lifelong causal effect of protein levels predicted by genetics. This distinction is critical for disentangling cause from consequence. For example, a protein elevated due to tumor progression would not be identified as causal in MR if its genetic predictors are unrelated to PCa risk.

We acknowledge that clinical translation requires further validation of these proteins in observational studies measuring actual protein levels. However, MR provides a robust first step by prioritizing candidates with causal roles, thereby reducing the risk of investing in biomarkers confounded by disease processes.

Author response:

We thank the reviewing editors, senior editors, and reviewers for their time, efforts, and constructive feedback. We believe the points raised are addressable and we would like to proceed with a revised submission for further review. Specifically, we plan the following revisions:

Editor’s Comments

We will clarify study definitions to ensure the meaning of "5-year crude overall survival time" is explicit for readers.

Reviewer 1 Comments

- Clarify and supplement the work with detailed sources of study origin (cancer registries or single-center cohorts).

- Conduct a multi-level hierarchical meta-analysis to address concerns of ecological fallacy in interpreting results.

- Perform an ecological sensitivity analysis and clarify findings regarding small study effects.

- Expand the search base significantly by including African local databases; preliminary searches have identified over 50 potentially eligible doctoral theses, dissertations, local journal articles, and gray literature, potentially adding data from five or more additional countries.

Reviewer 2 Comments

- Conduct subgroup analyses by sex and assess the influence of the percentage of males in mixed cohorts.

- Enhance the limited meta-analysis and provide supplementary full forest plots for all analyses.

- Clarify phrasing in sections identified by the reviewer.

Additional Planned Clarifications and Analyses

- Elucidate the role of cumulative meta-analysis in mitigating lead-time bias.

- Include supplementary cumulative meta-analysis based on the year of investigation (instead of publication year).

- Perform subgroup analyses by clinical staging, TNM grading, and treatment modalities where data from ≥10 studies is available.

- Expand discussion on the merits of quality assessment versus risk of bias evaluation in large scale epidemiological and observational studies, in line with other studies of this scale.

- Condense the comparison with 2018 estimates, as per reviewer suggestions.

Clarification Regarding SSA vs. AU Classification

We do not intend to compare survival between "Sub-Saharan Africa" (SSA) and North Africa, as this binary classification is historically rooted and does not reflect current African Union (AU) administrative or policy groupings. Our regional analyses will adhere to the AU’s contemporary regional framework to better reflect political, cultural, and healthcare system realities.

On Registry Data

We will clarify that we will not extract raw registry data, as such data is typically unprocessed and does not provide 5-year overall survival metrics. As such extracting raw, individual-level data from registries or vital statistics systems falls outside the methodological scope of a meta-analysis. Meta-analyses are designed to synthesize published survival estimates or those available from reports where survival analyses have already been conducted. Utilizing raw surveillance data would require primary data processing and survival analysis — effectively creating new data, not synthesizing existing results. This would represent a distinct study design, such as a pooled analysis or original cohort study, rather than a meta-analysis. Where registry reports present summary survival estimates (e.g., 5-year overall survival) in a format compatible with meta-analysis, we will certainly include them.

All planned additional analyses will depend on data quality, consistency, and feasibility for pooling using state-of-the-art statistical techniques. Where pooling is not possible, we will transparently report limitations.

Author response:

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

The main points made by all three reviewers were: to discuss the components of the omitted synapses and explore parameter sensitivity and broader physiological variability; to provide deeper physical insights into phase separation; to clarify terminology and provide better presentation and context in relation to previous studies.

We fully agree with the first point, suggesting that parameter sensitivity and broader physiological variability should be explored. Our model omits scaffold proteins such as GKAP, Shank and Homer, which are present at the bottom of the PSD hierarchy. In addition, there are many other interactions in PSDs whose affinity is altered by phosphorylation, and the phase separation state of the condensate is likely to be affected by ionic concentration and other environmental factors. We will include a more detailed discussion of these environmental factors and a limitation of our study in the Discussion section. Furthermore, regarding to the sensitivity of the parameters, the reviewer's point that the membrane potential parameter is an important value is right since it directly regulates the difference between 3D and 2D systems. We plan to verify this by changing the strength of the membrane potential, and by running simulations again to see how much it affects the morphology of condensates.

The second point is that we should provide deeper physical insight into phase separation in different dimensions. It would not be straightforward to directly estimate the entropy of the system due to the nature of the model. However, as pointed out, the difference of phase behavior can be elucidated through various simplified theories such as the lattice model. In this context, the reduced coordination number in 2D systems compared to 3D systems, and the decreased pseudo-attractive force due to the depletion effect, can offer rationalizations. We would like to add some theoretical discussion of these aspects with equations.

Third, we will clarify terminology and provide better explanation in relation to previous studies. In some parts in manuscripts, such as complexes containing receptors, there were some disunity in terminology and lack of annotations in figures. We will improve the wording and visualization in the text for further clarity and add relevant references, as suggested by the reviewers.

Also, as additionally suggested, scripts for the simulation and analysis together with the initial structure obtained will be deposited to Zenodo or GitHub.

Author response:

eLife Assessment

This work presents an important technical advancement with the release of MorphoNet 2.0, a user-friendly, standalone platform for 3D+T segmentation and analysis in biological imaging. The authors provide convincing evidence of the tool's capabilities through illustrative use cases, though broader validation against current state-of-the-art tools would strengthen its position. The software's accessibility and versatility make it a resource that will be of value for the bioimaging community, particularly in specialized subfields.

We would like to thank the editors and reviewers for their careful and constructive evaluation of our manuscript “MorphoNet 2.0: An innovative approach for qualitative assessment and segmentation curation of large-scale 3D time-lapse imaging datasets”. We are grateful for the positive assessment of MorphoNet 2.0 as a valuable and accessible tool for the bioimaging community, and for the recognition of its technical advancements, particularly in the context of complex 3D+t segmentation tasks.

The reviewers have highlighted several important points that we will address in the revised manuscript. These include:

- The need for a clearer demonstration that improvements in unsupervised quality metrics correspond to actual improvements in segmentation quality. In response, we will provide comparisons with gold standard annotations where available and clarify how to interpret metric distributions.<br /> - The potential risk of circular logic when using unsupervised metrics to guide model training. We now explicitly discuss this limitation and emphasize the importance of external validation and expert input.<br /> - The value of comparing MorphoNet 2.0 to other tools such as FIJI and napari. We will include a comparative table to help readers understand MorphoNet’s positioning and complementarity.<br /> - The importance of clearer documentation and terminology. We will overhaul the help pages, standardize plugin naming, and add a glossary-style table to the manuscript.<br /> - Suggestions for future developments, such as mesh export and interoperability with napari, which we will explore for the revision.

We appreciate the detailed feedback on both scientific and editorial aspects, including corrections to figures and text, and we will integrate all suggested revisions to improve the manuscript’s clarity and impact. We are confident that these changes will strengthen the manuscript and enhance the utility of MorphoNet 2.0 for the community.

Public Reviews:

Reviewer #1 (Public review):

The authors present a substantial improvement to their existing tool, MorphoNet, intended to facilitate assessment of 3D+t cell segmentation and tracking results, and curation of high-quality analysis for scientific discovery and data sharing. These tools are provided through a user-friendly GUI, making them accessible to biologists who are not experienced coders. Further, the authors have re-developed this tool to be a locally installed piece of software instead of a web interface, making the analysis and rendering of large 3D+t datasets more computationally efficient. The authors evidence the value of this tool with a series of use cases, in which they apply different features of the software to existing datasets and show the improvement to the segmentation and tracking achieved.

While the computational tools packaged in this software are familiar to readers (e.g., cellpose), the novel contribution of this work is the focus on error correction. The MorphoNet 2.0 software helps users identify where their candidate segmentation and/or tracking may be incorrect. The authors then provide existing tools in a single user-friendly package, lowering the threshold of skill required for users to get maximal value from these existing tools. To help users apply these tools effectively, the authors introduce a number of unsupervised quality metrics that can be applied to a segmentation candidate to identify masks and regions where the segmentation results are noticeably different from the majority of the image.

This work is valuable to researchers who are working with cell microscopy data that requires high-quality segmentation and tracking, particularly if their data are 3D time-lapse and thus challenging to segment and assess. The MorphoNet 2.0 tool that the authors present is intended to make the iterative process of segmentation, quality assessment, and re-processing easier and more streamlined, combining commonly used tools into a single user interface.

We sincerely thank the reviewer for their thorough and encouraging evaluation of our work. We are grateful that they highlighted both the technical improvements of MorphoNet 2.0 and its potential impact for the broader community working with complex 3D+t microscopy datasets. We particularly appreciate the recognition of our efforts to make advanced segmentation and tracking tools accessible to non-expert users through a user-friendly and locally installable interface, and for pointing out the importance of error detection and correction in the iterative analysis workflow. The reviewer’s appreciation of the value of integrating unsupervised quality metrics to support this process is especially meaningful to us, as this was a central motivation behind the development of MorphoNet 2.0. We hope the tool will indeed facilitate more rigorous and reproducible analyses, and we are encouraged by the reviewer’s positive assessment of its utility for the community.

One of the key contributions of the work is the unsupervised metrics that MorphoNet 2.0 offers for segmentation quality assessment. These metrics are used in the use cases to identify low-quality instances of segmentation in the provided datasets, so that they can be improved with plugins directly in MorphoNet 2.0. However, not enough consideration is given to demonstrating that optimizing these metrics leads to an improvement in segmentation quality. For example, in Use Case 1, the authors report their metrics of interest (Intensity offset, Intensity border variation, and Nuclei volume) for the uncurated silver truth, the partially curated and fully curated datasets, but this does not evidence an improvement in the results. Additional plotting of the distribution of these metrics on the Gold Truth data could help confirm that the distribution of these metrics now better matches the expected distribution.

Similarly, in Use Case 2, visual inspection leads us to believe that the segmentation generated by the Cellpose + Deli pipeline (shown in Figure 4d) is an improvement, but a direct comparison of agreement between segmented masks and masks in the published data (where the segmentations overlap) would further evidence this.

We agree that demonstrating the correlation between metric optimization and real segmentation improvement is essential. We will add new analysis comparing the distributions of the unsupervised metrics with the gold truth data before and after curation. Additionally, we will provide overlap scores where ground truth annotations are available, confirming the improvement. We will also explicitly discuss the limitation of relying solely on unsupervised metrics without complementary validation.

We would appreciate the authors addressing the risk of decreasing the quality of the segmentations by applying circular logic with their tool; MorphoNet 2.0 uses unsupervised metrics to identify masks that do not fit the typical distribution. A model such as StarDist can be trained on the "good" masks to generate more masks that match the most common type. This leads to a more homogeneous segmentation quality, without consideration for whether these metrics actually optimize the segmentation

We thank the reviewer for this important and insightful comment. It raises a crucial point regarding the risk of circular logic in our segmentation pipeline. Indeed, relying on unsupervised metrics to select “good” masks and using them to train a model like StarDist could lead to reinforcing a particular distribution of shapes or sizes, potentially filtering out biologically relevant variability. This homogenization may improve consistency with the chosen metrics, but not necessarily with the true underlying structures.

We fully agree that this is a key limitation to be aware of. We will revise the manuscript to explicitly discuss this risk, emphasizing that while our approach may help improve segmentation quality according to specific criteria, it should be complemented with biological validation and, when possible, expert input to ensure that important but rare phenotypes are not excluded.

In Use case 5, the authors include details that the errors were corrected by "264 MorphoNet plugin actions ... in 8 hours actions [sic]". The work would benefit from explaining whether this is 8 hours of human work, trying plugins and iteratively improving, or 8 hours of compute time to apply the selected plugins.

We will clarify that the “8 hours” refer to human interaction time, including exploration, testing, and iterative correction using plugins.

Reviewer #2 (Public review):

Summary:

This article presents Morphonet 2.0, a software designed to visualise and curate segmentations of 3D and 3D+t data. The authors demonstrate their capabilities on five published datasets, showcasing how even small segmentation errors can be automatically detected, easily assessed, and corrected by the user. This allows for more reliable ground truths, which will in turn be very much valuable for analysis and training deep learning models. Morphonet 2.0 offers intuitive 3D inspection and functionalities accessible to a non-coding audience, thereby broadening its impact.

Strengths:

The work proposed in this article is expected to be of great interest to the community by enabling easy visualisation and correction of complex 3D(+t) datasets. Moreover, the article is clear and well written, making MorphoNet more likely to be used. The goals are clearly defined, addressing an undeniable need in the bioimage analysis community. The authors use a diverse range of datasets, successfully demonstrating the versatility of the software.

We would also like to highlight the great effort that was made to clearly explain which type of computer configurations are necessary to run the different datasets and how to find the appropriate documentation according to your needs. The authors clearly carefully thought about these two important problems and came up with very satisfactory solutions.

We would like to sincerely thank the reviewer for their positive and thoughtful feedback. We are especially grateful that they acknowledged the clarity of the manuscript and the potential value of MorphoNet 2.0 for the community, particularly in facilitating the visualization and correction of complex 3D(+t) datasets. We also appreciate the reviewer’s recognition of our efforts to provide detailed guidance on hardware requirements and access to documentation—two aspects we consider crucial to ensuring the tool is both usable and widely adopted. Their comments are very encouraging and reinforce our commitment to making MorphoNet 2.0 as accessible and practical as possible for a broad range of users in the bioimage analysis community.

Weaknesses:

There is still one concern: the quantification of the improvement of the segmentations in the use cases and, therefore, the quantification of the potential impact of the software. While it appears hard to quantify the quality of the correction, the proposed work would be significantly improved if such metrics could be provided.

The authors show some distributions of metrics before and after segmentations to highlight the changes. This is a great start, but there seem to be two shortcomings: first, the comparison and interpretation of the different distributions does not appear to be trivial. It is therefore difficult to judge the quality of the improvement from these. Maybe an explanation in the text of how to interpret the differences between the distributions could help. A second shortcoming is that the before/after metrics displayed are the metrics used to guide the correction, so, by design, the scores will improve, but does that accurately represent the improvement of the segmentation? It seems to be the case, but it would be nice to maybe have a better assessment of the improvement of the quality.

We thank the reviewer for this constructive and important comment. We fully agree that assessing the true quality improvement of segmentation after correction is a central and challenging issue. While we initially focused on changes in the unsupervised quality metrics to illustrate the effect of the correction, we acknowledge that interpreting these distributions may not be straightforward, and that relying solely on the metrics used to guide the correction introduces an inherent bias in the evaluation.

To address the first point, we will revise the manuscript to provide clearer guidance on how to interpret the changes in metric distributions before and after correction, with additional examples to make this interpretation more intuitive.

Regarding the second point, we agree that using independent, external validation is necessary to confirm that the segmentation has genuinely improved. To this end, we will include additional assessments using complementary evaluation strategies on selected datasets where ground truth is accessible, to compare pre- and post-correction segmentations with an independent reference. These results reinforce the idea that the corrections guided by unsupervised metrics generally lead to more accurate segmentations, but we also emphasize their limitations and the need for biological validation in real-world cases.

Reviewer #3 (Public review):

Summary:

A very thorough technical report of a new standalone, open-source software for microscopy image processing and analysis (MorphoNet 2.0), with a particular emphasis on automated segmentation and its curation to obtain accurate results even with very complex 3D stacks, including timelapse experiments.

Strengths:

The authors did a good job of explaining the advantages of MorphoNet 2.0, as compared to its previous web-based version and to other software with similar capabilities. What I particularly found more useful to actually envisage these claimed advantages is the five examples used to illustrate the power of the software (based on a combination of Python scripting and the 3D game engine Unity). These examples, from published research, are very varied in both types of information and image quality, and all have their complexities, making them inherently difficult to segment. I strongly recommend the readers to carefully watch the accompanying videos, which show (although not thoroughly) how the software is actually used in these examples.

We sincerely thank the reviewer for their thoughtful and encouraging feedback. We are particularly pleased that the reviewer appreciated the comparative analysis of MorphoNet 2.0 with both its earlier version and existing tools, as well as the relevance of the five diverse and complex use cases we selected. Demonstrating the software’s versatility and robustness across a variety of challenging datasets was a key goal of this work, and we are glad that this aspect came through clearly. We also appreciate the reviewer’s recommendation to watch the accompanying videos, which we designed to provide a practical sense of how the tool is used in real-world scenarios. Their positive assessment is highly motivating and reinforces the value of combining scripting flexibility with an interactive 3D interface.

Weaknesses:

Being a technical article, the only possible comments are on how methods are presented, which is generally adequate, as mentioned above. In this regard, and in spite of the presented examples (chosen by the authors, who clearly gave them a deep thought before showing them), the only way in which the presented software will prove valuable is through its use by as many researchers as possible. This is not a weakness per se, of course, but just what is usual in this sort of report. Hence, I encourage readers to download the software and give it time to test it on their own data (which I will also do myself).

We fully agree that the true value of MorphoNet 2.0 will be demonstrated through its practical use by a wide range of researchers working with complex 3D and 3D+t datasets. In this regard, we will improve the user documentation and provide a set of example datasets to help new users quickly familiarize themselves with the platform. We are also committed to maintaining and updating MorphoNet 2.0 based on user feedback to further support its usability and impact.

In conclusion, I believe that this report is fundamental because it will be the major way of initially promoting the use of MorphoNet 2.0 by the objective public. The software itself holds the promise of being very impactful for the microscopists' community.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public Review):

Summary: 

The manuscript by Nicoletti et al. presents a minimal model of habituation, a basic form of non-associative learning, addressing both from dynamical and information theory aspects of how habituation can be realized. The authors identify that negative feedback provided with a slow storage mechanism is sufficient to explain habituation.

Strengths: 

The authors combine the identification of the dynamical mechanism with information-theoretic measures to determine the onset of habituation and provide a description of how the system can gain maximum information about the environment.

We thank the reviewer for highlighting the strength of our work and for their comments, which we believe have been instrumental in significantly improving our work and its scope. Below, we address all their concerns.

Weaknesses: 

I have several main concerns/questions about the proposed model for habituation and its plausibility. In general, habituation does not only refer to a decrease in the responsiveness upon repeated stimulation but as Thompson and Spencer discussed in Psych. Rev. 73, 16-43 (1966), there are 10 main characteristics of habituation, including (i) spontaneous recovery when the stimulus is withheld after response decrement; dependence on the frequency of stimulation such that (ii) more frequent stimulation results in more rapid and/or more pronounced response decrement and more rapid spontaneous recovery; (iii) within a stimulus modality, the less intense the stimulus, the more rapid and/or more pronounced the behavioral response decrement; (iv) the effects of repeated stimulation may continue to accumulate even after the response has reached an asymptotic level (which may or may not be zero, or no response). This effect of stimulation beyond asymptotic levels can alter subsequent behavior, for example, by delaying the onset of spontaneous recovery. 

These are only a subset of the conditions that have been experimentally observed and therefore a mechanistic model of habituation, in my understanding, should capture the majority of these features and/or discuss the absence of such features from the proposed model. 

We are really grateful to the reviewer for pointing out these aspects of habituation that we overlooked in the previous version of our manuscript. Indeed, our model is able to capture most of these 10 observed behaviors, specifically: 1) habituation; 2) spontaneous recovery; 3) potentiation of habituation; 4) frequency sensitivity; 5) intensity sensitivity; 6) subliminal accumulation. Here, we are following the same terminology employed in Eckert et al., Current Biology 34, 5646–5658 (2024), the paper highlighted by the reviewer. We have dedicated a section of the revised version of the manuscript to these hallmarks, substantiating the validity of our framework as a minimal model to have habituation. We remark that these are the sole hallmarks that can be discussed by considering one single external stimulus and that can be identified without ambiguity in a biochemical context. This observation is again in line with Eckert et al., Current Biology 34, 5646–5658 (2024).

In the revised version, we employ the same strategy of the aforementioned work to determine when the system can be considered “habituated”. Indeed, we introduce a response threshold that is now discussed in the manuscript. We also included a note in the discussions stating that, since any biochemical model will eventually reach a steady state, subliminal accumulation, for example, can only be seen with the use of a threshold. The introduction of different storage mechanisms, ideally more detailed at a molecular level, can shed light on this conceptual gap. This is an interesting direction of research.

Furthermore, the habituated response in steady-state is approximately 20% less than the initial response, which seems to be achieved already after 3-4 pulses, the subsequent change in response amplitude seems to be negligible, although the authors however state "after a large number of inputs, the system reaches a time-periodic steady-state". How do the authors justify these minimal decreases in the response amplitude? Does this come from the model parametrization and is there a parameter range where more pronounced habituation responses can be observed? 

The reviewer is correct, but this is solely a consequence of the specific set of parameters we selected. We made this choice solely for visualization purposes in the previous version. In the revised version, in the section discussing the hallmarks of habituation, we also show other parameter choices when the response decrement is more pronounced. Moreover, we remark that the contour plot of \Delta⟨U> clearly shows that the decrement can largely exceed the 20% threshold presented in the previous version.

In the revised version, also in light of the works highlighted by the reviewer, we decided to move the focus of the manuscript to the information-theoretic advantage of habituation. As such, we modified several parts of the main text. Also, in the region of optimal information gain, habituation is at an intermediate level. For this reason, we decided to keep the same parameter choice as the previous version in Figure 2.

We stated that the time-periodic steady-state is reached “after a large number of stimuli” from a mathematical perspective. However, by using a habituation threshold, as done in Eckert et al., Current Biology 34, 5646–5658 (2024), we can state that the system is habituated after a few stimuli for each set of parameters. This aspect is highlighted in the revised version of the manuscript (see also the point above).

The same is true for the information content (Figure 2f) - already at the first pulse, IU, H ~ 0.7 and only negligibly increases afterwards. In my understanding, during learning, the mutual information between the input and the internal state increases over time and the system extracts from these predictions about its responses. In the model presented by the authors, it seems the system already carries information about the environment which hardly changes with repeated stimulus presentation. The complexity of the signal is also limited, and it is very hard to clarify from the presented results, whether the proposed model can actually explain basic features of habituation, as mentioned above. 

As for the response decrement of the readout, we can certainly choose a set of parameters for which the information gain is higher. In the revised version, we also report the information at the first stimulation and when the system is habituated to give a better idea of the range of these quantities. At any rate, as the referee correctly points out, it is difficult to give an intuitive interpretation of the information in our minimal model.

It is also important to remark that, since the readout population and the receptor both undergo fast dynamics (with appropriate timescales as discussed in the text), we are not observing the transient gain of information associated with the first stimulus. As such, the mutual information presents a discontinuous behavior that resembles the dynamics of the readout, thereby starting at a non-zero value already at the first stimulus.

Additionally, there have been two recent models on habituation and I strongly suggest that the authors discuss their work in relation to recent works (bioRxiv 2024.08.04.606534; arXiv:2407.18204).

We thank the reviewer for pointing out these relevant references. In the revised version, we highlighted that we discuss the information-theoretic aspects of habituation, while the aforementioned references focus on the dynamics of this phenomenon.

Reviewer #1 (Recommendations for the authors):

I would also like to note here the simplification of the proposed biological model - in particular, that the receptor can be in an active/passive state, as well as proposing the Nf-kB signaling module as a possible molecular realization. Generally, a large number of cell surface receptors including RTKs of GPCRs have much more complex dynamics including autocatalytic activation that generally leads to bistability, and the Nf-kB has been demonstrated to have oscillatory even chaotic dynamics (works of Savas Tsay, Mogens Jensen and others). Considering this, the authors should at least discuss under which conditions these TNF-Alpha signaling could potentially serve as a molecular realisation for habituation. 

We thank the reviewer for bringing this to our attention. In the previous version, we reported the TNF signaling network only to show a similar coarse-grained modular structure. However, following a suggestion of reviewer #2, we decided to change Figure 1 to include a simplified molecular scheme of chemotaxis rather than TNF signaling, to avoid any source of confusion about this issue.

Also, a minor point: Figures 2d-e are cited before 2a-c. 

We apologize for the oversight. The structure of the Figures and their order is now significantly different, and they are now cited in the correct order. 

Reviewer #2 (Public review):

In this study, the authors aim to investigate habituation, the phenomenon of increasing reduction in activity following repeated stimuli, in the context of its information-theoretic advantage. To this end, they consider a highly simplified three-species reaction network where habituation is encoded by a slow memory variable that suppresses the receptor and therefore the readout activity. Using analytical and numerical methods, they show that in their model the information gain, the difference between the mutual information between the signal and readout after and before habituation, is maximal for intermediate habituation strength. Furthermore, they demonstrate that the Pareto front corresponds to an optimization strategy that maximizes the mutual information between signal and readout in the steady state, minimizes some form of dissipation, and also exhibits similar intermediate habituation strength. Finally, they briefly compare predictions of their model to whole-brain recordings of zebrafish larvae under visual stimulation. 

The author's simplified model might serve as a solid starting point for understanding habituation in different biological contexts as the model is simple enough to allow for some analytic understanding but at the same time exhibits all basic properties of habituation in sensory systems. Furthermore, the author's finding of maximal information gain for intermediate habituation strength via an optimization principle is, in general, interesting. However, the following points remain unclear or are weakly explained: 

We thank the reviewer for deeming our work interesting and for considering it a solid starting point for understanding habituation in biological systems.

(1) Is it unclear what the meaning of the finding of maximal information gain for intermediate habituation strength is for biological systems? Why is information gain as defined in the paper a relevant quantity for an organism/cell? For instance, why is a system with low mutual information after the first stimulus and intermediate mutual information after habituation better than one with consistently intermediate mutual information? Or, in other words, couldn't the system try to maximize the mutual information acquired over the whole time series, e.g., the time series mutual information between the stimulus and readout?

This is a delicate aspect to discuss and we thank the referee for the comment. In the revised version, we report information gain, initial and final information, highlighting that both gain and final information are higher in regions where habituation is present. They have qualitatively similar behavior and highlight a clear information-theoretic advantage of this dynamical phenomenon. An important point is that, to determine the optimal Pareto front, we consider a prolonged stimulus and its associated steady-state information. Therefore, from the optimization point of view, there is no notion of “information gain” or “final information”, which are intrinsically dynamical quantities. As a result, the fact that optimal curve lies in the region of optimal information gain is a-priori not expected and hints at the potential crucial role of this feature. In the revised version, we elucidate this aspect with several additional analyses.

We would like to add that, from a naive perspective, while the first stimulation will necessarily trigger a certain (non-zero) mutual information, multiple observations of the same stimulus have to reflect into accumulated information that consequently drives the onset of observed dynamical behaviors, such as habituation.

(2) The model is very similar to (or a simplification of previous models) for adaptation in living systems, e.g., for adaptation in chemotaxis via activity-dependent methylation and demethylation. This should be made clearer.

We apologize for having missed this point. Our choice has been motivated by the fact that we wanted to avoid confusion between the usual definition of (perfect) adaptation and habituation. However, we now believe that this is not the case for the revised manuscript, and we now include chemotaxis as an example in Figure 1.

(3) It remains unclear why this optimization principle is the most relevant one. While it makes sense to maximize the mutual information between stimulus and readout, there are various choices for what kind of dissipation is minimized. Why was \delta Q_R chosen and not, for instance, \dot{\Sigma}_int or the sum of both? How would the results change in that case? And how different are the results if the mutual information is not calculated for the strong stimulation input statistics but for the background one?

We thank the reviewer for the suggestion. We agree that a priori, there is no reason to choose \delta Q_R or a function of the internal energy flux J_int (that, in the revised version, we are using in place of \dot\Sigma_int following the suggestion of reviewer #3). The rationale was to minimize \delta Q_R since this dissipation is unavoidable and stems from the presence of the storage inhibiting the receptor through the internal pathway. Indeed, considering the existence of two different pathways implementing sensing and feedback, the presence of any input will result in a dissipation produced by the receptor. This energy consumption is reflected in \delta Q_R.

In the revised version, we now include in the optimization principle two energy contributions (see Eq. (14) of the revised manuscript): \delta Q_R and E_int, which is the energy consumption associated with the driven storage production per unit energy. All Figures have been updated accordingly. The results remain similar, as \delta Q_R still represents the main contribution, especially at high \beta.

Furthermore, in the revised version, we include examples of the Pareto optimization for different values of input strength. As detailed both in the main text and the Supplementary Information, changing the value of ⟨H⟩ moves the Pareto frontier in the (\beta, \sigma) space, since the signal needs to be strong enough for the system to distinguish it from the intrinsic thermal noise (controlled by beta). We also show that if the system is able to tune the inhibition strength \kappa, the Pareto frontiers at different ⟨H⟩ collapse into a single curve. This shows that, although the values of, e.g., the mutual information, depend on ⟨H⟩, the qualitative behavior of the system in this regime is effectively independent of it. We also added more details about this in the Supplementary Information.

(4) The comparison to the experimental data is not too strong of an argument in favor of the model. Is the agreement between the model and the experimental data surprising? What other behavior in the PCA space could one have expected in the data? Shouldn't the 1st PC mostly reflect the "features", by construction, and other variability should be due to progressively reduced activity levels? 

The agreement between data and model is not surprising - we agree on this - since the data exhibit habituation. However, we believe that the fact that our minimal model is able to capture the features of a complex neural system just by looking at the PCs, without any explicit biological details, is non-trivial. We also stress that the 1st PC only reflects the feature that captures most of the variance of the data and, as such, it is difficult to have a-priori expectations on what it should represent. In the case of the data generated from the model, most of the variance of the activity comes from the switching signal, and similar considerations can be made for the looming stimulations in the data. We updated the manuscript to clarify this point.

Reviewer #2 (Recommendations for the authors):

(1) The abstract makes it sound like a new finding is that habituation is due to a slow, negative feedback mechanism. But, as mentioned in the introduction, this is a well-known fact. 

We agree with the reviewer. We have revised the abstract.

(2) Figure 2c Why does the range of Delta Delta I_f include negative values if the corresponding region is shaded (right-tilted stripes)? 

The negative values in the range are those attained in the shaded region with right-tilted stripes. We decided to include them in the colorbar for clarity, since Delta Delta I_f is also plotted in the region where it attains negative values.

(3) What does the Pareto front look like if the optimization is done for input statistics given by ⟨H⟩_min? 

In the revised version, we include examples of the Pareto optimization for different values of input strength. As detailed both in the main text and the Supplementary Information, changing the value of ⟨H⟩ moves the Pareto frontier in the (\beta, \sigma) space, since the strength of the signal is crucial for the system to discriminate input and thermal noise (see also the answers above).

In particular, in Figure 4 we explicitly compare the results of the Pareto optimization (which is done with a static input of a given statistics) with the dynamics of the model for different values of ⟨H⟩ in two scenarios, i.e., adaptive and non-adaptive inhibition strength (see answers above for details).

We also remark that ⟨H⟩_min represents the background signal that the system is not trying to capture, which is why we never used it for optimization.

(4) From the main text, it is rather difficult to understand how the comparison to the experimental data was performed. How was the PCA done exactly? What are the "features" of the evoked neural response? 

The PCA on data is performed starting from the single-neuron calcium dynamics. To perform a far comparison, we reconstruct a similar but extremely simplified dynamics using our model as explained in Methods to perform the PCA on analogous simulated data. We added a comment on this in the revised version. While these components capture most of the variance in the data, their specific interpretation is usually out of reach and we believe that it lies beyond the scope of this theoretical work. We also remark that the model does not contain all these biological details - a strong aspect in our opinion - and, as such, it cannot capture specific biological features.

Reviewer #3 (Public review):

The authors use a generic model framework to study the emergence of habituation and its functional role from information-theoretic and energetic perspectives. Their model features a receptor, readout molecules, and a storage unit, and as such, can be applied to a wide range of biological systems. Through theoretical studies, the authors find that habituation (reduction in average activity) upon exposure to repeated stimuli should occur at intermediate degrees to achieve maximal information gain. Parameter regimes that enable these properties also result in low dissipation, suggesting that intermediate habituation is advantageous both energetically and for the purpose of retaining information about the environment. 

A major strength of the work is the generality of the studied model. The presence of three units (receptor, readout, storage) operating at different time scales and executing negative feedback can be found in many domains of biology, with representative examples well discussed by the authors (e.g. Figure 1b). A key takeaway demonstrated by the authors that has wide relevance is that large information gain and large habituation cannot be attained simultaneously. When energetic considerations are accounted for, large information gain and intermediate habituation appear to be a favorable combination. 

We thank the reviewer for this positive assessment of our work and its generality.

While the generic approach of coarse-graining most biological detail is appealing and the results are of broad relevance, some aspects of the conducted studies, the problem setup, and the writing lack clarity and should be addressed: 

(1) The abstract can be further sharpened. Specifically, the "functional role" mentioned at the end can be made more explicit, as it was done in the second-to-last paragraph of the Introduction section ("its functional advantages in terms of information gain and energy dissipation"). In addition, the abstract mentions the testing against experimental measurements of neural responses but does not specify the main takeaways. I suggest the authors briefly describe the main conclusions of their experimental study in the abstract.

We thank the reviewer for raising this point. In the revised version, we have changed the abstract to reflect the reviewer’s points and the new structure and results of the manuscript.

(2) Several clarifications are needed on the treatment of energy dissipation. 

-   When substituting the rates in Eq. (1) into the definition of δQ_R above Eq. (10), "σ" does not appear on the right-hand side. Does this mean that one of the rates in the lower pathway must include σ in its definition? Please clarify.

We apologize to the reviewer for this typo. Indeed, \sigma sets the energy scale of feedback and, as such, it appears in the energetic driving given by the feedback on the receptor, i.e., in Eq. (1) together with \kappa. This typo has been corrected in the revised manuscript, and all subsequent equations are consistent.

-   I understand that the production of storage molecules has an associated cost σ and hence contributes to dissipation. The dependence of receptor dissipation on ⟨H⟩, however, is not fully clear. If the environment were static and the memory block was absent, the term with ⟨H⟩ would still contribute to dissipation. What would be the nature of this dissipation?

In the spirit of building a paradigmatic minimal model with a thermodynamic meaning, we considered H to act as an external thermodynamic driving. Since this driving acts on a different pathway with respect to the one affected by the storage, the receptor is driven out of equilibrium by its presence.

By eliminating the memory block, we would also be necessarily eliminating the presence of the pathway associated with the storage effect (“internal pathway” in the manuscript), since its presence is solely due to the existence of a storage population. Therefore, in this case, the receptor would be a 2-state, 1-pathway system and, as such, it would always satisfy an effective detailed balance. As a consequence, the definition of \delta Q_R reported in the manuscript would not hold anymore and the receptor would not exhibit any dissipation. Thus, in a static environment and without a memory block, no receptor dissipation would be present. We would also like to stress that our choice to model two different pathways has been motivated by the observation that the negative feedback acts along a different pathway in several biochemical and biological examples. We made some changes to the model description in the revised version and we hope that this aspect has been clarified.

-   Similarly, in Eq. (9) the authors use the ratio of the rates Γ_{s → s+1} and Γ_{s+1 → s} in their expression for internal dissipation. The first-rate corresponds to the synthesis reaction of memory molecules, while the second corresponds to a degradation reaction. Since the second reaction is not the microscopic reverse of the first, what would be the physical interpretation of the log of their ratio? Since the authors already use σ as the energy cost per storage unit, why not use σ times the rate of producing S as a metric for the dissipation rate? 

