Author Response

Reviewer #1 (Public Review):

In Figure 1A, the authors should show TEM images of control mock treated samples to show the difference between infected and healthy tissue. Based on the data shown in Figure 1B-E that the overexpression of GFP-P in N. benthamiana leads to formation of liquid-like granules. Does this occur during virus infection? Since authors have infectious clones, can it be used to show that the virally encoded P protein in infected cells does indeed exist as liquid-like granules? If the fusion of GFP to P protein affects its function, the authors could fuse just the spGFP11 and co-infiltrate with p35S-spGFP1-10. These experiments will show that the P protein when delivered from virus does indeed form liquid-like granules in plants cells. Authors should include controls in Figure 1H to show that the interaction between P protein and ER is specific.

We agree with the reviewer and appreciate the helpful suggestion. As suggested, we added TEM images of control mock treated barley leaves. We also carried out immune-electron microscope to show the presence of BYSMV P protein in the viroplasms. Please see Figure 1–Figure supplement 1.

BYSMV is a negative-stranded RNA virus, and is strictly dependent on insect vector transmission for infecting barley plants. We have tried to fuse GFP to BYSMV P in the full-length infectious clones. Unfortunately, we could not rescue BYSMV-GFP-P into barley plants through insect transmission.

In Figure 1H, we used a PM localized membrane protein LRR84A as a negative control to show LRR84A-GS and BYSMV P could not form granules although they might associate at molecular distances. Therefore, the P granules were formed and tethered to the ER tubules. Please see Figure 1–Figure supplement 4

Data shown in Figure 2 do demonstrate that the purified P protein could undergo phase separation. Furthermore, it can recruit viral N protein and part of viral genomic RNA to P protein induced granules in vitro.

Because the full-length BYSMV RNA has 12,706 nt and is difficult to be transcribed in vitro, we cannot show whether the BYSMV genome is recruited into the droplets. We have softened the claim and state that the P-N droplets can recruit 5′ trailer of BYSMV genome as shown in Figure 3B. Please see line 22, 177 and 190.

Based on the data shown in Figure 4 using phospho-null and phospho-mimetic mutants of P protein, the authors conclude that phosphorylation inhibits P protein phase separation. It is unclear based on the experiments, why endogenous NbCK1 fails to phosphorylate GFP-P-WT and inhibit formation of liquid-like granules similar to that of GFP-P-S5D mutant? Is this due to overexpression of GFP-P-WT? To overcome this, the authors should perform these experiments as suggested above using infectious clones and these P protein mutants.

As we known, phosphorylation and dephosphorylation are reversible processes in eukaryotic cells. Therefore, as shown in Figure 5B and 6B, the GFP-PWT protein have two bands, corresponding to P74 and P72, which represent hyperphosphorylation and hypophosphorylated forms, respectively. Only overexpression of NbCK1 induced high ratio of P74 to P72 in vivo, and then abolished phase separation of BYSMV.

In Figure 5, the authors overexpress NbCK1 in N. benthamiana or use an in vitro co-purification scheme to show that NbCK1 inhibits phase separation properties of P protein. These results show that overexpression of both GFP-P and NbCK1 proteins is required to induce liquid-like granules. Does this occur during normal virus infection? During normal virus infection, P protein is produced in the plant cells and the endogenous NbCK1 will regulate the phosphorylation state of P protein. These are reasons for authors to perform some of the experiments using infectious clones. Furthermore, the authors have antibodies to P protein and this could be used to show the level of P protein that is produced during the normal infection process.

We detected the P protein existed as two phosphorylation forms in BYSMV-infected barley leaves, and λPPase treatment decreased the P44 phosphorylation form. Therefore, these results indicate that endogenous CK1 cannot phosphorylate BYSMV P completely.

Based on the data shown in Figure 6, the authors conclude that phase separated P protein state promotes replication but inhibits transcription by overexpressing P-S5A and P-S5D mutants. To directly show that the NbCK1 controlled phosphorylation state of P regulates this process, authors should knockdown/knockout NbCK1 and see if it increases P protein condensates and promote recruitment of viral proteins and genomic RNA to increase viral replication.

In our previous studies, BLAST searches showed that the N. benthamiana and barley genomes encode 14 CK1 orthologs, most of which can phosphorylated the SR region of BYSMV P. Therefore, it is difficult to make knockdown/knockout lines of all the CK1 orthologues. Accordingly, we generated a point mutant (K38R and D128N) in HvCK1.2, in which the kinase activity was abolished. Overexpression of HvCK1.2DN inhibit endogenous CK1-mediated phosphorylation of BYSMV P, indicating that HvCK1.2DN is a dominant-negative mutant.

It is important to note that both replication and transcription are required for efficient infection of negative-stranded RNA viruses. Therefore, our previous studies have revealed that both PS5A and PS5D are required for BYSMV infection. Therefore, expression of HvCK1.2DN in BYSMV vector inhibit virus infection by impairing the balance of endogenous CK1-mediated phosphorylation in BYSMV P.

Reviewer #2 (Public Review):

The manuscript by Fang et al. details the ability of the P protein from Barley yellow striate mosaic virus (BYSMV) to form phase-separated droplets both in vitro and in vivo. The authors demonstrate P droplet formation using recombinant proteins and confocal microscopy, FRAP to demonstrate fluidity, and observed droplet fusion. The authors also used an elaborate split-GFP system to demonstrate that P droplets associate with the tubulur ER network. Next, the authors demonstrate that the N protein and a short fragment of viral RNA can also partition into P droplets. Since Rhabdovirus P proteins have been shown to phase separate and form "virus factories" (see https://doi.org/10.1038/s41467-017-00102-9), the novelty from this work is the rigorous and conclusive demonstration that the P droplets only exist in the unphosphorylated form. The authors identify 5 critical serine residues in IDR2 of P protein that when hyper-phosphorylated /cannot form droplets. Next, the authors conclusively demonstrate that the host kinase CK1 is responsible for P phosphorylation using both transient assays in N. benthamiana and a co-expression assay in E. coli. These findings will likely lead to future studies identifying cellular kinases that affect phase separation of viral and cellular proteins and increases our understanding of regulation of condensate formation. Next, the authors investigated whether P droplets regulated virus replication and transcription using a minireplicon system. The minireplicon system needs to be better described as the results were seemingly conflicting. The authors also used a full-length GFP-reporter virus to test whether phase separation was critical for virus fitness in both barley and the insect vector. The authors used 1, 6-hexanediol which broadly suppresses liquid-liquid phase separation and concluded that phase separation is required for virus fitness (based on reduced virus accumulation with 1,6 HD). However, this conclusion is flawed since 1,6-hexanediol is known to cause cell toxicity and likely created a less favorable environment for virus replication, independent of P protein phase separation. These with other issues are detailed below:

1. In Figure 3B, the authors display three types of P-N droplets including uniform, N hollow, and P-N hollow droplets. The authors do not state the proportion of droplets observed or any potential significance of the three types. Finally, as "hollow" droplets are not typically observed, is there a possibility that a contaminating protein (not fluorescent) from E. coli is a resident client protein in these droplets? The protein purity was not >95% based on the SDS-PAGE gels presented in the supplementary figures. Do these abnormalities arise from the droplets being imaged in different focal planes? Unless some explanation is given for these observations, this reviewer does not see any significance in the findings pertaining to "hollow" droplets.

Thanks for your constructive suggestions. We removed the "hollow" droplets as suggested. We think that the hollow droplets might be an intermediate form of LLPS. Please see PAGE 7 and 8 of revised manuscript.

1. Pertaining to the sorting of "genomic" RNA into the P-N droplets, it is unlikely that RNA sorting is specific for BYSMV RNA. In other words, if you incubate a non-viral RNA with P-N droplets, is it sorted? The authors conclusion that genomic RNA is incorporated into droplets is misleading in a sense that a very small fragment of RNA was used. Cy5 can be incorporated into full-length genomic RNAs during in vitro transcription and would be a more suitable approach for the conclusions reached.

Thanks for your constructive suggestions. Unfortunately, we could not obtain the in vitro transcripts of the full-length genomic RNAs (12706 nucleotides). We have softened the claim and state that the P-N droplets can recruit the 5′ trailer of BYSMV genome as shown in Figure 3B. Please see line 22, 177 and 190.

According to previous studies (Ivanov, et al., 2011), the Rhabdovirus P protein can bind to nascent N moleculaes, forming a soluble N/P complex, to prevent from encapsidating cellular RNAs. Therefore, we suppose that the P-N droplets can incorporate viral genomic RNA specifically.

Reference: Ivanov I, Yabukarski F, Ruigrok RW, Jamin M. 2011. Structural insights into the rhabdovirus transcription/ replication complex. Virus Research 162:126–137. DOI: https://doi.org/10.1016/j.virusres.2011.09.025

1. In Figure 4C, it is unclear how the "views" were selected for granule counting. The methods should be better described as this reviewer would find it difficult to select fields of view in an unbiased manner. This is especially true as expression via agroinfiltration can vary between cells in agroinfiltrated regions. The methods described for granule counting and granule sizes are not suitable for publication. These should be expanded (i.e. what ImageJ tools were used?).

We agree with the reviewer that it is important to select fields of view in an unbiased manner. We selected the representative views and provided large views in the new Supplement Figures. In addition, we added new detail methods in revision. Please see Figure 4–Figure supplement 1, Figure 5–Figure supplement 1, and method (line 489-498).

1. In Figure 4F, the authors state that they expected P-S5A to only be present in the pellet fraction since it existed in the condensed state. However, WT P also forms condensates and was not found in the pellet, but rather exclusively in the supernatant. Therefore, the assumption of condensed droplets only being found in the pellet appears to be incorrect.

Many thanks for pointing this out. This method is based on a previous study (Hubstenberger et al., 2017). The centrifugation method might efficiently precipitate large granules more than small granules. As shown in Figure 4B, GFP-PS5A formed large granules, therefore GFP-PS5A mainly existed in the pellet. In contrast, GFP-PWT only existed in small granule and fusion state, thus most of GFP-PWT protein was existed in supernatant, and only little GFP-PWT protein in the pellet. These results also indicate the increased phase separation activity of GFP-PS5A compared with GFP-PWT. Please see the new Figure 4F.

Reference: Hubstenberger A, Courel M, Benard M, Souquere S, Ernoult-Lange M, Chouaib R, Yi Z, Morlot JB, Munier A, Fradet M, et al. 2017. P-Body Purification Reveals the Condensation of Repressed mRNA Regulons. Molecular Cell 68(1): 144-157 e145.

1. The authors conclude that P-S5A has enhanced phase separation based on confocal microscopy data (Fig S6A). The data presented is not convincing. Microscopy alone is difficult for comparing phase separation between two proteins. Quantitative data should be collected in the form of turbidity assays (a common assay for phase separation). If P-S5A has enhanced phase separation compared to WT, then S5A should have increased turbidity (OD600) under identical phase separation conditions. The microscopy data presented was not quantified in any way and the authors could have picked fields of view in a biased manner.

Thanks for your constructive suggestions. As suggested, turbidity assays were performed to show both GFP-PWT and GFP-PS5A had increased turbidity (OD600) compared with GFP. Please see Figure 4–Figure supplement 3.

1. The authors constructed minireplicons to determine whether mutant P proteins influence RNA replication using trans N and L proteins. However, this reviewer finds the minireplicon design confusing. How is DsRFP translated from the replicon? If a frameshift mutation was introduced into RsGFP, wouldn't this block DsRFP translation as well? Or is start/stop transcription used? Second, the use of the 2x35S promoter makes it difficult to differentiate between 35S-driven transcription and replication by L. How do you know the increased DsRFP observed with P5A is not due to increased transcription from the 35S promoter? The RT-qPCR data is also very confusing. It is not clear that panel D is only examining the transcription of RFP (I assume via start/stop transcription) whereas panel C is targeting the minireplicon.

Thank you for your questions and we are sorry for the lack of clarity regarding to the mini-replicon vectors. Here, we updated the Figure supplement 14 to show replication and transcription of BYSMV minireplicon, a negative-stranded RNA virus derivative. In addition, we insert an A after the start codon to abolish the translation of GFP mRNA, which allow us to observe phase separation of GFP-PWT, GFP-PS5A, and GFP-PS5D during virus replication. Use this system, we wanted to show the localization and phase separation of GFP-PWT, GFP-PS5A, and GFP-PS5D during replication and transcription of BYS-agMR. Please see Figure 6–Figure supplement 1.

1. Pertaining to the replication assay in Fig. 6, transcription of RFP mRNA was reduced by S5A and increased by S5D. However, the RFP translation (via Panel A microscopy) is reversed. How do you explain increased RFP mRNA transcription by S5D but very low RFP fluorescence? The data between Panels A, C, and D do not support one another.

Many thanks for pointing this out! We also noticed the interesting results that have been repeated independently. As shown the illustration of BYSMV-agMR system in Figure 6–Figure supplement 1, the relative transcriptional activities of different GFP-P mutants were calculated from the normalized RFP transcript levels relative to the gMR replicate template (RFP mRNA/gMR), because replicating minigenomes are templates for viral transcription.