We agree with the referee that the reverse reaction we considered is not the microscopic reverse of the storage production. In the case of a fast readout population, we employed a coarse-grained view to compute this entropy production. To be more precise, we gladly welcomed the referee’s suggestion in the revised version and modified the manuscript accordingly. As suggested, we now employ the energy flux associated with the storage production to estimate the internal dissipation (see new Fig. 3). 

In the revised version, we also use this quantity in the optimization procedure in combination with \deltaQ_R (see new Fig. 4) to have a complete characterization of the system’s energy consumption. The conclusions are qualitatively identical to before, but we believe that now they are more solid from a theoretical perspective. For this important advance in the robustness and quality of our work, we are profoundly grateful to the referee.

(3) Impact of the pre-stimulus state. The plots in Figure 2 suggest that the environment was static before the application of repeated stimuli. Can the authors comment on the impact of the pre-stimulus state on the degree of habituation and its optimality properties? Specifically, would the conclusions stay the same if the prior environment had stochastic but aperiodic dynamics? 

The initial stimulus is indeed stochastic with an average constant in time and mimics the background (small) signal. We apply the (strong) stimulation when the system already reached a stationary state with respect to the background. As it can be appreciated in Fig. 2 of the revised version, the model response depends on the pre-stimulus level, since it sets the storage concentration before the stimulation arrives and, as such, the subsequent habituation dynamics. This dependence is important from a dynamical perspective. The information-theoretic picture has been developed, as said above, by letting the system relax before the first stimulus. This eliminates this arbitrary dependence and provides a clearer idea of the functional advantages of habituation. Moreover, the optimization procedure is performed in a completely different setting, with no pre-stimulus at all, since we only have one prolonged stimulation. We hope that the revised version is clearer on all these points.

(4) Clarification about the memory requirement for habituation. Figure 4 and the associated section argue for the essential role that the storage mechanism plays in habituation. Indeed, Figure 4a shows that the degree of habituation decreases with decreasing memory. The graph also shows that in the limit of vanishingly small Δ⟨S⟩, the system can still exhibit a finite degree of habituation. Can the authors explain this limiting behavior; specifically, why does habituation not vanish in the limit Δ⟨S⟩ -> 0?

We apologize for the lack of clarity and we thank the reviewer for spotting this issue. In Figure 4 (now Figure 5 in the revised manuscript) Δ⟨S⟩ is not exactly zero, but equal to 0.15% at the final point. It appeared as 0% in the plot due to an unwanted rounding in the plotting function that we missed. This has been fixed in the revised version, thank you.

Reviewer #3 (Recommendations for the authors):

(1) Page 2 | "Figure 1b-e" should be "Figure 1b-d" since there is no panel (e) in Figure 1. 

(2) Figure 1a | In the top schematic, the symbol "k" is used, while in the rest of the text, the proportionality constant is denoted by κ. 

We thank the reviewer for pointing this out. Figure 1 has been revised and the panels are now consistent. The proportionality constant (the inhibition strength) has also been fixed.

(3) Figure 1a | I find the upper part of the schematic for Storage hard to perceive. I understand the lower part stands for the degradation reaction for storage molecules. The upper part stands for the synthesis reaction catalyzed by the readout population. I think the bolded upper arrow would explain it sufficiently well; the left/right arrows, together with the crossed green circle make that part of the figure confusing. Consider simplifying. 

We decided to remove the left/right arrows, as suggested by the reviewer, as we agree that they were unnecessarily complicating the schematic. We hope that the revised version will be easier to understand.

(4)Page 3 | It would be helpful to tell what the temporal statistics of the input signal $p_H(h,t)$ is, i.e. <h(t) h(t')>. Looking at the example trajectory in Figure 1a, consecutive signal values do not seem correlated. 

We agree with the reviewer that this is an important detail and worth mentioning. We now explicitly state that consecutive values are not correlated, for simplicity. 

(5)Figure 2 | I believe the label "EXTERNAL INPUT" refers to the *average* external input, not one specific realization (similar to panels (d) and (e) that report on average metrics). I suggest you indicate this in the label, or, what may be even better, add one particular realization of the stochastic input to the same graph.

We thank the reviewer for spotting this. We now write that what we show is the average external signal. We prefer this solution rather than showing a realization of the stochastic input, since it is more consistent with the rest of the plots, where we always show average quantities. We also note that Figure 2 is now Figure 3 in the revised manuscript.

(6)Figure 2d | The expression of Δ⟨U⟩ is the negative of the definition in Eq. (5). It should be corrected. 

In the revised version, both the definitions in Figure 2 (now Figure 3) and in the text (now Eq. (11)) are consistent.

(7) Figure 3(d-e) caption | "where ⟨U⟩ starts to be significantly smaller than zero." There, it should be Δ⟨U⟩ instead of ⟨U⟩. 

Thanks again, we corrected this typo.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

(1) Wnt3 cue and global PCP. PCP has been described in detail in a previous paper on Clytia (Momose et al, 2012): its orientation along the oral-aboral body axis (ciliary basal body positioning studies), and its function in directional polarity during gastrulation (Stbm-, Fz1-, and Dsh-MO experiments). I wonder if this part could be shortened. What is new, however, are the knockdown and Wnt3-mRNA rescue experiments, which provide a deeper insight into the link between Wnt3 function in the blastopore organiser as a source or cue for axis formation. These experiments demonstrate that the Wnt3 knockdown induces defects equivalent to PCP factor knockdown, but can be rescued by Wnt3-mRNA injection, even at a distance of 200 µm away from the Wnt-positive area. The experimental set-up of these new molecular experiments follows in important aspects those of Freeman's experiments of 1981 (who in turn was motivated to re-examine Teissier's work of 1931/1933 ...). Freeman did not use the term "global polarity" but the concept of an axis-inducing source and a long-range tissue polarity can be traced back to both researchers.

We appreciate the reviewer’s insightful comments for evolutionary biology and cnidarian developmental biology.

Concerning the presentation of the basic PCP structure of Clytia embryo epidermal cells, we prefer to retain this section unless there is a strict limit on manuscript length. These experiments provide background information necessary to establish the biological system for the readers. The structures of cells, notably cell adhesion, cilia, and the cytoskeleton, are essential components of this system.

We have restored sentences concerning the historical contributions of Freeman and Teissier from a previous version of the manuscript.

Freeman’s work offered two key insights. The first is the concept that cell polarity spreads and self-organizes over the distances revealed by the tissue orientation of aggregate embryonic cells (Freeman, 1981 https://doi.org/10.1007/BF00867804), which was termed “global polarity” in a review by Primus and Freeman (2004 https://doi.org/10.1002/bies.20031). This concept closely resembles the modern understanding of PCP coordination mechanisms mediated by core PCP interactions. Remarkably, Freeman proposed this idea in the early 1980s, at the same time of the first characterization of PCP mutants in Drosophila (Gubb and Garcia-Bellido 1982). The second is the role of egg polarity in defining the axis. Freeman demonstrated that the position of the first cleavage furrow predicts the oral-aboral axis by a series of sophisticated experiments. This was a milestone for the studies of cnidarian body axis development.

However, some of Freeman’s interpretations were misleading. In the 1981 paper, he stated:

"Polarity

Other work that I have done has established that the anterior-posterior axis of the planula is set up at the time of the first cleavage; the site where cleavage is initiated specifies the posterior pole of this axis (Freeman 1980). The experiment reported here in which embryos were cut into halves and each half regulated to form a normal planula with the same polarity properties as the embryo it is from provides evidence that these polarity properties are remarkably stable at all developmental stages tested ranging from 4 cell to postgastrula embryos. "

Freeman hypothesised that cell polarity at the 2- or 4-cell stage, referred to as the “polarity of first cell cleavage,” is directly inherited as the global polarity observed in later developmental stages.

In the review by Primus and Freeman (2004), two hypotheses were introduced: (1) maternally localised factors, such as mRNA, determine the axis, and (2) cell polarity of cleavage furrow formation, is inherited to later stages and determines the axis. Freeman described these two hypotheses as mutually exclusive. However, we now know that cell polarity at early cleavage stages does not directly contribute to global polarity/PCP. Instead, Wnt/β-catenin signaling is regionally activated by maternally localised mRNAs distributed along the egg polarity (Momose, 2007; Momose, 2008), which maintain Wnt3 localisation and direct morphological axis patterning. Our study shown in this article unified these hypotheses.

On the second point, as the reviewer noted, Freeman indeed revisited the work of Georges Teissier (Teissier, 1931), who conducted similar experiments on Amphisbetia embryos. It was Teissier who first described how the egg polarity is preserved in later stages and defines the axis. Teissier, however, carefully avoided asserting continuity between egg and blastula polarities, allowing for the possibility of “rétablissement” (re-establishment). As Teissier stated:

"…On constate, en second lieu, que la polarité de l’œuf se conserve dans chacun de se fragment et que le maintien ou le rétablissement de cette polarité sont indispensables à un développement normal. Un fragment d’œuf ou de morula n’a aucune partie ni aucun blastomère qui soit rigoureusement déterminé comme endoderme, mais possède, par contre, un pôle antérieur et un pôle postérieur bien définis.…

Mais cette proposition, qui ne semble pourtant guère dépasser la simple constatation des faits, soulève de grave difficulté. Elle donne en effet à la polarité, propriété encore bien mystérieuse, un rôle morphogénétique de premier ordre et implique des conséquences trop importantes pour qu’on puisse l’accepter sans un très sérieux examen.

Comme je ne pense pas que les questions relatives à la nature des localisation germinales, à l’existence et au fonctionnement des organisateurs de l’œuf des Cœlentérés, puissant, dans l’état actuel de nos connaissances, être discutées utilement, je ne veux voir dans la proposition précédente qu’une façons commode et tout provisoire de systématiser les faits."

English translation:

“We note also that the polarity of the egg is preserved in each fragment and that the maintenance or re-establishment of this polarity is essential for normal development. A fragment of egg or morula has no part or blastomere that is rigorously determined as endoderm, but has, on the other hand, a well-defined anterior and posterior pole....

But this proposition, which hardly seems to go beyond the simple observation of facts, raises serious difficulties. It gives polarity, still a mysterious property, a morphogenetic role of the first order, and implies consequences too important to be accepted without very serious examination.

As I do not believe that questions concerning the nature of germinal localisation, or the existence and functioning of the egg organisers in Coelenterates, can, in the present state of our knowledge, be usefully discussed, I prefer only to see in the foregoing proposition a convenient and very provisional way of systematising the facts.”

Teissier, G. (1931). Étude Expérimentale du Développement de Quelques Hydraires. Ann. Sc. Nat. Zool 14, 5–59.

Teissier's interpretation and caution were reasonable.

Our work connects recent molecular research on axis specification mechanisms in cnidarians with the classic experimental studies of Freeman and Teissier. We believe it is essential to present and acknowledge their conceptual contributions.  We have updated the Discussion to include these points.

(2) PCP propagation and β-catenin. The central but unanswered question in this study focuses on the interaction between Wnt3 and PCP and the propagation of PCP. Wnt3 has been described in cnidarians but also in vertebrates and insects as a canonical Wnt interacting with β-catenin in an autocatalytic loop. The surprising result of this study is that the action of Wnt3 on PCP orientation is not inhibited in the presence of a dominant-negative form of CheTCF (dnTCF) ruling out a potential function of β-catenin in PCP. This was supported by studies with constitutively active β-catenin (CA-β-cat) mRNA which was unable to restore PCP coordination nor elongation of Wnt3-depleted embryos but did restore β-catenin-dependent gastrulation. Based on these data, the authors conclude that Wnt3 has two independent roles: Wnt/β-catenin activation and initial PCP orientation (two-step model for PCP formation). However, the molecular basis for the interaction of Wnt3 with the PCP machinery and how the specificity of Wnt3 for both pathways is regulated at the level of Wnt-receiving cells (Fz-Dsh) remain unresolved. Also, with respect to PCP propagation, there is no answer with respect to the underlying mechanisms. The authors found that PCP components are expressed in the mid-blastula stage, but without any further indication of how the signal might be propagated, e.g., by a wavefront of local cell alignment. Here, it is necessary to address the underlying possible cellular interactions more explicitly.

The question of how Wnt3 interacts with the core PCP complex remains open for future investigation. An obvious hypothesis is that one of the Frizzled receptors binds Wnt3 ligands. For additional details, please refer to the response to Reviewer 2’s comment. Regarding other non-classic Wnt receptors, studies in the developing mouse limb have demonstrated that a Wnt5a gradient controls PCP polarisation via ROR receptors and graded Strabismus phosphorylation (Gao et al., 2011, https://doi.org/10.1016/j.devcel.2011.01.001). However, in this context, the Wnt5a gradient influences the frequency of polarised cells rather than PCP orientation. In Clytia, we performed gene knockdown experiments targeting ROR and RYK receptors using Morpholinos but did not observe any effect on axial patterning, suggesting that these receptors are unlikely to be involved in Wnt3 interaction.

Concerning PCP propagation mechanisms, these are well-characterized in both Drosophila and vertebrates and conserved across taxa. The localised Fz-Fmi complex at the apical cortex of a cell interacts with the oppositely localised Stbm-Fmi complex in neighbouring cells, enabling coordination of PCP between directly adjacent cells. This interaction provides a comprehensive explanation for PCP propagation mechanisms. In Drosophila, the “domineering non-autonomy” effect is a well-documented phenomenon where PCP orientation autonomously propagates from core PCP mutant mosaic patches. Overall, PCP propagation is a conserved and robust mechanism across metazoans.

(3) The proposed two-step model for PCP formation has important evolutionary implications in that it excludes the current alternate model according to which a long-range Wnt3-gradient orients PCP ("Wnt/β-catenin-first"). Nevertheless, the initial PCP orientation by Wnt3 - as proposed in the two-step model - is not explained at all on the molecular level. Another possible, but less well-discussed and studied option for linking Wnt3 with PCP action could be the role of other Wnt pathways. The authors present compelling evidence that Wnt3 is the most highly expressed Wnt in Clytia at all stages of development. The authors convincingly show that Wnt3 is the most highly expressed Wnt in Clytia at all stages of development (Figure S1). However, Wnt7 is also more highly expressed, which makes it a candidate for signal transduction from canonical Wnts to PCP Wnts. An involvement of Wnt7 in PCP regulation has been described in vertebrates (http://dx.doi.org/10.1016/j.celrep.2013.12.026). This would challenge the entire discussion and speculation on the evolutionary implications according to which PCP Wnt signaling comes first (PCP-first scenario") and canonical Wnt signaling later in metazoan evolution.

First of all, we apologise that the expression profile of Wnt7originally provided in Figure S1 was incorrect; Wnt7 is not expressed in the embryonic stage. The error came from the accession number XLOC_034538 assigned to two transcripts, Wnt7 and Ataxin10, in the published genome assembly. Once the expression profile is revised in this light, the data are consistent with the in situ hybridisation data published in Momose et al. (2012, https://doi.org/10.1242/dev.084251). Wnt3 is the only Wnt ligand detectable between egg and gastrula stages. We appreciate the reviewer highlighting this issue and have corrected Figure S1

If we understand correctly, the reviewer raises the possibility that Wnt3's downstream canonical Wnt/β-catenin pathway activates the expression of other Wnt genes, which in turn orient the PCP. Indeed, we showed that the expression of Wnt1 (previously called WntX2), Wnt2 (WntX1A), Wnt5 and Wnt6 (Wnt9) all becomes undetectable at the planula stage following Wnt3-MO injection (Momose et al., 2012). So, it is a reasonable concern.

This possibility can be excluded because the canonical pathway activation by CA-β-cat does not restore PCP in Wnt3-MO-injected embryos and Wnt3 can orient PCP without Wnt/β-catenin pathway activity in the presence of dominant negative TCF (dnTCF). Concerning Wnt1b and Wnt11b, these transcripts are maternally stored and even more abundant than Wnt3. However, we can conclude that these do not have any role in axis patterning based on the complete axis loss in Wnt3-MO morphants.

Lastly, it should of course be remembered that the chronological order of characters appearing in a developmental process does not necessarily reflect their appearance in evolution from ancestral to modern.

(4) The discussion, including Figure 6, is strongly biased towards the traditional evolutionary scenario postulating a choanzoan-sponge ancestry of metazoans. Chromosome-linkage data of pre-metazoans and metazoans (Schulz et al., 2023; https://doi.org/10(1038/s41586-023-05936-6) now indicate a radically different scenario according to which ctenophores represent the ancestral form and are sister to sponges, cnidarians and bilaterians (the Ctenophora-sister hypothesis). This has also implications for the evolution of Wnt signalling, as discussed in the recent Nature Genetics Review by Holzem et al. (2024) (https://doi.org/10.1038/s41576-024-00699-w). Furthermore, it calls into question the hypothesis of a filter-feeding multicellular gastrula-like ancestor as proposed by Haeckel (Maegele et al., 2023). These papers have not yet been referenced, but they would provide a more robust discussion.

I overlooked the excellent work of Holzem and colleagues. I appreciate this suggestion. The work, unfortunately, focusses mainly on the Wnt/β-catenin pathway. The PCP pathway consists of not only core PCP (Fmi Stbm, Pk, Dgo, Fz and Dsh) but many other components, such as Rho GTPase, which are all dealt with as "PCP” in this review. While the full set of core PCP is present only in the phylum Cnidaria and bilaterians, Pk and Dgo are present in choanoflagellate and Rho GTPase or ROCK are present even in Fungi (Lapébie et al,  2011 DOI 10.1002/bies.201100023). Holzem et al., described PCP as absent in ctenophores, likely based on the lack of Fmi/Stbm, while claiming its presence in fungi based on Rho GTPase and ROCK. This led to their argument that the Wnt/β-catenin pathway is more ancestral, supported by the absence of PCP components in ctenophores alongside the ctenophore-sister hypothesis.

This likely reflects the limited attention given to PCP in the metazoan evolutionary biology community. Our work sheds light on the importance of PCP regulation in metazoan evolution. In the revised Discussion, we emphasise this point together with the importance of cell biology studies in basal metazoans and compare them based on functional studies.

The observation of Aiptasia’s predatory “gastrula-like” larvae is indeed fascinating. Understanding how early metazoan ancestors obtained nutrients is a key to uncovering the origins of metazoans. However, the relevance of this work to metazoan evolution remains unclear. Predatory nutrient uptake is common among cnidarians, and the findings of Maegele et al. could suggest that the predatory gastrula-like state is ancestral, with the symbiotic state being derived, within Cnidaria, but does not notably support it in metazoa. Also, it has to be clarified how predation is defined. Fundamentally, there is little distinction between filter-feeding and predatory feeding regarding heterotrophy; both feeding types require digestive machinery. If active feeding behaviour is the essence of predation, this would be better addressed as an evolutionary neurobiology or neuroscience question. Another mystery is what the metazoan ancestors took as food if they were predatory; there has to be a non-predatorial metazoan, as a food, already present before them.<br /> Overall, Maegele’s work seems premature to be incorporated into the metazoan evo-devo discussion. In either case, the standard approach would involve comparative studies across taxa. It will be interesting to see follow-up works on comparative and functional genomics of predatory/digestive machinery within phylum cnidaria and across metazoan, including sponge and ctenophores.

Reviewer #2 (Recommendations for the authors):

We appreciate the reviewer’s expertise and recommendations regarding Wnt and PCP signalling. It would be our great pleasure if our work is seen and referenced by the cell biology community using model animals.

(1) According to the 2-step model, one would expect that there is a temporal gradient in the spreading of the PCP from oral to aboral. Is there any indication for this?

The best indication of a spatial and temporal gradient of PCP establishment observed so far is at the blastula stage (Fig.2B). PCP gradually becomes coordinated starting at 9 hpf, when PCP is slightly better organised close to the Wnt3-positive area (oral) compared to distal (aboral) areas. We did live imaging with tagged Poc1 to track the positions of centrioles in each cell (Fig. 2E), but this did not provide any further information about the spreading of the PCP. We hypothesise that there is a delay between PCP polarisation—established through the subcellular localisation of core PCP components—and its structural manifestation as ciliary positioning and orientation. This delay likely varies between cells, preventing the formation of a precise spatial PCP wave. We hope in the future to address this temporal aspect by live-imaging of core PCP proteins labelled with fluorescent proteins.

(2) PCP is likely to be an all-or-nothing effect, while axial patterning is dose-dependent. is there a critical dose of Wnt3 level required to kick off the PCP pathway?

We agree that the PCP phenotype is all-or-nothing.  Although we did not perform a quantitative test, we have not seen any intermediate phenotypes in Wnt3-rescue experiments. In our experimental condition (100 ng/µl mRNA), the Wnt3 mRNA injection into a blastomere consistently restores the body axis (via PCP) of Wnt3-MO injected embryos. No axis restoration was observed at 1 ng/µl. At 10 ng/µl, some embryos showed a restored elongated axis, while others showed no axis. The volume of injection is not precisely controllable and can easily vary two-fold, so we assume the limit is somewhere around 10 ng/µl. This contrasts with endoderm rescue via Wnt/β-catenin activation by GSK-β-inhibitors (alsterpaullone) or the constitutively active β-catenin (CA-β-cat), which occurs in a dose-dependent manner (ex. Supplementary Figure S2).

(3) The key question left unaddressed is whether Wnt3 signals through one or two different Frizzled receptors? Which Frizzled receptors are candidates for this? Could they be knocked down to see which pathway (or both) is affected?

How Wnt3 orientates the PCP system is an extremely interesting question that needs to be answered, and we plan to address this in the future. In Clytia, four Frizzled genes have been identified in the genome: CheFz1 (vertebrate counterpart of Fz1, 2, 3, 6 and 7), CheFz2 (Fz5 and 8), CheFz3 (Fz9/10) and CheFz4 (Fz4). Knockdown of CheFz1, hereby called Fz1, by Morpholino showed a PCP phenotype (Momose 2012, supplementary data). For a long time, we have suspected that the most likely candidate for PCP mediation is CheFz1. The Wnt3-rescue experiment in CheFz1-blocked background (similar experiment to Figure 3E, F) could potentially have answered this question. No PCP orientation would be expected even near the Wnt3-mRNA injected area if CheFz1 was the Wnt3 receptor for PCP orientation. Unfortunately, no reliable PCP phenotype was observed in this experiment, so this experiment was not included in the manuscript. We initially thought this was due to incomplete suppression of CheFz1 mRNA translation by the Morpholino when used at sub-toxic doses. But we now favour the alternative explanation that Fz1 does not mediate the Wnt3 signal responsible for initiating PCP orientation. We have previously shown that Fz1 is required for the Wnt/ β-catenin pathway (indicated by nuclear β-catenin localisation Momose 2007), which is then required to maintain Wnt3 expression. We cannot rule out that the PCP phenotype obtained previously following Fz1 knockdown (supplementary data in Momose 2012) is an indirect effect of Wnt3 downregulation.

In future work, we plan to test the PCP involvement of the other Clytia Frizzleds, notably CheFz2 and CheFz4, which are not present as maternal mRNAs but are zygotically expressed in the early gastrula stage. CheFz3 is unlikely to be a candidate because it is aborally localised and acts as a negative receptor for the Wnt/β-catenin pathway (Momose 2007). Lastly, in unpublished experiments, no axial phenotype was obtained with ROR and RYK knockdown by Morpholino (T. Momose unpublished). 

Based on these considerations, our current working hypothesis is that Wnt3 somehow stabilises or activates one of the Frizzled receptors acting as a core PCP protein in a polarised manner, likely at the oral side of each cell (Stbm is localised at the aboral side), which breaks the PCP symmetry and is propagated across the body axis.

A few lines have been added to the discussion regarding this point.

(4) Is there also PCP within the Wnt3 expressing domain? In other words, (and linked to question 2), does PCP require a certain concentration of Wnt3 or a gradient of Wnt3 in order to provide an orientation?

In the context of a simple Wn3-MO rescue experiment, PCP is coordinated within the Wnt3-positive area. But this could be because PCP can propagate in both orientations, so it does not answer the question. In the Wnt3-rescue experiments in Fmi-MO and Stbm-MO embryos, PCP seemed better oriented close to the boundary between Wnt3-positive and -negative areas, in particular outside the Wnt3-positive area and rather uncoordinated deep in the middle of Wnt3-RNA positive area. 

If Wnt3 expression is uniform across an embryo, as achieved by Wnt3-mRNA injection into the egg, the axis will be lost entirely (Momose 2008). We interpret these observations as indicating that Wnt3 expression "contrasts" (or steep gradients) act as the PCP orientation cue rather than a permissive manner.

In normal development, mRNA expression detected by in situ hybridisation has a slight gradient, but we do not have any information about the endogenous protein distribution.

We greatly appreciate the reviewer’s insightful comments. A few sentences addressing points (2) and (4) have been added. The graphical models in Figures 4 and 6A have been updated. While these are relatively minor changes to the manuscript, they significantly impact future perspectives.

Minor comments:

(1) Labeling in some of the figures is too small and not legible, e.g. Figures 4E-H. Please check and improve.

Agreed. Some labelling was way too small (2.5 points). This has been corrected. The minimum font size is now 6-point for most labelling in the revised Figures. 

(2) Page 13: ...and allow us to novel scenarios for PCP-driven axis symmetry breaking... seems to lack the verb "propose"

Corrected.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

Compelling and clearly described work that combines two elegant cell fate reporter strains with mathematical modelling to describe the kinetics of CD4+ TRM in mice. The aim is to investigate the cell dynamics underlying the maintenance of CD4+TRM.

The main conclusions are that:

(1) CD4+ TRM are not intrinsically long-lived.

(2) Even clonal half-lives are short: 1 month for TRM in skin, and even shorter (12 days) for TRM in lamina propria.

(3) TRM are maintained by self-renewal and circulating precursors.

Strengths:

(1) Very clearly and succinctly written. Though in some places too succinctly! See suggestions below for areas I think could benefit from more detail.

(2) Powerful combination of mouse strains and modelling to address questions that are hard to answer with other approaches.

(3) The modelling of different modes of recruitment (quiescent, neutral, division linked) is extremely interesting and often neglected (for simpler neutral recruitment).

Weaknesses/scope for improvement:

(1) The authors use the same data set that they later fit for generating their priors. This double use of the same dataset always makes me a bit squeamish as I worry it could lead to an underestimate of errors on the parameters. Could the authors show plots of their priors and posteriors to check that the priors are not overly-influential? Also, how do differences in priors ultimately influence the degree of support a model gets (if at all)? Could differences in priors lead to one model gaining more support than another?

We now show the priors and posteriors overlaid in Figure S2. The posteriors lie well within the priors, giving us confidence that the priors are not overly influential.

(2) The authors state (line 81) that cells were "identified as tissue-localised by virtue of their protection from short-term in vivo labelling (Methods; Fig. S1B)". I would like to see more information on this. How short is short term? How long after labelling do cells need to remain unlabelled in order to be designated tissue-localised (presumably label will get to tissue pretty quickly -within hours?). Can the authors provide citations to defend the assumption that all label-negative cells are tissue-localised (no false negatives)?

And conversely that no label-positive cells can be found in the tissue (no false positives)? I couldn't actually find the relevant section in the methods and Figure S1B didn't contain this information.

We did describe the in vivo labeling in the first section of Methods (it was for 3 mins before sacrifice). The two aims of Fig S1B were to show the gating strategy (label-positive and negatives from tissue samples were clearly separated) and to address the false-positive issue. Less than 3% of cells in our tissue samples were positive; therefore, at most 3% of truly tissue-resident cells acquired the i.v. label, and likely less. Excluding those (as we did) therefore makes little difference to our analyses in terms of cell numbers. False negative rates are expected to be extremely low; labeling within circulating cells is typically >99% (see refs in Methods).

(3) Are the target and precursor populations from the same mice? If so is there any way to reflect the between-individual variation in the precursor population (not captured by the simple empirical fit)? I am thinking particularly of the skin and LP CD4+CD69- populations where the fraction of cells that are mTOM+ (and to a lesser extent YFP+) spans virtually the whole range. Would it be nice to capture this information in downstream predictions if possible?

This is a great point. We do indeed isolate all populations from each mouse. We are very aware of the advantages of using this grouping of information to reduce within-mouse uncertainty – we employ this as often as we can. The issue here was that the label content within the tissue (target) at any time depends on the entire trajectory of the label frequency in the precursor, in that mouse, up to that point. We can’t identify this curve for each animal individually – so we are obliged to use a population average.

To mitigate this lack of pairing we do take a very conservative approach and fit this empirical function describing the trajectories of YFP and mTom in precursors at the same time as the label kinetics in the target; that is, we account for uncertainty in label influx in our fits and parameter estimates.

Another issue is that to be sure that we are performing model selection appropriately, we only use the distribution of the likelihood on the target observations when comparing support for different precursors with LOO-IC. If we had been able to pair the precursor and target data in some way, the two would then be entangled and model comparison across precursors would not be possible.

We’ve added some of this to the discussion.

(4) In Figure 3, estimates of kinetics for cells in LP appear to be more dependent on the input model (quiescent/neutral/division-linked) than the same parameters in the skin. Can the authors explain intuitively why this is the case?

This is a nice observation and it has a fairly straightforward explanation. As we pointed out in the paper, estimated rates of self renewal become more sensitive to the mode of recruitment the greater the rate of influx. If immigrants are quiescent, all Ki67 in the tissue has to be explained by self renewal. If all new immigrants are Ki67 high, the estimate of the rate of self renewal within the tissue will be lower. Across the board, the estimated rates of influx into gut were consistently higher than those in skin, and so the sensitivity of parameters to the mode of recruitment was much more obvious at that site.

The importance of this trade-off for the division linked model can also be seen when you look at the neutral and quiescent models; they give similar parameter estimates because the Ki67 levels within all precursor populations were all less than 25% and so those two modes of recruitment are difficult to distinguish.

(5) Can the authors include plots of the model fits to data associated with the different strengths of support shown in Figure 4? That is, I would like to know what a difference in the strength of say 0.43 compared with 0.3 looks like in "real terms". I feel strongly that this is important. Are all the fits fantastic, and some marginally better than others? Are they all dreadful and some are just less dreadful? Or are there meaningful differences?

This is another good point (and from the author recommendations list, is your most important concern).

We find that a fairly common issue is that models that are clearly distinguished by information criteria or LRTs can often give visually quite similar fits. Our experience is that this is partly due to the fact that models are usually fit on transformed scales (e.g. log for cell counts, logit for fractions) to normalise residuals, and this uncertainty is compressed when one looks at fits on the observed scale (e.g. linear). Another issue in our case is that for each model (precursor, target, and mode of recruitment) we fit 6 time courses simultaneously. Visual comparisons of fits of different models can then be a little difficult or misleading; apparently small differences in each fitted timecourse can add up to quite significant changes in the combined likelihood. We added this to the Discussion.

The number of models is combinatorial (Fig. 4) so showing them all seems a bit cumbersome. But now in the supporting information (Fig. S3), for each target we show the best, second best, and the worst model fits overlaid, to give a sense of the dynamic range of the models we considered. As you will now see, visual differences among the most strongly supported models were not huge (but refer to our point just above). Measures of out-of-sample prediction error (LOO-IC) discriminated between these models reasonably well, though (weights shown in Fig. 4).

It’s also worth mentioning here that we have substantially greater confidence in the identity of the precursors than in the precise modes of recruitment - you can see this clearly in the groupings of weights in Figure 4A. We did comment on this in the text but now emphasise it more.

(6) Figure 4 left me unclear about exactly which combinations of precursors and targets were considered. Figure 3 implies there are 5 precursors but in Figure 4A at most 4 are considered. Also, Figure 4B suggests skin CD69- were considered a target. This doesn't seem to be specified anywhere.

Thanks for pointing this out. When we were considering CD4+ EM in bulk as target, this population includes CD69- cells; in those fits, therefore, we couldn't use CD69- as a precursor. We now clarify this in the caption. Thanks also for the observation about Figure 4B; we didn’t consider CD69- cells as a target, so we’ve also made that clearer.

Reviewer #2 (Public review):

This manuscript addresses a fundamental problem of immunology - the persistence mechanisms of tissue-resident memory T cells (TRMs). It introduces a novel quantitative methodology, combining the in vivo tracing of T-cell cohorts with rigorous mathematical modeling and inference. Interestingly, the authors show that immigration plays a key role in maintaining CD4+ TRM populations in both skin and lamina propria (LP), with LP TRMs being more dependent on immigration than skin TRMs. This is an original and potentially impactful manuscript. However, several aspects were not clear and would benefit from being explained better or worked out in more detail.

(1) The key observations are as follows:

a) When heritably labeling cells due to CD4 expression, CD4+ TRM labeling frequency declines with time. This implies that CD4+ TRMs are ultimately replenished from a source not labeled, hence not expressing CD4. Most likely, this would be DN thymocytes.

That’s correct.

b) After labeling by Ki67 expression, labeled CD4+ TRMs also decline - This is what Figure 1B suggests. Hence they would be replaced by a source that was not in the cell cycle at the time of labeling. However, is this really borne out by the experimental data (Figure 2C, middle row)? Please clarify.

(2) For potential source populations (Figure 2D): Please discuss these data critically. For example, CD4+ CD69- cells in skin and LP start with a much lower initial labeling frequency than the respective TRM populations. Could the former then be precursors of the latter?

A similar question applies to LN YFP+ cells. Moreover, is the increase in YFP labeling in naïve T cells a result of their production from proliferative thymocytes? How well does the quantitative interpretation of YFP labeling kinetics in a target population work when populations upstream show opposite trends (e.g., naïve T cells increasing in YFP+ frequency but memory cells in effect decreasing, as, at the time of labeling, non-activated = non-proliferative T cells (and hence YFP-) might later become activated and contribute to memory)?

These are good (and related) points. We've added some text to the discussion, paragraphs 2 and 3; we reproduce it here, slightly expanded.

Fig 1B was a schematic but did faithfully reflect the impact of any waning of YFP in precursor on its kinetic in the targets. However, in our experiments, as you noted, the kinetics of YFP in most of the precursor populations were quite flat. This was due in part to memory subsets being sustained by the increasing levels of YFP within naïve cells from the cohort of thymocytes labeled during treatment. There is also likely some residual permanent labeling of lymphocyte progenitor populations. We discussed this in Lukas Front Imm 2023. (The latter is not a problem; all that matters for our analysis is that we generate a reasonable empirical description of the label kinetics in naive cells, however it arises). YFP is therefore not cleanly washed out in the periphery; and so for models with circulating memory as the tissue precursor, the flatness of their YFP curves leads to rather flat curves in the tissues.

The mTom labelling was more informative as it was clearly diluted out of all peripheral populations by mTom-negative descendants of thymically-derived cells, as you point out in (a).

Regarding (2), re: interpreting the initial levels of labels in precursors and targets. The important point here is that YFP and mTom were induced quickly in all populations we studied; therefore our inferences regarding precursors and targets aren’t informed by the initial levels of levels in each. (Imagine a slow precursor feeding a rapidly dividing target; YFP levels in the former would start lower than those in the latter). The causal issue that we think you’re referring to would matter if one expects the targets to begin with no label at all; for instance, in our busulfan chimeric mouse model (e.g. Hogan PNAS 2015) new, thymically derived ‘labelled’ (donor) cells progressively infiltrate replete ‘unlabelled’ (host) populations. In that case, one can immediately reject certain differentiation pathways by looking the sequence of accrual of donor cells in different subsets.

The trends in YFP and mTom frequencies after treatment do matter for pathway inference, though, because precursor kinetics must leave an imprint on the target. For the case you mentioned, with opposite trends in label kinetics, such models would unlikely to be supported strongly; indeed, we never saw strong support for naïve cells (strongly increasing YFP) as a direct precursor of TRM (fairly flat).

We’ve added a condensed version of this to the Discussion.

(3) Please add a measure of variation (e.g., suitable credible intervals) to the "best fits" (solid lines in Figure 2).

Added.

(4) Could the authors better explain the motivation for basing their model comparisons on the Leave-OneOut (LOO) cross-validation method? Why not use Bayesian evidence instead?

Bayes factors are very sensitive to priors and are either computationally unstable if calculated with importance sampling methods, or very expensive to calculate, if ones uses the more stable bridge sampling method. (We also note that fitting just a single model here takes a substantial amount of time). Further, using BF can be unreliable unless one of the models is close to the 'true' data generating model; though they seem to work well, we can be sure that none of our models are! For us, a more tractable and real-world selection criterion is based on the usefulness of a model, for which predictive performance is a reasonable proxy. In this case the mean out-of-sample prediction error (which LOO-IC reflects) is a wellestablished and valid means of ascribing support to different models.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review): 

Summary: 

Wang et al. identify Hamlet, a PR-containing transcription factor, as a master regulator of reproductive development in Drosophila. Specifically, the fusion between the gonad and genital disc is necessary for the development of continuous testes and seminal vesicle tissue essential for fertility. To do this, the authors generate novel Hamlet null mutants by CRISPR/Cas9 gene editing and characterize the morphological, physiological, and gene expression changes of the mutants using immunofluorescence, RNA-seq, cut-tag, and in-situ analysis. Thus, Hamlet is discovered to regulate a unique expression program, which includes Wnt2 and Tl, that is necessary for testis development and fertility. 

Strengths: 

This is a rigorous and comprehensive study that identifies the Hamlet-dependent gene expression program mediating reproductive development in Drosophila. The Hamlet transcription targets are further characterized by Gal4/UAS-RNAi confirming their role in reproductive development. Finally, the study points to a role for Wnt2 and Tl as well as other Hamlet transcriptionally regulated genes in epithelial tissue fusion. 

We appreciate that the reviewer thinks our study is rigorous.

Weaknesses: 

The image resolution and presentation of figures is a major issue in this study. As a nonexpert, it is nearly impossible to see the morphological changes as described in the results. Quantification of all cell biological phenotypes is also lacking therefore reducing the impact of this study to those familiar with tissue fusion events in Drosophila development. 

In the revised version, we have improved the image presentation and resolution. For all the images with more than two channels, we included single-channel images, changed the green color to lime and the red to magenta, highlighted the testis (TE) and seminal vescicles to make morphological changes more visible.  

We had quantification for marker gene expression in the original version, and now also included quantification for cell biological phenotypes which are generally with 100% penetrance.  

Reviewer #2 (Public review): 

Strengths: 

Wang and colleagues successfully uncovered an important function of the Drosophila PRDM16/PRDM3 homolog Hamlet (Ham) - a PR domain-containing transcription factor with known roles in the nervous system in Drosophila. To do so, they generated and analyzed new mutants lacking the PR domain, and also employed diverse preexisting tools. In doing so, they made a fascinating discovery: They found that PR-domain containing isoforms of ham are crucial in the intriguing development of the fly genital tract. Wang and colleagues found three distinct roles of Ham: (1) specifying the position of the testis terminal epithelium within the testis, (2) allowing normal shaping and growth of the anlagen of the seminal vesicles and paragonia and (3) enabling the crucial epithelial fusion between the seminal vesicle and the testis terminal epithelium. The mutant blocks fusion even if the parts are positioned correctly. The last finding is especially important, as there are few models allowing one to dissect the molecular underpinnings of heterotypic epithelial fusion in development. Their data suggest that they found a master regulator of this collective cell behavior. Further, they identified some of the cell biological players downstream of Ham, like for example E-Cadherin and Crumbs. In a holistic approach, they performed RNAseq and intersected them with the CUT&TAG-method, to find a comprehensive list of downstream factors directly regulated by Ham. Their function in the fusion process was validated by a tissue-specific RNAi screen. Meticulously, Wang and colleagues performed multiplexed in situ hybridization and analyzed different mutants, to gain a first understanding of the most important downstream pathways they characterized, which are Wnt2 and Toll. 

This study pioneers a completely new system. It is a model for exploring a process crucial in morphogenesis across animal species, yet not well understood. Wang and colleagues not only identified a crucial regulator of heterotypic epithelial fusion but took on the considerable effort of meticulously pinning down functionally important downstream effectors by using many state-of-the-art methods. This is especially impressive, as the dissection of pupal genital discs before epithelial fusion is a time-consuming and difficult task. This promising work will be the foundation future studies build on, to further elucidate how this epithelial fusion works, for example on a cell biological and biomechanical level. 

We appreciate that the reviewer thinks our study is orginal and important.

Weaknesses: 

The developing testis-genital disc system has many moving parts. Myotube migration was previously shown to be crucial for testis shape. This means, that there is the potential of non-tissue autonomous defects upon knockdown of genes in the genital disc or the terminal epithelium, affecting myotube behavior which in turn affects fusion, as myotubes might create the first "bridge" bringing the epithelia together. The authors clearly showed that their driver tools do not cause expression in myoblasts/myotubes, but this does not exclude non-tissue autonomous defects in their RNAi screen. Nevertheless, this is outside the scope of this work. 

We thank the reviewer’s consideration of non-tissue autonomous defects upon gene knockdown. The driver, hamRSGal4, drives reporter gene expression mainly in the RS epithelia, but we did observe weak expression of the reporter in the myoblasts before they differentiate into myotubes. Thus, we could not rule out a non-tissue autonomou effect in the RNAi screen. So we now included a statement in the result, “Given that the hamRSGal4 driver is highly expressed in the TE and SV epithelia, we expect highly effective knockdown occurs only in these epithelial cells. However, hamRSGal4 also drives weak expression in the myoblasts before they differentiated into myotubes (Supplementary Fig. 5B), which may result in a non-tissue autonomous effect when knocking down the candidate genes expressed in myoblasts.”

However, one point that could be addressed in this study: the RNAseq and CUT&TAG experiments would profit from adding principal component analyses, elucidating similarities and differences of the diverse biological and technical replicates. 

Thanks for the suggestion. We now have included the PCA analyses in supplementary figure 6A-B and the corresponding description in the text. The PCA graphs validated the consistency between biological replicates of the RNA-seq samples. The Cut&Tag graphs confirm the consistency between the two biological replicates from the GFP samples, but show a higher variability between the w1118 replicates. Importantly, we only considered the overlapped peaks pulled by the GFP antibody from the ham_GFP genotype and the Ham antibody from the wildtype (w1118) sample as true Ham binding sites. 

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors): 

Major Concern: 

(1) The image resolution and presentation of figures (Figures 2, 5, 6, and 7) is a major issue in this study. As a non-expert, it is nearly impossible to see the morphological changes as described in the results. Images need to be captured at higher resolution and zoomed in with arrows denoting changes as described. Individual channels, particularly for intensity measurement need to be shown in black and white in addition to merged images. Images also need pseudo-colored for color-blind individuals (i.e. no red-green staining). 

The images were captured at a high resolution, but somehow the resolution was drammaticlly reduced in the BioRxiv PDF. We try to overcome this by directly submitting the PDF in the Elife submission system. In the revised version, we have included single-channel images, changed the green and red colors to lime and magenta for color blindness. We also highlighted the testis (TE) and seminal vescicle structures in the images to make morphological changes more visible.  

(2) The penetrance of morphological changes observed in RT development is also unclear and needs to be rigorously quantified for data in Figures 2, 5, and 7. 

We now included quantification for cell biological phenotypes which are generally with 100% penetrance. The percentage of the penetrance and the number of animals used are indicated in each corresponding image.  

Reviewer #2 (Recommendations for the authors): 

Major Points 

(1) Lines 193- 220 I would strongly suggest pointing out the obvious shape defects of the testes visible in Figure 2A ("Spheres" instead of "Spirals"). These are probably a direct consequence of a lack in the epithelial connection that myotubes require to migrate onto the testis (in a normal way) as depicted in the cartoons, allowing the testis to adopt a spiral shape through myotube-sculpting (Bischoff et al., 2021), further confirming the authors' findings! 

Good point. In the revised text, we have added more description of the testis shape defects and pointed out a potential contribution from compromised myotube migration.   

(2) Line 216: "Often separated from each other". Here it would be important to mention how often. If the authors cannot quantify that from existing data, I suggest carrying it out in adult/pharate adult genital tracts (if there is no strong survivor bias due to the lethality of stronger affected animals), as this is much easier than timing prepupae. This should be a quick and easy experiment. 

Because it is hard to tell whether the separation of the SV and TE was caused by developmental defects or sometimes could be due to technical issues (bad dissection), we now change the description to, “control animals always showed connected TE and SV, whereas ham mutant TE and SV tissues were either separated from each other, or appeared contacted but with the epithelial tubes being discontinuous (Fig. 2B).” Additionally, we quantified the disconnection phenotype, which is 100% penetrance in 18 mutant animals. This quantification is now included in the figure. 

(3) Lines 289-305, Figure 3. I could only find how many replicates were analyzed in the RNAseq/CUT&Tag experiments in the Material & Methods section. I would add that at least in the figure legends, and perhaps even in the main text. Most importantly, I would add a Principal Component Analysis (one for RNAseq and one for the CUT&TAG experiment), to demonstrate the similarity of biological replicates (3x RNaseq, 4x Cut&Tag) but also of the technical replicates (RNAseq: wt & wt/dg, ham/ham & ham/df, GD & TE; CUT&TAG: Antibody & GFP-Antibody, TG&TE...). This should be very easy with the existing data, and clearly demonstrate similarities & differences in the different types of replicates and conditions. 

Principle component analysis and its description are now added to Supplementary Fig 6 and the main text respectively. 

(4) Line 321; Supplementary Table 1: In the table, I cannot find which genes are down- or upregulated - something that I think is very important. I would add that, and remove the "color" column, which does not add any useful information. 

In Supplementary table 1, the first sheet includes upregulated genes while the second sheet includes downregulated genes. We removed the column “color” as suggested.  

(5) Line 409: SCRINSHOT was carried out with candidate genes from the screen. One gene I could not find in that list was the potential microtubule-actin crosslinker shot. If shot knockdown caused a phenotype, then I would clearly mention and show it. If not, I would mention why a shot is important, nonetheless. 

shot is one of the candidate target genes selected from our RNA-seq and Cut&Tag data. However, in the RNAi screen, knocking down shot with the available RNAi lines did not cause any obvious phenotype. These could be due to inefficient RNAi knockdown or redundancy with other factors. We anyway wanted to examine shot expression pattern in the developing RS, give the important role of shot in epithelial fusion (Lee S., 2002). Using SCRINSHOT, we could detect epithelial-specific expression of shot, implying its potential function in this context. We now revised the text to clarify this point. 

Minor points 

(1) Cartoons in Figure 1: The cartoons look like they were inspired by the cartoon from Kozopas et al., 1998 Fig. 10 or Rothenbusch-Fender et al., 2016 Fig 1. I think the manuscript would greatly profit from better cartoons, that are closer to what the tissue really looks like (see Figure 1H, 2G), to allow people to understand the somewhat complicated architecture. The anlagen of the seminal vesicles/paragonia looks like a butterfly with a high columnar epithelium with a visible separation between paragonia/seminal vesicles (upper/lower "wing" of the "butterfly"). Descriptions like "unseparated" paragonia/seminal vesicle anlagen, would be much easier to understand if the cartoons would for example reflect this separation. It would even be better to add cartoons of the phenotypic classes too, and to put them right next to the micrographs. (Another nitpick with the cartoons: pigment cells are drastically larger and fewer in number (See: Bischoff et al., 2021 Figure 1E & MovieM1).) 

Thanks for the suggestion. We have updated Figure 1 by adding additional illustrations showing the accessory gland and seminal vesicle structures in the pupal stage and changing the size of pigment cells.

(2) Line 95-121 I would also briefly introduce PR domains, here. 

We have added a brief descripition of the PR domains.

(3) Line 152, 158, 160, 162. When first reading it, I was a bit confused by the usage of the word sensory organ. I would at least introduce that bristles are also known as external mechanosensory organs. 

We have now revised the description to “mechano-sensory organ”.

eg. Line 184, 194, and many more. Most times, the authors call testis muscle precursors "myoblasts". This is correct sometimes, but only when referring to the stage before myoblast-fusion, which takes place directly before epithelial fusion (28 h APF). Postmyoblast-fusion (eg. during migration onto the testis), these cells should be called myotubes or nascent myotubes, as the fly muscle community defined the term myoblast as the singlenuclei precursors to myotubes. 

We have now revised the description accordingly.  

(4) Line 217/Figure 2B. It looks like there is a myotube bridge between the testis and the genital disc. I would point that out if it's true. If the authors have a larger z-stack of this connection, I suggest creating an MIP, and checking if there are little clusters of two/three/four nuclei packed together. This would clearly show that the cells in between are indeed myotubes (granted that loss of ham does not introduce myoblast-fusion-defects). 

We do not have a Z-stack of this connection, and thus can not confirm whether the cells in this image are myotubes. However, we found that mytubes can migrate onto the testis and form the muscular sheet in the ham mutant despite reduced myotube density. At the junction there are myotubes, suggesting that loss of ham does not introduce myoblast-fusion defects. These results are now included in the revised manuscript, supplementary Fig. 5 C-D.

(5) Line 231/Supplementary Fig. 3C-G: I would add to the cartoons, where the different markers are expressed. 

We have added marker gene expression in the cartoons.

(6) Line 239. I don't see what Figure 1A/1H refers to, here. I would perhaps just remove it. 

Yes, we have removed it.

(7) Line 232. I would rephrase the beginning of the sentence to: Our data suggest Ham to be... 

Yes, we have revised it.

(8) Line 248-250/Figure 2F. Clonal analyses are great, but I think single channels should be shown in black and white. Also, a version without the white dashed line should be shown, to clearly see the differences between wt and ham-mutant cells. 

Now single channel images from the green and red images are presented in Supplementary Figures. This particular one is in Supplementary Figure 3B. 

(9) Line 490. The Toll-9 phenotype was identified on the sterility effect/lack-of-spermphenotype alone, and it was deduced, that this suggests connection defects. By showing the right focus plane in Fig S8B (lower right), it should be easy to directly show whether there is a connection defect or not. Also, one would expect clearer testis-shaping defects, like in ham-mutants, as a loss of connection should also affect myotube migration to shape the testis. This is just a minor point, as it only affects supplementary data with no larger impact on the overall findings, even if Toll-9 is shown not to have a defect, after all. 

We find that scoring defects at the junction site at the adult stage is difficult and may not be always accurate. Instead, we score the presence of sperms in the SV, which indirectly but firmly suggests successful connection between the TE and SV. We have now included a quantification graph, showing the penetrance of the phentoype in the new Supplementary Fig.14C. There were indeed morphological defects of TE in Toll-9 RNAi animals. We now included the image and quantification in the new Supplementary Fig.14B.

Author response:

The following is the authors’ response to the original reviews

Response to the public reviews:

We are very pleased to see these positive reviews of our preprint.

Reviewers 1 and 3 raise issues around PIP-PP1 interactions.

(1) Role of the “RVxF-ΦΦ-R-W string”

Most PIPs interact with the globular PP1 catalytic core through short linear interaction motifs (SLiMs) and Choy et al (PNAS 2014) previously showed that many PIPs interact with PP1 through conserved trio of SLiMs, RVxF-ΦΦ-R, which is also present in the Phactrs.

Previous structural analysis showed the trajectory of the PPP1R15A/B, Neurabin/Spinphilin (PPP1R9A/B), and PNUTS (PPP1R10) PIPs across the PP1 surface encompasses not only the RVxF-ΦΦ-R trio, but also additional sequences C-terminal to it (Chen et al, eLife, 2015). This extended trajectory is maintained in the Phactr1-PP1 complex (Fedoryshchak et al, eLife (2020). Based on structural alignment we proposed the existence of an additional hydrophobic “W” SLiM that interacts with the PP1 residues I133 and Y134.

The extended “RVxF-ΦΦ-R-W” interaction brings sequences C-terminal to the “W” SLiM into the vicinity of the hydrophobic groove that adjoins the PP1 catalytic centre. In the Phactr1/PP1 complex, these sequences remodel the groove, generating a novel pocket that facilitates sequence-specific substrate recognition.

This raises the possibility that sequences C-terminal to the extended “RVxF-ΦΦ-R-W string” in the other complexes also confer sequence-specific substrate recognition, and our study aims to test this hypothesis. Indeed, the hydrophobic groove structures of the Neurabin/Spinophilin/PP1 and Phactr1/PP1 complexes differ significantly (Ragusa et al, 2010; see Fedoryshchak et al 2020, Fig2 FigSupp1).

(2) Orientation of the W side chain

Reviewer 1 points out that in the substrate-bound PP1/PPP1R15A/Actin/eIF2 pre-dephosphorylation complex the W sidechain is inverted with respect to its orientation in  PP1-PPP1R15B complex (Yan et al, NSMB 2021). The authors proposed that this may reflect the role of actin in assembly of the quaternary complex. This does not necessarily invalidate the notion that sequences C-terminal to the “W” motif might play a role in actin-independent substrate recognition, and we therefore consider our inclusion of the R15A/B fusions in our analysis to be reasonable.

(3) Conservation of W

The motif ‘W’ does not mandate tryptophan - Phactrs and PPP1R15A/B indeed have W at this position but Neurabin/spinophilin contain VDP, which makes similar interactions. Similarly the “RVxF” motifs in Phactr1, Neurabin/Spinophilin, PPP1R15A/B and PNUTS are LIRF, KIKF, KV(R/T)F and TVTW respectively.

In our revision, we will present comparisons of the differentially remodelled/modified PP1 hydrophobic groove in the various complexes, discuss the different orientations of the tryptophan in the previously published PPP1R15A/PP1 and PPP1R15B/PP1 structures. We will also address the other issues raised by the referees.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Comments and suggestions for revisions

(1) The authors do not provide strong evidence that the interactions of the 'W' of the RVxF- øø -R-W string with the hydrophobic groove of PP1 is conserved in PIPs. Whereas the RVxF motif is well conserved and validated since its discovery in 1997, as are the øø - (an extension of the RVxF motif), and the 'R', the conservation of the Trp residue in the RVxF-øø-R-W string is not conserved.

We did not mean to imply that the W motif is conserved amongst all PIPs.

Most PIPs interact with the globular PP1 catalytic core through short linear interaction motifs (SLiMs). Choy et al (PNAS 2014) previously showed that many PIPs interact with PP1 through a conserved trio of SLiMs, RVxF-ΦΦ-R, which is also present in the Phactrs.

Previous structural analysis showed that the PPP1R15A/B, Neurabin/Spinophilin (PPP1R9A/B), and PNUTS (PPP1R10) PIPs share a trajectory across the PP1 surface that encompasses not only the RVxF-ΦΦ-R SLIMs, but also additional sequences C-terminal to the R SLIM (Chen et al, eLife, 2015). This trajectory is also shared by the Phactr1-PP1 complex (Fedoryshchak et al, eLife, 2020). Based on this structural alignment we proposed the existence of an additional hydrophobic “W” SLiM that interacts with the PP1 residues I133 and Y134 (See Fedoryshchak et al, 2020, Figure 1 figure supplement 2).

Introduction, paragraph 2 is rewritten to make this clearer.

The sequence and positions of W differ in amino acid type and position relative to the RVxF-øø-R string.

The motif ‘W’ does not mandate tryptophan, it is our name for a common structurally aligned motif: although the Phactrs and PPP1R15A/B indeed have W at this position, Neurabin and spinophilin contain VDP, which nevertheless makes similar interactions. Similarly the _“_RVxF” motifs in Phactr1, Neurabin/Spinophilin, PPP1R15A/B and PNUTS are LIRF, KIKF, KV(R/T)F and TVTW respectively.

In the Discussion the authors state that the hydrophobic groove of PP1 is remodelled by Neurabin. However, details of this are not described or shown in the manuscript.

The shared trajectory determined by the RVxF-øø-R-W string brings the sequences C-terminal to the W SLIM into the vicinity of the PP1 hydrophobic groove. In the Phactr1/PP1 holoenzyme this generates a novel pocket required for substrate recognition (Fedoryshchak et al, 2020). These observations raised the possibility that sequences C-terminal to the “W” motif in the other RVxF-øø-R-W PIPs also play a role in substrate recognition.

Introduction paragraph 3 now cites a new Figure 1-S2, which shows how the hydrophobic groove is remodelled in the various different PIP/PP1 complexes. A revised Figure 1A now indicates the hydrophobic residues defining the hydrophobic groove by grey shading.

(2) To add to the confidence of the structure, the authors should include a 2Fo-Fc simulated annealing omit map, perhaps showing the R and W interactions of the RVxF-øø-R-W string.

This is now included as new Figure 6 Figure supplement 1. Note that in Neurabin, the W motif is VDP, where the valine and proline sidechains interact similarly to the tryptophan (see also new Figure 1-S2G,H).

We also add a new supplementary Figure 6-S1 comparing our PBM-liganded Neurabin PDZ domain with the previously published unliganded structure (Ragusa et al 2010).

(3) Page 16. The authors state that spinophilin remodels the PP1 hydrophobic groove differently from Phactrs. Arguably spinophilin does not remodel the PP1 hydrophobic groove at all. There are no contacts between spinophilin and the PP1 hydrophobic groove in the spinophilin-PP1 structure, correlating with the absence of 'W" in the RVxF-øø-R-W string in spinophilin.

The VDP sequence corresponding to the W motif in spinophilin and neurabin makes analogous contacts to those made by the W in Phactr1 (see Fedoryshchak et al 2020).

Remodelling is meant in the sense of altering the structure of the major groove by bringing new sequences into its vicinity rather than necessarily directly interacting with it. The spinophilin/PP1 and Phactr/PP1 hydrophobic grooves are compared in new Figure 1-S2 (see also Fedoryshchak et al 2020, Figure 2 figure supplement 1)

(4) Page 8. For the cell-based/proteomics-dephosphorylation assay in Figure 2, it isn't clear why there were no dephosphorylation sites detected for the PPP1R15A/B-PP1 fusion (except PPP6R1 S531 for PPP1R15B). One might have expected a correlation with PP1 alone. Does this imply that PPP1R15A/B are inhibiting PP1 catalytic activity? Was the activity tested in vitro?

The R15A/B data are compared to average abundance of all the phosphosites in the dataset, including those of PP1.

We have not tested for a general inhibitory effect of R15A/B on PP1 activity. Many PIPs including R15A/B do occlude one or more of the PP1 substrate groove and therefore generally act as inhibitors of PP1 activity against some potential substrates, while enhancing activities against others.

Other points 

(4) Figure S1: Colour sequence similarities/identities.

Done

(6) Figures: Structure figures lacked labels:

Figure 1A, label PP1, Phactrs etc.

Done

Figure 6, label PP1, Neurabin, previous Neurabin structure (Fig. 6C), hydrophobic groove, PDZ domain, etc.

Done

(7) Statistical analysis. p values should be shown for data in:

Figure 5.

To avoid cluttering the Figure, a new sheet, “statistical significance” has been added to Supplementary Table 3, summarizing the analysis.

Figure 1.

Figure amended (now figure 1-S1).

(8) Some inconsistency with labels, eg '34-WT' used in Fig. 5C, whereas '34A-WT' (better) in Methods.

Now changed to 34A etc where used.

(9) Page 6. PPP1R9A/B is not shown in Figure 1A and Figure S1A.

PPP1R9A/B are Neurabin and spinophilin - now clarified in Introduction paragraph 2, Results paragraph 1, Discussion paragraph 1.

(10) Page 7: lines 4, 'site' not 'side'.

Done

(11) Page 9: DTL and CAMSAP3 were found to be dephosphorylated in the PP1-Neurabin/spinophilin screen. Are these PDZ-binding proteins?

Neither DTL nor CAMSAP3 contain C-terminal hydrophobic residues characteristic of classical PBMs. Sentence added in Discussion, paragraph 5

(12) Page 12 and Figure 5 and S5: The synthetic p4E-BP1 and IRSp53WT peptides with PBM should be given more specific names to indicate the presence of the PBM.

We have renamed 4E-BP1^WT and IRSp53^WT to 4E-BP1^PBM and  IRSp53^PBM respectively, emphasising the inclusion of the wildtype or mutated PBM from 4E-BP1 on these peptides.

Text, Figure 5, and Figure S5 all revised accordingly.

(13) Give PDB code for spinophilin-PP1 complex coordinates shown in Figure 6C.

PDB codes for the various PIP/PP1 complexes now given in new Figure 1-S2 and revised Figure 6C.

Reviewer #2 (Recommendations for the authors):

The work undertaken by the authors is extensive and robust, however, I believe that some improvement in the writing and some detailed explanation of certain results sections would help with the presentation of the work and clarity for the readers.

(1) The introduction should contain more information about the interaction between PP1 and Neurabin, given that this is the focus of the paper. This would give the reader the necessary background required to follow the paper.

Introduction paragraph 2 revised to describe the different SLIMs in more detail. New Figure 1-S2 shows detail of the different remodelled hydrophobic grooves in the various PIP/PP1 complexes.

(2) More information on PP1-IRSp53L460A has to be added before discussing results in S1B.

Sentence explaining that IRSp53 L460 docks with the remodelled PP1 hydrophobic groove in the Phactr1/PP1 holoenzyme added in Results paragraph 2.

(3) Page 6: "as expected, the +5 residue L460A mutation, which impairs dephosphorylation by the intact Phactr1/PP1 holoenzyme, impaired sensitivity to all the fusions, indicating that they recognise phosphorylated IRSp53 in a similar way (Figure S1B)". Statistics between IRSp53 and IRSp53L460A across PP1-PIPs need to be conducted before concluding the above. From the graph and the images, the impairment to dephosphorylation is not convincing.

For each of the four PP1-Phactr fusions, the IRSp53 L460A peptide shows significantly less reactivity than the IRSp53WT peptide (p<0.05 for each fusion).

Since the proteomics studes in Figure 2 show that the substrate specificity of the four PP1-Phactr1 fusions is virtually identical, we combined the data for the four different fusions. The IRSp53 L460A peptide shows significantly less reactivity than the IRSp53WT peptide in this analysis (p< 0.0001). This result shown in revised Figure S1B and legend.

(4) mCherry-4E-BP1(118+A), in which an additional C-terminal alanine should still allow TOSmediated phosphorylation, but prevent PDZ interaction. Does 4EBP1 (118+A) actually prevent interaction between PP1-Neurabin? This interaction needs to be validated, especially since spinophilin was shown to bind to multiple regions of PP1.

It is not clear what the referee is asking for here. The biochemical analysis in Figure 4C shows that the C-terminus of 4E-BP1 constitutes a classical PBM. The X-ray crystallography in Figure 6 confirms this, demonstrating H-bond interactions between the 4E-BP1 C-terminal carboxylate and main chain amides of L514, G515 and I516.

We consider the possibility that the 4E-BP1(118+A) mutant inhibits the activity of PP1-neurabin via a mechanism other than direct blocking 4E-BP1 / PDZ interaction to be unlikely for the following reasons:

(1) Addition of a C-terminal alanine will disrupt the PBM interaction because the extra residue sterically blocks access to the PBM-binding groove. This is the most parsimonious explanation, and is based on our solid structural and biochemical evidence that the 4E-BP1 C-terminus is a classical PBM.

(2) Alphafold3 modelling predicts Neurabin PDZ / 4E-BP1 PBM interaction with high confidence (shown in Figure 6-S2E), but it does not predict any PDZ interaction with 4E-BP1(118+A). Note added in Figure 6-S2 legend.

(3) Recognition of the 4E-BP1(118+A) mutation without loss of binding affinity would require that the mutant becapable of binding formally equivalent to recognition of an “internal” PDZ-binding peptide. Recognition of such “internal peptides” is dependent on their adopting a specifically constrained conformation, which typically requires reorganisation of the PDZ carboxylate-binding GLGF loop. Such “internal site” recognition typically involves more than one residue C-terminal to the conventional PDZ “0” position (see Penkert et al NSMB 2004, doi:10.1038/nsmb839; Gee et al JBC 1998, DOI: 10.1074/jbc.273.34.21980; Hillier et al 1999, Science PMID: 10221915).

(5) It is nice to see that the various PP1-Phactr fusions have around 60% substrate overlap between them. Would it be possible to compare these results with previously published mass spec data of Phactr1XXX from the group? There is mention of some substrates being picked up, but a comparison much like in Figure 2E would be more informative about the extent to which the described method captures relevant information.

This is difficult to do directly as the PP1-Phactr fusion data are from human cells while that in Fedoryshchak et al 2020 is from mouse.

However, manual curation shows that of the 28 top hits seen in our previous analysis of Phactr1XXX in NIH3T3 cells, 18 were also detectable in the HEK293 system; of these, 13 were also detected as as PP1-Phactr fusion hits. Data summarised in new Figure 2-S1C. Text amended in Results, “Proteomic analysis...”, paragraph 2.

(6) Figure 3D Why are the levels of pT70, pT37/46 and total protein in vector controls much lower as compared to 0nM Tet in PP1-Neurabin conditions? It is also weird that given total protein is so low, why are the pS65/101 levels high compared to the rest?

We think it likely these phenomena reflect a low level expression of PP1-Neurabin expression in uninduced cells. Now noted in Figure 3D legend, basal PP1-Neurabin expression shown in new Figure 3-S1C. This alters the relative levels of the different species detected by the total 4E-BP1 antibody in favour of the faster migrating forms, which are less phosphorylated than the slower ones, and the total amount increases about 2-fold (Figure 3D, compare 0nM Tet lanes).

The altered p65/101-pT70 ratio is also likely to reflect the leaky PP1-Neurabin expression, since the relative intensities of the various phosphorylated species are dependent on both the relative rates of phosphorylation and dephosphorylation. Expression of a phosphatase would therefore be expected to differentially affect the phosphorlyation levels of different sites according to their reactivity.

(7) Figure 3E: Does inhibiting mTORC further reduce translation when PP1-Neurabin is expressed? If this is the case, this might suggest that they might not necessarily be mTORC inhibitors?

We have not done this experiment. Since Rapamycin cannot be guaranteed to completely block 4E-BP1 phosphorylation, and PP1-Neurabin cannot be guaranteed to completely dephosphorylate 4E-BP1, any further reduction upon their combination would be hard to interpret.

(8) Substrate interactions with the remodelled PP1 hydrophobic groove do not affect PP1-Neurabin specificity. Is there evidence that PP1-Neurabin remodels the hydrophobic groove? Is it not possible that Neurabin does not remodel the PP1 groove to begin with and hence there is no effect observed with the various mutants? If this is not the case, it should be explained in a bit more detail.

Comparison of the Neurabin/PP1 and Phactr1/PP1 structures shows that the hydrophobic groove is remodelled differently in the two complexes. Now shown in new Figure 1-S2B,C,G.

(9) Figure 5B has a lot of interesting information, which I believe has not been discussed at all in the results section.

To help interpretation of the enzymology in Figure 5 we have renamed 4E-BP1WT and IRSp53WT to 4E-BP1PBM and IRSp53PBM respectively, emphasising the inclusion of the wildtype or mutated PBM from 4E-BP1 on these peptides. Text in Results, “PDZ domain interaction…”, paragraph 1, and Figures 5 and S5 revised accordingly.

Why does the 4E-BP1Mut affect catalytic efficiency of PP1 alone when compared with WT, while no difference is observed with IRSp53WT and mutant?

We do not understand the basis for the differential reactivity of 4E-BP1PBM and 4E-BP1MUT with PP1 alone; we suspect that it reflects the hydrophobicity change resulting from the MDI -> SGS substitution. However this is unlikely to be biologically significant as PP1 is sequestered in PIP-PP1 complexes.

Importantly, the two PP1 fusion proteins behave consistently in this assay – the presence of the intact PBM increases reactivity with PP1-Neurabin, but has no effect on dephosphorylation by PP1-Phactr1.

Why does PP1 alone not have a difference between IRSp53WT and mutant, while PP1-Neurabin does have a difference?

This is due to the presence of the PBM in IRSp53WT (now renamed IRSp53PBM), which affects increases affinity for PP1 Neurabin, but not PP1 alone. Likewise, PP1-Phactr1, which does not possess a PDZ domain, is also unaffected by the integrity of the PBM.

(7) “Strikingly, alanine substitutions at +1 and +2 in 4E-BP1WT increased catalytic efficiency by both fusions, perhaps reflecting changes at the catalytic site itself (Figure 5E, Figure S5E)”. This could be expanded upon, because this suggests a mechanism that makes the substrate refractory to PDZ/hydrophobic groove remodelling?

We favour the idea that this reflects a requirement to balance dephosphorylation rates between the multiple 4E-BP1 phosphorylation sites, especially if multiple rounds of dephosphorylation occur for each PBM—PDZ interaction. Additional sentences added in Discussion paragraph 7.

(8) Typographical errors and minor comments:

a) PIPs can target PP1 to specific subcellular locations, and control substrate specificity through autonomous substrate-binding domains, occupation or extension of the substrate grooves, or modification of PP1 surface electrostatics.

b) Phosphophorylation side site abundances within triplicate samples from the same cell line were comparable between replicates (Figure 2B).

c) While the alanine substitutions had little effect, conversion of +4 to +6 to the IRSp534E-BP1 sequence LLD increased catalytic efficiency some 20-fold (Figure 5C, Figure S5C). 

d) Figure 3E labels are not clear. The graph can be widened to make the labels of the conditions clearer.

All corrected

Reviewer #3 (Recommendations for the authors):

This was a very well-written manuscript.

However, I was looking for a summary mechanistic figure or cartoon to help me navigate the results.

I noted a few typos in the text.

New summary Figure 5-S2 added, cited in results, and discussed in Discussion paragraph 6,7.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This article presents a meta-analysis that challenges established abundance-occupancy relationships (AORs) by utilizing the largest known bird observation database. The analysis yields contentious outcomes, raising the question of whether these findings could potentially refute AORs.

We thank the Reviewer for their positive comments.

Strengths:

The study employed an extensive aggregation of datasets to date to scrutinize the abundance-occupancy relationships (AORs).

We thank the Reviewer for their positive comments.

Weaknesses:

While the dataset employed in this research holds promise, a rigorous justification of the core assumptions underpinning the analytical framework is inadequate. The authors should thoroughly address the correlation between checklist data and global range data, ensuring that the foundational assumptions and potential confounding factors are explicitly examined and articulated within the study's context.