Since GFP-PS5D supported decreased replication, the ratio of RFP mRNA/gMR increased although the RFP mRNA of GFP-PS5D is not increased. In addition, the foci number of GFP-PS5D is much less than GFP-PWT and GFP-PS5A, indicating mRNAs in GFP-PS5D samples may contain aberrant transcripts those cannot be translated the RFP protein. In contrast, mRNAs in GFP-PS5A samples are translated efficiently. These results were in consistent with our previous studies using the free PWT, PS5A, and PS5D.

Reference: Gao Q, et al. 2020. Casein kinase 1 regulates cytorhabdovirus replication and transcription by phosphorylating a phosphoprotein serine-rich motif. The Plant Cell 32(9): 2878-2897.

1. The authors relied on 1,6-hexanediol to suppress phase separation in both insect vectors and barley. However, the authors disregarded several publications demonstrating cellular toxicity by 1,6-hexanediol and a report that 1,6-HD impairs kinase and phosphatase activities (see below). doi: 10.1016/j.jbc.2021.100260,

We agree with the reviewer that 1, 6-hexanediol induced cellular toxicity. Therefore, we removed these results, which does not affect the main conclusion of our results.

1. The authors state that reduced accumulation of BYSMV-GFP in insects and barley under HEX treatment "indicate that phase separation is important for cross-kingdom infection of BYSMV in insect vectors and host plants." The above statement is confounded by many factors, the most obvious being that HEX treatment is most likely toxic to cells and as a result cannot support efficient virus accumulation. Also, since HEX treatment interferes with phosphorylation (see REF above) its use here should be avoided since P phase separation is regulated by phosphorylation.

We agree with the reviewer that 1, 6-hexanediol induced cellular toxicity and hereby affected infections of BYSMV and other viruses. In addition, 1, 6-hexanediol would inhibit LLPS of cellular membraneless organelles, such as P-bodies, stress granules, cajal bodies, and the nucleolus, which also affect different virus infections directly or indirectly. Therefore, we removed these results, which does not affect the main conclusion of our results.

Reviewer #3 (Public Review):

Membrane-less organelles formed through liquid-liquid phase separation (LLPS) provide spatiotemporal control of host immunity responses and other cellular processes. Viruses are obligate pathogens proliferating in host cells which lead their RNAs and proteins are more likely to be targeted by immune-related membrane-less organelles. To successfully infect and proliferate in host cells, virus need to efficiently suppressing the immune function of those immune-related membrane-less organelles. Moreover, viruses also generate exogenous membrane-less organelles/RNA granules to facilitate their proliferation. Accordingly, host cells also need to target and suppress the functions of exogenous membrane-less organelles/RNA granules generated by viruses, the underlying mechanisms of which are still mysterious.

In this study, Fang et al. investigated how plant kinase confers resistance against viruses via modulating the phosphorylation and phase separation of BYSMV P protein. They firstly characterized the phase separation feature of BYSMV P protein. They also discovered that droplets formed by P protein recruit viral RNA and other viral protein in vivo. The phase separation activity of P protein is inhibited by the phosphorylation on its intrinsically disordered region. Combined with their previous study, this study demonstrated that host casein kinase (CK1) decreases the phase separation of P protein via increasing the phosphorylation of P protein. Finally, the author claimed that the phase separation of P protein facilitates BYSMV replication but decreases its transcription. Taking together, this study uncovered the molecular mechanism of plant regulating viral proliferation via decreasing the formation of exogenous RNA granules/membraneless organelles. Overall, this paper tells an interesting story about the host immunity targeting viruses via modulating the dynamics of exogenous membraneless organelles, and uncovers the modulation of viral protein phase separation by host protein, which is a hotspot in plant immunity, and the writing is logical.

Thanks for your positive comment on our studies.

Author Response:

Reviewer #1 (Public Review):

Here the authors use a variety of sophisticated approaches to assess the contribution of synaptic parameters to dendritic integration across neuronal maturation. They provide high-quality data identifying cellular parameters that underlie differences in AMPAR-mediated synaptic currents measured between adolescent and adult cerebellar stellate cells, and conclude that differences are attributed to an increase in the complexity of the dendritic arbor. This conclusion relies primarily on the ability of a previously described model for adult stellate cells to recapitulate the age-dependent changes in EPSCs by a change in dendritic branching with no change in synapse density. These rigorous results have implications for understanding how changing structure during neuronal development affects integration of AMPR-mediated synaptic responses.

The data showing that younger SCs have smaller dendritic arbors but similar synapse density is well-documented and provides compelling evidence that these structural changes affect dendritic integration. But the main conclusion also relies on the assumption that the biophysical model built for adult SCs applies to adolescent SCs, and there are additional relevant variables related to synaptic function that have not been fully assessed. Thus, the main conclusions would be strengthened and broadened by additional experimental validation.

We thank the reviewer for the positive assessment of the quality and importance of our manuscript. Below we address the reviewer’s comments directly but would like to stress that the goal of the manuscript was to understand the cellular mechanisms underlying developmental slowing of mEPSCs in SCs and the consequent implication for developmental changes in dendritic integration, which have rarely been examined to date, and not to establish a detailed biophysical model of cerebellar SCs. The latter would require dual-electrode recordings (one on 0.5 um dendrites), detailed description of the expression, dendritic localization of the gap junction protein connexin 36 (as done in Szoboszlay neuron 2016), and a detailed description prameter variability across the SC population (e.g. variations in AMPAR content at synapses, Rm, and dendritic morphology). Such experiments are well beyond the scope of the manuscript. Here we use biophysical simulations to support conclusions derived from specific experiments, more as a proof of principle rather than a strict quantitative prediction.

Nevertheless, we would like to clarify our selection of parameters for the biophysical models for immature and adult SCs. We did not simply “assume” that the biophysical models were the same at the two developmental stages. We either used evidence from the literature or our own measured parameters to establish an immature SC model. As compared to adult SCs, we found that immature SCs had 1) an identical membrane time constant, 2) an only slightly larger dendrite diameter, 3) decreased dendritic branching and maximum lengths, 4) a comparable synapse density, and 5) a homogeneous synapse distribution. Taken together, we concluded that increased dendritic branching during SC maturation resulted in a larger fraction of synapses at longer electrotonic distances in adult SCs. These experimental findings were incorporated into two distinct biophysical models representing immature and adult SCs. Evidence from the literature suggests that voltage-gated channels expression is not altered between the two developmental stages studied here. Therefore, like the adult SC model, we considered only the passive membrane properties and the dendritic morphology. The simulation results supported our conclusion that the increased apparent dendritic filtering of mEPSCs resulted from a change in the distribution of synapse distance to the soma rather than cable properties. Some of the measured parameters (e.g., membrane time constant) were not clearly stated manuscript, which we have corrected in the revised manuscript.

We are not sure what the reviewer meant by suggesting that we did not examine “other relevant variables related to synaptic function.” Later, the reviewer refers to alterations in AMPAR subunit composition or changes in cleft glutamate concentration (low-affinity AMPAR antagonist experiments). We performed experiments to directly examine both possible contributions by comparing qEPSC kinetics and performing low-affinity antagonist experiments, respectively, but we found that neither mechanism could account for the developmental slowing of mEPSCs. We, therefore, did not explore further possible developmental changes AMPAR subunits. See below for a more specific response and above for newly added text.

While many exciting questions could be examined in the future, we do not think the present study requires additional experiments. Nevertheless, we recognize that perhaps we can improve the description of the results to justify our conclusions better (see specifics below).

Reviewer #2 (Public Review):

This manuscript investigates the cellular mechanisms underlying the maturation of synaptic integration in molecular layer interneurons in the cerebellar cortex. The authors use an impressive combination of techniques to address this question: patch-clamp recordings, 2-photon and electron microscopy, and compartmental modelling. The study builds conceptually and technically on previous work by these authors (Abrahamsson et al. 2012) and extends the principles described in that paper to investigate how developmental changes in dendritic morphology, synapse distribution and strength combine to determine the impact of synaptic inputs at the soma.

1) Models are constructed to confirm the interpretation of experimental results, mostly repeating the simulations from Abrahamsson et al. (2012) using 3D reconstructed morphologies. The results are as expected from cable theory, given the (passive) model assumptions. While this confirmation is welcome and important, it is disappointing to see the opportunity missed to explore the implications of the experimental findings in greater detail. For instance, with the observed distributions of synapses, are there more segregated subunits available for computation in adult vs immature neurons?

As described in our response to reviewer 1, this manuscript intends to identify the cellular mechanisms accounting developmental slowing of mEPSCs and its implication for dendritic integration. The modeling was designed to support the most plausible explanation that increased branching resulted in more synapses at longer electrotonic distances. This finding is novel and merits more in-depth examination at a computation level in future studies.

Quantifying dendritic segregation is non-trivial due to dendritic nonlinearities and the difficulties in setting criteria for electrical “isolation” of inputs. However, because the space constant does not change with development, while both dendrite length and branching increase, it is rather logical to conclude qualitatively that the number of computational segments increases with development.

We have added the following sentence to the Discussion (line 579):

“Moreover, since the space constant does not change significantly with development and the dendritic tree complexity increases, the number of computational segments is expected to increase with development.”

How do SCs respond at different developmental stages with in vivo-like patterns of input, rather than isolated activation of synapses? Answering these sorts of questions would provide quantitative support for the conclusion that computational properties evolve with development.

While this is indeed a vital question, the in vivo patterns of synaptic activity are not known, so it is difficult to devise experiments to arrive at definitive conclusions.

2) From a technical perspective, the modeling appears to be well-executed, though more methodological detail is required for it to be reproducible. The AMPA receptor model and reversal potential are unspecified, as is the procedure for fitting the kinetics to data.

We did not use an explicit channel model to generate synaptic conductances. We simply used the default multiexponential function of Neuron (single exponential rise and single exponential decay) and adjusted the parameters tauRise and tauDecay such that simulated EPSCs matched somatic quantal EPSC amplitude, rise time and τdecay (Figure 4).

We added the following text to the methods (line 708):

“The peak and kinetics of the AMPAR-mediated synaptic conductance waveforms (gsyn) were set to simulate qEPSCs that matched the amplitude and kinetics of experimental somatic quantal EPSCs and evoked EPSCs. Immature quantal gsyn had an peak amplitude of 0.00175 μS, a 10-90 % RT of 0.0748 ms and a half-width of 0.36 ms (NEURON synaptic conductance parameter Tau0 = 0.073 ms, Tau1 = 0.26 ms and Gmax = 0.004 μS) while mature quantal gsyn had an peak amplitude of 0.00133 μS, a 10-90 % RT of 0.072 ms and a half-width of 0.341 ms (NEURON synaptic conductance parameters Tau0 = 0.072 ms, Tau1 = 0.24 ms and Gmax = 0.0032 μS). For all simulations, the reversal potential was set to 0 mV and the holing membrane potential was to – 70 mV. Experimental somatic PPR for EPSCs were reproduced with a gsyn 2/ gsyn 1 of 2.25.”

Were simulations performed at resting potential, and if yes, what was the value?

The membrane potential was set at – 70 mV to match that of experimental recordings and has been updated in the Methods section.

How was the quality of the morphological reconstructions assessed? Accurate measurement of dendritic diameters is crucial to the simulations in this study, so providing additional morphometrics would be helpful for assessing the results. Will the models and morphologies be deposited in ModelDB or similar?

For the two reconstructions imported into NEURON for simulations, we manually curated the dendritic diameters to verify a matching of the estimated diameter to that of the fluorescence image using NeuroStudio, which uses a robust subpixel estimation algorithm (Rayburst diameter, Rodriguez et al. 2008). The reconstructions include all variations in diameter throughout the dendritic tree (see as a example the the result of the reconstruction on the image below for the immature SC presented in the Figure 2D). The mean diameter across the entire dendritic tree of the reconstructed immature and adult SC was 0.42 and 0.36 μm, respectively, similar to the ratio of measured diameters estimated using confocal microscopy.

We have updated the methods section to include how reconstructions were curated and analyzed (line 693).

“An immature (P16) and adult SC (P42) were patch loaded with 30 μM Alexa 594 in the pipette and imaged using 2PLSM. Both cells were reconstructed in 3D using NeuronStudio in a semiautomatic mode which uses a robust subpixel estimation algorithm (calculation of Rayburst diameter (Rodriguez et al., 2008)). We manually curated the diameters to verify that it matched the fluorescence image to faithfully account for all variations in diameter throughout the dendritic tree. The measured diameter across the entire dendritic tree of the reconstructed immature and adult SCs was 0.42 and 0.36 μm, respectively. The 16% smaller diameter in adult was similar to the 13% obtained from confocal image analysis from many SCs (see Figure 2B).”

We agree with the reviewer that accurate measurements of dendritic diameters are crucial for the simulations. We did not rely soley on the reconstructed SCs, but we also performed highresolution confocal microscopy analysis of 16 different dye-filled SCs. We examined differences in the FWHM of intensity line profiles drawn perpendicular to the dendrite between immature and adult SCs. The FWHM is a good approximation of dendritic diameter and was performed similarly to adult SCs (Abrahamsson et al., 2012) to allow direct assessment of possible developmental differences. We confirmed that 98% of the estimated diameters are larger than the imaging resolution (0.27 μm). We observed only a small developmental difference in the mean FWHM (0.41 vs. 0.47 μm, 13% reduction) using this approach. Because the dendritic filtering is similar for diameters ranging from 0.3 to 0.6 μm (Figure 4G and 4H, Abrahamsson et al. 2012), we concluded that developmental changes in dendritic diameter cannot account for for developmental differences in mEPSC time course.

We added the following text to the methods (line 777):

“The imaging resolution within the molecular layer was estimated from the width of intensity line profiles of SC axons. The FWHM was 0.30 +/- 0.01 μm (n = 57 measurements over 16 axons) and a mean of 0.27 +/- 0.01 μm (n = 16) when taking into account the thinnest section for each axon. Only 2% of all dendritic measurements are less than 270 nm, suggesting that the dendritic diameter estimation is hardly affected by the resolution of our microscope”

Regarding additional morphometrics:

1) We added two panels (H and I) to Figure 6 showing the number of primary dendrites and branch points for immature and adult using the same estimation criteria as Myoga et al;, 2009. We have updated the Results section (line 389). “Thus, the larger number of puncta located further from the soma in adult SCs is not due to increased puncta density with distance, but a larger dendritic lengths (Figure 6E and 6F) and many more distal dendritic branches (Figure 6G, Sholl analysis) due to a larger number of branch points (Figure 6H), but not a larger number of primary dendrites (Figure 6I). The similarity between the shapes of synapse (Figure 6B) and dentric segment (Figure 6C) distributions was captured by a similarity in their skewness (0.38 vs. 0.32 for both distributions in immature and -0.10 and -0.08 for adult distributions). These data demonstrate that increased dendritic complexity during SC maturation is responsible for a prominent shift toward distal synapses in adult SCs.

2) As suggested by the reviewer, we estimated the dendritic width as a function branch order and observed a small reduction of dendritic segments as a function of distance from the soma that does not significantly alter the dendritic filtering (0.35 to 0.6 μm): there is a tendency to observe smaller diameter for more distal segments.

3) We also show the variability in dendritic diameter within single SCs and between different SCs, which can be very large. These results have been added to Figure 2B. See also point one below in response to “comment to authors.”

We will upload the two SC reconstructions to ModelDB.

3) The Discussion should justify the assumption of AMPA-only synapses in the model (by citing available experimental data) as well as the limitations of this assumption in the case of different spatiotemporal patterns of parallel fiber activation.

NMDARs are extrasynaptic in immature and adult SCs. Therefore they do not contribute to postsynaptic strength in response to low-frequency synaptic activation. We therefore do not consider their contribution to synaptic integration in this study. Please see also out detailed response to reviewer’s point 4. We have updated the Results accordingly.

4) What is the likely influence of gap junction coupling between SCs on the results presented here, and on synaptic integration in SCs more generally - and how does it change during development? This should also be discussed.

Please see a detailed response to Editor’s point 2. In brief, all recordings were performed without perturbing gap junction coupling between cells, which have been shown to affect axial resistance and membrane capacitance in other cell types (Szoboszlay et al., 2016). While our simulations do not explicitly include gap junctions, their effect on passive membrane properties is implicitly included because we matched the simulated membrane time constant to experimental values. Moreover, gap junctions are more prominent in cerebellar basket cells than SCs in both p18 to p21 animals (Rieubland 2015) and adult mice (Hoehne et al., 2020). Ultimately, the impact of gap junctions also depends on their distance from the activated synapses (Szoboszlay et al., 2016). Unfortunately, the distribution of gap junctions in SCs and their conductance is not known at this time. We, therefore, did not explicitly consider gap junction in this study.

Nevertheless, we have added a section in the Discussion (line 552):

“We cannot rule out that developmental changes in gap junction expression could contribute to the maturation of SC dendritic integration, since they are thought to contribute to the axial resistivity and capacitance of neurons (Szoboszlay et al., 2016). All the recordings were made with gap junctions intact, including for membrane time constant measurements. However, their expression in SCs is likely to be lower than their basket cell counterparts (Hoehne et al., 2020; Rieubland et al., 2014).”

5) All experiments and all simulations in the manuscript were done in voltage clamp (the Methods section should give further details, including the series resistance). What is the significance of the key results of the manuscript on synapse distribution and branching pattern of postsynaptic dendrites in immature and adult SCs for the typical mode of synaptic integration in vivo, i.e. in current clamp? What is their significance for neuronal output, considering that SCs are spontaneously active?

It should be noted that not all simulations were done in voltage-clamp, see figure 8.

Nevertheless, we have given additional details about the following experimental and simulation parameters:

1) Description of the whole-cell voltage-clamp procedure.

2) Series resistance values of experiments and used for simulations.

Initial simulations with the idealized SC model were performed with a Rs of 20 MOhm. In the reconstructed model Rs was set at 16 mOhm to match more precisely the experimental values obtained for the mEPSC experiments. We verified that there were no statistical difference in Rs between Immature and adult recordings.

Reviewer #3 (Public Review):

1) Although the authors were thorough in their efforts to find the mechanism underlying the differences in the young and adult SC synaptic event time course, the authors should consider the possibility of inherently different glutamate receptors, either by alterations in the subunit composition or by an additional modulatory subunit. The literature actually suggests that this might be the case, as several publications described altered AMPA receptor properties (not just density) during development in stellate cells (Bureau, Mulle 2004; Sun, Liu 2007; Liu, Cull-Candy 2002). The authors need to address these possibilities, as modulatory subunits are known to alter receptor kinetics and conductance as well.

Properties of synaptic AMPAR in SCs are known to change during development and in an activity-dependent manner. EPSCs in immature SC have been shown to be mediated by calcium permeable AMPARs, predominantly containing GluR3 subunits that are associated with TARP γ2 and γ7 (Soto et al. 2007; Bats et al., 2012). During development GluR2 subunits are inserted to the synaptic AMPAR in an activity-dependent manner (Liu et al, 2000), affecting the receptors’ calcium permeability (Liu et al., 2002). However, those developmental changes do not appear to affect EPSC kinetics (Liu et al., 2002) and have very little impact on AMPAR conductance (Soto et al., 2007). When we compare qEPSC kinetics for somatic synapses between immature and adult SC, we did not observe changes in EPSC decay. In the light of this observation and also consistent with the studies cited above, we concluded that differences in AMPAR composition could not contribute to kinetics differences observed in the developmental changes in mEPSC properties.

We have modified the manuscript to make this point clearer (see section starting line 332) :

“This reduction in synaptic conductance could be due to a reduction in the number of synaptic AMPARs activated and/or a developmental change in AMPAR subunits. SC synaptic AMPARs are composed of GluA2 and GluA3 subunits associated with TARP γ2 and γ7 (Bats et al., 2012; Liu and Cull-Candy, 2000; Soto et al., 2007; Yamazaki et al., 2015). During development, GluR2 subunits are inserted to the synaptic AMPAR in an activity-dependent manner (Liu and Cull-Candy, 2002), affecting receptors calcium permeability (Liu and Cull-Candy, 2000). However, those developmental changes have little impact on AMPAR conductance (Soto et al., 2007), nor do they appear to affect EPSC kinetics (Liu and Cull-Candy, 2002); the latter is consistent with our findings. Therefore the developmental reduction in postsynaptic strength most likely results from fewer AMPARs activated by the release of glutamate from the fusion of a single vesicle. “

The authors correctly identify the relationship between local dendritic resistance and the reduction of driving force, but they assume the same relationship for young SCs as well in their model. This assumption is not supported by recordings, and as there are several publications about the disparity of input impedance for young versus adult cells (Schmidt-Hieber, Bischoffberger 2007).

The input resistance of the dendrite will indeed determine local depolarization and loss of driving force. However, its impact on dendritic integration depends on it precise value, and perhaps the reviewer thought we “assumed” that the input resistance to be the same between immature and adult SCs. This was not the case, and we have since clarified this in the manuscript. We performed three important measurements that support a loss of driving force in immature SCs (for reference, the input resistance for an infinite cable is described by the following equation (Rn= sqrt(RmRi/2)/(2pi*r^(3/2)), where r is the dendrite radius):

1) The input resistance is inversely proportional to the dendritic diameter, which we measured to be only slightly larger in immature SCs (0.47 versus 0.41 μm). This result is described in Figure 2.

2) We measured the membrane time constant, which provides an estimate of the total membrane conductance multiplied by the total capacitance. The values between the two ages were similar, suggesting a slightly larger membrane resistance to compensate the smaller total membrane capacitance of the immature SCs. This was explicitly accounted for when performing the simulations using reconstructed immature and adult SCs (Figure 2 and 7 and 8) by adjusting the specific membrane resistance until the simulated membrane time constant matched experimental values. These values were not clearly mentioned and are now included on line 233 in the Results and 704 in the Methods.

3) We directly examined paired-pulse facilitation of synapses onto immature SC dendrites versus that for somatic synapses. We previously showed in adult SCs that sublinear summation of synaptic responses, due to loss of synaptic current driving force (Tran- Van-Minh et al. 2016), manifests in decreased facilitation for dendritic synapses (Abrahamsson et al. 2012). Figure 8A shows that indeed dendritic facilitation was less than observed in the soma. We have now modified Figure 8 to include the results of the simulations showing that the biophysical model could reproduce this difference in shortterm plasticity (Figure 8B).

Together, we believe these measurements support the presence of similar sublinear summation mechanisms in immature SCs.

2) The authors use extracellular stimulation of parallel fibers. The authors note that due to the orientation of the PF, and the slicing angle, they can restrict the spatial extent of the stimuli. However, this method does not guarantee that the stimulated fibers will all connect to the same dendritic branch. Whether two stimulated synapses connect to the same dendrite or not can heavily influence summation. This is especially a great concern for these cells as the Scholl analysis showed that young and adult SC cells have different amount of distal dendrites. Therefore, if the stimulated axons connect to several different neighboring dendrites instead of the one or two in case of young SC cells, then the model calculations and the conclusions about the summation rules may be erroneous.

We selected isolated dendrites and delivered voltage stimuli using small diameter glass electrodes (~ 1 μm) 10 - 15 V above threshold to stimulate single dendrites. This procedure excites GC axons in brain slices made from adult mice within less than 10 μm from the tip (Figure 2C, Tran-Van-Minh et al. 2016). It produces large dendritic depolarizations that are sufficient to decrease synaptic current driving force (Figure 1, Tran-Van-Minh et al. 2016). When we reproduced the conductance ratio using uncaging of single dendrites, we observed paired-pulse facilitation in the dendrites – suggesting that electrical stimulation activated synapses on common dendritic branches, or at least within close electrotonic distance to cause large dendritic depolarizations (Figure 7, Abrahamsson et al. 2012). Finally, we expect that the decreased branching in immature SCs further ensures that a majority of recorded synapses are contacting a common dendritic segment. We cannot rule out that occasionally some synaptic responses recorded at the soma are from synapses on different dendritic branches, but we do not see how this would alter our results and change our principal conclusions, particularly since this possible error only effects the interpretation of how many synapses are activated in paired-pulse experiments. The majority of the conclusions arise from the stimulation of single vesicle release events, and given the strikingly perpendicular orientation of GC axons, a 10 μm error in synapse location along a dendrite when we stimulated in the outthird would not alter our interpretations of the data.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Teplenin and coworkers assesses the combined effects of localized depolarization and excitatory electrical stimulation in myocardial monolayers. They study the electrophysiological behaviour of cultured neonatal rat ventricular cardiomyocytes expressing the light-gated cation channel Cheriff, allowing them to induce local depolarization of varying area and amplitude, the latter titrated by the applied light intensity. In addition, they used computational modeling to screen for critical parameters determining state transitions and to dissect the underlying mechanisms. Two stable states, thus bistability, could be induced upon local depolarization and electrical stimulation, one state characterized by a constant membrane voltage and a second, spontaneously firing, thus oscillatory state. The resulting 'state' of the monolayer was dependent on the duration and frequency of electrical stimuli, as well as the size of the illuminated area and the applied light intensity, determining the degree of depolarization as well as the steepness of the local voltage gradient. In addition to the induction of oscillatory behaviour, they also tested frequency-dependent termination of induced oscillations.

Strengths:

The data from optogenetic experiments and computational modelling provide quantitative insights into the parameter space determining the induction of spontaneous excitation in the monolayer. The most important findings can also be reproduced using a strongly reduced computational model, suggesting that the observed phenomena might be more generally applicable.