We thank the Reviewer for these comments. We agree that more justification and transparency is needed of the core assumptions that form the foundation of our methods. In our revised version, we have taken the following steps to achieve this:

- Altered the title to be more explicit about the core assumptions, which now reads: “Local-scale relative abundance is decoupled from global range size”

- We have added more details on why and how we treat global range size as a measure of ‘occupancy.’

- We have added a section that discusses the limitations of using eBird relative abundance

Reviewer #2 (Public Review):

Summary:

The goal is to ask if common species when studied across their range tend to have larger ranges in total. To do this the authors examined a very large citizen science database which gives estimates of numbers, and correlated that with the total range size, available from Birdlife. The average correlation is positive but close to zero, and the distribution around zero is also narrow, leading to the conclusion that, even if applicable in some cases, there is no evidence for consistent trends in one or other direction.

We thank the Reviewer for these comments.

Strengths:

The study raises a dormant question, with a large dataset.

We thank the Reviewer for these comments. We intended to take a longstanding question and attempt to apply novel datasets that were not available mere decades ago. While we do not imply that we have ‘solved’ the question, we hope this work highlights the potential for further interrogation using these large datasets.

Weaknesses:

This study combines information from across the whole world, with many different habitats, taxa, and observations, which surely leads to a quite heterogeneous collection.

We agree that there is a heterogeneous collection of data across many habitats, taxa, and observations. However, rather than as a weakness, we see this as a significant strength. Our work assumes we are averaging over this variability to assess for a large-scale pattern in the relationship - something that was potentially a limitation of previous work, as these large datasets were often focused on particular contexts (e.g., much work focused solely on the UK), which we believe could limit some of the generalizability of the previous work. However, the reviewer makes a fair point in regard to the heterogeneity of data collection. We have now added some text in the discussion which is explicit about this - see the new section named “Potential limitations of current work and future work –-although our findings challenge some long-held assumptions about the consistency of the abundance-occupancy relationship, our work only deals with interspecific AORs among birds, synthesizing observations of potentially heterogeneous locations, context and quality”.

First, scale. Many of the earlier analyses were within smaller areas, and for example, ranges are not obviously bounded by a physical barrier. I assume this study is only looking at breeding ranges; that should be stated, as 40% of all bird species migrate, and winter limitation of populations is important. Also are abundances only breeding abundances or are they measured through the year? Are alien distributions removed?

Second, consider various reasons why abundance and range size may be correlated (sometimes positively and sometimes negatively) at large scales. Combining studies across such a large diversity of ecological situations seems to create many possibilities to miss interesting patterns. For example:

(1) Islands are small and often show density release.

See comment below.

(2) North temperate regions have large ranges (Rapoport's rule) and higher population sizes than the tropics.

See comment below.

(3) Body size correlates with global range size (I am unsure if this has recently been tested but is present in older papers) and with density. For example, cosmopolitan species (barn owl, osprey, peregrine) are relatively large and relatively rare.

See comment below.

(4) In the consideration of alien species, it certainly looks to me as if the law is followed, with pigeon, starling, and sparrow both common and widely distributed. I guess one needs to make some sort of statement about anthropogenic influences, given the dramatic changes in both populations and environments over the past 50 years.

See comment below. We also added a sentence in the methods that highlighted we did not remove alien ranges and provided reasons why. Still, we do acknowledge the dramatic changes in populations and environments over the past 50 years (see the new section  “Potential limitations of current work and futur work”)

(5) Wing shape correlates with ecological niche and range size (e.g. White, American Naturalist). Aerial foraging species with pointed wings are likely to be easily detected, and several have large ranges reflecting dispersal (e.g. barn swallow).

We agree that all of the points above are interesting data explorations. As said above, our main purpose was to highlight the potential for further interrogation using these large datasets. However, we have added some additional text in the discussion that explicitly mentions/encourages these additional data explorations. We hope people will pick up on the potential for these data and explore them further.

Third, biases. I am not conversant with ebird methodology, but the number appearing on checklists seems a very poor estimate of local abundance. As noted in the paper, common species may be underestimated in their abundance. Flocking species must generate large numbers, skulking species few. The survey is often likely to be in areas favorable to some species and not others. The alternative approach in the paper comes from an earlier study, based on ebird but then creating densities within grids and surely comes with similar issues.

We agree that if we were interested in the absolute abundance of a given species, the local number on an eBird checklist would be a poor representation. However, our study aims not to estimate absolute abundance but to examine relative abundance among species on each checklist. By focusing on relative abundance, we leverage eBird data's strengths in detecting the presence and frequency of species across diverse locations and times, thereby capturing community composition trends that can provide meaningful insights despite individual checklist biases. This approach allows us to assess the comparative prominence of species in the community as reported by the observer, providing a consistent metric of relative abundance. Despite detectability biases, the structure of eBird checklists reflects the observer’s encounter rates with each species under similar conditions, offering a valuable snapshot of relative species composition across sites and times. The key to our assumption is that these biases discussed are not directional and, therefore, random throughout the sampling process, which would translate to no ‘real’ bias in our effect size of interest.

Range biases are also present. Notably, tropical mountain-occupying species have range sizes overestimated because holes in the range are not generally accounted for (Ocampo-Peñuela et al., Nature Communications). These species are often quite rare, too.

We thanks the reviewer for pointing to this issue and reference. We included a discussion on these biases in our limitations section and reference Ocampo-Peñuela et al. to emphasize the need for improved spatial resolution in range data for more accurate AOR assessments.”More precise range-size estimates would also improve the accuracy of AOR assessments, since species range data are often overestimated due to the failure to capture gaps in actual distributions ”

Fourth, random error. Random error in ebird assessments is likely to be large, with differences among observers, seasons, days, and weather (e.g. Callaghan et al. 2021, PNAS). Range sizes also come with many errors, which is why occupancy is usually seen as the more appropriate measure.

If we consider both range and abundance measurements to be subject to random error in any one species list, then the removal of all these errors will surely increase the correlation for that list (the covariance shouldn't change but the variances will decrease). I think (but am not sure) that this will affect the mean correlation because more of the positive correlations appear 'real' given the overall mean is positive. It will definitely affect the variance of the correlations; the low variance is one of the main points in the paper. A high variance would point to the operation of multiple mechanisms, some perhaps producing negative correlations (Blackburn et al. 2006).

We agree random errors can affect estimates, but as we wrote above, random errors, regardless of magnitudes, would not bias estimates. After accounting for sampling error (a part of random errors), little variance is left to be explained as we have shown in the MS. This suggests that many of the random errors were part of the sampling errors. And this is where meta-analysis really shines.

On P.80 it is stated: "Specifically, we can quantify how AOR will change in relation to increases in species richness and sampling duration, both of which are predicted to reduce the magnitude of AORs" I haven't checked the references that make this statement, but intuitively the opposite is expected? More species and longer durations should both increase the accuracy of the estimate, so removing them introduces more error? Perhaps dividing by an uncertain estimate introduces more error anyway. At any rate, the authors should explain the quoted statement in this paper.

It would be of considerable interest to look at the extreme negative and extreme positive correlations: do they make any biological sense?

Extremely high correlations would not make any biological sense if these observations were based on large sample sizes. However, as shown in Figure 2, all extreme correlations come from small sample sizes (i.e., low precision), as sampling theory expects (actually our Fig 2 a text-book example of the funnel shape). Therefore, we do not need to invoke any biological explanations here.

Discussion:

I can see how publication bias can affect meta-analyses (addressed in the Gaston et al. 2006 paper) but less easily see how confirmation bias can. It seems to me that some of the points made above must explain the difference between this study and Blackburn et al. 2006's strong result.

We agree. Now, we extended an explanation of why confirmation bias could result in positive AOR. Yet, we point out confirmation bias is a very common phenomena which we cite relevant citations in the original MS. The only way to avoid confirmation bias is to conduct a study blind but this is not often possible in ecological work.

“Meta-research on behavioural ecology identified 79 studies on nestmate recognition, 23 of which were conducted blind. Non-blind studies confirmed a hypothesis of no aggression towards nestmates nearly three times more often. It is possible that confirmation bias was at play in earlier AOR studies.”

Certainly, AOR really does seem to be present in at least some cases (e.g. British breeding birds) and a discussion of individual cases would be valuable. Previous studies have also noted that there are at least some negative and some non-significant associations, and understanding the underlying causes is of great interest (e.g. Kotiaho et al. Biology Letters).

We agree. And yes, we pointed out these in our introduction.

Reviewer #3 (Public Review):

Summary:

This paper claims to overturn the longstanding abundance occupancy relationship.

Strengths:

(1) The above would be important if true.

(2) The dataset is large.

We have clarified this point by changing the title to emphasize that we do not suggest overturning AORs entirely but instead provide a refined view of the relationship at a global scale. Our results suggest a weaker and more context-dependent AOR than previously documented. We hope our revised title and additional clarifications in the text convey our intent to contribute to a more nuanced understanding rather than a whole overturning of the AOR framework.

Weaknesses:

(1) The authors are not really measuring the abundance-occupancy relationship (AOR). They are measuring abundance-range size. The AOR typically measures patches in a metapopulation, i.e. at a local scale. Range size is not an interchangeable notion with local occupancy.

We have refined this in our revision to be more explicitly focused on global range size. However, we note that the classic paper by Bock and Richlefs (1983, Am Nat) also refers to global (species entire) range size in the context of the AOR. Importantly, Bock and Richlefs pointed out the importance of using species’ entire ranges; without such uses, there will be sampling artifacts creating positive AORs when using arbitrary geographical ranges, which were used in some studies of AORs. So we highlight that our work is well in line with the previous work, allowing us to question the longstanding macroecological work. One of the issues of AOR has been how to define occupancy and global range size, which provides a relatively ambiguous measure, which is why we used this measure.

(2) Ebird is a poor dataset for this. The sampling unit is non-standard. So abundance can at best be estimated by controlling for sampling effort. Comparisons across space are also likely to be highly heterogenous. They also threw out checklists in which abundances were too high to be estimated (reported as "X"). As evidence of the biases in using eBird for this pattern, the North American Breeding Bird Survey, a very similar taxonomic and geographic scope but with a consistent sampling protocol across space does show clear support for the AOR.

Yes, we agree the sampling unit is non-standard. However, this is a significant strength in that it samples across much heterogeneity (as discussed in response to Reviewer 2, above). We were interested in relative abundance and not direct absolute abundance per se, which is accurate, especially since we did control for sampling effort.

We appreciate the reviewer’s attention to our data selection criteria. We excluded checklists containing ‘X’ entries to minimize biases in our abundance estimates. The 'X' notation is often used for the most common species, reflecting the observer's identification of presence without specifying a count. This approach was chosen to avoid disproportionately inflating presence data for these abundant species, which could distort the relative abundance calculations in our analysis. By excluding such checklists, we aimed to retain consistency and ensure that local abundance estimates were representative across all species on each checklist. We have revised our manuscript to clarify this methodological choice and hope this explanation addresses the reviewer’s concern. We modified our text in the methods to make the entries ‘X’ clearer (see the Method section).

(3) In general, I wonder if a pattern demonstrated in thousands of data sets can be overturned by findings in one data set. It may be a big dataset but any biases in the dataset are repeated across all of those observations.

Overturning a major conclusion requires careful work. This paper did not rise to this level.

We appreciate the reviewer’s caution regarding broad conclusions based on a single dataset, even one as large as eBird. Our intention was not to definitively overturn the abundance-occupancy relationship (AOR) but to re-evaluate it with the most extensive and globally representative dataset currently available. We recognise that potential biases in citizen science data, such as observer variation, may influence our findings, and we have taken steps to address these in our methodology and limitations sections. We see this work as a contribution to an ongoing discourse, suggesting that AOR may be less universally consistent than previously believed, mainly when tested with large-scale citizen science data. We hope this study will encourage additional research that tests AORs using other expansive datasets and approaches, further refining our understanding of this classic macroecological relationship. However, we have left our broad message about instigating credible revolution and also re-examining ecological laws.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The investigation focuses solely on interspecific relationships among birds; thus, the extrapolation of these conclusions to broader ecological contexts requires further validation.

We have now added this point to our new section: “Although our findings challenge some long-held assumptions about the consistency of the abundance-occupancy relationship, our work only deals with interspecific AORs among birds, so we hope this work serves as a foundation for further investigations that utilize such comprehensive datasets.”

(2) The rationale for combining data from eBird - a platform predominantly representing individual observations from urban North America - with the more globally comprehensive BirdLife International database needs to be substantiated. The potential underrepresentation of global abundance in the eBird checklist data could introduce a sampling bias, undermining the foundational premises of AORs.

We agree with the limitation of ebird sampling coverage, but it should not bias our results. In statistical definitions, bias is directional, and if not directional, it will become statistical noise, making it difficult to detect the signal. In fact, our meta-analyses adjust what statisticians call sampling bias and it is the strength of meta-analysis.

(3) In the full mixed-effect model, checklist duration and sampling variance (inversely proportional to sample size N) are treated as fixed effects. However, these variables are likely to be negatively correlated, which could introduce multicollinearity, inflating standard errors and diminishing the statistical significance of other factors, such as the intercept. This calls into question the interpretation of insignificance in the results.

Multicollinearity is an issue with sample sizes. For example, with small datasets, correlations of 0.5 could be an issue, and such an issue would usually show up as a large SE. We do not have such an issue with ~ 17 million data points. Please refer to this paper.

Freckleton, Robert P. "Dealing with collinearity in behavioural and ecological data: model averaging and the problems of measurement error." Behavioral Ecology and Sociobiology 65 (2011): 91-101.

(4) The observed low heterogeneity may stem from discrepancies in sampling for abundance versus occupancy, compounded by uncertainties in reporting behavior.

If we assume everybody underreports common species or overreports rare species, this could happen. However, such an assumption is unlikely. If some people report accurately (but not others), we should see high heterogeneity, which we do not observe).  We have touched upon this point in our original MS.

(5) The contribution and implementation of phylogenetic comparative analysis remain ambiguous and were not sufficiently clarified within the study.

We need to add more explanation for the global abundance analysis

“To statistically test whether there was an effect of abundance and occupancy at the macro-scale, we used phylogenetic comparative analysis.  This analysis also addresses the issue of positive interspecific AORs potentially arising from not accounting for phylogenetic relatedness among species examined ”

(6) The use of large N checklists could skew the perceived rarity or commonality of species, potentially diminishing the positive correlation observed in AORs. A consistent observer effect could lead to a near-zero effect with high precision.

Regardless of the number of N species in checklists (seen in Fig 2), correlations are distributed around zero. This means there is nothing special about large N checklists. 

(7) The study should acknowledge and discuss any discrepancies or deviations from previous literature or expected outcomes.

We felt we had already done this as we discussed the previous meta-analysis and what we expected from this meta-analysis.  Nevertheless, we have added some relevant sentences in the new version of MS.

In addition to these major points, there are several minor concerns:

(1) Figure 2B lacks discussion, and the metric for the number of observations is not clarified. Furthermore, the labeling of the y-axis appears to be incorrect.

Thank you very much for pointing out this shortcoming. Now, the y-axis label has been fixed and we mention 2B in the main text.

(2) The study should provide a clear, mathematical expression of the multilevel random effect models for greater transparency.

Many thanks for this point, and now we have added relevant mathematical expressions in Table S6.

(3) On Line 260, the term "number of species" should be refined to "number of species in a checklist," ideally represented by a formula for precision.

This ambiguity has been mended as suggested.

Please provide the data and R code linked to the outputs.

The referee must have missed the link (https://github.com/itchyshin/AORs) in our original MS. In addition to our GitHub repository link, we now have added a link to our Zenodo repository (https://doi.org/10.5281/zenodo.14019900).

Reviewer #3 (Recommendations For The Authors):

The authors cite Rabinowitz's 7 forms of rarity paper as a suggestion that previous findings also break the AOR. In fact empirical studies of the 7 forms of rarity typically find that all three forms of rareness vs commonness are heavily correlated (e.g. Yu & Dobson 2000).

We thank the reviewer for drawing attention to Yu & Dobson (2000) and similar studies that find positive correlations among the axes of rarity. Ref 3 is correct in that Rabinowitz’s (1981) framework does not require that local abundance and geographic range size be uncorrelated for every species; instead, it highlights conceptual scenarios where a species may be common locally yet have a restricted distribution (or vice versa).

Empirical analyses such as Yu & Dobson (2000) show that, on average, these axes can be correlated, which may align with conventional AOR findings in some taxonomic groups. However, Rabinowitz’s key insight was that exceptions do occur, so these exceptions demonstrate that strong positive AORs may not be universally applicable. Our results do not claim that Rabinowitz’s framework “breaks” the AOR outright; instead, we use it to underscore that local abundance can, in principle, be “decoupled” from global occupancy.  Whether the correlation found by Yu & Dobson (2000) implies a positive AOR, requires a detailed simulation study, which is an interesting avenue for future research. 

Thus, citing Rabinowitz serves to highlight the potential heterogeneity and complexity of abundance–occupancy relationships rather than to refute every positive correlation reported in the literature. Our findings suggest that when examined at large spatiotemporal scales (with unbiased sampling), the overall AOR signal may be less robust than traditionally believed. This is consistent with Rabinowitz’s view that local abundance and global range can vary along independent axes. Now we added

“Although studies using her framework found positive correlations between species range and local abundance.”

Author response:

The following is the authors’ response to the original reviews

Reviewer #1:

Summary:

This manuscript uses a well-validated behavioral estimation task to investigate how optimistic belief updating was attenuated during the 2020 global pandemic. Online participants recruited during and outside of the pandemic estimated how likely different negative life events were to happen to them in the future and were given statistics about these events happening. Belief updating (measured as the degree to which estimations changed after viewing the statistics) was less optimistically biased during the pandemic (compared to outside of it). This resulted from reduced updating from "good news" (better than expected information). Computational models were used to try to unpack how statistics were integrated and used to revise beliefs. Two families of models were compared - an RL set of models where "estimation errors" (analogous to prediction errors in classic RL models) predict belief change and a Bayesian set of models where an implied likelihood ratio was calculated (derived from participants estimations of their own risk and estimation of the base rate risk) and used to predict belief change. The authors found evidence that the former set of models accounted for updating better outside of the pandemic, but the latter accounted for updating during the pandemic. In addition, the RL model provides evidence that learning was asymmetrically positively biased outside of the pandemic but symmetric during it (as a result of reduced learning rates from good news estimation errors).

Strengths:

Understanding whether biases in learning are fixed modes of information processing or flexible and adapt in response to environmental shocks (like a global pandemic or economic recession) is an important area of research relevant to a wide range of fields, including cognitive psychology, behavioral economics, and computational psychiatry. The study uses a well-validated task, and the authors conduct a power analysis to show that the sample sizes are appropriate. Furthermore, the authors test that their results hold in both a between-group analysis (the focus of the main paper) and a within-group analysis (mainly in the supplemental).

The finding that optimistic biases are reduced in response to acute stress, perceived threat, and depression has been shown before using this task both in the lab (social stress manipulation), in the real world (firefighters on duty), and clinical groups (patients with depression). However, the work does extend these findings here in important ways:

(1) Examining the effect of a new real-world adverse event (the pandemic).<br /> (2) The reduction in optimistic updating here arises due to reduced updating from positive information (previously, in the case of environmental threat, this reduction mainly arose from increased sensitivity to negative information).<br /> (3) Leveraging new RL-inspired computational approaches, demonstrating that the bias - and its attenuation - can be captured using trial-by-trial computational modeling with separate learning rates for positive and negative estimation errors.

Weaknesses:

Some interpretation and analysis (the computational modeling in particular) could be improved.

On the interpretation side, while the pandemic was an adverse experience and stressful for many people (including myself), the absence of any measures of stress/threat levels limits the conclusions one can draw. Past work that has used this task to examine belief updating in response to adverse environmental events took physiological (e.g., SCR, cortisol) and/or self-report (questionnaires) measures of mood. In SI Table 1, the authors possibly had some questionnaire measures along these lines, but this might be for the participants tested during the pandemic.

Thank you for this review.

We agree that the lack of physiological and self-report measures of stress, threat, and perceived uncertainty limits the interpretation of findings regarding potential psychological factors. Some self-reported anxiety and perceived risk measures experienced during the lockdowns were collected in a subset of participants (n=40, counting n=21 tested before and during the 1st strict lockdown, and n=19 tested solely during the 1st lockdown). These reports were given retrospectively at the time of release of the 1st lockdown in summer 2020 when the pandemic was still unfolding (SI Table 1).

Exploratory correlations revealed some noteworthy trends. We found that participants who reported to have perceived a bigger risk of death due to contagion were also those who were less optimistically biased when updating their beliefs about adverse future life risks during the first strict COVID-19-related lockdown (Pearson’s r = -0.36, p = 0.02).

Moreover, parameter estimates from the computational models of belief updating showed associations with specific survey responses: The rational Bayesian model’s scaling parameter correlated positively with adherence to distancing measures (r = 0.41, p = 0.01) and negatively with the need for social contact (r = -0.37, p = 0.02). This result indicated that participants who were updating their beliefs faster were more likely to follow preventive guidelines and felt less social craving. Meanwhile, the asymmetry parameter correlated negatively with mask wearing (r = -0.41, p = 0.01), positively with physical contact with close others (r = 0.32, p = 0.04) and satisfaction with social interactions (r = 0.33, p = 0.04). This suggests that participants who displayed some asymmetry in belief updating during the COVID-19 pandemic were less likely to comply with mask-wearing rules and more likely to engage in social interactions.

However, these results did not survive correction for multiple comparisons and the sample size for correlational analyses is in the lower range. The subjective measures of anxiety and fear of contagion did not significantly correlate to the updating bias, or any other variable measured by the belief updating task (e.g. estimation error, updating magnitude).

We now further discuss on page 12 the limitation, which reads:

“We did not collect physiological measures of stress or information about the COVID-19 infection status of participants, which precludes a direct exploration of the immediate effects of experiencing the infection on belief-updating behavior and the potential interaction with anxiety and stress levels. Although subjective ratings of the perceived risk of death from COVID-19 correlated negatively to the beliefs updating bias measured during the pandemic, this result was obtained retrospectively in a subset of participants (SI section 4). We thus cannot directly attribute the observed lack of optimistically biased belief updating during the lockdown to psychological causes such as heightened anxiety and stress. This limitation is noteworthy, as the impact of experiencing the pandemic on belief updating about the future could differ between those who directly experienced infection and those who remained uninfected. It is also important to acknowledge that our study was timely and geographically limited to the context of the COVID-19 outbreak in France. Cultural variations and differences in governmental responses to contain the spread of SARS-CoV-2 may have impacted the optimism biases in belief updating differently.”

On the analysis side, it was unclear what the motivation was for the different sets of models tested. Both families of models test asymmetric vs symmetric learning (which is the main question here) and have similar parameters (scaling and asymmetry parameters) to quantify these different aspects of the learning process. Conceptually, the different behavioral patterns one could expect from the two families of models needed to be clarified.

Thank you for raising this point. We agree that a clearer conceptual distinction between the two model families can help strengthen the interpretation of our findings. We have added the following considerations to the introduction on pages 2–3, which now reads:

“The underlying mechanism of optimistically biased belief updating involves an asymmetry in learning from positive and negative belief-disconfirming information[2,3,4], which can unfold in two ways following Reinforcement learning (RL) or Bayes rule[5].

Conceptually, Reinforcement learning (RL) and Bayesian models of belief updating are complementary but make different assumptions about the hidden process humans may use to adjust their beliefs when faced with information that contradicts them. The RL models assume belief updating is proportional to the estimation error. The key idea of the estimation error expresses the difference between how much someone believes they will experience a future life event and the actual prevalence of the event in the general population. This difference can be positive or negative. A scaling and an asymmetry parameter quantify the propensity to consider the estimation error magnitude and its valence, respectively. These two free parameters form the learning rate, which indicates how fast and biased participants update their beliefs.

In contrast, Bayesian models assume that following Bayes’ rule the posterior, updated belief is a new hypothesis, formed by pondering prior knowledge with new evidence. The prior knowledge consists in information about the prevalence of life events in the general population. The new evidence comprises various alternative hypotheses. It examines how likely a specific event is to occur or not occur for oneself, compared to the likelihood that it will happen or not happen to others. This probabilistic adjustment of beliefs about future life events can be considered as an approximation of a participant’s confidence in the future. The two free parameters of the Bayesian belief updating model scale how much the initial belief deviates from the updated, posterior belief (i.e., scaling parameter) and the propensity to consider the valence of this deviance (i.e., asymmetry parameter).

Although RL-like and Bayesian updating models make different assumptions about the updating strategy, they are complementary and powerful formalizations of human reasoning. Both models provide insight into hidden, latent variables of the updating process. Most notably, the learning rate and its components, the scaling and asymmetry parameters, which can vary between individuals and contexts and, through this variance, offer possible explanations for the idiosyncrasy in belief-updating behavior and its cognitive biases. “

Do the "winning" models produce the main behavioral patterns in Figure 1, and are they in some way uniquely able to do so, for instance? How would updating look different for an optimistic RL learner versus an optimistic Bayesian RL learner?

We now show that the winning models can reproduce the main behavioral patterns (revised Figure 1b).

Moreover, we plotted estimated and observed average belief updating for each participant (n=123) using the overall best-fitting asymmetrical RL-like updating model shown in SI Figure 6.

Would the asymmetry parameter in the former be correlated with the asymmetry parameter in the latter? Moreover, crucially, would one be able to reliably distinguish the models from one another under the model estimation and selection criteria that the authors have used here (presenting robust model recovery could help to show this)?

The asymmetry parameter estimated with the optimistically biased RL- and Bayesian models did correlate (r = 0.735; p < 0.001).

However, we argue that while the observed updating behavior and estimated free parameters are similar for RL-like and Bayesian learners, the underlying assumed cognitive processes differed and are identifiable. To test this assumption, we have added a model recovery analysis now reported in the supplement section 2c and main manuscript’s methods section pages 24–25.

As shown in SI Figure 5 confusion matrix, there is evidence for strong recovery of nearly all models, and importantly for the two winning models: the optimistically biased RL-like model and the rational Bayesian model of belief updating. This analysis thus rules out that the two model families were confused and mitigate concerns about the validity of the model selection.

Note, one exception was observed. The RL-like and Bayesian updating models that assumed no scaling and asymmetry were best recovered by their respective models that estimated the asymmetry parameter. Many factors could explain this. For example, it could be that the models, which assumed asymmetry, but no scaling, may have captured some bias in updating due to noise generated by the zero parameter models.

A justification is also needed to focus on the "RL-like updating model with an asymmetry and scaling learning rate component" in Figure 3. As I understand it, this model fits best outside of the pandemic, but another model - the Rational Bayesian Model - does worse (and does the best during the pandemic). What model best combines the groups (outside and inside the pandemic)?

We thank the reviewer for highlighting the need to justify our focus on the biased RL-like updating model in Figure 3. The model chosen for parameter comparison was selected based on a model comparison procedure conducted across all 12 models, including data from all participants (both those tested outside and during the pandemic, n=123). This model comparison revealed that Model 1 — the RL model with both asymmetry and scaling learning rate parameters estimated — provided the best fit across the entire dataset (Ef = 0.40, pxp = 0.99). As such, we focused on this model for parameter comparisons in Figure 3 to ensure consistency with the model comparison results and to interpret the parameters in the context of the overall best-fitting model. We added this information on top of the model parameter comparison results on page 8. Moreover, SI Figure 6 in the supplements shows how this model reproduces the observed belief updating in each of the 123 participants.

Why do the authors use absolute belief updating (|UPD|) in the first linear mixed effects model (equation iv)? Since an update is calculated differently depending on whether information calls for an update in an upward or downward direction, I do not understand the need to do this (and it means that updates that go in the wrong direction - away from the information - are counted as positive)

Thank you for driving our attention to this point. The ‘absolute belief updating’ note was incorrect, and we apologize for the confusion. To be precise, we did not use absolute updating values in our analyses. Belief updating was assumed on each trial to go either toward the base rate (e.g., Update = E2 – E1) for negative estimation errors or away from it for positive estimation errors (e.g., Update = E1 – E2). Updates that went in the wrong direction, further away from the base rate, were thus counted and included in the analysis with their negative sign. We have corrected this important point in equation iv of the methods section on page 19.

Figure 4: The task schema does not show a confidence rating for base rates.

Thank you for catching this. We have now added the confidence ratings for base rates to the task in Figure 4b in the revised version of the manuscript. We have furthermore corrected a typo in Figure 4a: The sample size for the group 3 tested in Mai 2021 now indicates 31.

The authors report that base rates are uniformly distributed - this is quite different to other instances of the task where base rates are normally distributed (ideally around the midpoint of the scale). Why this deviation in the design?

We used life events and base rates like those used in past studies of belief updating (Garrett and Sharot 2017, Sharot et al. 2011, Garrett et al. 2017, Korn et al. 2017), which were normal to uniformly distributed (W = 0.952, p = 0.088, Shapiro-Wilk test). The base rates ranged between 10% and 70%, with a mean of 40%. Participants rated their estimates between 3% and 77%, which ensured that for most likely (base rate = 70%) and most unlikely events (base rate = 10%) there was the same space (7%) to update beliefs toward the base rates. Moreover, all statistical models included the absolute estimation errors as a control for variance potentially explained by different estimation error magnitude[42,43]. We added this extra base rate information to the methods section’s task description on page 16.

The task is comprised of only negative life events, which arguably this hinders the generalizability of the results. The authors could mention this as a limitation (there has been a significant quantity of debate about this point in relation to this task: see the work from Ulrike Hahn's lab).

We have added a paragraph to the discussion page 13 to provide a rationale for using only adverse events. This paragraph now reads:

“In this study we tested how actual adverse experiences affect the updating of negative future outlooks in healthy participants and in analogy to studies conducted in depressed patients[19,20,24] following the cognitive model of depression[37]. One open question is whether findings were specific to the adverse event framing[38,39,40]. We argue that under normal, non-adverse contexts belief updating should also be optimistically biased for positive life events, as shown by previous research[41,42]. However, how context such as experiencing a challenging or favorable situation influence the updating of beliefs about positive and negative outlooks remains an open question.”

It would be useful to show the parameter recovery for all parameters (not just the learning rates) and the correlation between parameters (both in simulations and in the fitted parameters).

We apologize for being unclear on this part. The models included two free parameters that were the components of the learning rates: The scaling and the asymmetry parameter. We now have added parameter recovery analyses for the scaling and asymmetry components of the learning rates for (1) the Bayesian model of belief updating during the pandemic, and (2) the RL-like model of belief updating outside the pandemic to the supplement (SI section 2b, SI Figure 4).

Reviewer #2:

The authors investigated how experiencing the COVID-19 pandemic affected optimism bias in updating beliefs about the future. They ran a between-subjects design testing for participants on cognitive tasks before, during, and after lifting the sanitary state of emergence during the pandemic. The authors show that optimism bias varied depending on the context in which it was tested. Namely, it disappeared during COVID-19 and re-emerged at the time of lift of sanitary emergency measures. Through advanced computational modeling, they are able to thoroughly characterize the nature of such alternations, pinpointing specific mechanisms underlying the lack of optimistic bias during the pandemic.

Strengths pertain to the comprehensive assessment of the results via computational modeling and from a theoretical point of view to the notion that environmental factors can affect cognition. However, the relatively small sample size for each group is a limitation.

Thank you for this review.

We acknowledge that sample sizes in each group are lower, especially when breaking down the participant sample into four sub-samples tested in the different contexts. To mitigate concerns we checked the power of the observed context by valence interaction on belief updating. To this aim we simulated new belief updates using the parameters from the best fitting optimistic RL-like model of observed belief updating outside the pandemic, and the rational Bayesian model of observed belief updating during the pandemic. At each iteration we performed a linear mixed effects model analysis of the simulated belief updates[44] analogous to equation iv in the main text. The frequency across 1000 iterations with which the LMEs detected a significant interaction of valence by context on simulated belief updating was 75 %. This frequency indicates the power of the valence by context interaction on observed belief updating. In other words, false negatives were 25% likely, which meant type II errors of failing to reject the null hypothesis when the effect was there. We have added these extra analyses to the main manuscript’s results section page 4 and method’s section page 20.

A major impediment interpreting of the findings is the need for additional measures. While the information on for example, risk perception or the need for social interaction was collected from participants during the pandemic, the fact that these could not be included in the analysis hinders the interpretation of findings, which is now generally based on data collected during the pandemic, for example, reporting increased stress. While authors suggest an interpretation in terms of uncertainty of real-life conditions it is currently difficult to know if that factor drove the effect. Many concurrent elements might have accounted for the findings. This limits understanding of the underlying mechanisms related to changes in optimism bias.

We agree with the reviewer on the limitation arising from the lack of physiological and self-report measures of stress, threat, and perceived uncertainty. To address this point and a similar point raised by reviewer 1 we have added a section to the supplement (SI section 4) that now reports explorative correlations between questionnaire responses of subjective perceptions of risk and anxiety, behavior (e.g. mask wearing, social distancing) and belief updating measured during the 1st strict lockdown.

We now also further discuss this limitation on page 12 of the main text’s discussion.

I recommend that the authors spend more time on explaining the belief-updating task in the presentation of the experiment.

Thank you for this advice. We now provide a clearer and more detailed description of the belief-updating task in the main manuscript’s methods section and have updated Figure 4b to display the confidence rating event in the task schema.

The task description now reads:

“As illustrated in Figure 4b, each of the 40 trials began with presenting an adverse life event. Participants estimated their own risk and the risk of someone else their age and gender. Then the base rate of the event occurring in the general population was displayed on the computer screen. Participants rated their confidence in the accuracy of the presented base rate. Finally, they re-estimated their risk for experiencing the event now informed by the base rate.”

The experimental task seems to include a self-other dimension, which is completely disregarded in the analysis. It would be interesting to explore whether the effect of diluted optimism bias during the pandemic is specific to information about self vs. Other.

We appreciate the reviewer's observation regarding the self-versus-other dimension in the belief updating task design. As now shown in SI Figure 2 the participants indeed displayed an optimism bias: They estimated that adverse events are more likely to happen to others than to themselves (ß = 3.02, SE = 0.86, t (232) = 3.53, p = 5.09e-04, 95% CI [1.33 – 4.71]; SI Figure 2; SI Table 18). This effect was observed overall participants. The pandemic context had no significant effect (ß = -1.91, SE = 3.00, t (232) = -0.64, p = 0.52, 95% CI [-7.82 – 4.00]; SI Table 18). Moreover, following previous studies of optimistically biased belief updating we tested the effect of estimation errors (EE) calculated on the difference between the estimate for someone else (eBR) and the base rate (BR), following: EE = eBR – BR[4,5,25,26]. When categorizing trials as good news or bad news based on this alternative EE calculation the context-by-EE valence interaction remained significant (SI Table 6).

We conclude from these additional analyses that experiencing the pandemic specifically influenced belief updating but did not affect optimism biases in initial beliefs about the future.

Please provide an English translation of the instructions for the task.

We now provide an English translation of the task instructions in the Supplement section 5.

Author response:

Public Reviews:

Reviewer #1 (Public review):

(1) The production of ROS has been measured in a very superficial way.