Weaknesses:

While the study is thoroughly performed and provides interesting mechanistic insights into scenarios of ventricular arrhythmogenesis in the presence of localized depolarized tissue areas, the translational perspective of the study remains relatively vague. In addition, the chosen theoretical approach and the way the data are presented might make it difficult for the wider community of cardiac researchers to understand the significance of the study.

Reviewer #2 (Public review):

In the presented manuscript, Teplenin and colleagues use both electrical pacing and optogenetic stimulation to create a reproducible, controllable source of ectopy in cardiomyocyte monolayers. To accomplish this, they use a careful calibration of electrical pacing characteristics (i.e., frequency, number of pulses) and illumination characteristics (i.e., light intensity, surface area) to show that there exists a "sweet spot" where oscillatory excitations can emerge proximal to the optogenetically depolarized region following electrical pacing cessation, akin to pacemaker cells. Furthermore, the authors demonstrate that a high-frequency electrical wave-train can be used to terminate these oscillatory excitations. The authors observed this oscillatory phenomenon both in vitro (using neonatal rat ventricular cardiomyocyte monolayers) and in silico (using a computational action potential model of the same cell type). These are surprising findings and provide a novel approach for studying triggered activity in cardiac tissue.

The study is extremely thorough and one of the more memorable and grounded applications of cardiac optogenetics in the past decade. One of the benefits of the authors' "two-prong" approach of experimental preps and computational models is that they could probe the number of potential variable combinations much deeper than through in vitro experiments alone. The strong similarities between the real-life and computational findings suggest that these oscillatory excitations are consistent, reproducible, and controllable.

Triggered activity, which can lead to ventricular arrhythmias and cardiac sudden death, has been largely attributed to sub-cellular phenomena, such as early or delayed afterdepolarizations, and thus to date has largely been studied in isolated single cardiomyocytes. However, these findings have been difficult to translate to tissue and organ-scale experiments, as well-coupled cardiac tissue has notably different electrical properties. This underscores the significance of the study's methodological advances: the use of a constant depolarizing current in a subset of (illuminated) cells to reliably result in triggered activity could facilitate the more consistent evaluation of triggered activity at various scales. An experimental prep that is both repeatable and controllable (i.e., both initiated and terminated through the same means).

The authors also substantially explored phase space and single-cell analyses to document how this "hidden" bi-stable phenomenon can be uncovered during emergent collective tissue behavior. Calibration and testing of different aspects (e.g., light intensity, illuminated surface area, electrical pulse frequency, electrical pulse count) and other deeper analyses, as illustrated in Appendix 2, Figures 3-8, are significant and commendable.

Given that the study is computational, it is surprising that the authors did not replicate their findings using well-validated adult ventricular cardiomyocyte action potential models, such as ten Tusscher 2006 or O'Hara 2011. This may have felt out of scope, given the nice alignment of rat cardiomyocyte data between in vitro and in silico experiments. However, it would have been helpful peace-of-mind validation, given the significant ionic current differences between neonatal rat and adult ventricular tissue. It is not fully clear whether the pulse trains could have resulted in the same bi-stable oscillatory behavior, given the longer APD of humans relative to rats. The observed phenomenon certainly would be frequency-dependent and would have required tedious calibration for a new cell type, albeit partially mitigated by the relative ease of in silico experiments.

For all its strengths, there are likely significant mechanistic differences between this optogenetically tied oscillatory behavior and triggered activity observed in other studies. This is because the constant light-elicited depolarizing current is disrupting the typical resting cardiomyocyte state, thereby altering the balance between depolarizing ionic currents (such as Na+ and Ca2+) and repolarizing ionic currents (such as K+ and Ca2+). The oscillatory excitations appear to later emerge at the border of the illuminated region and non-stimulated surrounding tissue, which is likely an area of high source-sink mismatch. The authors appear to acknowledge differences in this oscillatory behavior and previous sub-cellular triggered activity research in their discussion of ectopic pacemaker activity, which is canonically expected more so from genetic or pathological conditions. Regardless, it is exciting to see new ground being broken in this difficult-to-characterize experimental space, even if the method illustrated here may not necessarily be broadly applicable.

We thank the reviewers for their thoughtful and constructive feedback, as well as for recognizing the conceptual and technical strengths of our work. We are especially pleased that our integrated use of optogenetics, electrical pacing, and computational modelling was seen as a rigorous and innovative approach to investigating spontaneous excitability in cardiac tissue.

At the core of our study was the decision to focus exclusively on neonatal rat ventricular cardiomyocytes. This ensured a tightly controlled and consistent environment across experimental and computational settings, allowing for direct comparison and deeper mechanistic insight. While extending our findings to adult or human cardiomyocytes would enhance translational relevance, such efforts are complicated by the distinct ionic properties and action potential dynamics of these cells, as also noted by Reviewer #2. For this foundational study, we chose to prioritize depth and clarity over breadth.

Our computational domain was designed to faithfully reflect the experimental system. The strong agreement between both domains is encouraging and supports the robustness of our framework. Although some degree of theoretical abstraction was necessary (thereby sometimes making it a bit harder to read), it reflects the intrinsic complexity of the collective behaviours we aimed to capture such as emergent bi-stability. To make these ideas more accessible, we included simplified illustrations, a reduced model, and extensive supplementary material.

A key insight from our work is the emergence of oscillatory behaviour through interaction of illuminated and non-illuminated regions. Rather than replicating classical sub-cellular triggered activity, this behaviour arises from systems-level dynamics shaped by the imposed depolarizing current and surrounding electrotonic environment. By tuning illumination and local pacing parameters, we could reproducibly induce and suppress these oscillations, thereby providing a controllable platform to study ectopy as a manifestation of spatial heterogeneity and collective dynamics.

Altogether, our aim was to build a clear and versatile model system for investigating how spatial structure and pacing influence the conditions under which bistability becomes apparent in cardiac tissue. We believe this platform lays strong groundwork for future extensions into more physiologically and clinically relevant contexts.

In revising the manuscript, we carefully addressed all points raised by the reviewers. We have also responded to each of their specific comments in detail, which are provided below.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the authors):

Please find my specific comments and suggestions below:

(1) Line 64: When first introduced, the concept of 'emergent bi-stability' may not be clear to the reader.

We concur that the full breadth of the concept of emergent bi-stability may not be immediately clear upon first mention. Nonetheless, its components have been introduced separately: “emergent” was linked to multicellular behaviour in line 63, while “bi-stability” was described in detail in lines 39–56. We therefore believe that readers could form an intuitive understanding of the combined term, which will be further clarified as the manuscript develops. To further ease comprehension of the reader, we have added the following clarification to line 64:

“Within this dynamic system of cardiomyocytes, we investigated emergent bi-stability (a concept that will be explained more thoroughly later on) in cell monolayers under the influence of spatial depolarization patterns.”

(2) Lines 67-80: While the introduction until line 66 is extremely well written, the introduction of both cardiac arrhythmia and cardiac optogenetics could be improved. It is especially surprising that miniSOG is first mentioned as a tool for optogenetic depolarisation of cardiomyocytes, as the authors would probably agree that Channelrhodopsins are by far the most commonly applied tools for optogenetic depolarisation (please also refer to the literature by others in this respect). In addition, miniSOG has side effects other than depolarisation, and thus cannot be the tool of choice when not directly studying the effects of oxidative stress or damage.

The reviewer is absolutely correct in noting that channelrhodopsins are the most commonly applied tools for optogenetic depolarisation. We introduced miniSOG primarily for historical context: the effects of specific depolarization patterns on collective pacemaker activity were first observed with this tool (Teplenin et al., 2018). In that paper, we also reported ultralong action potentials, occurring as a side effect of cumulative miniSOG-induced ROS damage. In the following paragraph (starting at line 81), we emphasize that membrane potential can be controlled much better using channelrhodopsins, which is why we employed them in the present study.

(3) Line 78: I appreciate the concept of 'high curvature', but please always state which parameter(s) you are referring to (membrane voltage in space/time, etc?).

We corrected our statement to include the specification of space curvature of the depolarised region:

“In such a system, it was previously observed that spatiotemporal illumination can give rise to collective behaviour and ectopic waves (Teplenin et al. (2018)) originating from illuminated/depolarised regions (with high spatial curvature).”

(4) Line 79: 'bi-stable state' - not yet properly introduced in this context.

The bi-stability mentioned here refers back to single cell bistability introduced in Teplenin et al. (2018), which we cited again for clarity.

“These waves resulted from the interplay between the diffusion current and the single cell bi-stable state (Teplenin et al. (2018)) that was induced in the illuminated region.”

(5) Line 84-85: 'these ion channels allow the cells to respond' - please describe the channel used; and please correct: the channels respond to light, not the cells. Re-ordering this paragraph may help, because first you introduce channels for depolarization, then you go back to both de- and hyperpolarization. On the same note, which channels can be used for hyperpolarization of cardiomyocytes? I am not aware of any, even WiChR shows depolarizing effects in cardiomyocytes during prolonged activation (Vierock et al. 2022). Please delete: 'through a direct pathway' (Channelrhodopsins a directly light-gated channels, there are no pathways involved).

We realised that the confusion arose from our use of incorrect terminology: we mistakenly wrote hyperpolarisation instead of repolarisation. In addition to channelrhodopsins such as WiChR, other tools can also induce a repolarising effect, including light-activatable chloride pumps (e.g., JAWS). However, to improve clarity, we recognize that repolarisation is not relevant to our manuscript and therefore decided to remove its mention (see below). Regarding the reported depolarising effects of WiChR in Vierock et al. (2022), we speculate that these may arise either from the specific phenotype of the cardiomyocytes used in the study, i.e. human induced pluripotent stem cell-derived atrial myocytes (aCMs), or from the particular ionic conditions applied during patch-clamp recordings (e.g., a bath solution containing 1 mM KCl). Notably, even after prolonged WiChR activation, the aCMs maintained a strongly negative maximum diastolic potential of approximately –55 mV.

“Although effects of illuminating miniSOG with light might lead to formation of depolarised areas, it is difficult to control the process precisely since it depolarises cardiomyocytes indirectly. Therefore, in this manuscript, we used light-sensitive ion channels to obtain more refined control over cardiomyocyte depolarisation. These ion channels allow the cells to respond to specific wavelengths of light, facilitating direct depolarisation (Ördög et al. (2021, 2023)). By inducing cardiomyocyte depolarisation only in the illuminated areas, optogenetics enables precise spatiotemporal control of cardiac excitability, an attribute we exploit in this manuscript (Appendix 2 Figure 1).”

(6) Figure 1: What would be the y-axis of the 'energy-like curves' in B? What exactly did you plot here?

The graphs in Figure 1B are schematic representations intended to clarify the phenomenon for the reader. They do not depict actual data from any simulation or experiment. We clarified this misunderstanding by specifying that Figure 1B is a schematic representation of the effects at play in this paper.

“(B) Schematic representation showing how light intensity influences collective behaviour of excitable systems, transitioning between a stationary state (STA) at low illumination intensities and an oscillatory state (OSC) at high illumination intensities. Bi-stability occurs at intermediate light intensities, where transitions between states are dependent on periodic wave train properties. TR. OSC, transient oscillations.”

To expand slightly beyond the paper: our schematic representation was inspired by a common visualization in dynamical systems used to illustrate bi-stability (for an example, see Fig. 3 in Schleimer, J. H., Hesse, J., Contreras, S. A., & Schreiber, S. (2021). Firing statistics in the bistable regime of neurons with homoclinic spike generation. Physical Review E, 103(1), 012407.). In this framework, the y-axis can indeed be interpreted as an energy landscape, which is related to a probability measure through the Boltzmann distribution: . Here, p denotes the probability of occupying a particular state (STA or OSC). This probability can be estimated from the area (BCL × number of pulses) falling within each state, as shown in Fig. 4C. Since an attractor corresponds to a high-probability state, it naturally appears as a potential well in the landscape.

(7) Lines 92-93: 'this transition resulted for the interaction of an illuminated region with depolarized CM and an external wave train' - please consider rephrasing (it is not the region interacting with depolarized CM; and the external wave train could be explained more clearly).

We rephrased our unclear sentence as follows:

“This transition resulted from the interaction of depolarized cardiomyocytes in an illuminated region with an external wave train not originating from within the illuminated region.”

(8) Figure 2 and elsewhere: When mentioning 'frequency', please state frequency values and not cycle lengths. Please also reconsider your distinction between high and low frequencies; 200 ms (5 Hz) is actually the normal heart rate for neonatal rats (300 bpm).

In the revised version, we have clarified frequency values explicitly and included them alongside period values wherever frequency is mentioned, to avoid any ambiguity. We also emphasize that our use of "high" and "low" frequency is strictly a relative distinction within the context of our data, and not meant to imply a biological interpretation.

(9) Lines 129-131: Why not record optical maps? Voltage dynamics in the transition zone between depolarised and non-depolarised regions might be especially interesting to look at?