The term "ROS" confers a plethora of chemical species which exerts different physiological effects on different cells and situations.

Mitochondria through one of the source, but not the only source of ROS production. Only measuring ROS with mitosox do not reflect the cellular condition of ROS in a specific condition. I would suggest authors consider doing IF of oxidative stress specific markers , carbonyl group and also, maybe, Amplex red for determining average oxidative stress and ros production in the cells.

We agree with the reviewer that a detailed analysis of ROS production and its markers would strengthen the manuscript. Accordingly, we will perform the Amplex Red assay for Figure 1.

(2) 8-OHG signal seems very confusing in Figure 7E. 8-ohg is supposed to be mainly in the nucleus and to some extent in mitochondria. The signal is very diffused in the images. I would suggest a higher magnification and better resolution images for 8-ohg. Also, the VWF signal is pretty weak whereas it should be strong given the staining is in aorta. Authors should redo the experiments.

The reviewer’s comment is correct regarding the expected signal. We will repeat the assays. However, we would like to note that the flat morphology of the endothelial cell monolayer on the aortic surface may limit the visualization of subcellular signal differentiation when transversely sectioned.

(3) PCA analysis is quite not clear. Why is there a convergence among the plots? Authors should explain. Also, I would suggest that the authors do the analysis done in Figure 8B again with R based packages. IPA, though being user-friendly, mostly does not yield meaningful results and the statistics carried out is not accurate. Authors should redo the analysis in R or Python whichever is suitable for them.

Thank you for your valuable feedback. We acknowledge the concern regarding the PCA analysis and the convergence observed in the plots. In the revised manuscript, we will revise our interpretation to clarify this observation.

Additionally, we appreciate your suggestion to use R-based packages for pathway analysis. We will make efforts to regenerate the analysis presented in Figure 8B using R to enhance the statistical robustness and reproducibility of our results.

(4) The MS analysis part seems pretty vague in methods. Please rewrite.

We will revise the methods section to improve the legibility.

Reviewer #2 (Public review):

All the experiments performed here are in overexpression background therefore, it would be crucial to show that p66Shc is SUMO2ylated at physiological levels.

To address this concern, we will attempt to assess p66Shc-SUMO2 levels under physiological conditions. However, we would like to highlight a technical limitation: the currently available antibodies do not distinguish p66Shc from other isoforms, nor SUMO2 from SUMO3. Therefore, enriching for the endogenous p66Shc-SUMO2 adduct will require novel tools and techniques, which we are actively exploring.

Reviewer #3 (Public review):

One notable weakness is that the link between the observed cellular changes and the ultimate in vivo phenotype remains only partially explored. While the authors successfully show that p66ShcK81R knockin mice are protected from endothelial dysfunction in a hyperlipidemic context, additional experiments characterizing the broader tissue-specific roles, or examining further endothelial assays in vivo, would strengthen the mechanistic conclusions. It would also be beneficial to see more direct evaluations of p66Shc subcellular localization in the protective knockin mice to complement the proteomic findings.

That is an excellent suggestion. We will determine the tissue specific distribution of endogenous p66ShcK81R.

Despite these gaps, the data broadly support the authors' main conclusions. The authors lay out a plausible mechanistic pathway for how hyperlipidemia and increased global SUMOylation can converge on the oxidative stress pathway to provoke vascular dysfunction.

The likely impact of this work on the field is noteworthy. Beyond clarifying how a single post-translational modification event can influence the pathophysiology of endothelial cells, the study provides a model for investigating broader roles of SUMO2 in other cardiovascular conditions and highlights the importance of identifying additional SUMOylation sites and their downstream impact.

In conclusion, by demonstrating the direct SUMOylation of p66Shc at lysine-81 and linking that modification to endothelial dysfunction in a hyperlipidemic mouse model, this paper offers valuable insights into how broadly acting post-translational modifiers can evoke specific pathological effects.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript assesses the utility of spatial image correlation spectroscopy (ICS) for measuring physiological responses to DNA damage. ICS is a long-established (~1993) method similar to fluorescence correlation spectroscopy, for deriving information about the fluorophore density that underlies the intensity distributions of images. The authors first provide a technical but fairly accessible background to the theory of ICS, then compare it with traditional spot-counting methods for its ability to analyze the characteristics of γH2AX staining. Based on the degree of aggregation (DA) value, the authors then survey other markers of DNA damage and uncover some novel findings, such as that RPA aggregation inversely tracks the sensitivity to PARP inhibitors of different cell lines.

The need for a more objective and standardized tool for analyzing DNA damage has long been felt in the field and the authors argue convincingly for this. The data in the manuscript are in general well-supported and of high quality, and show promise of being a robust alternative to traditional focus counting. However, there are a number of areas where I would suggest further controls and explanations to strengthen the authors' case for the robustness of their ICS method.

Strengths:

The spatial ICS method the authors describe and demonstrate is easy to perform and applicable to a wide variety of images. The DDR was well-chosen as an arena to showcase its utility due to its well-characterized dose-responsiveness and known variability between cell types. Their method should be readily useable by any cell biologist wanting to assess the degree of aggregation of fluorescent tags of interest.

Weaknesses:

The spatial ICS method, though of longstanding history, is not as intuitive or well-known as spot-based quantitation. While the Theory section gives a standard mathematical introduction, it is not as accessible as it could be. Additionally, the values of TNoP and DA shown in the Results are not discussed sufficiently with regard to their physical and physiological interpretation.

We agree that a major limitation in adaption of this approach is a deeper understanding of the theory and results. We have updated the theory section to include further discussion (Page 4 line 132)

The correlation of TNoP with γH2AX foci is high (Figure 2) and suggestive that the ICS method is suitable for measuring the strength of the DDR. The authors correctly mention that the number of spots found using traditional means can vary based on the parameters used for spot detection. They contrast this with their ICS detection method; however, the actual robustness of spatial ICS is not given equal consideration.

We found it difficult to give equal consideration of robustness to ICS. The major limitation of traditional approaches is proper selection of an intensity threshold that is necessary to define and separate foci from background intensity. However, ICS does not employ a threshold, therefore we could not test different thresholding applications in ICS as we did with traditional methods. In our view the absence of the need for a threshold is profoundly advantageous. The only inputs we employ in the ICS analysis are used to segment cell nuclei, yet these have no impact on the ICS calculation and are necessary for any analysis of the DDR.

Reviewer #2 (Public review):

Summary:

Immunostaining of chromatin-associated proteins and visualization of these factors through fluorescence microscopy is a powerful technique to study molecular processes such as DNA damage and repair, their timing, and their genetic dependencies. Nonetheless, it is well-established that this methodology (sometimes called "foci-ology") is subject to biases introduced during sample preparation, immunostaining, foci visualization, and scoring. This manuscript addresses several of the shortcomings associated with immunostaining by using image correlation spectroscopy (ICS) to quantify the recruitment of several DNA damage response-associated proteins following various types of DNA damage.

The study compares automated foci counting and fluorescence intensity to image correlation spectroscopy degree of aggregation study the recruitment of DNA repair proteins to chromatin following DNA damage. After validating image correlation spectroscopy as a reliable method to visualize the recruitment of γH2AX to chromatin following DNA damage in two separate cell lines, the study demonstrates that this new method can also be used to quantify RPA1 and Rad51 recruitment to chromatin following DNA damage. The study further shows that RPA1 signal as measured by this method correlates with cell sensitivity to Olaparib, a widely-used PARP inhibitor.

Strengths:

Multiple proof-of-concept experiments demonstrate that using image correlation spectroscopy degree of aggregation is typically more sensitive than foci counting or foci intensity as a measure of recruitment of a protein of interest to a site of DNA damage. The sensitivity of the SKOV3 and OVCA429 cell lines to MMS and the PARP inhibitors Olaparib and Veliparib as measured by cell viability in response to increasing amounts of each compound is a valuable correlate to the image correlation spectroscopy degree of aggregation measurements.

Weaknesses:

The subjectivity of foci counting has been well-recognized in the DNA repair field, and thus foci counts are usually interpreted relative to a set of technical and biological controls and across a meaningful time period. As such:

(1) A more detailed description of the numerous prior studies examining the immunostaining of proteins such as γH2AX, RAD51, and RPA is needed to give context to the findings presented herein.

We apologize for not providing enough detail. We have added further references and discussion. γH2AX foci counting, in particular, has been used in thousands of previous studies. (Pages 18 line 513 and 517)

(2) The benefits of adopting image correlation spectroscopy should be discussed in comparison to other methods, such as super-resolution microscopy, which may also offer enhanced sensitivity over traditional microscopy.

Thank you for raising this point. We have added this discussion (page 19 line 553). The limiting factor that ICS addresses is the partition coefficient of signal in a foci or cluster versus outside the cluster. Super-resolution will not necessarily improve this unless it is resolved down to single molecule counting. However, one would still need to evaluate how to define a cluster or foci in the background of non-cluster distribution.

(3) Additional controls demonstrating the specificity of their antibodies to detection of the proteins of interest should be added, or the appropriate citations validating these antibodies included.

We have added text stating that we only use validated antibodies (page 6 line 193). One thing to note is that we are measuring differences between treatment conditions, thus, if an antibody has non-specific labeling of proteins of cellular structures that do not change upon treatment, our approach would overcome this limitation.

Reviewer #3 (Public review):

Summary:

This paper described a new tool called "Image Correlation Spectroscopy; ICS) to detect clustering fluorescence signals such as foci in the nucleus (or any other cellular structures). The authors compared ICS DA (degree of aggregation) data with Imaris Spots data (and ImageJ Find Maxima data) and found a comparable result between the two analyses and that the ICS sometimes produced a better quantification than the Imaris. Moreover, the authors extended the application of ICS to detect cell-cycle stages by analyzing the DAPI image of cells. This is a useful tool without the subjective bias of researchers and provides novel quantitative values in cell biology.

Strengths:

The authors developed a new tool to detect and quantify the aggregates of immunofluorescent signals, which is a center of modern cell biology, such as the fields of DNA damage responses (DDR), including DNA repair. This new method could detect the "invisible" signal in cells without pre-extraction, which could prevent the effect of extracted materials on the pre-assembled ensembles, a target for the detection. This would be an alternative method for the quantification of fluorescent signals relative to conventional methods.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major comments:

(1) The ICS theory section is essential and based on an excellent review from one of the authors. It would benefit greatly from a diagram showing where the quantities 𝒈(𝟎, 𝟎), 𝝎𝟎, and 𝒈inf come from in the 2D Gaussian fit, ideally for two cases where these quantities differ (i.e., how they correspond to different DA or TNoP values). In my opinion, this addition would greatly increase the manuscript's accessibility for DDR researchers. The citation of the review at the beginning would also be a plus.

We have added the review citation at the front of the theory section (page 3 line 87).We have highlighted where g(0,0), the most critical measurement for determination of TNoP and DA, derives from in Figure 2D. However, it is difficult to describe all the curve fit parameters in an image as they have some interdependency on each other and thus labeling one in a single image would not independently capture how they might be observed in a different curve fit.

(2) The TNoP measured in Figure 2 is a quantity about 2000-3000 times greater than the number of "traditionally detected" foci by both methods and the linear relations have very low Y intercepts. Can the authors comment explicitly on the physical interpretation of this number - are 2 to 3 thousand independent particles present within each "focus" detected by traditional means? If so, then what might one "particle" correspond to? (a single secondary antibody or fluorophore? a nucleosome?). In a similar vein, the X intercepts lie at around 25 foci, meaning that in images with fewer than that number of foci detected by ImageJ or Imaris, the ICS method should detect zero TNoP - is this in line with the authors' predictions? Is it possible that a first-order line fit is not the most appropriate relation between the two methods?

We apologize for our brevity here. Since DA proved to be a more useful metric we did not spend much effort discussing TNoP. TNoP correlates to the number of clustered particles, or non-diffuse fluorophores. TNoP is the inverse of the number of individual particles per nucleus, but the value is not a direct measure of foci. If a sample had no clustering at all, the number of individual particles would be at a maximum and the TNoP would be at a minimum. However, as fluorophores cluster, the number of individual particles (i.e. non-clustered fluorophores) decreases, which increases the TNoP value. Therefore, TNoP has a correlation to the number of foci detected through traditional measurements, as we found here. Yet, TNoP is a relative measurement and cannot be compared across different conditions. Similar to foci counting, TNoP is unable to factor the size or intensity of each cluster, thus DA is a more appropriate quantification of the DNA damage response.

The value of TNoP is dependent on the fitted point spread function and the area of the nucleus. The y=0 intercept of TNoP is defined by the optical setup and is not expected to necessarily go through x=0. Intriguingly, other groups have found that some foci identified through traditional measurements are actually clusters of multiple smaller foci, thus the concept of what a foci represents is difficult to interpret. Thus, here we aimed to show a general correlation of TNoP with foci count through traditional methods to reflect how ICS is similar to foci counting, then employed DA to overcome the limitations of defining a foci.

We have tried to clarify this in the text (page 8, line 266)

(3) Some suggestions to address the robustness of ICS:

For a given sample (i.e. one segmented nucleus), the calculation of DA and TNoP should be similar between different images of that same nucleus taken at different times, similar to how the number of traditionally detected foci would be fairly invariant. In particular, it should be shown that these values are not just scaling with the higher normalized intensity seen in stronger DDR responses. In the same vein, the linear relationship between TNoP and "foci" should not change even if the confocal settings are slightly different (i.e., higher/lower illumination intensity) as long as the condition stipulated by the authors in the Discussion holds ("ICS can be implemented on any fluorescence image as long as the square relative fluorescence intensity fluctuations are detectable above noise fluctuations."). To show, as the title states, that spatial ICS is a robust tool, it would be desirable to demonstrate this with a series of images of the same cell at the same or varying excitation intensities.

Thank you for your suggestions. Indeed, the calculation will be the same over sequential images of the same cell. Observations of dose dependent DA that does not correlate with intensity for RPA1 and RAD51 results (Fig. S5) directly demonstrates that DA does not just scale with intensity.

We would not expect the TNoP to change with confocal setting, however we show in Figure 1 that the number of foci does indeed change with intensity settings as captured by thresholds. Therefore, any interpretation of TNoP vs. foci count would be very difficult to make at different microscope settings. To ensure we are fairly comparing ICS to existing analysis we keep the settings the same and measure changes between conditions.

(4) More information is needed on how intensity normalization was performed. The Methods states "Measurements across experiments were normalized by the control in each dataset." The DMSO (0mM drug) plots all appear to have a mean of 1.0, so it appears the values for each set of control nuclei were divided by their own mean, and then the values for each set of experimental nuclei were divided by the mean value of all 3 controls as an aggregate; is this correct?

We apologize for not being more clear. Thank you for raising this point. We normalized data to a control from each experimental group. Thus, in figures 3,4 and 5 data were collected over multiple experiments with one control per experiment and each treatment condition included in each experiment. Therefore, we normalized each result to the corresponding control from that imaging session. However, in Figure 8 we ran experiments at much higher throughput with multiple controls per experiment, thus the data were normalized to the overall average of the controls, which is why the control averages are not all at a value of 1. We have clarified this in the text. (Page 7 line 218).

(5) Some more information about the ICS analysis should be given if the full code is not provided - in particular, how the nucleus mask was implemented on the "signal" channel (were the edges abruptly set to zero or was a window function introduced to avoid edge effects in the discrete FFT?

Thank you for raising this point. We have added the code to GitHub - github.com/ dubachLab/ics. The signal region was established by simply applying the nuclear mask from the DAPI channel to the IF channel. Each region is padded with average intensity value at the edges for 2x the dimensions of the ROI to remove edge effects in the FFT.

Minor comments:

(1) Figure 3, 4, 5: I think it would aid figure readability if channels were labeled in the images themselves, not just in the legend.

Thank you for the suggestion, we tried doing this and struggle to fit a label with the layout of the images. We were also concerned about interpretation of data in each column and the potential to assign data to each figure if they were so prominently labeled.

(2) Supplemental Figures are mislabeled; the order given in the legends is S1, S2, S3, S2, S3. S4 is called out in the main text where it should be S5.

Thank you for catching this error. We have made the necessary corrections. S4 contains data on cellular response to the drugs, while S5 contains intensity data in response to MMS.

(3) It should be stated for each Figure what kind of microscopy was performed - I assume that it is confocal for everything except when widefield is explicitly stated, but for clarity please add this information.

Indeed, this is correct, we have indicated which microscopy was used for each figure.

(4) The MATLAB code and full (uncropped) Western blots should be provided as supplemental data if possible.

We have included a GitHub link for the code and un-cropped western blots.

(5) The p values from significance tests should indicate whether multiple comparisons correction was necessary (if suggested by Prism) and performed.

Apologies for a lack of clarity but this was not necessary, significance was calculated vs. the next lower dose (e.g. 10 micromolar vs. 1 micromolar). We have clarified this in the methods (page 7 line 221).

Reviewer #2 (Recommendations for the authors):

Major points:

In addition to the weaknesses noted above, to encourage widespread adoption of this method, the authors should make the tools that they used for their analysis publicly available. In a few instances (e.g., compare Figures 3J and 3L), other methods outperform DA. It would be meaningful to discuss when especially DA may be a better measure than others (such as intensity or number of foci).

We have made code available on Github. We expect results, such as those in Figures 3J and 3L where intensity is significantly higher at the highest concentration but DA is not are reflective of the underlying biology and this may be interpreted differently under different experimental conditions. Imaris spots (Fig. 3K) also does not capture a significant increase at the highest dose of olaparib, suggesting that intensity may raise but it doesn’t not generate more foci. These results are likely highly dependent on the mechanism of olaparib at such a high concentration and the DDR response. We are hesitant to draw biological conclusions from these results and instead would like to highlight the capacity of ICS to evaluate the DDR, therefore we don’t want to make any broad comments about different applications.

Minor points:

(1) Pg. 12: "We used MMS to induce DNA damage in SKOV3 and OVCA429 cells. As expected, normalized intensity for RPA1 and RAD51 values (Figure S5) did not display a dose dependence on MMS concentration."

Please provide a citation for the claim that RPA1 and RAD51 normalized intensities do not display a dose dependence on MMS concentration.

These were data that we generated. We were not expecting an intensity change as that would presumably require increased protein generation in response to MMS, compared to gH2AX where the phospho-specific H2AX is generated in the DDR.

(2) Pg. 12: "Similar to RPA1, RAD51 does not form distinguishable foci in the nuclei in cells without preextraction (Fig. 5)." Please provide a citation for this claim.

We did not do pre-extraction and our results don’t produce changes in distinguishable foci. We provided citations discussing how, without pre extraction, foci formation for these proteins is not obvious (REF 38 and 39).

(3) I noted that the authors cite one paper [38] apparently showing that RPA and Rad51 do not always form foci, however, this is in the C. elegans germline in response to micro irradiation, therefore I am not sure that it is applicable to human cells.

We apologize for referencing a paper on C elegans. Most papers looking at RPA and RAD51 in the DDR use pre-extraction as it seems necessary to observe foci. Therefore, there are not as many papers, that we could find, that do not use pre-extraction. Reference 39 is in Hela cells.

Reviewer #3 (Recommendations for the authors):

Major points:

(1) Page 8, the second paragraph: In the Result section, it is better to describe how the authors carried out immuno-staining (without pre-extract subtraction) and ICS briefly, although the method is described in detail in the Method section.

Thank you for the suggestion, we have added this description (page 8, line 259)

(2) In Figure 5K-P: The authors analyzed "invisible" RAD51 foci on the image (Fig. 5L, M, O, and P) without pre-extraction. As a control experiment, it is useful to check whether pre-extraction would provide "visible" RAD51 foci and to examine the similar MMS concentration dependency shown in Figure 5R (or 5T). This would strengthen the power of the ICS analysis.

Thank you for the suggestion. In our hands, pre-extraction is extremely subjective. We have tried performing pre-extraction but find highly variable results depending on conditions. Therefore, we did not include any pre-extraction here. We expect that performing these experiments may or may not agree with results in Figure 5 largely because we are unable to achieve repeatable pre-extraction foci counting.

(3) Figure 6D (and 6C) looks very interesting. It would be important to show the interpretation of this correlation shown in the graph. Although the authors argued that ICS analysis results shown in the graph could provide new insight into the DDR (page 14, last line 5), as shown in another part, it is important to carry out the same analysis by using Imaris Spots. Moreover, it is interesting to apply the analysis to RAD51 foci (shown in Figure 5), given that the PARPi effect is enhanced in the absence of RAD51mediated recombination.

We completely agree that this analysis may generate interesting results to help interpret the DDR response to PARP inhibition. These experiments are part of an ongoing follow up study where we extend the use of ICS to other parts of the DDR and investigate protein clustering across several proteins with impact on PARPi response. Therefore, since the focus of this manuscript is introducing ICS as a tool to study the DDR, we believe that omitting those data here does not deter from the central points of the manuscript. We including results in Figure 6 because we wanted to show how ICS could impact DDR research. Furthermore, combined with our advances shown in Figures 7 and 8, we are currently working on adapting ICS to be high-throughput and much simpler than Imaris spots for handling large datasets needed to generate results like those in Figure 6.

Minor points:

(1) Figure 1I, blue arrows: These showed an area with a higher background. Because of a low magnification, it is very hard to see the difference from the other areas of the background. It is better to show a magnified image of the representative region with a higher background.

We hope that readers can see the higher intensity in the diffuse area. We attempted to construct a zoomed in area, but that either blocked a significant portion of the nonzoomed image or added complexity to the figure. We have noted that images in Figure S1 are larger and more obviously capture an increase in background intensity.

(2) Figure 2 legend, line 5, the same as "A)": This should be "B".

Here, the number of independent particle clusters is intended to be the same as A, the difference is that the independent particles are clusters in C and individual fluorophores in A.

(3) Page 9, the first paragraph, last line, foci formation, and foci composition: These should be "focus formation and focus composition".

We have changed this.

(4) Page 15, the first paragraph, line 5, palbociclib, camptothecin, or etoposide: please explain what kinds of the drugs are.

We have added that these drugs cause cells to stall at different cell cycle stages. Explaining the drugs would take considerable room in the text.

(5) Page 16, the first paragraph, line 1, bleomycin: Please explain what this drug is.

Similar to above, we have stated that this drug causes DNA damage, going into detail would take several sentences.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Triple-negative breast cancer (TNBC) accounts for approximately 15-20% of all breast cancers. Compared to other types of breast cancer, TNBC exhibits highly aggressive clinical characteristics, a greater likelihood of metastasis, poorer clinical outcomes, and lower survival rates. Immunotherapy is an important treatment option for TNBC, but there is significant heterogeneity in treatment response. Therefore, it is crucial to accurately identify immunosuppressive patients before treatment and actively seek more effective therapeutic approaches for TNBC patients.

Strengths:

In this work, the authors collected and integrated data from single cells and large volumes of RNA sequencing and RNA-SEQ to analyze the TME landscape mediated by genes associated with iron death. On this basis, the prediction model of prognosis and treatment response of 131 patients was constructed using a machine learning algorithm, which is beneficial to provide individualized and precise treatment guidance for breast cancer patients.

Thank you for your appreciation of our work. We are encouraged by your positive feedback and will continue to explore new avenues in personalized medicine for breast cancer.

Weaknesses:

However, there are still some issues that need to be clarified:

(1) The description of the research background is too brief and concise, and it is necessary to add some information about the limitations of existing methods and the differences and advantages of this study compared with other published relevant studies, so as to better highlight the necessity and research value of this study.

Thank you for your suggestions. We have supplemented the research background and compared the differences between this study and other studies, further highlighting the research value of our study.

(2) This study is a retrospective analysis of a public data set and lacks experimental validation and prospective experiments to support the results of bioinformatics analysis. This should be added to the acknowledgment of limitations in the study.

Thank you for the constructive feedback. We also acknowledge that the lack of experimental evidence is one of the limitations of this study. Therefore, we plan to conduct in vivo and in vitro experiments in our future research to support the findings of our bioinformatics analysis, and have already supplemented the relevant content in the limitations of Discussion.

Reviewer #2 (Public review):

Summary:

This study aims to explore the ferroptosis-related immune landscape of TNBC through the integration of single-cell and bulk RNA sequencing data, followed by the development of a risk prediction model for prognosis and drug response. The authors identified key subpopulations of immune cells within the TME, particularly focusing on T cells and macrophages. Using machine learning algorithms, the authors constructed a ferroptosis-related gene risk score that accurately predicts survival and the potential response to specific drugs in TNBC patients.

Strengths:

The study identifies distinct subpopulations of T cells and macrophages with differential expression of ferroptosis-related genes. The clustering of these subpopulations and their correlation with patient prognosis is highly insightful, especially the identification of the TREM2+ and FOLR2+ macrophage subtypes, which are linked to either favorable or poor prognoses. The risk model thus holds potential not only for prognosis but also for guiding treatment selection in personalized oncology.

Thank you for your thorough review and insightful comments.

Weaknesses:

The study has a relatively small sample size, with only 9 samples analyzed by scRNA-seq. Given the typically high heterogeneity of the tumor microenvironment (TME) in cancer patients, this may affect the accuracy of the conclusions. The scRNA-seq analysis focuses on the expression of ferroptosis-related genes in various cells within the TME. In contrast, bulk RNA sequencing uses data from tumor samples, and the results between the two analyses are not consistent. The bulk RNA sequencing results may not accurately capture the changes happening in the microenvironment.

Thank you for your constructive feedback. Although this study only included 9 samples, given the limited availability of scRNA-seq datasets for untreated TNBC in public databases, we chose to utilize a dataset that contains a relatively larger number of untreated TNBC samples. We are fully aware of the complexity and high heterogeneity of the TME. Despite the limited sample size, we first conducted rigorous quality control on the data and, based on this, preliminarily revealed the landscape of the TME mediated by ferroptosis-related genes. These findings provide a new perspective for understanding the biological mechanisms underlying the onset and progression of breast cancer. To enhance the reliability and generalizability of our research results, we plan to strive to expand the sample size in future work and consider integrating other omics technologies, such as proteomics and metabolomics, with scRNA-seq data for a more in-depth exploration of the complex interactions within the TME.

We also agree with your viewpoint that scRNA-seq data reveals gene expression within individual cells, while bulk RNA-seq data reveals the average gene expression in tumor tissues, and there are differences in data acquisition and processing methods between the two. However, we believe that there are also some close connections between them in terms of gene expression levels. By comparing the expression specificity of marker genes for specific cell types in breast cancer tissues, we found that they are correlated with patient prognosis, and the results have been validated in both internal and external validation sets. Thank you once again for your valuable suggestions, which will play an important guiding role in our subsequent research.

Reviewer #1 (Recommendations for the authors):

(1) The breast cancer scRNA-seq dataset files of GSE176078 include 10 TNBC primary tumors (DOI:10.1016/j.compbiomed.2023.107066). However, in this study, only 9 cases were listed, please explain the reason for the data exclusion.

Thank you for your questions. Although it was clearly stated in the original paper that "To elucidate the cellular architecture of breast cancers, we analyzed 26 primary pre-treatment tumors, including 11 ER+, 5 HER2+ and 10 TNBCs, by scRNA-Seq (Supplementary Table 1)," upon downloading and carefully examining the patient information in Supplementary Table 1, we only included 9 patients explicitly labeled as TNBC in our study (https://pmc.ncbi.nlm.nih.gov/articles/PMC9044823/#SD1).

(2) The description of the technique in the methods section should be more detailed, such as parameter settings, quality control standards, etc.

Thank you for your valuable suggestions. We have already supplemented the relevant content in the methods section.

(3) Please check and correct formatting errors to improve readability, such as lines 176 and 177.

We were really sorry for our careless mistakes. Thank you for your reminder. We have corrected the “Pseudotime analysis with scRNA-seq data helps to obtain an approximate landscape of gene expression dynamics” into “Pseudotime analysis of scRNA-seq snapshot data helps to provide an approximate landscape of gene expression dynamics”. And we have further checked and revised the formatting errors of the manuscript.

Reviewer #2 (Recommendations for the authors):

(1) In multiple sections of the paper, abbreviations are used without being defined when first mentioned.

We were really sorry for our careless mistakes. Thank you for your reminder. We have already added definitions for the abbreviations in both the abstract and the main text.

(2) The authors should analyze whether the transcription factors in Figure 2 are correlated with the expression of ferroptosis-related genes.

Thank you for your valuable feedback. Some transcription factors in Figure 2 correlate with the expression of ferroptosis-related genes, which we have supplemented in the Discussion.

(3) Figures 3d and 4e lack explanations for the axis values, and for Figure 4e, is the unit of the y-axis labeled "survival" in days?

Thank you for your valuable feedback. We apologize for the lack of explanations for the axis values in Figures 3d and 4e and we have made revisions to both figures accordingly. We have noted that the unit "survival" on the y-axis of Figure 4e is in years, and we have already made the necessary supplement to clarify this. Thank you very much for your reminder.

(4) The authors conducted their analysis using public databases but did not cite the original literature, nor did they discuss the similarities and differences between their findings and those in the original studies.

Thank you for your valuable suggestions, and we deeply apologize for our carelessness. We have supplemented the original literature in the references and discussed the differences between this study and the original literature in the Discussion.

(5) Some figures, particularly those involving heatmaps and t-SNE plots (e.g., Figures 1 and 3), present dense and complex data that may be challenging for readers to interpret. The heatmaps (Figure 1e-f and 3d) include many genes, but it is unclear how these genes were selected, and the scale of gene expression differences is difficult to interpret. Simplifying these figures by focusing on the most differentially expressed and clinically relevant genes (e.g., those with prognostic value) would improve readability.

Thank you for your valuable suggestions. The t-SNE plots in Figures 1 and 3 primarily serve as a dimensionality reduction technique to visually present the clustering of multiple cells or samples based on gene expression, aiding readers in quickly identifying cell subpopulations. The heatmaps, on the other hand, are mainly used to showcase the differential expression of ferroptosis-related genes across different clinicopathological classifications and cell subpopulations, with varying shades of color helping readers quickly recognize gene expression differences among different cell subpopulations. The genes included in the heatmaps (Figures 1e-f and 3d) are sourced from the FerrDb website. We have uploaded the list of ferroptosis-related genes used in this study as Supplementary Table 1 and added the relevant steps in Method 2.3.

(6) The study analyzes the expression of ferroptosis-related genes in different immune cells within the TME. The authors should discuss how these changes in gene expression may impact the function and behavior of immune cells.

Thank you for your valuable feedback. We have supplemented the discussion with detailed effects of the main differential genes (FOLR2 and TREM2) on the tumor immune response.

(7) The authors analyzed the expression of ferroptosis-related genes in immune cells using single-cell sequencing data. However, they subsequently applied the selected genes to perform a risk factor analysis in tumor cells. Is the expression and function of these genes the same in immune cells and tumor cells? This seems questionable.

Thank you very much for your suggestion. We also believe that there may be differences in the expression and function of genes between immune cells and tumor cells. However, some genes may exhibit similarities in their expression and function in immune cells and tumor cells, especially within the tumor immune microenvironment, due to the complex and tight interactions between immune cells and tumor cells (as shown in Figures 1d and 2h), and their expression levels can be related to the onset, progression, and prognosis of tumors.

(8) While the risk score model based on ferroptosis-related genes is promising, it lacks experimental validation, which weakens the strength of the conclusions. The authors should consider conducting in vitro or in vivo experiments. These functional studies would provide essential evidence to support the model's predictive capability.

Thank you for the constructive feedback. We fully recognize the importance of conducting functional studies to substantiate the predictive capability of the model. Therefore, we plan to conduct in vitro and in vivo experiments in our future research to provide the necessary evidence and further validate the model's effectiveness.

(9) The manuscript predicts sensitivity to 27 drugs based on the risk score, but it lacks mechanistic insight into why patients in the high-risk group might be more responsive to certain drugs. Including a more detailed discussion of the molecular mechanisms underlying this drug sensitivity, particularly linking ferroptosis-related genes to drug metabolism or efficacy, would provide a stronger rationale for the clinical application of these findings.

Thank you very much for your valuable suggestions. In the discussion, we thoroughly analyzed the mechanism of action of the drugs (ABT-263 and erlotinib) with the greatest difference in sensitivity between high-risk and low-risk groups, as well as their correlation with ferroptosis.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this revised report, Yamanaka and colleagues investigate a proposed mechanism by which testosterone modulates seminal plasma metabolites in mice. The authors identify oleic acid as a particularly important metabolite, derived from seminal vesicle epithelium, that stimulates linear progressive motility in isolated cauda epidydimal sperm in vitro. The authors provide additional experimental evidence of a testosterone dependent mechanism of oleic acid production by the seminal vesicle epithelium.

Strengths:

Often, reported epidydimal sperm from mice have lower percent progressive motility compared with sperm retrieved from the uterus or by comparison with human ejaculated sperm. The findings in this report may improve in vitro conditions to overcome this problem, as well as add important physiological context to the role of reproductive tract glandular secretions in modulating sperm behaviors. The strongest observations are related to the sensitivity of seminal vesicle epithelial cells to testosterone. The revisions include addition of methodological detail, modified language to reflect the nuance of some of the measurements, as well as re-performed experiments with more appropriate control groups. The findings are likely to be of general interest to the field by providing context for follow-on studies regarding the relationship between fatty acid beta oxidation and sperm motility pattern.

Thank you for summarizing and your positive evaluation of our study.

Weaknesses:

Support for the proposed mechanism is stronger in this revised report than in the previous report, but there are many challenges in measuring sperm metabolism and its direct relationship with motility patterns. This study is no exception and largely relies on correlations between various experiments in lieu of direct testing. Additionally, the discussion is framed from a human pre-clinical perspective, and it should be noted that the reproductive physiology between mice and humans is very different.

Thank you for pointing out the challenges in our paper. We appreciate your comment on the limited evidence supporting the direct relationship between sperm metabolism and motility patterns under current experimental conditions. Based on your and reviewer2’s suggestions, we have decided to remove the experiments and discussion on the “effects of OA on sperm metabolism, motility and fertility (Fig. 7, Supplemental Figure 5A and C-F.)” and the corresponding parts in the Discussion section from the paper. (See also Reviewer 2's main comment) These data mainly show correlations, and did not show direct evidence of causality. Instead, we added a new experiment to the manuscript, in which a lipid mixture that mimics the fatty acid profile secreted testosterone-dependently from seminal vesicle epithelial cells was added to the sperm culture medium (New Supplemental Figure 5, Lines 259-268). In this experiment, motility parameters were measured using CASA. This experiment evaluates the direct effects of lipid exposure on sperm motility. With these revisions, we are able to focus on the metabolic changes caused by testosterone in seminal vesicle epithelial cells, which are the central focus of our research. We have added a short statement agreeing the potential importance of OA and our intention to more rigorously investigate the role of OA in sperm function in subsequent studies (Lines 402-407).

Furthermore, we have revised text, clearly state the limitations of the species difference and clarify that the translational aspects to humans are speculative (Lines 383-384, 395-397, 408-410).

We appreciate your guidance. We believe that these changes will strengthen our research.

Reviewer #2 (Public review):

Using a combination of in vivo studies with testosterone-inhibited and aged mice with lower testosterone levels as well as isolated mouse and human seminal vesicle epithelial cells the authors show that testosterone induces an increase in glucose uptake. They find that testosterone induces a difference in gene expression with a focus on metabolic enzymes. Specifically, they identify increased expression of enzymes regulating cholesterol and fatty acid synthesis, leading to increased production of 18:1 oleic acid. The revised version strengthens the role of ACLY as the main regulator of seminal vesicle epithelial cell metabolic programming. 18:1 oleic acid is secreted by seminal vesicle epithelial cells and taken up by sperm, inducing an increase in mitochondrial respiration. The difference in sperm motility and in vivo fertilization in the presence of 18:1 oleic acid and the absence of testosterone, however, is small. Additional experiments should be included to further support that oleic acid positively affects sperm function.

Thank you very much for carefully reading the manuscript and for your comments. We appreciate your understanding that the role of ACLY in metabolic programming of seminal vesicle epithelial cells has been strengthened in the revised version. On the other hand, we agree with your view that the increase in sperm motility and fertilization rate by oleic acid is minimal under the current experimental conditions. We agree that further evidence is needed to support our conclusion regarding the positive effects of oleic acid on sperm function. Based on your comments and our re-evaluation of the data, we have decided to remove the experiments and discussion on “OA and sperm motility” from the current paper (Fig. 7, Supplemental Figure 5A and C-F). In the revised paper, we have significantly toned down the claims on the previous role of oleic acid and instead focused on the metabolic regulatory mechanisms of seminal vesicle epithelial cells.

We hope that these revisions address your concerns and improve the overall clarity of the manuscript.

Recommendations for the authors:

Note from the reviewing editor: The reviewers agree that the revised manuscript is significantly improved and view the work as important. Both reviewers agree that the evidence for testosterone effects on seminal vesicle epithelial cells to support fatty acid synthesis is strong and suggest that the authors tone down their conclusion of oleic acid effect on sperm motility as the effect is very small. With this minor changes, the evidence to support the conclusion of the study is viewed as solid.

Thank you for recognizing the improvements that we have made to our manuscript and for appreciating the importance of our research. We also appreciate your assessment that the evidence for the effect of testosterone on seminal vesicle epithelial cells that support fatty acid synthesis is solid.

On the other hand, we agree with the two reviewers that the effect of oleic acid on sperm motility is limited and that the relevant data do not measure a direct relationship. Therefore, we have decided to withdraw the data set on the effect of oleic acid on sperm (Fig. 7, Supplemental Figure 5A and C-F) and focus this paper on seminal vesicle epithelial cells (in response to reviewer 2's suggestion). Given that testosterone-induced lipid (Fatty acid) synthesis in seminal vesicle epithelial cells is a key aspect of our study, we have included additional experiments in the revised manuscript to show how lipids affect sperm (New Supplemental Figure5, Lines 259-263).

With these revisions, the manuscript emphasizes the importance of testosterone-dependent fatty acid synthesis in seminal vesicle epithelial cells and the fact that this includes oleic acid. The title has also been partially revised in line with these revisions.

Reviewer #1 (Recommendations for the authors):

Minor Comments:

(1) The authors indicate in the methods that extracellular flux analysis was normalized to cell count. However, the y-axis units in Figs 4, 8, 9 and SFig 9 are not normalized.

(2) The OA label appears to be missing from Fig 7A. Additionally, the scale bar is offset in one of the images and the length of the scale bar does not appear to be mentioned in the figure legend.

Thank you for raising these points. We have corrected.

Fig. 7 has been withdrawn in response to Reviewer 2's suggestion.

Reviewer #2 (Recommendations for the authors):

With the experiments included in their revised version the authors strengthen their conclusions about testosterone-induced metabolic reprogramming in seminal vesicle cells resulting in reduced proliferation. The experiments surrounding ACLY are well-designed and give insights into the underlying molecular mechanisms. For other parts, the manuscript became less clear and it is often hard to follow the author's line of thoughts for their conclusions.

Based on the experiments shown in the manuscript this reviewer is still not convinced that OA positively affects sperm function. The changes in linear motility are minor, blastocyst levels are lower and the authors do not show that OA alone positively affects cleavage rate during AI. Without additional experiments that show a stronger effect on sperm function, the authors should consider focusing the manuscript exclusively on seminal vesicle epithelial cells.

Thank you for your constructive comments on our paper. We thank the reviewer for pointing out that the effect of oleic acid (OA) on sperm function is limited in our current experiments. As reviewer 1 also pointed out, we agree that further experiments and improved methodology are needed to reliably demonstrate the functional effects of OA on sperm. Because the strength of the data on the direct relationship between fatty acids in seminal fluid and improved sperm function is currently insufficient, we have removed the data set for oleic acid and sperm motility (Fig. 7, Supplemental Figure 5A and C-F) and focused on the “the mechanism of metabolic regulation of testosterone in seminal vesicle epithelial cells”. We have consistently narrowed the focus of the paper to the theme of “how testosterone changes energy metabolism in seminal vesicle epithelial cells”. In accordance with this change, the structure of the paper has also been partially revised (red text in the manuscript). With these revisions, the main point of the paper focuses on the mechanism by which testosterone regulates metabolic pathways in the seminal vesicle epithelial cells.

For more detailed revisions, please see the responses to your comments below.

(1) 45-55 still need major revision. It will not become clear to the reader what the authors mean by epididymal maturation. 'Ability to fertilize in in vitro?' Epididymal sperm are moving linearly in the absence of seminal vesicle fluid. Increased progressive motility, hyperactivation, and the ability to undergo the acrosome reaction are induced upon exposure to seminal vesicle fluid. The authors should introduce the concept of capacitation and that capacitation can be induced in vitro by exposure to bicarbonate and a cholesterol acceptor.

Thank you for pointing out the ambiguity of epididymal maturation, the need to clarify the concept of capacitation, and the role of seminal plasma in this context. The revised text explains that epididymal maturation only gives sperm their potential ability to fertilize. It also explains that it is the subsequent capacitation process—inducible in vitro by incubation with bicarbonate and cholesterol acceptors—that gives full fertilization potential. On the other hands, we emphasize that in vivo, seminal plasma, which contains both capacitation-promoting and decapacitation factors, plays a key role in fine-tuning the timing of capacitation, ensuring that sperm acquire fertilization competence at the appropriate moment. We hope that these revisions clarify our intended meaning and strengthen the overall message of the paragraph. (lines 42-54)

“Sperm that have completed spermatogenesis in the testis acquire their potential to fertilize while maturing in the epididymis (5–7). The physiological change of sperm during fertilization process are collectively referred to as “capacitation”. This change includes a large amplitude of flagella (called hyperactivation) and developing the capacity to undergo the acrosome reaction, and can be induced by culturing sperm collected from the epididymis in a medium containing bicarbonate and cholesterol acceptors (8, 9). However, once capacitation is complete, sperm cannot maintain that state for a long time. Therefore, even if epididymal sperm that have not been exposed to seminal plasma are artificially inseminated into the cervix or uterus, the fertilization rate remains low (10–12). That is because, in vivo, during ejaculation, exposure of epididymal sperm to seminal plasma masks the unintended capacitation as they pass through the female reproductive tract and ensures fertilization of sperm that reach the oviduct (13). In other words, seminal plasma plays an important role in fine-tuning the timing of sperm capacitation and in maintaining the sustained sperm motility needed to reach the oviduct.”

(2) 81: Similar as in their rebuttal the authors should further elute on the connection between fructose, citrate, and testosterone. That still does not become clear. Based on the author's explanation in the rebuttal, why are citrate and fructose levels higher when the animals are castrated?

We thank you for the opportunity to clarify our statement regarding the relationship between fructose, citrate, and testosterone. Our original explanation was intended to reflect the fact that testosterone from the testes has a stimulating effect on the accessory reproductive glands, and to report that the concentrations of fructose and citric acid were higher in the non-castrated (control) animals than in the castrated animals. In castrated animals, the absence of testosterone leads to decreased activity of these glands and, consequently, lower levels of these metabolites. To make this clear, we have revised the manuscript as follows. (lines 76-82)

“Several specific factors produced by the male accessory glands that contribute to seminal plasma and impact male fertility have been elucidated. For example, surgical removal of seminal vesicles in male mice and rats was associated with infertility (17, 22, 23). The observations that fructose (24) and citric acid (25) concentrations in seminal plasma of control mice and rats are higher than in castrated animals suggest that the specific metabolism of the accessory glands might be affected by testosterone derived from the testes, which activate intracellular androgen receptors (AR; NR3C4) required for gene regulation of transcription.”

(3) 111: This reviewer does not understand the author's obsession with reporting linear motility. Sperm are moving linearly when isolated from the epididymis. Again, increase of progressive motility is a well-defined hallmark of capacitation and primarily used in the field when discussing changes in sperm motility during capacitation. This reviewer is assuming that the changes in progressive vs linear motility in Fig. 7 are not significant because the data is more scattered. The % increase seems to be approximately the same. The same is true for Fig. 8. The increase in LIN is so small and not dose-dependent that this reviewer is not comfortable making that one of the main conclusions of the manuscript.

Our claim is based on the observation that seminal vesicle secretions significantly improve the linear motility (VSL and LIN) of sperm even in an environment that does not contain capacitation-inducing factors such as BSA. We interpret this as a survival strategy for sperm to pass through the female reproductive tract efficiently. Therefore, we believe that this does not mean that the meaning of “progressive motility” in the context of conventional capacitation is the same as that of progressive motility observed in seminal plasma.

However, the reviewer's point that the current data set does not sufficiently support what the minor increase in linear motility caused by oleic acid means is agreed with. Therefore, we have decided to withdraw the dataset on the effect of oleic acid on sperm motility (Fig. 7, Supplemental Figure 5A and C-F) and have revised the conclusion. (Lines 406-410)

(4) 128: For the mitochondrial membrane potential measurements the authors should mention that they included antimycin as a control. The manuscript would benefit from including scatter plots with unloaded controls to support their gating strategy. In its current stage, the gating between low and high membrane potential seems arbitrary.

Thank you for pointing this out. We have included an explanation of antimycin as a control in the main text (Lines 920-921). In addition, we have added some reference scatter plots and also added an explanation of the gating strategy between low and high membrane potentials (Supplemental Figure 1C and D, Lines 1101-1104). We hope this change will make the manuscript clearer.

(5) 190: What do the authors mean by: 'However, there was no difference in the Oligomycin-sensitive ECAR, indicating that testosterone may increase glucose metabolism but does not enhance the expression of a group of enzymes involved in the glycolytic pathway.'

Our original intention was to state that testosterone probably increases basal glycolytic flux via increased glucose uptake (as supported by the GLUT4 translocation data), but does not increase maximal glycolytic capacity, as indicated by the lack of difference in oligomycin-sensitive ECAR.

However, as Reviewer 1 previously pointed out, we agree that the assay conditions themselves, such as the use of oligomycin to inhibit oxidative mitochondria, may create non-physiological conditions and not fully reflect the energy distribution in vivo. Under these conditions, there is a possibility that the flow of glycolysis will increase artificially as a compensatory reaction, and parameters such as “maximum glycolytic capacity” should have been interpreted with caution.

Therefore, we have revised the manuscript to clarify that our data are a single-time point under defined experimental conditions and do not necessarily provide direct insight into changes in expression or activity of individual glycolytic enzymes.

“These data indicate that testosterone enhances glucose utilization. This leads to the interpretation that testosterone increases the flow of glycolysis by increasing glucose uptake and alters metabolic flux distribution.” (Lines 186-188)

(6) 205: Could the authors elaborate further on how they came to this conclusion: 'These results suggest that testosterone does not reduce transient enzyme activity in mitochondria but rather weakens the metabolic pathway of the mitochondrial TCA cycle and/or the electron transport chain due to the changes in gene expression patterns in seminal vesicle epithelial cells.' Based on their results at this point the authors have no insights about changes in enzyme activity or gene expression that might explain the phenotype.

Our statement is based on the following observations. In testosterone-treated cells, the addition of glucose increased ECAR, suggesting an increase in glycolytic flux due to an increase in glucose uptake. On the other hand, mitochondrial respiratory parameters (basal respiration, oligomycin-sensitive respiration, FCCP-uncoupled respiration, and reserve respiratory capacity) were significantly decreased under testosterone treatment.

From these results, it was speculated that testosterone promotes the redistribution of metabolic flux, directing it away from mitochondrial oxidative phosphorylation and towards the glycolytic pathway and, possibly, lipid synthesis. However, as the reviewers correctly point out, at this point, we have not directly measured changes in the activity or expression of individual enzymes in the TCA cycle or ETC. Therefore, in the next experiment, we extracted mRNA from the cells and performed gene expression analysis using real-time PCR. To make this clear, we have revised the manuscript as follows.

“Overall, these data indicate that testosterone promotes the redistribution of metabolic flux. In other words, testosterone increased glycolysis in seminal vesicle epithelial cells while decreasing mitochondrial respiration. To determine whether these changes were accompanied by changes in gene expression of specific metabolic-related enzymes, we analyzed gene expression levels.” (Lines 201-205)

(7) 219: Characterizing ACLY as an enzyme of the ETC is misleading. ACLY is a cytosolic enzyme that connects the TCA cycle with fatty acid synthesis.

We would like to thank you for pointing out that the description of the function of ACLY could be misunderstood. We agree that characterizing ACLY as an enzyme of the ETC could be misleading. Therefore, we have revised the sentence to clearly indicate that ACLY is a cytosolic enzyme that links the TCA cycle with fatty acid synthesis. The revised text is as follows:

"Interestingly, testosterone significantly increased the expression of Acly, which encodes a cytoplasmic enzyme that converts citrate transported from the TCA cycle into acetyl-CoA, a substrate that is essential for fatty acid synthesis." (lines216-218)

(8) 228: Which results support that ETC proteins were upregulated by flutamide?

We appreciate the reviewer for this point. In preliminary experiments, we analyzed ETC protein expression using real-time qPCR. Our data show that treatment with flutamide significantly upregulates the expression of genes involved in mitochondrial ETC, such as mtND6, while decreasing the expression of the lipogenic genes Acly and Acc. These additional data are now presented in Supplementary Figure S3B. (lines 223-226)

(9) 245: Aren't the authors showing in Fig. 5 that glut4 expression is reduced in seminal vesicle epithelial cells upon testosterone treatment? How does that fit into the author's hypothesis?

Thank you for pointing this out. We have already responded to a similar comment from Reviewer 3 in a previous revision. Please refer to our response to Reviewer 3 in a previous version.

(10) 285: Based on the author's results OA increases the oocyte cleavage rate but then reduces the rate of blastocyst to cleaved oocyte. Doesn't that mean OA affects negatively early development?

We thank the reviewer for the insightful comment. The one-hour pre-treatment is designed to reflect the transient exposure of sperm to the seminal plasma during ejaculation. In this context, it is unlikely that such a short exposure would impair the overall developmental potential of the embryo. However, although pre-conditioning with oleic acid does not ultimately affect the development of the offspring, it may lead to a decrease in the blastocyst rate at a certain point (approximately 96-120 hours after fertilization). We agree that additional research is needed to demonstrate this.

Therefore, because the experiments related to the effects of oleic acid on sperm and fertilization are currently incomplete, we have decided to withdraw them for future research.

(11) 305: What happens to pyruvate and lactate levels when ACLY expression is reduced?

We appreciate the reviewer’s question regarding the fate of pyruvate and lactate when ACLY expression is reduced. In the absence of testosterone (Ctrl), the expression level of ACLY decreases. At this time, the concentration of pyruvate in the culture medium increased compared to that of testosterone (Testo; Fig. 4D,E). This is probably a reflection of the fact that when the expression of ACLY is suppressed, the rate at which the products of the glycolytic pathway are converted to the fat-producing pathway (i.e., the conversion of citrate to acetyl-CoA) decreases.

On the other hand, lactate levels did not change significantly. This suggests that the flow of lactate production via lactate dehydrogenase is relatively constant, independent of metabolic reprogramming by ACLY.

Therefore, our data suggest that a decrease in ACLY expression leads to a decrease in pyruvate demand, while lactate production is maintained. We interpret these findings as supporting the idea that ACLY is important for directing the carbon produced by the glycolytic pathway to lipid synthesis (by transporting citrate from the mitochondria).

We hope that this explanation clarifies the interpretation of the data.

Minor revision:

189: ECAR: extracellular acidification rate. Please correct.

We have corrected this. (Lines 184-185)

199: Pyruvate is not synthesized, it is metabolized from PEP. Please correct.

The following corrections have been made. “pyruvate is metabolized from phosphoenolpyruvic acid through glycolysis”. (Lines 194-195)

In addition, minor revisions were made to improve the clarity of the overall text.

Author response:

The following is the authors’ response to the original reviews

Public reviews:

Reviewer #1:

(1) This manuscript introduces a useful curation pipeline of antibody-antigen structures downloaded from the PDB database. The antibody-antigen structures are presented in a new database called AACDB, alongside annotations that were either corrected from those present in the PDB database or added de-novo with a solid methodology. Sequences, structures, and annotations can be very easily downloaded from the AACDB website, speeding up the development of structure-based algorithms and analysis pipelines to characterize antibody-antigen interactions. However, AACDB is missing some key annotations that would greatly enhance its usefulness.

Here are detailed comments regarding the three strengths above:

I think potentially the most significant contribution of this database is the manual data curation to fix errors present in the PDB entries, by cross-referencing with the literature. However, as a reviewer, validating the extent and the impact of these corrections is hard, since the authors only provided a few anecdotal examples in their manuscript.

I have personally verified some of the examples presented by the authors and found that SAbDab appears to fix the mistakes related to the misidentification of antibody chains, but not other annotations.

(a) "the species of the antibody in 7WRL was incorrectly labeled as "SARS coronavirus B012" in both PDB and SabDab" → I have verified the mistake and fix, and that SAbDab does not fix is, just uses the pdb annotation.

(b) "1NSN, the resolution should be 2.9 , but it was incorrectly labeled as 2.8" → I have verified the mistake and fix, and that sabdab does not fix it, just uses the PDB annotation.

(c) "mislabeling of antibody chains as other proteins (e.g. in 3KS0, the light chain of B2B4 antibody was misnamed as heme domain of flavocytochrome b2)" → SAbDab fixes this as well in this case.

(d) "misidentification of heavy chains as light chains (e.g. both two chains of antibody were labeled as light chain in 5EBW)" → SAbDab fixes this as well in this case.

I personally believe the authors should make public the corrections made, and describe the procedures - if systematic - to identify and correct the mistakes. For example, what was the exact procedure (e.g. where were sequences found, how were the sequences aligned, etc.) to find mutations? Was the procedure run on every entry?

We appreciate the reviewer’s valuable feedback. Our correction procedures combined manual curation with systematic sequence analysis. While most metadata discrepancies were resolved through cross-referencing original literature, we implemented a structured approach for identifying mutations in specific cases. For PDB entries labeled as variants (e.g., "Bevacizumab mutant" or "Ipilimumab variant Ipi.106") where the "Mutation(s)" field was annotated as "NO," we retrieved the canonical therapeutic antibody sequence from Thera-SAbDab, then performed pairwise sequence alignment against the PDB entry using BLAST program to identified mutated residues.

This procedure was not applied to all entries, as mutations are context-dependent. Therapeutic antibodies have well-defined reference sequences, enabling systematic alignment. For antibodies lacking unambiguous wild-type references (e.g., research-grade or non-therapeutic antibodies), mutation annotations were directly inherited from the PDB or literature.

All corrections have been publicly archived in AACDB. We have added a detailed discussion of this issue in the section “2.3 Metadata” of revised manuscript.

(2) I believe the splitting of the pdb files is a valuable contribution as it standardizes the distribution of antibody-antigen complexes. Indeed, there is great heterogeneity in how many copies of the same structure are present in the structure uploaded to the PDB, generating potential artifacts for machine learning applications to pick up on. That being said, I have two thoughts both for the authors and the broader community. First, in the case of multiple antibodies binding to different epitopes on the same antigen, one should not ignore the potentially stabilizing effect that the binding of one antibody has on the complex, thereby enabling the binding of the second antibody. In general, I urge the community to think about what is the most appropriate spatial context to consider when modeling the stability of interactions from crystal structure data. Second, and in a similar vein, some antigens occur naturally as homomultimers - e.g. influenza hemagglutinin is a homotrimer. Therefore, to analyze the stability of a full-antigen-antibody structure, I believe it would be necessary to consider the full homo-trimer, whereas, in the current curation of AACDB with the proposed data splitting, only the monomers are present.

We sincerely appreciate the reviewer’s insightful comments regarding the splitting of PDB files and we appreciate the opportunity to address the reviewer’s thoughtful concerns.

Firstly, when two antibodies bind to distinct epitopes on the same antigen, we would like to clarify that this scenario can be divided into two cases based on the experimental context: Case1: When two antibodies bind to distinct epitopes on the same antigen, and their complexes are determined in separate structures. For example, SAR650984 (PDB: 4CMH) and daratumumab (PDB: 7DHA) target CD38 at non-overlapping epitopes. These two antibody-antigen complexes were determined independently, and their structures do not influence each other. Case 2 : When the crystal structure contains a ternary complex with two antibodies and an antigen, as in the example of 6OGE discussed in Section 2.2 of our manuscript. After reviewing the original literature, the experiment confirmed that the order of Fab binding does not affect the formation of the ternary complex, and the binding of one antibody does not enhance the binding of the other. This supports the rationale for splitting 6OGE into two separate structures. However, we acknowledge that not all ternary complexes in the PDB provide such detailed experimental descriptions in their original literature. We agree with the reviewer that in some cases, one antibody may stabilize the structure to facilitate the binding of a second antibody. For instance, in 3QUM, the 5D5A5 antibody stabilizes the structure, enabling the binding of the 5D3D11 antibody to human prostate-specific antigen. Such sandwich complexes are indeed valuable for identifying true epitopes and paratopes. Importantly, splitting the structure does not alter the interaction sites.

Secondly, we fully agree with the reviewer that for antigens that naturally exist as homomultimers (e.g., influenza hemagglutinin as a homotrimer), the full multimeric structure should be considered when analyzing stability. In such cases, users can directly utilize the original PDB structures provided in their multimeric form. Our splitting approach is intended to provide an additional option for cases where monomeric analysis is sufficient or preferred, but it does not preclude the use of the original multimeric structures when necessary.

(3) I think the manuscript is lacking in justification about the numbers used as cutoffs (1A^2 for change in SASA and 5A for maximum distance for contact) The authors just cite other papers applying these two types of cutoffs, but the underlying physico-chemical reasons are not explicit even in these papers. I think that, if the authors want AACDB to be used globally for benchmarks, they should provide direct sources of explanations of the cutoffs used, or provide multiple cutoffs. Indeed, different cutoffs are often used (e.g. ATOM3D uses 6A instead of 5A to determine contact between a protein and a small molecule https://datasets-benchmarks-proceedings.neurips.cc/paper/2021/hash/c45147dee729311ef5b5c3003946c48f-Abstract-round1.html). I think the authors should provide a figure with statistics pertaining to the interface atoms. I think showing any distribution differences between interface atoms determined according to either strategy (number of atoms, correlation between change in SASA and distance...) would be fundamental to understanding the two strategies. I think other statistics would constitute an enhancement as well (e.g. proportion of heavy vs. light chain residues).

Some obvious limitations of AACDB in its current form include:

AACDB only contains entries with protein-based antigens of at most 50 amino acids in length. This excludes non-protein-based antigens, such as carbohydrate- and nucleotide-based, as well as short peptide antigens.

AACDB does not include annotations of binding affinity, which are present in SAbDab and have been proven useful both for characterizing drivers of antibody-antigen interactions (cite https://www.sciencedirect.com/science/article/pii/S0969212624004362?via%3Dihub) and for benchmarking antigen-specific antibody-design algorithms (cite https://www.biorxiv.org/content/10.1101/2023.12.10.570461v1)).

We thank the reviewer for raising this critical point about the cutoff values used in AACDB. In the current study, the selection of the threshold value is very objective; the threshold chosen in the manuscript is summarized based on existing literature, and we have provided more literature support in the manuscript. The criteria for defining interacting amino acids in established tools, typically do not set the ΔSASA exceed 1 Å2 and the distance exceed 6 Å. While our manuscript emphasizes widely accepted thresholds for consistency with prior benchmarks, AACDB explicitly provides raw ΔSASA and distance values for all annotated residues. Users can dynamically filter the data from downloaded files by excluding entries exceeding their preferred thresholds (e.g., selecting 5Å instead of 6Å). This ensures adaptability to diverse research needs. In the revised version, we reset the distance threshold to 6 Å and calculated the interacting amino acids in order to give the user a wider range of choices. In the section “3.2 Database browse and search” of revised manuscript, we provide a description of the flexible choice of thresholds for practical use.

Furthermore, distance and ΔSASA are two distinct metrics for evaluating interactions. Distance directly quantifies spatial proximity between atoms, reflecting physical contacts such as van der Waals interactions or hydrogen bonds, and is ideal for identifying direct spatial adjacency. ΔSASA, on the other hand, measures changes in solvent accessibility of residues during binding, capturing the contribution of buried surfaces to binding free energy. Even for residues not in direct contact, reduced SASA due to conformational changes may indicate indirect functional roles.

As demonstrated through comparisons on the detailed information pages, the sets of interacting amino acids defined by these two methods differ by only a few residues, with no significant variation in their overall distributions. However, since interaction patterns vary significantly across different complexes, analyzing residue distributions across all structures using both criteria is not feasible.

We thank the reviewer for highlighting these limitations. AACDB currently focuses on protein-based antigens ≤50 amino acids to prioritize structural consistency, which excludes non-protein antigens and shorter peptides. While affinity annotations are critical for benchmarking antibody design tools, these data were not integrated in this release due to insufficient data verification caused by internal team constraints. We acknowledge these gaps and plan to expand antigen diversity and incorporate affinity metrics in future updates.

Reviewer #2:

Summary:

Antibodies, thanks to their high binding affinity and specificity to cognate protein targets, are increasingly used as research and therapeutic tools. In this work, Zhou et al. have created, curated, and made publicly available a new database of antibody-antigen complexes to support research in the field of antibody modelling, development, and engineering.

Strengths:

The authors have performed a manual curation of antibody-antigen complexes from the Protein Data Bank, rectifying annotation errors; they have added two methods to estimate paratope-epitope interfaces; they have produced a web interface that is capable of both effective visualisation and of summarising the key useful information in one page. The database is also cross-linked to other databases that contain information relevant to antibody developability and therapeutic applications.

Weaknesses:

The database does not import all the experimental information from PDB and contains only complexes with large protein targets.

Thank you for the valuable feedback. As previously responded to Reviewer 1, due to limitations within our team, comprehensive data integration from PDB has not been achieved in the current version. We acknowledge the significance of expanding the database to encompass a broader range of experimental information and complexes with diverse target sizes. Regrettably, immediate updates to address these limitations are not feasible at this time. Nevertheless, we are committed to enhancing the database in upcoming upgrades to provide users with a more comprehensive and inclusive resource

Recommendations for the authors:

Reviewer #1:

(1) Line 194: "produce" → "produced"

We thank the reviewer for the feedback. We have checked the grammar and spelling carefully in the revised manuscript.

(2) As mentioned in the public review, I think adding binding affinity annotations would greatly enhance the use cases for the database.

We thank the reviewer for the suggestion. As the response in “Public review”. Due to team constraints, these data are not integrated into this release but are being collated. We recognize these gaps and plan to expand antigenic diversity and incorporate affinity metrics in future updates.

(3) I think adding a visualization of interface atoms and contacts on an entry's webpage would be useful for someone exploring specific entries. It also would be useful if the authors provided a pymol command to select interface residues since that's a procedure any structural biologist is likely to do.

We sincerely appreciate the reviewer’s constructive suggestions. In response to the request for enhanced visualization and accessibility of interface residue information, we have implemented the following improvements: (1) Web Interface Visualization. On the entry-specific webpage, we have added an interactive visualization window that highlights the antigen-antibody interaction interface using distinct colors. The interaction interface visualization has been incorporated into Figure 5 of the revised manuscript, with a detailed description. (2) PyMOL Command Accessibility. The “Help” page now provides step-by-step PyMOL commands to select and visualize interface residues.

(4) I think the authors should provide headers to the files containing interface residues according to the change-in-SASA criterion, as they do for those computed according to contact. This would avoid unnecessary confusion - however slight - and make parsing easier. I was initially confused by the meaning of the last column, though after a minute I understood it to be the change in SASA.

We thank the reviewer for providing such detailed feedback. We thank the reviewer for the comment and the suggestion. We have provided headers for the files of the interacting residues defined by ΔSASA.

(5) Line 233: "AACDB's data processing pipeline supports mmCIF files" → The meaning and implications of this statement are not obvious to me, and are mentioned nowhere else in the paper. Do you mean that in AACDB there are structure entries that the RCSB PDB database only has in mmCIF file format, and not .pdb format? So, effectively, there are some entries in AACDB that are not in any other antibody-specific database?I checked and, as of Dec 3rd, 2024, there are 41 structures in AACDB that are NOT in SAbDab. Manually checking 5 of those 41 structures, none are mmCIF-only structures.

We thank the reviewer for the valuable comment. Because of the size of the structures within certain entries, representing them in a single PDB format data file is not feasible due to the excessive number of atoms and polymer chains they contain. As a result, PDB stores these structures in “mmcif” format files. In AACDB, 47 entries, such as 7SOF, 7NKT, 7B27, and 6T9D, are only available in the “mmCIF” format from the PDB. The “.pdb” and “.cif” files contain atomic coordinates in distinct text formats, and the segmentation of these structure files is automatically conducted based on manually annotated antibody-antigen chains. To accommodate this, we have incorporated these considerations into our file processing pipeline, thereby enabling a fully automated file segmentation process. Additionally, we employed Naccess to calculate interatomic distances. However, since this software only accepts .pdb format files as input, we also converted all split .cif files into .pdb format within our fully automated pipeline. We apologize for the lack of clarity in the original manuscript and have included a more detailed explanation in the "2.2 PDB Splitting" section of the revised manuscript.

Reviewer #2:

(1) In SabDab and PDB, experimental binding affinities are also reported: could the authors comment on whether they also imported this information and double-checked it against the original paper? If it wasn't imported, that might discourage some users and should be considered as an extension for the future.

We thank the reviewer for the comment and the suggestion. As the response in “Public review”. Due to current resource constraints, quantitative affinity data has not been incorporated into this release but is undergoing systematic curation. We explicitly recognize these limitations and propose a two-pronged strategy for future iterations: (1) broadening antigen diversity coverage through expanded structural sampling, and (2) integrating quantitative binding affinity measurements. In the Discussion section, we have included description outlining the planned enhancements.

(2) Line 49-50: the references mentioned in connection to deep learning methods for antibody-antigen predictions seem a bit limited given the amount of articles in this field, with 3 of 4 references on one method only (SEPPA), could the authors expand this list to reflect a bit more the state of the art?

We thank the reviewer for the suggestion. We agree that more relevant studies should be listed and therefore more references are provided in the revised manuscript.

When mentioning the limitations of the existing databases, it feels a bit that the criticism is not fully justified. For instance:

Line 52-53: could the authors elaborate on the reasons why such an identification is challenging? (Isn't it possible to make an efficient database-filtered search? Or rather, should one highlight that a more focussed resource is convenient and why?)

Thank you for feedback. In this study, the keywords "antibody complex," "antigen complex," and "immunoglobulin complex," were employed during data collection. PDB returned over 30,000 results, of which only one-tenth met our criteria after rigorous filtering. This demonstrates that keyword searches, while useful, inherently limit result precision and introduce substantial redundancy, likely due to the PDB's search mechanism. That’s why we illustrated the significant challenges in identifying antibody-antigen complexes from general protein structures in the PDB.

Line 55: reading the website http://www.abybank.org/abdb/, it would be fairer to say that the web interface lacks updates, as the database and the code have gone through some updates. Could the authors provide a concrete example of the reason why: 'The AbDb database currently lacks proper organization and management of this valuable data.'?

We thank the reviewer for highlighting this issue. In our original manuscript, the statement that the AbDb database "lacks proper organization and management" was based on the absence of explicit statement regarding data updates on its official website at the time of submission, even though internal updates to its content may have occurred. We fully respect the long-standing contributions of AbDb to antibody structural research, and our comments were solely directed at the specific state of the database at that time. As the reviewer noted, following the release of our preprint, we have also taken note of AbDb's recent updates. To reflect the latest developments and avoid potential misinterpretation, we have revised the original statement in revised manuscript.

Also 'this rapid updating process may inadvertently overlook a significant amount of information that requires thorough verification,': it's difficult for me to understand what this means in practice. Could the authors clarify if they simply mean that SabDab collects information from PDB and therefore tends to propagate annotation errors from there? If yes, I think it's enough to state it in these terms, and for sure I agree that the reason is that correcting these annotation errors requires a substantial amount of work.

We thank the reviewer for providing such detailed feedback on the manuscript. We acknowledge that SabDab represents a highly valuable contribution to the field, and its rapid update mechanism has significantly advanced related research areas. However, as stated by the reviewer, we aim to clarify that SabDab primarily relies on automated metadata extraction from the PDB for annotation, and its rapid update process inherently inherits raw data from upstream sources. According to their paper, manual curation is only applied when the automated pipeline fails to resolve structural ambiguities. This workflow—dependent on PDB annotations with limited manual verification—may propagate errors provided by PDB. Examples include species misannotation and mutation status misinterpretation. We fully agree with the reviewer's observation that correcting errors in such cases necessitates labor-intensive manual curation, which is a core motivation for our study.

Line 86: why 'Structures that consisted solely of one type of antibody were excluded'? Why exclude complexes with antigens shorter than 50 amino acids? These complexes are genuine antibody-antigen complexes.

We thank the reviewer for the valuable question. The AACBD database is dedicated to curating structural data of antigen-antibody complexes. Structures featuring only a single antibody type are classified as free antibodies and systematically excluded from the database due to the absence of protein-bound partners. During data screening , we retained sequences shorter than 50 amino acids by categorizing them as peptides rather than eliminating them outright. The current release exclusively encompasses complexes with protein-based antigens. Meanwhile, complexes involving peptide, haptens, and nucleic acid antigens are undergoing systematic curation, with planned inclusion in future updates to broaden antigen category representation.

Line 96 needs a capital letter at the beginning.

Line 107: 'this would generate' → 'this generates' (given it is something that has been implemented, correct?).

Line 124: missing an 'of'.

Line 163: inspiring by -> inspired by.

Thank you for feedback. All of the above grammatical or spelling errors have been revised in the manuscript.

Line 109-111: apart from the example, it would be good to spell out the general rule applied to anti-idiotypic antibodies.

We thank the reviewer for the valuable feedback. For anti-idiotypic antibodies complex. the partner antibody is treated as a dual-chain antigen, , necessitating individual evaluation of heavy chain and light chain interactions with the anti-idiotypic component. We have given a general rule for anti-idiotypic antibodies in section “2.2 PDB splitting” of revised manuscript.

Line 155-159: could the authors provide references for the two choices (based on sasa and any-atom distance) that they adopted to define interacting residues?