We would like to clarify that optical maps were recorded for every experiment, and all experimental traces of cardiac monolayer activity were derived from these maps. We agree with the reviewer that the voltage dynamics in the transition zone are particularly interesting. However, we selected the data representations that, in our view, best highlight the main mechanisms. When we analysed full voltage profiles, they didn’t add extra insights to this main mechanism. As the other reviewer noted, the manuscript already presents a wide range of regimes, so we decided not to introduce further complexity.

(10) Lines 156-157: Why was the model not adapted to match the biophysical properties (e.g., kinetics, ion selectivity, light sensitivity) of Cheriff?

The model was not adapted to the biophysical properties of Cheriff, because this would entail a whole new study involving extensive patch-clamping experiments, fitting, and calibration to model the correct properties of the ion channel. Beyond considerations of time efficiency, incorporating more specific modelling parameters would not change the essence of our findings. While numeric parameter ranges might shift, the core results would remain unchanged. This is a result of our experimental design where we applied constant illumination of long duration (6s or longer), thus making a difference in kinetical properties of an optogenetic tool irrelevant. In addition, we were able to observe qualitatively similar phenomena using many other depolarising optogenetic tools (e.g. ChR2, ReaChR, CatCh and more) in our in-vitro experiments. We ended up with Cheriff as our optotool-of-choice for the practical reasons of good light-sensitivity and a non-overlapping spectrum with our fluorescent dyes.

Therefore, computationally using a more general depolarising ion channel hints at the more general applicability of the observed phenomena, supporting our claim of a universal mechanism  (demonstrated experimentally with CheRiff and computationally with ChR2).

(11) Line 158: 1.7124 mW/mm^2 - While I understand that this is the specific intensity used as input in the model, I am convinced that the model is not as accurate to predict behaviour at this specific intensity (4 digits after the comma), especially given that the model has not been adapted to Cheriff (probably more light sensitive than ChR2). Can this be rephrased?

We did not aim for quantitative correspondence between the computational model and the biological experiments, but rather for qualitative agreement and mechanistic insight (see line 157). Qualitative comparisons are computationally obtained in a whole range of different intensities, as demonstrated in the 3D diagram of Fig. 4C. We wanted to demonstrate that at one fixed light intensity (chosen to be 1.7124 mW/mm^2 for the most clear effect), it was possible for all three states (STA, OSC. TR. OSC.) to coexist depending on the number of pulses and their period. Therefore the specific intensity used in the computational model is correct, and for reproducibility, we have left it unchanged while clarifying that it refers specifically to the in silico model:

“Simulating at a fixed constant illumination of 1.7124 𝑚𝑊∕𝑚𝑚² and a fixed number of 4 pulses, frequency dependency of collective bi-stability was reproduced in Figure 4A.”

(12) Lines 160, 165, and elsewhere: 'Once again, Once more' - please delete or rephrase.

We agree that we could have written these binding words better and reformulated them to:

“Similar to the experimental observations, only intermediate electrical pacing frequencies (500-𝑚𝑠 period) caused transitions from collective stationary behaviour to collective oscillatory behaviour and ectopic pacemaker activity had periods (710 𝑚𝑠) that were different from the stimulation train period (500 𝑚𝑠). Figure 4B shows the accumulation of pulses necessary to invoke a transition from the collective stationary state to the collective oscillatory state at a fixed stimulation period (600 𝑚𝑠). Also in the in silico simulations, ectopic pacemaker activity had periods (750 𝑚𝑠) that were different from the stimulation train period (600 𝑚𝑠). Also for the transient oscillatory state, the simulations show frequency selectivity (Appendix 2 Figure 4B).”

(13) Line 171: 'illumination strength': please refer to 'light intensity'.

We have revised our formulation to now refer specifically to “light intensity”:

“We previously identified three important parameters influencing such transitions: light intensity, number of pulses, and frequency of pulses.”

(14) Lines 187-188: 'the illuminated region settles into this period of sending out pulses' - please rephrase, the meaning is not clear.

We reformulated our sentence to make its content more clear to the reader:

“For the conditions that resulted in stable oscillations, the green vertical lines in the middle and right slices represent the natural pacemaker frequency in the oscillatory state. After the transition from the stationary towards the oscillatory state, oscillatory pulses emerging from the illuminated region gradually dampen and stabilize at this period, corresponding to the natural pacemaker frequency.”

(15) Figure 7: A)- please state in the legend which parameter is plotted on the y-axis (it is included in the main text, but should be provided here as well); C) The numbers provided in brackets are confusing. Why is (4) a high pulse number and (3) a low pulse number? Why not just state the number of pulses and add alpha, beta, gamma, and delta for the panels in brackets? I suggest providing the parameters (e.g., 800 ms cycle length, 2 pulses, etc) for all combinations, but not rate them with low, high, etc. (see also comment above).

We appreciate the reviewer’s comments and have revised the caption for figure 7, which now reads as follows:

“Figure 7. Phase plane projections of pulse-dependent collective state transitions. (A) Phase space trajectories (displayed in the Voltage – x_r plane) of the NRVM computational model show a limit cycle (OSC) that is not lying around a stable fixed point (STA). (B) Parameter space slice showing the relationship between stimulation period and number of pulses for a fixed illumination intensity (1.72 𝑚𝑊 ∕𝑚𝑚2) and size of the illuminated area (67 pixels edge length). Letters correspond to the graphs shown in C. (C) Phase space trajectories for different combinations of stimulus train period and number of pulses (α: 800 ms cycle length + 2 pulses, β: 800 ms cycle length + 4 pulses, γ: 250 ms cycle length + 3 pulses, δ: 250 ms cycle length + 8 pulses). α and δ do not result in a transition from the resting state to ectopic pacemaker activity, as under these circumstances the system moves towards the stationary stable fixed point from outside and inside the stable limit cycle, respectively. However, for β and γ, the stable limit cycle is approached from outside and inside, respectively, and ectopic pacemaker activity is induced.”

(16) Line 258: 'other dimensions by the electrotonic current' - not clear, please rephrase and explain.

We realized that our explanation was somewhat convoluted and have therefore changed the text as follows:

“Rather than producing oscillations, the system returns to the stationary state along dimensions other than those shown in Figure 7C (Voltage and x_r), as evidenced by the phase space trajectory crossing itself. This return is mediated by the electrotonic current.”

(17) Line 263: ‘increased too much’ – please rephrase using scientific terminology.

We rephrased our sentence to:

“However, this is not a Hopf bifurcation, because in that case the system would not return to the stationary state when the number of pulses exceeds a critical threshold.”

(18) Line 275: 'stronger diffusion/electrotonic influence from the non-illuminated region' - not sure diffusion is the correct term here. Please explain by taking into account the membrane potential. Please make sure to use proper terminology. The same applies to lines 281-282.

We appreciate this comment, which prompted us to revisit on our text. We realised that some sections could be worded more clearly, and we also identified an error in the legend of Supplementary Figure 7. The corresponding corrections are provided below:

“However, repolarisation reserve does have an influence, prolonging the transition when it is reduced (Appendix 2 Figure 7). This effect can be observed either by moving further from the boundary of the illuminated region, where the electrotonic influence from the non-illuminated region is weaker, or by introducing ionic changes, such as a reduction in I_Ks and/or I_to. For example, because the electrotonic influence is weaker in the center of the illuminated region, the voltage there is not pulled down toward the resting membrane potential as quickly as in cells at the border of the illuminated zone.”

“To add a multicellular component to our single cell model we introduced a current that replicates the effect of cell coupling and its associated electrotonic influence.”

“Figure 7. The effect of ionic changes on the termination of pacemaker activity. The mechanism that moves the oscillating illuminated tissue back to the stationary state after high frequency pacing is dependent on the ionic properties of the tissue, i.e. lower repolarisation reserves (20% 𝐼_𝐾𝑠 + 50% 𝐼_𝑡𝑜) are associated with longer transition times.”

(19) Line 289: -58 mV (to be corrected), -20 mV, and +50 mV - please justify the selection of parameters chosen. This also applies elsewhere- the selection of parameters seems quite arbitrary, please make sure the selection process is more transparent to the reader.

Our choice of parameters was guided by the dynamical properties of the illuminated cells as well as by illustrative purposes. The value of –58 mV corresponds to the stimulation threshold of the model. The values of 50 mV and –20 mV match those used for single-cell stimulation (Figure 8C2, right panel), producing excitable and bistable dynamics, respectively. We refer to this point in line 288 with the phrase “building on this result.” To maintain conciseness, we did not elaborate on the underlying reasoning within the manuscript and instead reported only the results.

We also corrected the previously missed minus sign: -58 mV.

(20) Figure 8 and corresponding text: I don't understand what stimulation with a voltage means. Is this an externally applied electric field? Or did you inject a current necessary to change the membrane voltage by this value? Please explain.

Stimulation with a specific voltage is a standard computational technique and can be likened to performing a voltage-clamp experiment on each individual cell. In this approach, the voltage of every cell in the tissue is briefly forced to a defined value.

(21) Figure 8C- panel 2: Traces at -20 mV and + 50 mV are identical. Is this correct? Please explain.

Yes, that is correct. The cell responds similarly to a voltage stimulus of -20 mV or one of 50 mV, because both values are well above the excitation threshold of a cardiomyocyte.

(22) Line 344 and elsewhere: 'diffusion current' - This is probably not the correct terminology for gap-junction mediated currents. Please rephrase.

A diffusion current is a mathematical formulation for a gap junction mediated current here, so , depending on the background of the reader, one of the terms might be used focusing on different aspects of the results. In a mathematical modelling context one often refers to a diffusion current because cardiomyocytes monolayers and tissues can be modelled using a reaction-diffusion equation. From the context of fine-grain biological and biophysical details, one uses the term gap-junction mediated current. Our choice is motivated by the main target audience we have in mind, namely interdisciplinary researchers with a core background in the mathematics/physics/computer science fields.

However, to not exclude our secondary target audience of biological and medical readers we now clarified the terminology, drawing the parallel between the different fields of study at line 79:

“These waves resulted from the interplay between the diffusion current (also known in biology/biophysics as the gap junction mediated current) and the bi-stable state that was induced in the illuminated region.”

(23) Lines 357-58: 'Such ectopic sources are typically initiated by high frequency pacing' - While this might be true during clinical testing, how would you explain this when not externally imposed? What could be biological high-frequency triggers?

Biological high-frequency triggers could include sudden increases in heart rates, such as those induced by physical activity or emotional stress. Another possibility is the occurrence of paroxysmal atrial or ventricular fibrillation, which could then give rise to an ectopic source.

(24) Lines 419-420: 'large ionic cell currents and small repolarising coupling currents'. Are coupling currents actually small in comparison to cellular currents? Can you provide relative numbers (~ratio)?

Coupling currents are indeed small compared to cellular currents. This can be inferred from the I-V curve shown in Figure 8C1, which dips below 0 and creates bi-stability only because of the small coupling current. If the coupling current were larger, the system would revert to a monostable regime. To make this more concrete, we have now provided the exact value of the coupling current used in Figure 8C1.

“Otherwise, if the hills and dips of the N-shaped steady-state IV curve were large (Figure 8C-1), they would have similar magnitudes as the large currents of fast ion channels, preventing the subtle interaction between these strong ionic cell currents and the small repolarising coupling currents (-0.103649 ≈ 0.1 pA).”

(25) Line 426: Please explain how ‘voltage shocks’ were modelled.

We would like to refer the reviewer to our response to comment (20) regarding how we model voltage shocks. In the context of line 426, a typical voltage shock corresponds to a tissue-wide stimulus of 50 mV. Independent of our computational model, line 426 also cites other publications showing that, in clinical settings, high-voltage shocks are unable to terminate ectopic sustained activity, consistent with our findings.

(26) Lines 429 ff: 0.2pA/pF would correspond to 20 pA for a small cardiomyocyte of 100 pF, this current should be measurable using patch-clamp recordings.

In trying to be succinct, we may have caused some confusion. The difference between the dips (≈-0.07 pA/pF) and hills (_≈_0.11 pA/pF) is approximately 0.18 pA/pF. For a small cardiomyocyte, this corresponds to deviations from zero of roughly ±10 pA. Considering that typical RMS noise levels in whole-cell patch-clamp recordings range from 2-10 pA , it is understandable that detecting these peaks and dips in an I-V curve (average current after holding a voltage for an extended period)  is difficult. Achieving statistical significance would therefore require patching a large number of cells.

Given the already extensive scope of our manuscript in terms of techniques and concepts, we decided not to pursue these additional patch-clamp experiments.

Reviewer #2 (Recommendations for the authors):

Given the deluge of conditions to consider, there are several areas of improvement possible in communicating the authors' findings. I have the following suggestions to improve the manuscript.

(1) Please change "pulse train" straight pink bar OR add stimulation marks (such as "*", or individual pulse icons) to provide better visual clarity that the applied stimuli are "short ON, long OFF" electrical pulses. I had significant initial difficulty understanding what the pulse bars represented in Figures 2, 3, 4A-B, etc. This may be partially because stimuli here could be either light (either continuous or pulsed) or electrical (likely pulsed only). To me, a solid & unbroken line intuitively denotes a continuous stimulation. I understand now that the pink bar represents the entire pulse-train duration, but I think readers would be better served with an improvement to this indicator in some fashion. For instance, the "phases" were much clearer in Figures 7C and 8D because of how colour was used on the Vm(t) traces. (How you implement this is up to you, though!)

We have addressed the reviewer’s concern and updated the figures by marking each external pulse with a small vertical line (see below).

(2) Please label the electrical stimulation location (akin to the labelled stimulation marker in circle 2 state in Figure 1A) in at least Figures 2 and 4A, and at most throughout the manuscript. It is unclear which "edge" or "pixel" the pulse-train is originating from, although I've assumed it's the left edge of the 2D tissue (both in vitro and silico). This would help readers compare the relative timing of dark blue vs. orange optical signal tracings and to understand how the activation wavefront transverses the tissue.

We indicated the pacing electrode in the optical voltage recordings with a grey asterisk. For the in silico simulations, the electrode was assumed to be far away, and the excitation was modelled as a parallel wave originating from the top boundary, indicated with a grey zone.

(3) Given the prevalence of computational experiments in this study, I suggest considering making a straightforward video demonstrating basic examples of STA, OSC, and TR.OSC states. I believe that a video visualizing these states would be visually clarifying to and greatly appreciated by readers. Appendix 2 Figure 3 would be the no-motion visualization of the examples I'm thinking of (i.e., a corresponding stitched video could be generated for this). However, this video-generation comment is a suggestion and not a request.

We have included a video showing all relevant states, which is now part of the Supplementary Material.

(4) Please fix several typos that I found in the manuscript:

(4A) Line 279: a comma is needed after i.e. when used in: "peculiar, i.e. a standard". However, this is possibly stylistic (discard suggestion if you are consistent in the manuscript).

(4B) Line 382: extra period before "(Figure 3C)".

(4C) Line 501: two periods at end of sentence "scientific purposes.." .

We would like to thank the reviewer for pointing out these typos. We have corrected them and conducted an additional check throughout the manuscript for minor errors.

Author Response:

Reviewer #1 (Public Review):

[...] The major limitation of the manuscript lies in the framing and interpretation of the results, and therefore the evaluation of novelty. Authors claim for an important and unique role of beliefs-of-other-pain in altruistic behavior and empathy for pain. The problem is that these experiments mainly show that behaviors sometimes associated with empathy-for-pain can be cognitively modulated by changing prior beliefs. To support the notion that effects are indeed relating to pain processing generally or empathy for pain specifically, a similar manipulation, done for instance on beliefs about the happiness of others, before recording behavioural estimation of other people's happiness, should have been performed. If such a belief-about-something-else-than-pain would have led to similar results, in terms of behavioural outcome and in terms of TPJ and MFG recapitulating the pattern of behavioral responses, we would know that the results reflect changes of beliefs more generally. Only if the results are specific to a pain-empathy task, would there be evidence to associate the results to pain specifically. But even then, it would remain unclear whether the effects truly relate to empathy for pain, or whether they may reflect other routes of processing pain.

We thank Reviewer #1's for these comments/suggestions regarding the specificity of belief effects on brain activity involved in empathy for pain. Our paper reported 6 behavioral/EEG/fMRI experiments that tested effects of beliefs of others’ pain on empathy and monetary donation (an empathy-related altruistic behavior). We showed not only behavioral but also neuroimaging results that consistently support the hypothesis of the functional role of beliefs of others' pain in modulations of empathy (based on both subjective and objective measures as clarified in the revision) and altruistic behavior. We agree with Reviewer 1# that it is important to address whether the belief effect is specific to neural underpinnings of empathy for pain or is general for neural responses to various facial expressions such as happy, as suggested by Reviewer #1. To address this issue, we conducted an additional EEG experiment (which can be done in a limited time in the current situation), as suggested by Reviewer #1. This new EEG experiment tested (1) whether beliefs of authenticity of others’ happiness influence brain responses to perceived happy expressions; (2) whether beliefs of happiness modulate neural responses to happy expressions in the P2 time window as that characterized effects of beliefs of pain on ERPs.

Our behavioral results in this experiment (as Supplementary Experiment 1 reported in the revision) showed that the participants reported less feelings of happiness when viewing actors who simulate others' smiling compared to when viewing awardees who smile due to winning awards (see the figure below). Our ERP results in Supplementary Experiment 1 further showed that lack of beliefs of authenticity of others’ happiness (e.g., actors simulate others' happy expressions vs. awardees smile and show happy expressions due to winning an award) reduced the amplitudes of a long-latency positive component (i.e., P570) over the frontal region in response to happy expressions. These findings suggest that (1) there are possibly general belief effects on subjective feelings and brain activities in response to facial expressions; (2) beliefs of others' pain or happiness affect neural responses to facial expressions in different time windows after face onset; (3) modulations of the P2 amplitude by beliefs of pain may not be generalized to belief effects on neural responses to any emotional states of others. We reported the results of this new ERP experiment in the revision as Supplementary Experiment 1 and also discussed the issue of specificity of modulations of empathic neural responses by beliefs of others' pain in the revised Discussion (page 49-50).

Supplementary Experiment Figure 1. EEG results of Supplementary Experiment 1. (a) Mean rating scores of happy intensity related to happy and neutral expressions of faces with awardee or actor/actress identities. (b) ERPs to faces with awardee or actor/actress identities at the frontal electrodes. The voltage topography shows the scalp distribution of the P570 amplitude with the maximum over the central/parietal region. (c) Mean differential P570 amplitudes to happy versus neutral expressions of faces with awardee or actor/actress identities. The voltage topographies illustrate the scalp distribution of the P570 difference waves to happy (vs. neutral) expressions of faces with awardee or actor/actress identities, respectively. Shown are group means (large dots), standard deviation (bars), measures of each individual participant (small dots), and distribution (violin shape) in (a) and (c).

In the revised Introduction we cited additional literatures to explain the concept of empathy, behavioral and neuroimaging measures of empathy, and how, similar to previous research, we studied empathy for others' pain using subjective (self reports) and objective (brain responses) estimation of empathy (page 6-7). In particular, we mentioned that subjective estimation of empathy for pain depends on collection of self-reports of others' pain and ones' own painful feelings when viewing others' suffering. Objective estimation of empathy for pain relies on recording of brain activities (using fMRI, EEG, etc.) that differentially respond to painful or non-painful stimuli applied to others. fMRI studies revealed greater activations in the ACC, AI, and sensorimotor cortices in response to painful or non-painful stimuli applied to others. EEG studies showed that event-related potentials (ERPs) in response to perceived painful stimulations applied to others' body parts elicited neural responses that differentiated between painful and neutral stimuli over the frontal region as early as 140 ms after stimulus onset (Fan and Han, 2008; see Coll, 2018 for review). Moreover, the mean ERP amplitudes at 140–180 ms predicted subjective reports of others' pain and ones' own unpleasantness. Particularly related to the current study, previous research showed that pain compared to neutral expressions increased the amplitude of the frontal P2 component at 128–188 ms after stimulus onset (Sheng and Han, 2012; Sheng et al., 2013; 2016; Han et al., 2016; Li and Han, 2019) and the P2 amplitudes in response to others' pain expressions positively predicted subjective feelings of own unpleasantness induced by others' pain and self-report of one's own empathy traits (e.g., Sheng and Han, 2012). These brain imaging findings indicate that brain responses to others' pain can (1) differentiate others' painful or non-painful emotional states to support understanding of others' pain and (2) predict subjective feelings of others' pain and one's own unpleasantness induced by others' pain to support sharing of others' painful feelings. These findings provide effective subjective and objective measures of empathy that were used in the current study to investigate neural mechanisms underlying modulation of empathy and altruism by beliefs of others’ pain.

In addition, we took Reviewer #1’s suggestion for VPS analyses which examined specifically how neural activities in the empathy-related regions identified in the previous research (Krishnan et al., 2016, eLife) were modulated by beliefs of others’ pain. The results (page 40) provide further evidence for our hypothesis. We also reported new results of RSA analyses(page 39) that activities in the brain regions supporting affective sharing (e.g., insula), sensorimotor resonance (e.g., post-central gyrus), and emotion regulation (e.g., lateral frontal cortex) provide intermediate mechanisms underlying modulations of subjective feelings of others' pain intensity due to lack of BOP. We believe that, putting all these results together, our paper provides consistent evidence that empathy and altruistic behavior are modulated by BOP.

Reviewer #2 (Public Review):

[...] 1. In laying out their hypotheses, the authors write, "The current work tested the hypothesis that BOP provides a fundamental cognitive basis of empathy and altruistic behavior by modulating brain activity in response to others' pain. Specifically, we tested predictions that weakening BOP inhibits altruistic behavior by decreasing empathy and its underlying brain activity whereas enhancing BOP may produce opposite effects on empathy and altruistic behavior." While I'm a little dubious regarding the enhancement effects (see below), a supporting assumption here seems to be that at baseline, we expect that painful expressions reflect real pain experience. To that end, it might be helpful to ground some of the introduction in what we know about the perception of painful expressions (e.g., how rapidly/automatically is pain detected, do we preferentially attend to pain vs. other emotions, etc.).

Thanks for this suggestion! We included additional details about previous findings related to processes of painful expressions in the revised Introduction (page 7-8). Specifically, we introduced fMRI and ERP studies of pain expressions that revealed structures and temporal procedure of neural responses to others' pain (vs. neutral) expressions. Moreover, neural responses to others' pain (vs. neutral) expressions were associated with self-report of others' feelings, indicating functional roles of pain-expression induced brain activities in empathy for pain.

1. For me, the key takeaway from this manuscript was that our assessment of and response to painful expressions is contextually-sensitive - specifically, to information reflecting whether or not targets are actually in pain. As the authors state it, "Our behavioral and neuroimaging results revealed critical functional roles of BOP in modulations of the perception-emotion-behavior reactivity by showing how BOP predicted and affected empathy/empathic brain activity and monetary donations. Our findings provide evidence that BOP constitutes a fundamental cognitive basis for empathy and altruistic behavior in humans." In other words, pain might be an incredibly socially salient signal, but it's still easily overridden from the top down provided relevant contextual information - you won't empathize with something that isn't there. While I think this hypothesis is well-supported by the data, it's also backed by a pretty healthy literature on contextual influences on pain judgments (including in clinical contexts) that I think the authors might want to consider referencing (here are just a few that come to mind: Craig et al., 2010; Twigg et al., 2015; Nicolardi et al., 2020; Martel et al., 2008; Riva et al., 2015; Hampton et al., 2018; Prkachin & Rocha, 2010; Cui et al., 2016).

Thanks for this great suggestion! Accordingly, we included an additional paragraph in the revised Discussion regarding how social contexts influence empathy and cited the studies mentioned here (page 46-47).

1. I had a few questions regarding the stimuli the authors used across these experiments. First, just to confirm, these targets were posing (e.g., not experiencing) pain, correct? Second, the authors refer to counterbalancing assignment of these stimuli to condition within the various experiments. Was target gender balanced across groups in this counterbalancing scheme? (e.g., in Experiment 1, if 8 targets were revealed to be actors/actresses in Round 2, were 4 female and 4 male?) Third, were these stimuli selected at random from a larger set, or based on specific criteria (e.g., normed ratings of intensity, believability, specificity of expression, etc.?) If so, it would be helpful to provide these details for each experiment.

We'd be happy to clarify these questions. First, photos of faces with pain or neutral expressions were adopted from the previous work (Sheng and Han, 2012). Photos were taken from models who were posing but not experience pain. These photos were taken and selected based on explicit criteria of painful expressions (i.e., brow lowering, orbit tightening, and raising of the upper lip; Prkachin, 1992). In addition, the models' facial expressions were validated in independent samples of participants (see Sheng and Han, 2012). Second, target gender was also balanced across groups in this counterbalancing scheme. We also analyzed empathy rating score and monetary donations related to male and female target faces and did not find any significant gender effect (see our response to Point 5 below). Third, because the face stimuli were adopted from the previous work and the models' facial expressions were validated in independent samples of participants regarding specificity of expression, pain intensity, etc (Sheng and Han, 2012), we did not repeat these validation in our participants. Most importantly, we counterbalanced the stimuli in different conditions so that the stimuli in different conditions (e.g., patient vs. actor/actress conditions) were the same across the participants in each experiment. The design like this excluded any potential confound arising from the stimuli themselves.

1. The nature of the charitable donation (particularly in Experiment 1) could be clarified. I couldn't tell if the same charity was being referenced in Rounds 1 and 2, and if there were multiple charities in Round 2 (one for the patients and one for the actors).

Thanks for this comment! Yes, indeed, in both Rounds 1 and 2, the participants were informed that the amount of one of their decisions would be selected randomly and donated to one of the patients through the same charity organization (we clarified these in the revised Method section, page 55-56). We made clear in the revision that after we finished all the experiments of this study, the total amount of the participants' donations were subject to a charity organization to help patients who suffer from the same disease after the study.