We thank the reviewer for the comment and the suggestion. As the same as the response to reviewer #1 in Public review. The interacting residues definition and the threshold chosen in the manuscript is summarized based on existing literature. We have added additional references for support in section “1.Introduction”. Our resource does not provide a fixed amino acid list. Instead, all interacting residues are explicitly documented alongside their corresponding ΔSASA (solvent-accessible surface area changes) and intermolecular distances, allowing researchers to flexibly select residue pairs based on customized thresholds from downloadable datasets. Furthermore, aligning with widely adopted criteria in current literature—where interactions are defined by ΔSASA >1 Ų and atomic distances <6 Å, we have recalibrated our analysis in the revised version. Specifically, we replaced the previous 5 Å distance threshold with a 6 Å cutoff to recalculate interacting residues.

Line 176-178: could the authors re-phrase this sentence to clarify what they mean by 'change in the distribution'?

We thank the reviewer for the suggestion. Our search was conducted with an end date of November 2023. However, Figure 3B includes an entry dated 2024. Upon reviewing this record, we identified that the discrepancy arises from the supersession of the 7SIX database entry (originally released in December 2022) by the 8TM1 version in January 2024. This version update explains the apparent chronological inconsistency. We regret any lack of clarity in our original description and have revised the corresponding section in the manuscript to explicitly clarify this change of database.

Caption Figure 3: please spell out all the acronyms in the figure. Provide the date when the last search was performed (i.e., the date of the last update of these statistics).

We thank the reviewer for the comment. We have systematically expanded all acronyms and included update dates for statistics in the legend of Figure 3. Corresponding changes have also been made to the statistical pages on the website.

Finally, it would be advisable to do a general check on the use of the English language (e.g. I noted a few missing articles). In Figure 5 DrugBank contains typos.

We sincerely appreciate the reviewer's meticulous attention to linguistic precision. We have corrected the typographical error in Figure 5 and conducted a comprehensive review of the entire manuscript to ensure accuracy and clarity.

Author response:

We are highly appreciative of your constructive criticism and that you found that our findings of interest and significance. Based on your helpful suggestions, we plan to revise the paper as following:

(1) Although ETFDH is reduced, but not mutated across neoplasia, we appreciate your point pertinent to catalytically activity of ETFDH. To this end, in the revision we are planning to compare the effects of rescues using wild type ETFDH or one of the MADD-associated mutants with compromised catalytic activity.

(2) We intend to measure steady-state nucleotide levels as a function of ETFDH status in the cell. If time and/or funding allow, we will also perform appropriate labelling experiments.

(3) We will revise the text of the manuscript to address the minor points raised by the reviewers.

Again, we would like to thank you for helpful comments, which we aim to address as outlined above and hopefully further improve our report.

Author response:

We sincerely thank all reviewers for their thoughtful, detailed, and supportive evaluations of our manuscript. We are very pleased that the reviewers appreciated the integrative approach of our study, the quality of the imaging and analyses, and the insights provided into the parallel evolution of biomineralization mechanisms in sponges and corals.

We are carefully considering all the suggestions made, including those regarding the improvement of figure clarity and the clarification of certain image interpretations. These comments are extremely valuable, and we are preparing a detailed point-by-point reply to accompany our revised manuscript.

It was also brought to our attention that the links to the Zenodo repository were incorrect. We apologize for this oversight and any inconvenience it may have caused and will updae the links in our revised manuscript. In the meantime, the correct Zenodo repositories can be accessed using the following links:

https://zenodo.org/records/14755899

https://zenodo.org/records/13847772

We again thank the reviewers for their constructive feedback, which will help us to further strengthen the manuscript.

Author response:

We thank the editors and reviewers for their thoughtful and constructive evaluation of our manuscript, “Krüppel Regulates Cell Cycle Exit and Limits Adult Neurogenesis of Mushroom Body Neural Progenitors in Drosophila.” We are pleased that all reviewers recognised the novelty and significance of identifying Krüppel (Kr) as a key transcription factor promoting timely termination of mushroom body neuroblast (MBNB) proliferation, and the potential antagonistic function of Kr-h1.

We appreciate the helpful suggestions aimed at improving the mechanistic clarity and presentation of our findings. Below, we outline how we plan to address the major points raised in the full revision.

(1) Characterisation of the KrIf-1 allele and Kr expression

We agree that clarifying the nature of the KrIf-1 allele is important. In response to this concern, we will examine Kr expression in KrIf-1 mutant larval, pupal, and adult brains using immunostaining and available reporter lines. These experiments will help determine whether the observed neuroblast retention phenotype correlates with altered Kr expression in MBNBs.

(2) Regulatory relationships between Kr, Kr-h1, Imp, Syp, Chinmo, and E93

We are currently performing additional experiments to clarify the interactions among these temporal factors. For instance, we are testing whether Kr-h1 overexpression alters the expression of Imp, Syp, and E93. We have obtained a published E93 antibody from Dr Chris Doe (Syed et al., 2017) and will include E93 expression analysis in our revised manuscript.

While Chinmo is of interest, its expression is well established to be regulated downstream of Imp/Syp via mRNA stability (Liu et al., 2015; Ren et al., 2017). Given that we currently lack reliable tools to assess Chinmo levels, we will focus primarily on Imp, Syp, and E93 as readouts for Kr/Kr-h1 function. If we succeed in obtaining Chinmo antibodies or reporter lines in time, we will include corresponding data.

(3) Expression of Kr-h1 in MBNBs

We fully agree that direct evidence for Kr-h1 expression in MBNBs is important. To address this, we have obtained the Kr-h1::GFP BAC transgenic line (BDSC #96786) and are currently using it to assess Kr-h1 expression in MBNBs. We also tested an anti–Kr-h1 antibody previously reported by Kang et al. (2017), developed in the context of fat body studies, but it did not yield clear signals in larval MBNBs. However, previous work by Shi et al. (2007) clearly demonstrated Kr-h1 expression in the developing MB, including MBNBs, using a custom antibody developed by their lab. We also contacted the Lee lab to request this antibody, but unfortunately, it is no longer available. We will include the results obtained using the GFP BAC line in the revised manuscript and, if needed, pursue RNA in situ hybridisation to further validate Kr-h1 expression in MBNBs.

(4) Temporal Kr knockdown and MARCM analysis

We appreciate the suggestion to validate our RNAi-based temporal knockdown results using MARCM. We plan to perform MBNB-specific MARCM analysis following the strategy described by Rossi et al. (2020). However, this approach requires additional time due to the logistics of acquiring the necessary fly stocks, generating appropriate genetic combinations, and conducting clonal analyses. While we will make every effort to include these data, we note that RNAi-based knockdown offers the advantage of temporal reversibility and has been essential for assessing stage-specific requirements in our current study.

(5) Details of the targeted genetic screen

Kr was initially identified as part of a broader, ongoing effort to screen for candidate transcription factors and cell cycle regulators involved in neuroblast cell cycle exit and/or quiescence. As this screen is still preliminary and incomplete, we prefer not to include the full dataset at this stage. Instead, we will revise the manuscript to clarify that Kr was prioritised for further investigation based on the striking MBNB-specific phenotype observed upon RNAi-mediated knockdown and in the KrIf-1 mutant, rather than through a completed screening process.

(6) Clarifying the model (Figure 6D) and interactions

We will revise the proposed model to distinguish between experimentally supported interactions and speculative ones. As noted above, we will primarily focus on the Imp/Syp and E93 axis in relation to Kr and Kr-h1 activity. Chinmo will be omitted from the model unless further data become available to support its inclusion.

(7) Clarifications on figures and data presentation

We appreciate the feedback on figure clarity. We will revise figures such as 1B, 2C, and 3A to improve legibility and presentation. We will also correct typographical errors and figure references, and clarify the activity patterns of the GAL4 drivers. Specifically, while UASmCD8::GFP expression driven by OK107-GAL4 is markedly weaker in MBNBs than in their neuronal progeny (as seen, for example, in Figure S3C), the driver remains active and functionally relevant in MBNBs. We believe the weak expression in MBNBs likely explains the absence of a NB retention phenotype in OK107>KrIR adult brains (see main text, Lines 374–376). As suggested by the reviewer, we will clarify this point earlier in the manuscript and can include additional data showing OK107>GFP expression patterns in pupal MB lineages as supplementary material.

(8) Analysis of public datasets

We will include results from our analysis of publicly available datasets such as FlyAtlas2, modENCODE, and a time-course RNA-seq dataset specific to MBNBs (Liu et al., 2015). While the spatial resolution of FlyAtlas2 and modENCODE is limited, the MBNB dataset provides valuable temporal information up to 36 h after puparium formation (APF). From this dataset, we observe that Kr expression remains consistently low throughout development, with only a modest increase at 84 h ALH (mean TPM ~11) and 36 h APF (~7), suggesting it does not undergo strong transcriptional regulation in MBNBs. In contrast, Kr-h1 is highly expressed during early larval stages (24–84 h ALH; mean TPM ~55–60) and shows a marked suppression by 36 h APF (mean TPM ~2), consistent with its proposed role in promoting MBNB proliferation. Importantly, Eip93F (E93) exhibits a reciprocal pattern to Kr-h1—with minimal expression until 84 h ALH (mean TPM ~24), followed by a substantial induction at 36 h APF (mean TPM ~104), aligning with its known role in triggering neuroblast termination. These temporal expression dynamics support our model that Kr-h1 and E93 function in opposition during the transition from proliferative to terminating neuroblast states. We will summarise these findings in the revised manuscript, along with appropriate discussion of dataset limitations.

We hope this provisional response conveys our strong commitment to thoroughly addressing the reviewers’ concerns and improving the manuscript. We are currently carrying out additional experiments and will submit a revised version with new data and enhanced clarity in due course.

References:

Kang et al., 2017. Sci Rep. 7(1):16369. doi: 10.1038/s41598-017-16638-1.

Shi et al., 2007. Dev Neurobiol. 67(11):1614–1626. doi: 10.1002/dneu.20537.

Rossi et al., 2020. eLife. 9:e58880. doi: 10.7554/eLife.58880.

Liu et al., 2015. Science. 350(6258):317–320. doi: 10.1126/science.aad1886.

Ren et al., 2017. Curr Biol. 27(9):1303–1313. doi: 10.1016/j.cub.2017.03.018. Syed et al., 2017. eLife. 6:e26287. doi: 10.7554/eLife.26287.

Author response:

Reviewer #1 (Public review):

Summary:

The manuscript by Garcia et al. describes how the expression of a respiratory chain alternative oxidase (AOX) from the tunicate Ciona intestinalis, capable of transferring electrons directly from reduced coenzyme Q (CoQ) to oxygen, is able to induce an increase in the mass of Drosophila melanogaster larvae and an accelerated development, especially when the larvae are kept at low temperatures. In order to explain this phenomenon, the paper addresses the modifications in the activity and levels of the 'canonical' electron transfer system (ETS), i.e., complexes I-IV and of the ATP synthase. In addition, the abundance of different metabolites as well as the NAD+/NADH ratios are measured, finding significant differences between the larvae.

Strengths:

The observations of differences in growth, body mass and food intake in the wt D. melanogaster larvae vs. those expressing the AOX transgene are solid. The evidence that mild uncoupling of the ETS might accelerate development of the fly larvae is convincing."

We appreciate the reviewer’s attention to our results and hope we can improve the manuscript to address all criticism appropriately.

Weaknesses:

Some of the observations, especially those concerning the origin of the metabolic remodelling in AOX-expressing larvae, are left unexplained, and the argumentation is somewhat speculative. What the authors mean by "reconfiguration" of the mitochondrial electron transfer system is not clear. If this implies that there is an actual change in ETS function and/or structural organisation in the presence of AOX, this conclusion is not supported by the experimental data. In addition, the influence of AOX activity in the mitochondrial ETS system is tested in vitro in the presence of saturating concentrations of substrates. The real degree to which AOX activity is actually influencing ETS activity in vivo remains unknown.

Indeed, the term “reconfiguration” may seem a little too strong. However, we do have preliminary structural data on larval mitochondria indicating that the term is adequate in this context. We plan to work on obtaining concrete data to sustain our claims that AOX imparts significant functional and structural remodeling of the organelle, which would be consistent with our respirometry and BN-PAGE data. If the data turns out not to be robust enough, we will consider replacing the term with one that better reflects our findings.

We also realize that the in vivo data we are presenting (body mass, mobility, food intake) are indirect measurements of metabolism and that a more direct approach is necessary to assess the real degree to which AOX influences ETS activity in vivo. To address this issue, we plan to expand our pharmacological treatments of the larval development and to measure whole larval oxygen consumption.

Reviewer #2 (Public review):

Summary:

This manuscript presents intriguing findings about the role of alternative oxidase (AOX) from the tunicate Ciona intestinalis in accelerating growth and development when expressed in Drosophila melanogaster.

Strengths:

The study is overall well-constructed, including appropriate analysis. Likewise, the manuscript is written clearly and supported by high-quality figures. The present study provides valuable insights into AOX's role in Drosophila development. The paper attempts to explore a unique mechanism by which AOX influences Drosophila development, providing insights into mitochondrial respiration and its physiological effects. This is relevant for understanding mitochondrial dysfunction and potential therapeutic applications. The study employs a variety of approaches, including calorimetry, infrared thermography, and genetic analyses, to investigate AOX's impact on metabolism and development.

We sincerely thank the reviewer for recognizing the strengths and acknowledging the novelty of our study.

Weaknesses:

There are a number of methodological limitations and substantial gaps in the interpretation of the data presented, which reduces the strength of its conclusions. For instance, there is a misunderstanding of the non-proton motive nature of the AOX - it does not uncouple respiration, merely decouple it as it neither contributes to nor dissipates the proton motive force, in contrast to chemical uncouplers or proton uncouplers such as UCPs. The authors need to reassess their data in light of the above.

The reviewer is absolutely right about the non-proton motive nature of AOX. We will reassess our data considering that AOX decouples respiration and, if necessary and possible, we will add new experiments to address the methodological limitations raised by the reviewer.

Author response:

We appreciate the reviewers' positive feedback on our paper. We especially thank them for their evaluation of the genetic analysis, which required a significant amount of timef time. We acknowledge that several aspects of our interpretation and description of the results need correction, as noted by both reviewers. Additionally, we recognize the importance of providing a more comprehensive overview of previous findings, including those conducted in mice, in the manuscript. In the revised version, we will thoroughly address the reviewers' concerns.

Both reviewers emphasized the need for further validation to ascertain whether the specific requirement of Hox genes in the Hoxba and Hoxbb clusters for pectoral fin bud formation is due to their expression patterns or the functional roles of Hox proteins. This consideration has been on our agenda for some time; however, our submitted paper does not sufficiently address this aspect. In the revised manuscript, we will conduct a comprehensive analysis of the expression patterns of Hox genes in zebrafish to draw informed conclusions on this matter.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

The authors investigate how the viscoelasticity of the fingertip skin can affect the firing of mechanoreceptive afferents and they find a clear effect of recent physical skin state (memory), which is different between afferents. The manuscript is extremely well-written and well-presented. It uses a large dataset of low threshold mechanoreceptive afferents in the fingertip, where it is particularly noteworthy that the SA-2s have been thoroughly analyzed and play an important role here. They point out in the introduction the importance of the non-linear dynamics of the event when an external stimulus contacts the skin, to the point at which this information is picked up by receptors. Although clearly correlated, these are different processes, and it has been very well-explained throughout. I have some comments and ideas that the authors could think about that could further improve their already very interesting paper. Overall, the authors have more than achieved their aims, where their results very much support the conclusions and provoke many further questions. This impact of the previous dynamics of the skin affecting the current state can be explored further in so many ways and may help us to better understand skin aging and the effects of anatomical changes of the skin.

At the beginning of the Results, it states that FA-2s were not considered as stimuli did not contain mechanical events with frequency components high enough to reliably excite them. Was this really the case, did the authors test any of the FA-2s from the larger dataset? If FA-2s were not at all activated, this is also relevant information for the brain to signal that it is not a relevant Pacinian stimulus (as they respond to everything). Further, afferent receptive fields that were more distant to the stimulus were included, which likely fired very little, like the FA-2s, so why not consider them even if their contribution was low?

Thank you for bringing this up, we have now clarified in the text that while FA-2s did respond at a low rate during the experiment, their responses were not reliably driven by the force stimuli. In the Methods section we have included the following text:

“Initially, 10 FA-2 neurons were also included in the analysis. But their responsiveness during the experiment was remarkably low, and unlike the other neuron types, their responses were rarely affected by force stimuli. Specifically, only one of the observed FA-2 neurons responded during the force protraction phases. Due to the lack of clear stimulus-driven responses, FA-2 neurons were subsequently excluded from further analysis.”

One question that I wondered throughout was whether you have looked at further past history in stimulation, i.e. not just the preceding stimulus, but 2 or 3 stimuli back? It would be interesting to know if there is any ongoing change that can be related back further. I do not think you would see anything as such here, but it would be interesting to test and/or explore in future work (e.g. especially with sticky, forceful, or sharp indentation touch). However, even here, it could be that certain directions gave more effects.

This is a very interesting question! A discernible effect from the previous stimulus could persist at the end of the current stimulation (see Figure 4C), potentially influencing the next one—a 2-stimuli-back effect. Unfortunately, our experimental design did not allow for rigorous testing of this effect. While all possible pairs of stimulus directions were included in immediately consecutive trials, this was not the case for pairs separated by additional trials. Hence, the combination of a likely weak effect and limited variation in history precluded a thorough analysis of a 2-stimuli-back effect. Future work should delve into the time course of the viscoelastic effect in greater detail.

Did the authors analyze or take into account the difference between receptive field locations? For example, did afferents more on the sides have lower responses and a lesser effect of history?

An investigation into the potential impact of the relationship between the receptive field location on the fingertip skin and the primary contact site of the stimulus surface revealed no discernible influence for SA-1 and SA-2 neurons. In contrast, FA-1 neurons, particularly those predominantly sensitive to the previous stimulation or displaying mixed sensitivity, exhibited a tendency to terminate near the primary stimulation site. We have added these observations to the text:

“We found no straightforward relationship between a neuron's sensitivity to current and previous stimulation and its termination site in fingertip skin. Specifically, there was no statistically significant effect of the distance between a neuron's receptive field center and the primary contact site of the stimulus surface on whether neurons signaled current, prior, or mixed information for SA-1 (Kruskal-Wallis test H(2)=3.86, p= 0.15) or SA-2 neurons (H(2)=0.75, p=0.69). However, a significant difference emerged for FA-1 neurons (H(2)=8.66, p=0.01), indicating that neurons terminating closer to the stimulation site on the flat part of the fingertip were more likely to signal past or mixed information.”

Was there anything different in the firing patterns between the spontaneous and non-spontaneously active SA-2s? For example, did the non-spontaneous show more dynamic responses?

The firing patterns of both spontaneously and non-spontaneously active SA-2 neurons shared similarities in terms of adaptation and range of firing rate modulation in response to force stimuli, i.e., ‘dynamic response’. The distinction lay in the pattern of modulation of the firing rate associated with stimulus presentations. For spontaneously active SA-2 neurons, this modulation occurred around a significant background discharge, implying that a force stimulus could either decrease or increase the firing rate, depending on how it deformed the fingertip. This characteristic is well illustrated by the firing pattern of the neuron depicted in the lower panels of Figure 3D. Conversely, in non-spontaneously active SA-2 neurons, a force stimulus could only induce an increase in the firing rate or no change. Although the neuron depicted in the upper panels of Figure 3D exhibited some background activity, it serves to exemplify this characteristic. In the text, we have elucidated the dynamics of the SA-2 neuron response by highlighting that force stimulation can either decrease or increase the firing rate in neurons with spontaneous activity through the following addition/change:

“This increased variability was most evident during the force protraction phase where most neurons exhibited the most intense responses. Increased variability was also observed in instances where the dynamic response to force stimulation involved a decrease in the firing rate (lower panels of Figure 3D). This phenomenon was observed in SA-2 neurons that maintained an ongoing discharge during intertrial periods (cf. Fig. 2A). In these cases, the response to a force stimulus constituted a modulation of the firing rate around the background discharge, signifying that a force stimulus could either decrease or increase the firing rate depending on the prevailing stimulus direction.”

Were the spontaneously active SA-2 afferents firing all the time or did they have periods of rest - and did this relate to recent stimulation? Were the spontaneously active SA-2s located in a certain part of the finger (e.g. nail) or were they randomly spread throughout the fingertip? Any distribution differences could indicate a more complicated role in skin sensing.

SA-2 neurons, in general, are well-known for undergoing significant post-stimulation depression (e.g., Knibestöl and Vallbo, 1970; Chambers et al., 1972; Burgess and Perl, 1973). In our force stimulations, this post-excitatory depression manifested as a reduced or absent response during the latter part of the stimulus retraction period for stimuli in directions that markedly excited the neuron. The excitability recovered when the fingertip relaxed during the subsequent intertrial period, and for "spontaneously active" neurons, the firing resumed (see examples in Figure 7A). Furthermore, some “spontaneously active” neurons could be silenced or exhibit a near-silent period during force stimulation for certain force directions, while the spontaneous firing returned during the upcoming intertrial period when the fingertip shape recovered (for example, see responses to stimulation in the proximal and especially ulnar directions in the top panel in Figure 7A).

Regarding the location of the receptive field centres of spontaneously active and non-spontaneously active SA-2 neurons on the fingertip we did not observe any obvious spatial segregation. To illustrate this, we have revised Figure 1A by color-marking SA-2 neurons that exhibited ongoing activity in intertrial periods, and the figure caption has been modified accordingly:

“Figure 1. Experimental setup. A. Receptive field center locations shown on a standardized fingertip for all first-order tactile neurons included in the study, categorized by neuron type. Purple symbols denote spontaneously active SA-2 neurons exhibiting ongoing activity without external stimulation.”

Did the authors look to see if the spontaneous firing in SA-2s between trials could predict the extent to which the type 1 afferents encode the proceeding stimulus? Basically, does the SA-2 state relate to how the type 1 units fire?

We found no clear indications that the responses of FA-1 and SA-1 could be readily anticipated based on the firing patterns of SA-2 neurons.

In the discussion, it is stated that "the viscoelastic memory of the preceding loading would have modulated the pattern of strain changes in the fingertip differently depending on where their receptor organs are situated in the fingertip". Can the authors expand on this or make any predictions about the size of the memory effect and the distance from the point of stimulation?

We have explored this topic further in the text, referring to recent studies modeling essential aspects of fingertip mechanics. However, in our view, current models lack the capability to predict the specific nature sought by the reviewer. These models should include a detailed understanding of the intricate networks of collagen fibers anchoring the pulp tissue at the distal phalangeal bone and the nail. They should also consider potential inherent directional preferences of the receptor organs, attributed to their microanatomy. The text modifications are as follows:

“In addition to the receptor organ locations, the variation in sensitivity among neurons to fingertip deformations in response to both previous and current loadings would stem from the fingertip’s geometry and its complex composite material properties. Possible inherent directional preferences of the receptor organs, attributed to their microanatomy, could also be significant. However, mechanical anisotropy, particularly within the viscoelastic subcutaneous tissue of the fingertip induced by intricately oriented collagen fiber strands forming fat columns in the pulp (Hauck et al., 2004), are likely to play a crucial role. This anisotropy would shape the dynamic pattern of strain changes at neurons' receptor sites, intricately influencing a neuron's sensitivity not only to current but also to preceding loadings. Indeed, recent modeling efforts suggest that such mechanical anisotropy strongly influences the spatiotemporal distribution of stresses and strains across the fingertip (Duprez et al., 2024).”

Relatedly, we have included additional text to provide a more comprehensive explanation of the “bulk deformation” of the fingertip that occurs during the loadings:

“As pressure increases in the pulp, the pulp tissue bulges at the end and sides of the fingertip. Simultaneously, the tangential force component amplifies the bulging in the direction of the force while stretching the skin on the opposite side.”

In the discussion, it would be good if the authors could briefly comment more on the diversity of the mechanoreceptive afferent firing and why this may be useful to the system.

The diversity in responses among neurons is instrumental in enhancing the information transmitted to the brain by averting redundancy in information acquisition. This diversity thereby contributes to an overall increase in information. We've included a brief statement, along with several references, underscoring this concept:

"The resulting diversity in the sensitivities of neurons might enhance the overall information collected and relayed to the brain by the neuronal population, facilitating the discrimination between tactile stimuli or mechanical states of the fingertip (see Rongala et al., 2024; Corniani et al., 2022; Tummala et al., 2023, for more extensive explorations of this idea)."

Also, the authors could briefly discuss why this memory (or recency) effect occurs - is it useful, does it serve a purpose, or it is just a by-product of our skin structure? There are examples of memory in the other senses where comparisons could be drawn. Is it like stimulus adaptation effects in the other senses (e.g. aftereffects of visual motion)?

We have expanded the concluding paragraph of the discussion, specifically delving into the question of whether the mechanical memory effect serves a deliberate purpose or is simply an incidental byproduct of our skin structure:

“In any case, the viscoelastic deformability of the fingertips plays a pivotal role in supporting the diverse functions of the fingers. For example, it allows for cushioned contact with objects featuring hard surfaces and allows the skin to conform to object shapes, enabling the extraction of tactile information about objects' 3D shapes and fine surface properties. Moreover, deformability is essential for the effective grasping and manipulation of objects. This is achieved, among other benefits, by expanding the contact surface, thereby reducing local pressure on the skin under stronger forces and enabling tactile signaling of friction conditions within the contact surface for control of grasp stability. Throughout, continuous acquisition of information about various aspects of the current state of the fingertip and its skin by tactile neurons is essential for the functional interaction between the brain and the fingers. In light of this, the viscoelastic memory effect on tactile signaling of fingertip forces can be perceived as a by-product of an overall optimization process within prevailing biological constraints.”

One point that would be nice to add to the discussion is the implications of the work for skin sensing. What would you predict for the time constant of relaxation of fingertip skin, how long could these skin memory effects last? Two main points to address here may be how the hydration of the skin and anatomical skin changes related to aging affect the results. If the skin is less viscoelastic, what would be the implications for the firing of mechanoreceptors?

It is likely that the time constant depends to some extent on mechanical factors of the skin, which will likely change due to age or environmental factors. However, while these questions are intriguing, they fall outside the scope of the current study and we are not aware of studies that have addressed these issues directly in experiments either.

How long does it take for the effect to end? Again, this will likely depend on the skin's viscoelasticity. However, could the authors use it in a psychophysical paradigm to predict whether participants would be more or less sensitive to future stimuli? In this way, it would be possible to test whether the direction modifies touch perception.

Time constants for tissue viscoelasticity have been estimated to extend up to several seconds (see citations in the introduction). While direct perceptual effects could indeed be explored through psychophysical experimental paradigms, we are currently unaware of any studies specifically addressing the type of effect described in this study. In addition to the statement that, concerning manipulation and haptic tasks, "to our knowledge, a possible influence of fingertip viscoelasticity on task performance has not been systematically investigated," we have now also addressed tactile psychophysical tasks conducted during passive touch with the following sentence in the text:

“Similarly, there is a lack of systematic investigation of potential effects of fingertip viscoelasticity on performance in tactile psychophysical tasks conducted during passive touch.”

Reviewer #2 (Public Review):

Summary:

The authors sought to identify the impact skin viscoelasticity has on neural signalling of contact forces that are representative of those experienced during normal tactile behaviour. The evidence presented in the analyses indicates there is a clear effect of viscoelasticity on the imposed skin movements from a force-controlled stimulus. Both skin mechanics and evoked afferent firing were affected based on prior stimulation, which has not previously been thoroughly explored. This study outlines that viscoelastic effects have an important impact on encoding in the tactile system, which should be considered in the design and interpretation of future studies. Viscoelasticity was shown to affect the mechanical skin deflections and stresses/strains imposed by previous and current interaction force, and also the resultant neuronal signalling. The result of this was an impaired coding of contact forces based on previous stimulation. The authors may be able to strengthen their findings, by using the existing data to further explore the link between skin mechanics and neural signalling, giving a clearer picture than demonstrating shared variability. This is not a critical addition, but I believe would strengthen the work and make it more generally applicable.

Strengths:

- Elegant design of the study. Direct measurements have been made from the tactile sensory neurons to give detailed information on touch encoding. Experiments have been well designed and the forces/displacements have been thoroughly controlled and measured to give accurate measurements of global skin mechanics during a set of controlled mechanical stimuli.

- Analytical techniques used. Analysis of fundamental information coding and information representation in the sensory afferents reveals dynamic coding properties to develop putative models of the neural representation of force. This advanced analysis method has been applied to a large dataset to study neural encoding of force, the temporal dynamics of this, and the variability in this.

Weaknesses:

- Lack of exploration of the variation in neural responses. Although there is a viscoelastic effect that produces variability in the stimulus effects based on prior stimulation, it is a shame that the variability in neural firing and force-induced skin displacements have been presented, and are similarly variable, but there has been no investigation of a link between the two. I believe with these data the authors can go beyond demonstrating shared variability. The force per se is clearly not faithfully represented in the neural signal, being masked by stimulation history, and it is of interest if the underlying resultant contact mechanics are.

Thank you for this suggestion. We have added a new section investigating the link between skin deformation and neural firing in more depth via a simple neural model. Please see our answer below in the ‘Recommendations’ section for further details.

Validity of conclusions:

The authors have succeeded in demonstrating skin viscoelasticity has an impact on skin contact mechanics with a given force and that this impacts the resultant neural coding of force. Their study has been well-designed and the results support their conclusions. The importance and scope of the work is adequately outlined for readers to interpret the results and significance.

Impact:

This study will have important implications for future studies performing tactile stimulation and evaluating tactile feedback during motor control tasks. In detailed studies of tactile function, it illustrates the necessity to measure skin contact dynamics to properly understand the effects of a force stimulus on the skin and mechanoreceptors.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(Very) minor comments

- The authors say at the beginning of the Results that, "The fourth type of tactile neurons in the human glabrous skin, fast adapting type II neurons...". Although generally written that there are four types of afferent in the glabrous skin, it would be better to state that these are low-threshold A-beta myelinated mechanoreceptive afferents, at least one time, as there are other types of afferent in the glabrous skin that respond to mechanical stimulation (e.g. low and high threshold C-fibers).

This is now clarified at the start of the Results section:

“We recorded action potentials in the median nerve of individual low-threshold A-beta myelinated first-order human tactile neurons innervating the glabrous skin of the fingertip…”

- Fig. 3: Could you add '(N)' as the measurement of force for Fig. 3A for Fz, Fy, and Fz? Also, please change 'Data was recorded' to 'Data were recorded' in the legend.

Fixed.

- At the beginning of the Methods, you say that your study conforms to the Declaration of Helsinki, which actually requires pre-registration in a database. If you did not pre-register your study, please can you add '... in accordance with the Declaration of Helsinki, apart from pre-registration in a database'.

Thanks for making us aware of this. We have added the suggested qualifier to the ethics statement.

Reviewer #2 (Recommendations For The Authors):

The neural representation/encoding of the actual displacement vectors would be a useful addition to the analyses. These vectors have been demonstrated to systematically change with the condition in the irregular series (Figure 2E) and will thus significantly act on the dynamics of induced mechanical changes in the skin with a given interaction force. Thus, it could be examined how the neurons code the magnitude of displacements as well as their direction. An evaluation of the extent to which the imposed displacement magnitudes are encoded in the neural responses would be a useful addition in explaining the signalling of the force events and how the central nervous system decodes these. Evaluating an alternative displacement encoding for comparison to pure force encoding may reveal more about how contact events are represented in the tactile system, which must decode these variable afferent signals to reconstruct a percept of the interaction. It could then be explored how the central nervous system may then scale the dynamic afferent responses based on the background viscoelastic state likely to be present in the SA-II afferent signals (Figure 7) for a context in which to evaluate the dynamic contact forces. This may of course be a complex relationship for the type-I afferents, where the underlying mechanical events evoking the firing (microslips not represented in global forces) have not been measured here. Such a model could be more widely applicable, as the skin viscoelasticity and displacement magnitudes are a straightforward measurement metric and could perhaps be used as a better proxy for neural signalling. This would allow the investigation of a wider variety of forces, and the study of the timing of the viscoelastic effect, both of which have been fixed here. This would give the work a broader impact, rather than just highlighting that this effect produces variability, it could reveal if this mechanical feature is structured in the neural representation. The categorical encoding/decoding tested here is specific to the stimuli used (magnitudes, intervals), but there is the possibility that this may be more generally applicable (within the bounds of forces/speeds) if the underlying basis of the variability in the signalling produced by the viscoelasticity is identified. Since the time course of the viscoelasticity has not been measured here (fixed forces and intervals), further study is required to fully understand the implications this has for a wider variety of situations.

We agree that a better understanding of how the mechanical deformations are reflected in the resulting spike trains would be valuable. While ultimately a full understanding will need precise measurements of skin deformation across the whole fingertip to account for mechanical propagation to mechanoreceptor locations, relating the deformations at the contact location with neural firing patterns directly can provide useful hints into which aspects of deformation are encoded and how. To this end, we ran a new analysis that aimed to predict the time-varying neural responses directly from the recorded mechanical movements of the contactor.

Below we have reproduced the new results and methods text along with the additional figures for this analysis. Note that we have also added text in the Discussion to interpret these findings in the context of our other results.

New section in Results titled Predicting neural responses from contactor movements: “The similarity in the history-dependent variation in neural firing and fingertip deformation at a given force stimulus suggests that neuronal firing is determined by how the fingertip deforms rather than the applied force itself. However, this similarity does not clarify the relationship between fingertip deformation dynamics and neural signaling. To investigate further, we fit cross-validated multiple linear regression models to evaluate how well distinct aspects of contactor movement could predict the time-varying firing rates of individual neurons during the protraction phases of the irregular sequence. The models used predictors based on (1) the three-dimensional position of the contactor, (2) its three-dimensional velocity, (3) a combination of position and velocity signals, and, finally, (4) position and velocity signals along with all possible two-way interactions between them, capturing potentially complex relationship between fingertip deformations and neural signaling.

Comparing the variance explained (R²) by each regression model for each neuron type revealed clear differences between the models (Figure 5A). A two-way mixed design ANOVA, with regression model as within-group effects and neuron type as a between-group effect revealed a main effect of model on variance explained (F(3,462) = 815.5, p < 0.001, η_p² = 0.84). Model prediction accuracy overall increased with the number of predictors, with the two-way interaction model outperforming all others (p < 0.001 for all comparisons, Tukey’s HSD). Additionally, a significant main effect of neuron type (F(2,154) = 29.8, p < 0.001, η_p² = 0.28) and a significant interaction between regression model and neuron type were observed (F(6,462) = 50.8, p < 0.001, η_p² = 0.40).

For neuron type, model predictions were most accurate for SA-2 neurons, followed by SA-1 neurons, with FA-1 neurons showing the lowest accuracy (p < 0.003 for all comparisons, Tukey’s HSD). The interaction between model and neuron type revealed distinct patterns. For SA-1 and SA-2 neurons, position-only and velocity-only models had similar prediction accuracy (p ≥ 0.996, Tukey’s HSD) with no significant differences between these neuron types (p ≥ 0.552, Tukey’s HSD). FA-1 neurons performed poorly with the position-only model but showed higher accuracy with the velocity-only model (p < 0.001, Tukey’s HSD) and better than SA-1 neurons (p = 0.006, Tukey’s HSD). Models combining position and velocity predictors (without interactions) surpassed both position-only and velocity-only models for SA-1 and SA-2 neurons (p < 0.001, Tukey’s HSD). Overall, the differences between neuron types broadly match their tuning to static and dynamic stimulus properties.

The two-way interaction model, accounting for most variance in neural responses, produced mean R² values of 0.75 for FA-1, 0.88 for SA-1, and 0.91 for SA-2 neurons (Figure 5A). To evaluate the contribution of the different predictors, we ranked them using the permutation feature importance method, focusing on the six most important ones. Regression analyses using only these variables explained almost all of the variance explained by the full model, with a median R² reduction of just 0.055 across all neurons. Across all neuron types, at least half included all three velocity components (dPx, dPy, dPz) among the top six, with FA-1 neurons showing the highest prevalence (Figure 5B). Interactions between normal position (Pz) and each velocity component were also frequently observed, while interactions involving tangential position and velocity components were less common. Interactions among velocity components were relatively well represented, followed by interactions limited to position components. Position signals were generally less represented, except for normal position (Pz) in slowly adapting neurons, where it appeared in 50% of SA-1 and 68% of SA-2 neurons. Despite these broad trends, important predictors varied widely across ranks even within a given neuron class (see Figure 5-figure supplement 1), and even the most frequent variables appeared in only a subset of cases, suggesting broad variability in sensitivity across neurons.”

New methods paragraph titled Predicting time-varying firing rates from skin deformations:

“This analysis was conducted in Python (v3.13) with pandas for data handling, numpy for numerical operations, and scikit-learn for model fitting and evaluation.

To assess how well individual neurons' time-varying firing rates could be predicted from simultaneous contactor movements, we fitted multiple linear regression models (see Khamis et al., 2015, for a similar approach}. This analysis focused on the force protraction phase of the irregular sequence, where neurons were most responsive and sensitive to stimulation history. Data from 100 ms before to 100 ms after the protraction phase (between -0.100 s and 0.225 s relative to protraction onset) were included for each trial. Neurons were included if they fired at least two action potentials during the force protraction phase and the following 100 ms in at least five of the 25 trials. This ensured sufficient variability in firing rates for meaningful regression analysis, resulting in 68 SA-1, 38 SA-2, and 51 FA-1 neurons being included.

Contractor position signals digitized at 400 Hz were linearly interpolated to 1000 Hz. Instantaneous firing rates, derived from action potentials sampled at 12.8 kHz, were resampled at 1000 Hz to align with position signals. A Gaussian filter (σ = 10 ms, cutoff ~16 Hz) was applied to the firing rate as well as to the position signals before differentiation. To account for axonal conduction (8–15 ms) and sensory transduction delays (1–5 ms), firing rates were advanced by 15 ms to align approximately with independent variables.

Regressions were performed using scikit-learn's Ridge and RidgeCV regressors, which apply L2 regularization to mitigate overfitting. Hyperparameter tuning for the regularization parameter (alpha) was performed using GridSearchCV with a predefined range (0.001–1000.0), incorporating five-fold cross-validation to select the best value. To minimize overfitting risks, model performance was further validated with independent five-fold cross-validation (KFold), and R² scores were computed using cross_val_score.

We constructed four linear regression models with increasing complexity: (1) Position-only, using three-dimensional contactor positions (Px, Py, Pz); (2) Velocity-only, using three-dimensional velocities (dPx, dPy, dPz); (3) Combined, including all position and velocity signals (6 predictors); and (4) Interaction, including all signals and their two-way interactions (21 predictors). All features were standardized using StandardScaler to improve regularization and model convergence. PolynomialFeatures generated second-order interaction terms for the interaction model. Feature importance was evaluated with permutation_importance, and simpler models were built using the most important features. These models were validated through cross-validation to assess retained explanatory power.”

Minor:

- It would be useful to add a brief description of the material aspects of the contactor tip to the methods (as per Birznieks 2001).

We have added the following statement:

“To ensure that friction between the contactor and the skin was sufficiently high to prevent slips, the surface was coated with silicon carbide grains (50–100 μm), approximating the finish of smooth sandpaper.”

- The axes labelling on Figure 3A and legend description is ambiguous, probably placing the Px, Py, and Pz labels on the far left axes and the Fx, Fy, and Fz on the right side of the far right axes would make this clearer.

Label placement has been improved along with some other minor fixes.

- For the quasi-static phase analysis, the phrase "absence of loading" used in reference to the interstimulus period and SA-II afferents does not seem to be a correct description. The finger is still loaded (at least in the normal direction), with a magnitude of imposed displacement that counteracts the viscoelastic force exerted by the skin mechanics of the fingertip. Although there is a zero net-force load, a mechanical stimulus is still being actively applied to the skin.

We have changed the wording throughout the text and now consistently refer either to the “interstimulus period” directly or to an “absence of externally applied stimulation” to avoid confusion.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #2 (Public review):

Summary:

The revised paper by Kim et al. reports two disease mutations in proBMP4, S91C and E93G, disrupt the FAM20C phosphorylation site at Ser91, blocking the activation of proBMP4 homodimers, while still allowing BMP4/7 heterodimers to function. Analysis of DMZ explants from Xenopus embryos expressing the proBMP4 S91C or E93G mutants showed reduced expression of pSmad1 and tbxt1. The expert amphibian tissue transplant studies were expanded to in vivo studies in Bmp4S91C/+ and Bmp4E93G/+ mice, highlighting the impact of these mutations on embryonic development, particularly in female mice, consistent with patient studies. Additionally, studies in mouse embryonic fibroblasts (MEFs) demonstrated that the mutations did not affect proBMP4 glycosylation or ER-to-Golgi transport but appeared to inhibit the furin-dependent cleavage of proBMP4 to BMP4. Based on these findings and AI modeling using AlphaFold of proBMP4, the authors speculate that pSer91 influences access of furin to its cleavage site at Arg289AlaLysArg292 in a new "Ideas and Speculation" section. Overall, the authors addressed the reviewers' comments, improving the presentation.

Strengths:

The strengths of this work continue to lie in the elegant Xenopus and mouse studies that elucidate the impact of the S91C and E93G disease mutations on BMP signaling and embryonic development. Including an "Ideas and Speculation" subsection for mechanistic ideas reduces some shortcomings regarding the analysis of the underlying mechanisms.

Weaknesses:

(1)  (Minor) In Figure S1 and lines 165-174 and 179-180, the authors should consider that, unlike the wild-type protein (Ser), which can be reversibly phosphorylated or dephosphorylated, phosphomimic mutations are locked into mimicking either the phosphorylated state (Asp) or the non-phosphorylated state (Ala). Consequently, if the S91D mutant exhibits lower activity than WT, it could imply that S91D interferes with other regulatory constraints, as the authors suggest. However, it may also be inhibiting activation. Therefore, caution is warranted when comparing S91D with S91C to conclude that Ser91 phosphorylation increases BMP4 activity. While additional experiments are not necessary, further consideration is essential.

(Minor) In lines 394-399, the authors cleverly speculate that pS91 interacts with Arg289-the essential P4 arginine for furin processing. If so, this interaction could hinder the cleavage of proBMP4, as indicated by the results in Figure S1. The discussion would benefit from considering that, contrary to their favored model, dephosphorylation at Ser91 might actually facilitate cleavage.

We have added a paragraph raising this possibility but explaining why it is unlikely and inconsistent with our in vivo data. The S91D construct was a simple control that was tested in ectopic expression assays and not in vivo.  We can make no conclusions about whether this construct resembles the phosphorylated state or whether it hinders or facilitates cleavage in vivo. The conclusion that dephosphorylation promotes BMP4 cleavage or activity is not compatible with the finding that two mutations associated with birth defects in humans (p.S91C or p.E93G) that are predicted to prevent FAM20C-mediated phosphorylation of the BMP4 prodomain lead to impaired proteolytic maturation of endogenous BMP4 and reduced BMP activity in vivo. 

(2)  In Figure 4, panels A, E, and I, the proBMP bands in the mouse embryonic lysates and MEFs expressing the mutations show a clear size shift. Are these shifts a cause or a consequence of the lack of cleavage? Regardless, the size shifts should be explicitly noted.

These intriguing shifts were observed in some but not all biological replicates.  When present, the shifts were not reversed by treatment with phosphatases or deglycosylases, and the shifts were never observed in epitope tagged wild type controls.  We have added a paragraph noting the shifts and our tests of whether they might be due to glycosylation, phosphorylation or epitope tags. 

(3)  (Minor) In line 314, the authors should consider modifying the wording to: "is required for modulating proprotein convertase..."

The original wording (“Collectively, our findings are consistent with a model in which FAM20C-mediated phosphorylation of the BMP4 prodomain is not required for folding or exit of the precursor protein from the ER, but is required for proprotein convertase recognition and/or for trafficking to post-TGN compartment(s) where BMP4 is cleaved”) more accurately reflects the model that is supported by our findings. Stating that “phosphorylation ……is required to modulate proprotein convertase recognition and/or trafficking” is vague and leaves open the possibility that it modulates in either direction, which our data do not support as described in point 1 above.

Author response:

The following is the authors’ response to the original reviews

Public Reviews: 

Reviewer #1 (Public Review): 

This study investigates the role of microtubules in regulating insulin secretion from pancreatic islet beta cells. This is of great importance considering that controlled secretion of insulin is essential to prevent diabetes. Previously, it has been shown that KIF5B plays an essential role in insulin secretion by transporting insulin granules to the plasma membrane. High glucose activates KIF5B to increase insulin secretion resulting in the cellular uptake of glucose. In order to prevent hypoglycemia, insulin secretion needs to be tightly controlled. Notably, it is known that KIF5B plays a role in microtubule sliding. This is important, as the authors described previously that beta cells establish a peripheral sub-membrane microtubule array, which is critical for the withdrawal of excessive insulin granules from the secretion sites. At high glucose, the sub-membrane microtubule array is destabilized to allow for robust insulin secretion. Here the authors aim to answer the question of how the peripheral array is formed. Based on the previously published data the authors hypothesize that KIF5B organizes the sub-membrane microtubule array via microtubule sliding. 

General comment: 

This manuscript provides data that indicate that KIF5B, like in many other cells, mediates microtubule sliding in beta cells. This study is limited to in vitro assays and one cell line. Furthermore, the authors provide no link to insulin secretion and glucose uptake and the overall effects described are moderate. Finally, the overall effect of microtubule sliding upon glucose stimulation is surprisingly low considering the tight regulation of insulin secretion. Moreover, the authors state "the amount of MT polymer on every glucose stimulation changes only slightly, often undetectable…. In fact, we observe a prominent effect of peripheral MT loss only after a long-term kinesin depletion (three-four days)". This challenges the view that a KIF5Bdependent mechanism regulating microtubule sliding plays a major role in controlling insulin secretion. 

(1) Our initial study was indeed done in a cell line, which is a normal approach to addressing molecular mechanisms of a phenomenon in a challenging cell model: primary pancreatic beta cells are prone to rapidly dedifferentiate outside of the organism and are hard to genetically modify. To address this reviewer’s comment, in the revised manuscript we now confirm the phenotype in beta cells within intact pancreatic islets from a KIF5B KO mouse model (New Figure 2 – Supplemental Figure 1).

(2) We agree that testing the effect of microtubule sliding on insulin secretion is an important question. Unfortunately, the experimental design needed to accomplish this task is not straighDorward. Importantly, besides microtubule sliding, KIF5B is heavily engaged in insulin granule transport, and GSIS deficiency upon KIF5B inactivation is well documented (e.g. Varadi et al 2002). In this study, we choose not to repeat this GSIS assay because of ample existing data. However, this reported GSIS deficiency could result from a combination of lack of insulin granule delivery to the periphery (previous data) and from the depletion of insulin granules from the periphery due to the loss of the submembrane MT bundle (this study and Bracey et al 2020).  In order to exclusively test the role of MT sliding in secretion, a significant investment in mutant tool development would be needed. Ideally, a new mutant mouse model where insulin granule transport is allowed by MT sliding in blocked must be developed to specifically address this question. To conclude, answering this question will be the subject for another, follow-up study. 

(3) We respecDully disagree with the reviewer’s opinion that the effect of MT sliding in beta cells is moderate. As MT networks go, even a slight change in MT configuration often has dramatic consequences. For example, in mitotic spindles, a tiny overgrowth of microtubule ends during metaphase, which causes them to attach to both kinetochores rather than just one, is very significant for the efficiency of chromosome segregation, causing aneuploidy and cancer. The changes in beta-cell MT networks that we are reporting are much stronger: the effect on the peripheral MT network accumulated over three days of KIF5B depletion is dramatic (Fig 2 B, C). Short-term gross MT network configurations after a single glucose stimulation are harder to detect, but MTs at the cell periphery are, in fact, destabilized and fragmented, as we and others have previously reported (Ho et al 2020, Mueller et al 2021). Preventing this MT rearrangement completely blocks GSIS (Zhu et al 2015, Ho et al 2020). 

One of the most fascinating features of insulin secretion regulation is that the amount of generated insulin granules significantly exceeds the normal physiological needs for insulin secretion (~100 times more than needed). At the same time, even slightly facilitated glucose depletion can be devastating. Accordingly, the excessive insulin content of a beta cell resulted in the development of multiple levels of control, preventing excessive secretion. Our previous data suggest that the peripheral MT array provides one of those mechanisms. This study indicates that microtubule sliding is necessary to form the proper peripheral network in the long term. Short-term glucose-induced changes in the peripheral MT array likely need to be subtle to prevent over-secretion. Thus, we are not surprised that a dramatic effect of sliding inhibition is only detectable by our approaches after the changes in the MT network accumulate over time. In the revised paper, we now discuss the potential impact of peripheral MT sliding on positive and negative regulation of secretion and add a schematic model illustrating these processes.

Specific comments: 

(1) Notably, the authors have previously reported that high glucose-induced remodeling of microtubule networks facilitates robust glucose-stimulated insulin secretion. This remodeling involves the disassembly of old microtubules and the nucleation of new microtubules. Using real-time imaging of photoconverted microtubules, they report that high levels of glucose induce rapid microtubule disassembly preferentially in the periphery of individual β-cells, and this process is mediated by the phosphorylation of microtubule-associated protein tau. Here, they state that the sub-membrane microtubule array is destabilized via microtubule sliding. What is the relevance of the different processes? 

In this comment, the summary of our previous conclusions is correct, but the conclusion of this current study is re-stated incorrectly. Indeed, we have previously shown that in high glucose, MTs are destabilized at the cell periphery and nucleated in the cell interior. However, this current paper does not state that “the sub-membrane microtubule array is destabilized via microtubule sliding”. To answer this reviewer’s question, our data support a model where, during glucose stimulation, MT sliding within the peripheral bundle might move fragments of MTs severed by other mechanisms. Importantly, we propose that MT sliding restores the partially destabilized peripheral bundle by delivery of MTs that are nucleated at the cell interior and incorporating them into that bundle. In our overall model, three processes (destabilization, nucleation, and sliding to restore the bundle) are coordinated to maintain beta cell fitness on each GSIS cycle.

(2) On one hand the authors describe how KIF5B depletion prevents sliding and the transport of microtubules to the plasma membrane to form the sub-membrane microtubule array. This indicates KIF5B is required to form this structure. On the other hand, they describe that at high glucose concentration, KIF5B promotes microtubule sliding to destabilize the sub-membrane microtubule array to allow robust insulin secretion. This appears contradictory. 

We never intended to make an impression that MT sliding destabilized the sub-membrane bundle. Apologies if there was a reason in our wording that caused this misunderstanding of our model. We propose that while the bundle is destabilized downstream of glucose signaling (e.g. due to tau phosphorylation, please see Ho et al Diabetes 2020), MT sliding remodels the bundle and thereafter rebuilds it to prevent over-secretion. In the revised manuscript, we have doublechecked the whole text to make sure that such misunderstanding is avoided. 

(3) Previously, it has been shown that KIF5B induces tubulin incorporation along the microtubule shaft in a concentration-dependent manner. Moreover, running KIF5B increases microtubule rescue frequency and unlimited growth of microtubules. Notably, KIF5B regulates microtubule network mass and organization in cells (PMID: 34883065). Consequently, it appears possible that the here observed phenomena of changes in the microtubule network might be due to alterations in these processes. 

We thank the reviewer for proposing this alternative explanation to the observed change in microtubule networks after KIF5B depletion. We have now directly tested this possibility. Namely, we have re-expressed the kinesin-1 motor domain in MIN6 cells depleted of KIF5B. This motor domain construct by itself is not capable of driving microtubule sliding because it lacks the tail domain. At the same time, it is known to move very efficiently at microtubules and should provide the effects as reported in the article cited by the reviewer. We found that the reexpression of the kinesin motor domain does not rescue microtubule network defects in beta cells (see new Figure 2 – Supplemental Figure 2). Thus, we conclude that the effects of kinesin depletion on the microtubule network in beta cells are due to the lack of microtubule sliding, as reported here.

(4) The authors provide data that indicate that microtubule sliding is enhanced upon glucose stimulation. They conclude that these data indicate that microtubule sliding is an integral part of glucose-triggered microtubule remodeling. Yet, the authors fail to provide any evidence that this process plays a role in insulin secretion or glucose uptake. 

We would like to point out that we do not “fail” but rather choose not to overload our study by repeating insulin secretion assays in KIF5B-inactivated cells because this would not have been very informative. It has been found previously that kinesin-1 inactivation or knockout significantly attenuates insulin secretion because kinesin-1 is actively transporting insulin granules and kinesin-1 activity is enhanced under high glucose conditions (e.g. Varadi et al 2002, Cui et al., 2011, Donelan et al, 2002). That said, our current finding is very much in line with these previous data. When kinesin is depleted, two things would be happening at the same time: in the absence of sub-membrane microtubule bundle pre-existing insulin granules would be over-secreted, and new insulin would not be delivered to the periphery, both decreasing GSIS. Unfortunately, we do not have tools yet that would allow us to dissect which part of the insulin secretion defect is due to prior over-secretion (the consequence of deficient MT sliding) and which part is due to the lack of new granule delivery. We plan to develop such tools in the future and elaborate on them in a follow-up study. Here, our goal is to understand microtubule organization principles in beta cells, and we choose not to extend the scope of the current study to metabolic assays.  

(5) The authors speculate that the sub-membrane microtubule array prevents the over-secretion of insulin. Would one not expect in this case a change in the distribution of insulin granules at the plasma membrane when this array is affected? Or after glucose stimulation? Notably, it has been reported that "the defects of β-cell function in KIF5B mutant mice were not coupled with observable changes in islet morphology, islet cell composition, or β-cell size" and "the subcellular localization of insulin vesicles was found to not be affected significantly by the decreased Kif5b level. The cytoplasm of both wild-type and mutant β-cells was filled with insulin vesicles. Insulin vesicle numbers per square μm were determined by counting all insulin vesicles in randomly photographed β-cells. More insulin granules were found in Kif5b knockout β-cells compared with control cells. This phenomenon is consistent with the observation that insulin secretion by β-cells is affected" whereby "Insulin vesicles (arrowheads) were distributed evenly in both mutant and control cells" (PMID: 20870970).  

Quantitative analyses in the study cited by the reviewer do not include assays that would be relevant to our study. Particularly, in that study neither the amount of insulin granules at the cell periphery nor the ratio between the number of granules at the periphery and the beta cell interior has been analyzed. In addition, in our preliminary observations not shown here, insulin content in beta cells in KIF5B KO mice is highly heterogeneous, with a subpopulation of cells severely depleted of insulin. This opens a new avenue of investigation into beta cell heterogeneity, which is out of the scope of this current study. Thus, we chose to restrict this current study to microtubule organization data.   

(6) Does the sub-membrane microtubule array exist in primary beta cells (in vitro and/or in vivo) and how it is affected in KIF5B knockout mice?  

Yes, it does exist. In fact, we have first reported it in mouse islets (Bracey et al 2020, Ho et al 2020). Now, we report that the sub-membrane bundle is defective, and microtubules are misaligned in KIF5B KO mice (new Figure 2 – Supplemental Figure 1).

Reviewer #2 (Public Review): 

In this article, Bracey et al. provide insights into the factors contributing to the distinct arrangement observed in sub-membrane microtubules (MTs) within mouse β-cells of the pancreas. Specifically, they propose that in clonal mouse pancreatic β-cells (MIN6), the motor protein KIF5B plays a role in sliding existing MTs towards the cell periphery and aligning them with each other along the plasma membrane. Furthermore, similar to other physiological features of β-cells, this process of MTs sliding is enhanced by a high glucose stimulus. Because a precise alignment of MTs beneath the cell membrane in β-cells is crucial for the regulated secretion of pancreatic enzymes and hormones, KIF5B assumes a significant role in pancreatic activity, both in healthy conditions and during diseases. 

The authors provide evidence in support of their model by demonstrating that the levels of KIF5B mRNA in MIN6 cells are higher compared to other known KIFs. They further show that when KIF5B is genetically silenced using two different shRNAs, the MT sliding becomes less efficient. Additionally, silencing of KIF5A in the same cells leads to a general reorganization of MTs throughout the cell. Specifically, while control cells exhibit a convoluted and non-radial arrangement of MTs near the cell membrane, KIF5B-depleted cells display a sparse and less dense sub-membrane array of MTs. Based on these findings, the Authors conclude that the loss of KIF5B strongly affects the localization of MTs to the periphery of the cell. Using a dominant-negative approach, the authors also demonstrate that KIF5B facilitates the sliding of MTs by binding to cargo MTs through the kinesin-1 tail binding domain. Additionally, they present evidence suggesting that KIF5B-mediated MT sliding is dependent on glucose, similar to the activity levels of kinesin-1, which increase in the presence of glucose. Notably, when the glucose concentrations in the culturing media of MIN6 cells are reduced from 20 mM to 5 mM, a significant decrease in MT sliding is observed. 

Strengths:

This study unveils a previously unexplained mechanism that regulates the specific rearrangement of MTs beneath the cell membrane in pancreatic β-cells. The findings of this research have implications and are of significant interest because the precise regulation of the MT array at the secretion zone plays a critical role in controlling pancreatic function in both healthy and diseased states. In general, the author's conclusions are substantiated by the provided data, and the study demonstrates the utilization of state-of-the-art methodologies including quantification techniques, and elegant dominant-negative experiments. 

Weaknesses:

A few relatively minor issues are present and related to data interpretation and the conclusions drawn in the study. Namely, some inconsistencies between what appears to be the overall and sub-membrane MT array in scramble vs. KIF5B-depleted cells, the lack of details about the sub-cellular localization of KIF5B in these cells and the physiological significance of the effect of glucose levels in beta-cells of the pancreas. 

We thank the reviewer for this insighDul review. In the revised version, we provided re-worded and extended interpretations and conclusions to prevent any issues or misunderstandings.  We trust that while some noted apparent inconsistencies may reflect the intrinsic heterogeneity of the beta cell population, all data presented here indicate the same trend in phenotypes.  In the revised version, we have provided additional cell views and, in places, alternative representative images and videos, to clear out any apparent inconsistencies. We also would like to point out that we in fact reported KIF5B localization: not surprisingly, KIF5B predominantly localized to insulin granules and the punctate staining fills the whole cytoplasm (Figure 2A, bottom panel). However, as pointed out in detail in our response to reviewer 1, we choose to leave out an extensive study of the physiological and metabolic consequences of the reported microtubule network dynamics to a follow-up study. 

Reviewer #3 (Public Review): 

Prior work from the Kaverina lab and others had determined that beta-cells build a microtubule network that differs from the canonical radial organization typical in most mammalian cell types and that this organization facilitates the regulated secretion of insulin-containing secretory granules (IGs). In this manuscript, the authors tested the hypothesis that kinesin-driven microtubule sliding is an underlying mechanism that establishes a sub-membranous microtubule array that regulates IG secretion. They employed knock-down and dominant-negative strategies to convincingly show microtubule sliding does, in fact, drive the assembly of the sub-membranous microtubule band. They also used live cell imaging assays to demonstrate that kinesin-mediated microtubule sliding in beta-cells is triggered by extracellular high glucose. Overall, this is an interesting and important study that relates microtubule dynamics to an important physiological process. The experiments were rigorous and well-controlled. 

We truly appreciate this reviewer’ opinion. 

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Figures: 

(1) Figure 1: 

a) Why can one not see here, and in most following images, the peripheral sub-membrane microtubule array? One can also not see an accumulation of microtubules in the cell interior. 

Microtubule pattern in beta cells is variable, and the sub-membrane array is seen in the whole population to a variable extent (see directionality histogram in Figure 2E for statistics). In fact, an array of peripheral MTs parallel to the cell border is present in the example shown in Figure 1 and in all following control images. To make it clearer, we now show the pre-bleach images in Figure 1 D-F at a lower magnification, so that the differences in MT density at the cell periphery and cell center are more clearly seen: MTs lack at the periphery in KF5B-depleted but not the control cells.  

b) 5 min appears to be a long time and enough time to polymerize a significant number of new microtubules. 

We interpret this comment as the reviewer’s concern that in FRAP assays, fluorescently-labeled MTs moving into the bleached area might be newly polymerizing MTs rather than preexisting MT relocated into that area. However, this is not the case because newly polymerized MTs contain predominantly quenched “dark” tubulin molecules and only a small percent of fluorescent tubulin. These dim MTs are not included in MT sliding assay analysis, where a threshold for bright MTs is introduced. Now, we added more details for the quantification of these data to Materials and Methods section.

c) The overall effects appear minor. It is unclear how Fig. 1-Suppl-Fig.1, where no significant difference is shown, is translated into Figure 1 J and K showing a significant difference. 

With all due respect, we do not agree that the effect is minor. Please see our response to the Public Review where we discuss the major consequences of MT defects in detail. 

To answer this specific comment, we show that there are significant differences in the number of rapidly moving MTs (5-sec displacement over 0.3 µm) and in the amount of stationary MTs (5sec displacement is below 0.15 µm). There is no significant difference in the amount of slightly displaced MTs (displacements between 0.15 and 0.3 µm; the central part of the histogram). This might indicate that these slight displacements do not depend on kinesin-1 motor but rather are caused by experimental noise, pushing by moving organelles, and/or myosin-dependent forces in the cell. In the revised manuscript, we have this quantification more clearly detailed in Methods and included in Figure legends.

d) The authors utilize single molecule tracking to further strengthen their conclusion that KIF5B promotes microtubule sliding. The observed effects are weaker than the data obtained from photobleaching experiments. The videos clearly show that there is still significant movement also in KIF5B-depleted cells. If K560RigorE236A binds irreversibly to a microtubule and this microtubule is growing (not only by the addition of tubulin dimers to the plus end; see PMID: 34883065) wouldn't that also result in movement of the tagged K560RigorE236A? As KIF5B is also required in the transport of insulin granules, it should also label "interior microtubules". And in Video 2 it appears that pretty much all "labeled" microtubules are moving. 

K560RigorE236A forms fiducial marks along the whole MTs lattice, as previously shown in (Tanenbaum et al., 2014). When it is bound to MT lattice, K560RigorE236A moves with the whole MT if it is being relocated. The mechanism described in (PMID: 34883065) appears to be absent or minor in beta cells (see Figure 2- Supplemental Figure 2), thus, even if this mechanism would displace already polymerized MTs, this is not happening in this cell type.

The reviewer is correct, K560RigorE236A does mark all MTs throughout a beta cell. All MTs are moving slightly in a living cell because they are pushed around by moving organelles, actin contractility, etc. MTs may also be slid by other MT-dependent motors (dynein against the membrane and such). So, it is not surprising that the MT network is “breezing,” and kinesindependent sliding is only a part of MT movement. What we show here is that the KIF5Bdependent MT sliding is responsible for a relatively “long-distance” relocation of MTs manifested in long, directional displacement of fiducial marks.  This does not exclude other movements. This makes extraction of kinesin-dependent MT movements somewhat challenging, of course, that is why we needed to do those extensive analyses. 

e) Figure 1 G to K is misleading, at least in the context of the provided videos. There are several microtubules that move extensively in shRNA#2-treated cells and overall there appears more movement in this cell as in the control cell. Figure 1I is clearly not representative of the movement shown in Video 2. 

We apologize if our selection of representative movies/figures for this experiment was imperfect. Indeed, in all depleted cells, SunTag puncta still move to a certain extent, either due to incomplete depletion or to alternative intracellular forces dislocating microtubules. However, there is a clear difference in the fraction of persistently moving puncta (please see Figure 1K and  histogram in Figure 1 - Supplemental Figure 1B). Unfortunately, when the number of SunTag puncta per a cell is variable, it sometimes prevents a good visual perception of the actual distribution of moving versus stationary microtubules. We now show an alternative representative movie for the Figure 1I and the corresponding Video 2, with a goal to compare cells with more consistent numbers of Sun-Tag puncta.

(2) Figure 2A. 

a) This is the only image that clearly shows the existence of a sub-membrane microtubule array and the concentration of microtubules in the cell interior. The differences are unclear between the experimental setups including the length of cultivation and knockdown of KIF5B or expression of mutants. 

We now provide a more detailed description of each image acquisition and processing in Materials and Methods. In brief, while the morphology of MT patterns is intrinsically variable in beta cells, all control cells have populated peripheral MTs that exhibit a more parallel configuration as compared to depletions and mutants.

b) The authors state "While control cells had convoluted non-radial MTs with a prominent sub-membrane array, typical for beta cells (Fig. 2A), KIF5B-depleted cells featured extra-dense MTs in the cell center and sparse reseeding MTs at the periphery (Fig. 2B, C)". Could that not be explained with the observation that "Kinesin-1 controls microtubule length" (PMID: 34883065)? 

Thank you for this interesting alternative idea. It does not appear to be the case for beta cells.

Please see Figure 2-Supplemental Figure 2  and our response to Public Review Comment #3.

Also, our apologies for the typo in the original manuscript: this is “receding” nor “reseeding”.

(3) Figure 3: 

a) This is an elegant way to determine whether KIF5B is involved in microtubule sliding independent of the fact that the effect appears very small. 

Thank you!            

b) The assay depends on ectopic expression of a dominant negative mutant. It appears important to show that KIFDNwt is high enough expressed to indeed block the binding of endogenous KIF5B. The authors need to provide a control for this. Furthermore, authors need to provide evidence that other functions of KIF5B are not impaired such as transport of insulin granules and tubulin incorporation or microtubule stability and length.

Expression of cargo-binding motor domains routinely causes a dominant-negative effect of their cargo transport. This exact construct has been used for the purpose of dominant-negative action previously (Ravindran et al., 2017). It does prevent the membrane cargo binding of KIF5B (Ravindran et al., 2017), thus the transport of insulin granules is also impaired in overexpression cells. Confirming this fact would not influence our study conclusions, so we chose not to repeat these assays for the sake of time.

c) N-numbers should be similar. The data for KIFDNmut are difficult to interpret with possibly 2 experiments showing little to no displacement and 3 showing displacement. 

In the revised manuscript, additional data have been added to increase N-numbers.

(4) Figure 4 and supplements: The morphology of the KIFDNwt cells is greatly affected and this makes it difficult to say whether the effect on microtubules at the cell periphery is a direct or indirect effect. 

Yes, these cells often have less spread appearance, obscuring visual perception of MT distribution. We have now replaced the image of KIFDNwt cell (Figure 4, Supplemental Figure 1 A) to a more visually representative example.

Things to do: 

(1) Notably, the authors have previously reported that high glucose-induced remodeling of microtubule networks facilitates robust glucose-stimulated insulin secretion. This remodeling involves the disassembly of old microtubules and the nucleation of new microtubules. Here, they state that the sub-membrane microtubule array is destabilized via microtubule sliding. What is the relevance of the different processes? Please discuss these in the manuscript. 

Thank you, we have now extended our discussion of these points and our prior findings. We have also added a schematic model figure for clarity (Figure 7).  

(2) 5 min appears to be a long time and enough time to polymerize a significant number of new microtubules. Do the authors have any information about the speed of MT formation in MIN6 cells? Can the authors repeat this experiment by preventing MT polymerization? Or repeat the experiment with EB1/EB3 reporter to visualize microtubule growth in the same experimental setting? 

While some MT polymerization will happen in this timeframe, newly polymerized MTs contain predominantly quenched “dark” tubulin molecules and only a small percent of fluorescent tubulin. These dim MTs are not included in MT sliding assay analysis, where a threshold for bright MTs is introduced. We apologize for initially omitting certain details from the FRAP assay analysis. Now these details have been added.   

Are the microtubules shown on the cell surface (TIRF microscopy) or do we see here all microtubules? 

Please see Materials and Methods for microscopy methods and image processing for each figure. Specifically, FRAP assays show a maximum intensity projection of spinning disk confocal stacks over 2.4µm in height (approximately the ventral half of a cell).

(3) Previously, it has been shown that KIF5B induces tubulin incorporation along the microtubule shaft in a concentration-dependent manner. Moreover, running KIF5B increases microtubule rescue frequency and unlimited growth of microtubules. Notably, KIF5B regulates microtubule network mass and organization in cells (PMID: 34883065). Consequently, it appears possible that the here observed phenomena of changes in the microtubule network might be due to alterations in these processes. Authors need to exclude these possibilities and discuss them. 

Thank you for this interesting alternative idea. It does not appear to be the case for beta cells. Please see Figure 2-Supplemental Figure 2  and our response to Public Review Comment #3.

(4) It is important that the authors describe in the text and possibly in the figure legends the differences between the experimental set-ups including the length of cultivation and knock down of KIF5B or expression of mutants. 

Thank you, please see these details in the text (Materials and Methods section).

(5) Figure 5: Does KIF5B depletion rescue the kinesore-induced defects 

Thank you for suggesting this control. We have now conducted corresponding experiments. The answer is yes, it does. Kinesore does not induce detectable changes in MT patterns in KIF5Bdepleted cells (new Figure 5-Supplemental Figure 2). 

(6) Can the authors block kinesin-1 resulting in microtubule accumulation in the cell center and then release the block, and best inhibiting microtubule formation, to see whether the microtubules accumulated in the cell center will be transported to the periphery? 

This proposed experiment would have been a nice illustration to the study, however it has proven to be too challenging. Unfortunately we have to leave it for the future studies. However,  the experiments already included in the paper are sufficient to prove our conclusions. 

Minor comments: 

(1) The English needs to be improved. Oaen it is unclear what the authors try to convey. The manuscript is difficult to read and contains several overstatements. 

The revised manuscript has been through several rounds of proof-reading for clarity.

(2) It is important to describe in more detail in the introduction what is known about KIF5B in beta cells. Previously, it has been demonstrated that silencing, or inactivation by a dominant negative form of KIF5B, blocks the sustained phase of glucose-stimulated insulin secretion (PMID: 9112396, PMID: 12356920, PMID: 20870970). 

Yes, this is of course very important and have been cited in the original manuscript. Now, we have expanded the discussion on the matter.