1. I'm also having a hard time understanding the authors' prediction that targets revealed to truly be patients in the 2nd round will be associated with enhanced BOP/altruism/etc. (as they state it: "By contrast, reconfirming patient identities enhanced the coupling between perceived pain expressions of faces and the painful emotional states of face owners and thus increased BOP.") They aren't in any additional pain than they were before, and at the outset of the task, there was no reason to believe that they weren't suffering from this painful condition - therefore I don't see why a second mention of their pain status should increase empathy/giving/etc. It seems likely that this is a contrast effect driven by the actor/actress targets. See the Recommendations for the Authors for specific suggestions regarding potential control experiments. (I'll note that the enhancement effect in Experiment 2 seems more sensible - here, the participant learns that treatment was ineffective, which may be painful in and of itself.)

Thanks for comments on this important point! Indeed, our results showed that reassuring patient identities in Experiment 1 or by noting the failure of medical treatment related to target faces in Experiment 2 increased rating scores of others' pain and own unpleasantness and prompted more monetary donations to target faces. The increased empathy rating scores and monetary donations might be due to that repeatedly confirming patient identity or knowing the failure of medical treatment increased the belief of authenticity of targets' pain and thus enhanced empathy. However, repeatedly confirming patient identity or knowing the failure of medical treatment might activate other emotional responses to target faces such as pity or helplessness, which might also influence altruistic decisions. We agree with Reviewer #2 that, although our subjective estimation of empathy in Exp. 1 and 2 suggested enhanced empathy in the 2nd_round test, there are alternative interpretations of the results and these should be clarified in future work. We clarified these points in the revised Discussion (page 41-42).

1. I noted that in the Methods for Experiment 3, the authors stated "We recruited only male participants to exclude potential effects of gender difference in empathic neural responses." This approach continues through the rest of the studies. This raises a few questions. Are there gender differences in the first two studies (which recruited both male and female participants)? Moreover, are the authors not concerned about target gender effects? (Since, as far as I can tell, all studies use both male and female targets, which would mean that in Experiments 3 and on, half the targets are same-gender as the participants and the other half are other-gender.) Other work suggests that there are indeed effects of target gender on the recognition of painful expressions (Riva et al., 2011).

Thanks for raising this interesting question! Therefore, we reanalyzed data in Exp. 1 by including participants' gender or face gender as an independent variable. The three-way ANOVAs of pain intensity scores and amounts of monetary donations with Face Gender (female vs. male targets) × Test Phase (1st vs. 2nd_round) × Belief Change (patient-identity change vs. patient-identity repetition) did not show any significant three-way interaction (F(1,59) = 0.432 and 0.436, p = 0.514 and 0.512, ηp2 = 0.007 and 0.007, 90% CI = (0, 0.079) and (0, 0.079), indicating that face gender do not influence the results (see the figure below). Similarly, the three-way ANOVAs with Participant Gender (female vs. male participants) × Test Phase × Belief Change did not show any significant three-way interaction (F(1,58) = 0.121 and 1.586, p = 0.729 and 0.213, ηp2 = 0.002 and 0.027, 90% CI = (0, 0.055) and (0, 0.124), indicating no reliable difference in empathy and donation between men and women. It seems that the measures of empathy and altruistic behavior in our study were not sensitive to gender of empathy targets and participants' sexes.

Figure legend: (a) Scores of pain intensity and amount of monetary donations are reported separately for male and female target faces. (b) Scores of pain intensity and amount of monetary donations are reported separately for male and female participants.

1. I was a little unclear on the motivation for Experiment 4. The authors state "If BOP rather than other processes was necessary for the modulation of empathic neural responses in Experiment 3, the same manipulation procedure to assign different face identities that do not change BOP should change the P2 amplitudes in response to pain expressions." What "other processes" are they referring to? As far as I could tell, the upshot of this study was just to demonstrate that differences in empathy for pain were not a mere consequence of assignment to social groups (e.g., the groups must have some relevance for pain experience). While the data are clear and as predicted, I'm not sure this was an alternate hypothesis that I would have suggested or that needs disconfirming.

Thanks for this comment! We feel sorry for not being able to make clear the research question in Exp. 4. In the revised Results section (page 27-28) we clarified that the learning and EEG recording procedures in Experiment 3 consisted of multiple processes, including learning, memory, identity recognition, assignment to social groups, etc. The results of Experiment 3 left an open question of whether these processes, even without BOP changes induced through these processes, would be sufficient to result in modulation of the P2 amplitude in response to pain (vs. neutral) expressions of faces with different identities. In Experiment 4 we addressed this issue using the same learning and identity recognition procedures as those in Experiment 3 except that the participants in Experiment 4 had to learn and recognize identities of faces of two baseball teams and that there is no prior difference in BOP associated with faces of beliefs of the two baseball teams. If the processes involved in the learn and reorganization procedures rather than the difference in BOP were sufficient for modulation of the P2 amplitude in response to pain (vs. neutral) expressions of faces, we would expect similar P2 modulations in Experiments 4 and 3. Otherwise, the difference in BOP produced during the learning procedure was necessary for the modulation of empathic neural responses, we would not expect modulations of the P2 amplitude in response to pain (vs. neutral) expressions in Experiment 4. We believe that the goal and rationale of Exp. 4 are clear now.

I like this model and I think it would do well to implement this into classrooms. Knowing is awareness, caring is the heart, and acting is doing something about that care and conviction. It allows our desire to help and be kind come into fruition, it helps rid us of preconceptions or close-mindedness we may have been subjected to. I think these three are very different (as mentioned), but they all complement each other, allowing us to take a step towards cultivating multicultural education.

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Authors’ reply (____Ono et al)

Review Commons Refereed Preprint #RC-2025-03137

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Ono et al addressed how condensin II and cohesin work to define chromosome territories (CT) in human cells. They used FISH to assess the status of CT. They found that condensin II depletion leads to lengthwise elongation of G1 chromosomes, while double depletion of condensin II and cohesin leads to CT overlap and morphological defects. Although the requirement of condensin II in shortening G1 chromosomes was already shown by Hoencamp et al 2021, the cooperation between condensin II and cohesin in CT regulation is a new finding. They also demonstrated that cohesin and condensin II are involved in G2 chromosome regulation on a smaller and larger scale, respectively. Though such roles in cohesin might be predictable from its roles in organizing TADs, it is a new finding that the two work on a different scale on G2 chromosomes. Overall, this is technically solid work, which reports new findings about how condensin II and cohesin cooperate in organizing G1 and G2 chromosomes.

We greatly appreciate the reviewer’s supportive comments. The reviewer has accurately recognized our new findings concerning the collaborative roles of condensin II and cohesin in establishing and maintaining interphase chromosome territories.

Major point:

They propose a functional 'handover' from condensin II to cohesin, for the organization of CTs at the M-to-G1 transition. However, the 'handover', i.e. difference in timing of executing their functions, was not experimentally substantiated. Ideally, they can deplete condensin II and cohesin at different times to prove the 'handover'. However, this would require the use of two different degron tags and go beyond the revision of this manuscript. At least, based on the literature, the authors should discuss why they think condensin II and cohesin should work at different timings in the CT organization.

We take this comment seriously, especially because Reviewer #2 also expressed the same concern.　

First of all, we must admit that the basic information underlying the “handover” idea was insufficiently explained in the original manuscript. Let us make it clear below:

• Condensin II bound to chromosomes and is enriched along their axes from anaphase through telophase (Ono et al., 2004; Hirota et al., 2004; Walther et al., 2018).
• In early G1, condensin II is diffusely distributed within the nucleus and does not bind tightly to chromatin, as shown by detergent extraction experiments (Ono et al., 2013).
• Cohesin starts binding to chromatin when the cell nucleus reassembles (i.e., during the cytokinesis stage shown in Fig. 1B), apparently replacing condensins I and II (Brunner et al., 2025).
• Condensin II progressively rebinds to chromatin from S through G2 phase (Ono et al., 2013). The cell cycle-dependent changes in chromosome-bound condensin II and cohesin summarized above are illustrated in Fig. 1A. We now realize that Fig. 1B in the original manuscript was inconsistent with Fig. 1A, creating unnecessary confusion, and we sincerely apologize for this. The fluorescence images shown in the original Fig. 1B were captured without detergent extraction prior to fixation, giving the misleading impression that condensin II remained bound to chromatin from cytokinesis through early G1. This was not our intention. To clarify this, we have repeated the experiment in the presence of detergent extraction and replaced the original Fig. 1B with a revised panel. Figs. 1A and 1B are now more consistent with each other. Accordingly, we have modified the correspsonding sentences as follows:

Although condensin II remains nuclear throughout interphase, its chromatin binding is weak in G1 and becomes robust from S phase through G2 (Ono et al., 2013). Cohesin, in contrast, replaces condensin II in early G1 (Fig. 1 B)(Abramo et al., 2019; Brunner et al., 2025), and establishes topologically associating domains (TADs) in the G1 nucleus (Schwarzer et al., 2017; Wutz et al., 2017)*. *

While there is a loose consensus in the field that condensin II is replaced by cohesin during the M-to-G1 transition, it remains controversial whether there is a short window during which neither condensin II nor cohesin binds to chromatin (Abramo et al., 2019), or whether there is a stage in which the two SMC protein complexes “co-occupy” chromatin (Brunner et al., 2025). Our images shown in the revised Fig. 1B cannot clearly distinguish between these two possibilities.

From a functional point of view, the results of our depletion experiments are more readily explained by the latter possibility. If this is the case, the “interplay” or “cooperation” rather than the “handover” may be a more appropriate term to describe the functional collaboration between condensin II and cohesin during the M-to-G1 transition. For this reason, we have avoided the use of the word “handover” in the revised manuscript. It should be emphasized, however, that given their distinct chromosome-binding kinetics, the cooperation of the two SMC complexes during the M-to-G1 transition is qualitatively different from that observed in G2. Therefore, the central conclusion of the present study remains unchanged.

For example, a sentence in Abstract has been changed as follows:

a functional interplay between condensin II and cohesin during the mitosis-to-G1 transition is critical for establishing chromosome territories (CTs) in the newly assembling nucleus.

While the reviewer suggested one experiment, it is clearly beyond the scope of the current study. It should also be noted that even if such a cell line were available, the proposed application of sequential depletion to cells progressing from mitosis to G1 phase would be technically challenging and unlikely to produce results that could be interpreted with confidence.

Other points:

Figure 2E: It seems that the chromosome length without IAA is shorter in Rad21-aid cells than H2-aid cells or H2-aid Rad21-aid cells. How can this be interpreted? This comment is well taken. A related comment was made by Reviewer #3 (Major comment #2). Given the substantial genetic manipulations applied to establish multiple cell lines used in the present study, it is, strictly speaking, not straightforward to compare the -IAA controls between different cell lines. Such variations are most prominently observed in Fig. 2E, although they can also be observed to lesser extent in other experiments (e.g., Fig. 3E). This issue is inherently associated with all studies using genetically manipulated cell lines and therefore cannot be completely avoided. For this reason, we focus on the differences between -IAA and +IAA within each cell line, rather than comparing the -IAA conditions across different cell lines. In this sense, a sentence in the original manuscript (lines 178-180) was misleading. In the revised manuscript, we have modified the corresponding and subsequent sentence as follows:

Although cohesin depletion had a marginal effect on the distance between the two site-specific probes (Fig.2, C and E), double depletion did not result in a significant change (Fig.2, D and E), consistent with the partial restoration of centromere dispersion (Fig. 1G).

• *

In addition, we have added a section entitled “Limitations of the study” at the end of the Discussion to address technical issues that are inevitably associated with the current approach.

Figure 3: Regarding the CT morphology, could they explain further the difference between 'elongated' and 'cloud-like (expanded)'? Is it possible to quantify the frequency of these morphologies? In the original manuscript, we provided data that quantitatively distinguished between the “elongated” and “cloud-like” phenotypes. Specifically, Fig. 2E shows that the distance between two specific loci (Cen 12 and 12q15) is increased in the elongated phenotype but not in the cloud-like phenotype. In addition, the cloud-like morphology was clearly deviated from circularity, as indicated by the circularity index (Fig. 3F). However, because circularity can also decrease in rod-shaped chromosomes, these datasets alone may not be sufficiently convincing, as the reviewer pointed out. We have now included an additional parameter, the aspect ratio, defined as the ratio of an object’s major axis to its minor axis (new Fig. 3F). While this intuitive parameter was altered upon condensin II depletion and double depletion, again, we acknowledge that it is not sufficient to convincingly distinguish between the elongated and cloud-like phenotypes proposed in the original manuscript. For these reasons, in the revised manuscript, we have toned down our statements regarding the differences in CT morphology between the two conditions. Nonetheless, together with the data from Figs. 1 and 2, it is that the Rabl configuration observed upon condensin II depletion is further exacerbated in the absence of cohesin. Accordingly, we have modified the main text and the cartoon (Fig 3H) to more accurately depict the observations summarized above.

Figure 5: How did they assign C, P and D3 for two chromosomes? The assignment seems obvious in some cases, but not in other cases (e.g. in the image of H2-AID#2 +IAA, two D3s can be connected to two Ps in the other way). They may have avoided line crossing between two C-P-D3 assignments, but can this be justified when the CT might be disorganized e.g. by condensin II depletion? This comment is well taken. As the reviewer suspected, we avoided line crossing between two sets of assignments. Whenever there was ambiguity, such images were excluded from the analysis. Because most chromosome territories derived from two homologous chromosomes are well separated even under the depleted conditions as shown in Fig. 6C, we did not encounter major difficulties in making assignments based on the criteria described above. We therefore remain confident that our conclusion is valid.

That said, we acknowledge that our assignments of the FISH images may not be entirely objective. We have added this point to the “Limitations of the study” section at the end of the Discussion.

Figure 6F: The mean is not indicated on the right-hand side graph, in contrast to other similar graphs. Is this an error? We apologize for having caused this confusion. First, we would like to clarify that the right panel of Fig. 6F should be interpreted together with the left panel, unlike the seemingly similar plots shown in Figs. 6G and 6H. In the left panel of Fig. 6F, the percentages of CTs that contact the nucleolus are shown in grey, whereas those that do not are shown in white. All CTs classified in the “non-contact” population (white) have a value of zero in the right panel, represented by the bars at 0 (i.e., each bar corresponds to a collection of dots having a zero value). In contrast, each CT in the “contact” population (grey) has a unique contact ratio value in the right panel. Because the right panel consists of two distinct groups, we reasoned that placing mean or median bars would not be appropriate. This was why no mean or median bars were shown in in the tight panel (The same is true for Fig. S5 A and B).

That said, for the reviewer’s reference, we have placed median bars in the right panel (see below). In the six cases of H2#2 (-/+IAA), Rad21#2 (-/+IAA), Double#2 (-IAA), and Double#3 (-IAA), the median bars are located at zero (note that in these cases the mean bars [black] completely overlap with the “bars” derived from the data points [blue and magenta]). In the two cases of Double#2 (+IAA) and Double#3 (+IAA), they are placed at values of ~0.15. Statistically significant differences between -IAA and +IAA are observed only in Double#2 and Double#3, as indicated by the P-value shown on the top of the panel. Thus, we are confident in our conclusion that CTs undergo severe deformation in the absence of both condensin II and cohesin.

Figure S1A: The two FACS profiles for Double-AID #3 Release-2 may be mixed up between -IAA and +IAA. The review is right. This inadvertent error has been corrected.

The method section explains that 'circularity' shows 'how closely the shape of an object approximates a perfect circle (with a value of 1 indicating a perfect circle), calculated from the segmented regions'. It would be helpful to provide further methodological details about it. We have added further explanations regarding the circularity in Materials and Methods together with a citation (two added sentences are underlined below):

To analyze the morphology of nuclei, CTs, and nucleoli, we measured “circularity,” a morphological index that quantifies how closely the shape of an object approximates a perfect circle (value =1). Circularity was defined as 4π x Area/Perimeter2, where both the area and perimeter of each segmented object were obtained using ImageJ. This index ranges from 0 to 1, with values closer to 1 representing more circular objects and lower values correspond to elongated or irregular shapes (Chen et al, 2017).

Chen, B., Y. Wang, S. Berretta and O. Ghita. 2017. Poly Aryl Ether Ketones (PAEKs) and carbon-reinforced PAEK powders for laser sintering. J Mater Sci 52:6004-6019.

Reviewer #1 (Significance (Required)):

Ono et al addressed how condensin II and cohesin work to define chromosome territories (CT) in human cells. They used FISH to assess the status of CT. They found that condensin II depletion leads to lengthwise elongation of G1 chromosomes, while double depletion of condensin II and cohesin leads to CT overlap and morphological defects. Although the requirement of condensin II in shortening G1 chromosomes was already shown by Hoencamp et al 2021, the cooperation between condensin II and cohesin in CT regulation is a new finding. They also demonstrated that cohesin and condensin II are involved in G2 chromosome regulation on a smaller and larger scale, respectively. Though such roles in cohesin might be predictable from its roles in organizing TADs, it is a new finding that the two work on a different scale on G2 chromosomes. Overall, this is technically solid work, which reports new findings about how condensin II and cohesin cooperate in organizing G1 and G2 chromosomes.

See our reply above.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Summary:

Ono et al use a variety of imaging and genetic (AID) depletion approaches to examine the roles of condensin II and cohesin in the reformation of interphase genome architecture in human HCT16 cells. Consistent with previous literature, they find that condensin II is required for CENP-A dispersion in late mitosis/early G1. Using in situ FISH at the centromere/q arm of chromosome 12 they then establish that condensin II removal causes lengthwise elongation of chromosomes that, interestingly, can be suppressed by cohesin removal. To better understand changes in whole-chromosome morphology, they then use whole chromosome painting to examine chromosomes 18 and 19. In the absence of condensin II, cells effectively fail to reorganise their chromosomes from rod-like structures into spherical chromosome territories (which may explain why CENP-A dispersion is suppressed). Cohesin is not required for spherical CT formation, suggesting condensin II is the major initial driver of interphase genome structure. Double depletion results in complete disorganisation of chromatin, leading the authors to conclude that a typical cell cycle requires orderly 'handover' from the mitotic to interphase genome organising machinery. The authors then move on to G2 phase, where they use a variety of different FISH probes to assess alterations in chromosome structure at different scales. They thereby establish that perturbation of cohesin or condensin II influences local and longer range chromosome structure, respectively. The effects of condensin II depletion become apparent at a genomic distance of 20 Mb, but are negligible either below or above. The authors repeat the G1 depletion experiment in G2 and now find that condensin II and cohesin are individually dispensable for CT organisation, but that dual depletion causes CT collapse. This rather implies that there is cooperation rather than handover per se. Overall this study is a broadly informative multiscale investigation of the roles of SMC complexes in organising the genome of postmitotic cells, and solidifies a potential relationship between condensin II and cohesin in coordinating interphase genome structure. The deeper investigation of the roles of condensin II in establishing chromosome territories and intermediate range chromosome structure in particular is a valuable and important contribution, especially given our incomplete understanding of what functions this complex performs during interphase.

We sincerely appreciate the reviewer’s supportive comments. The reviewer has correctly acknowledged both the current gaps in our understanding of the role of condensin II in interphase chromosome organization and our new findings on the collaborative roles of condensin II and cohesin in establishing and maintaining interphase chromosome territories.

Major comments:

In general the claims and conclusions of the manuscript are well supported by multiscale FISH labelling. An important absent control is western blotting to confirm protein depletion levels. Currently only fluorescence is used as a readout for the efficiency of the AID depletion, and we know from prior literature that even small residual quantities of SMC complexes are quite effective in organising chromatin. I would consider a western blot a fairly straightforward and important technical control.

Let me explain why we used immunofluorescence measurements to evaluate the efficiency of depletion. In our current protocol for synchronizing at the M-to-G1 transition, ~60% of control and H2-depleted cells, and ~30% of Rad21-depleted and co-depleted cells, are successfully synchronized in G1 phase. The apparently lower synchronization efficiency in the latter two groups is attributable to the well-documented mitotic delay caused by cohesin depletion. From these synchronized populations, early G1 cells were selected based on their characteristic morphologies (see the legend of Fig. 1C). In this way, we analyzed an early G1 cell population that had completed mitosis without chromosome segregation defects. We acknowledge that this represents a technically challenging aspect of M-to-G1 synchronization in HCT116 cells, whose synchronization efficiency is limited compared with that of HeLa cells. Nevertheless, this approach constitutes the most practical strategy currently available. Hence, immunofluorescence provides the only feasible means to evaluate depletion efficiency under these conditions.

Although immunoblotting can, in principle, be applied to G2-arrested cell populations, we do not believe that information obtained from such experiments would affect the main conclusions of the current study. Please note that we carefully designed and performed all experiments with appropriate controls: H2 depletion, RAD21 depletion, and double depletion, with outcomes confirmed using independent cell lines (Double-AID#2 and Double-AID#3) whenever deemed necessary.

We fully acknowledge the technical limitations associated with the AID-mediated depletion techniques, which are now described in the section entitled “Limitations of the study” at the end of the Discussion. Nevertheless, we emphasize that these limitations do not compromise the validity of our findings.

I find the point on handover as a mechanism for maintaining CT architecture somewhat ambiguous, because the authors find that the dependence simply switches from condensin II to both condensin II and cohesin, between G1 and G2. To me this implies augmented cooperation rather than handover. I have two further suggestions, both of which I would strongly recommend but would consider desirable but 'optional' according to review commons guidelines.

First of all, we would like to clarify a possible misunderstanding regarding the phrase “handover as a mechanism for maintaining CT architecture somewhat ambiguous”. In the original manuscript, we proposed handover as a mechanism for establishing G1 chromosome territories, not for maintaining CTs.

That said, we take this comment very seriously, especially because Reviewer #1 also expressed the same concern. Please see our reply to Reviewer #1 (Major point).

In brief, we agree with the reviewer that the word “handover” may not be appropriate to describe the functional relationship between condensin II and cohesin during the M-to-G1 transition. In the revised manuscript, we have avoided the use of the word “handover”, replacing it with “interplay”. It should be emphasized, however, that given their distinct chromosome-binding kinetics, the cooperation of the two SMC complexes during the M-to-G1 transition is qualitatively different from that observed in G2. Therefore, the central conclusion of the present study remains unchanged.

For example, a sentence in Abstract has been changed as follows:

a functional interplay between condensin II and cohesin during the mitosis-to-G1 transition is critical for establishing chromosome territories (CTs) in the newly assembling nucleus.

Firstly, the depletions are performed at different stages of the cell cycle but have different outcomes. The authors suggest this is because handover is already complete, but an alternative possibility is that the phenotype is masked by other changes in chromosome structure (e.g. duplication/catenation). I would be very curious to see, for example, how the outcome of this experiment would change if the authors were to repeat the depletions in the presence of a topoisomerase II inhibitor.

The reviewer’s suggestion here is somewhat vague, and it is unclear to us what rationale underlies the proposed experiment or what meaningful outcomes could be anticipated. Does the reviewer suggest that we perform topo II inhibitor experiments both during the M-to-G1 transition and in G2 phase, and then compare the outcomes between the two conditions?

For the M-to-G1 transition, Hildebrand et at (2024) have already reported such experiments. They used a topo II inhibitor to provided evidence that mitotic chromatids are self-entangled and that the removal of these mitotic entanglements is required to establish a normal interphase nucleus. Our own preliminary experiments (not presented in the current manuscript) showed that ICRF treatment of cells undergoing the M-to-G1 transition did not affect post-mitotic centromere dispersion. The same treatment also had little effect on the suppression of centromere dispersion observed in condensin II-depleted cells.

Under G2-arrested condition, because chromosome territories are largely individualized, we would expect topo II inhibition to affect only the extent of sister catenation, which is not the focus of our current study. We anticipate that inhibiting topo II in G2 would have only a marginal, if any, effect on the maintenance of chromosome territories detectable by our current FISH approaches.

In any case, we consider the suggested experiment to be beyond the scope of the present manuscript, which focuses on the collaborative roles of condensin II and cohesin as revealed by multi-scale FISH analyses.

Secondly, if the author's claim of handover is correct then one (not exclusive) possibility is that there is a relationship between condensin II and cohesin loading onto chromatin. There does seem to be a modest co-dependence (e.g. fig S4 and S7), could the authors comment on this?

First of all, we wish to point out the reviewer’s confusion between the G2 experiments and the M-to-G1 experiments. Figs. S4 and S7 concern experiments using G2-arrested cells, not M-to-G1 cells in which a possible handover mechanism is discussed. Based on Fig. 1, in which the extent of depletion in M-to-G1 cells was tested, no evidence of “co-dependence” between H2 depletion and RAD21 depletion was observed.

That said, as the reviewer correctly points out, we acknowledge the presence of marginal yet statistically significant reductions in the RAD21 signal upon H2 depletion (and vice versa) in G2-arrested cells (Figs. S4 and S7).

Another control experiment here would be to treat fully WT cells with IAA and test whether non-AID labelled H2 or RAD21 dip in intensity. If they do not, then perhaps there's a causal relationship between condensin II and cohesin levels?

According to the reviewer’s suggestion, we tested whether IAA treatment causes an unintentional decreases in the H2 or RAD21 signals in G2-arrested cells, and found that it is not the case (see the attached figure below).

Thus, these data indicate that there is a modest functional interdependence between condensin II and cohesin in G2-arrested cells. For instance, condensin II depletion may modestly destabilize chromatin-bound cohesin (and vice versa). However, we note that these effects are minor and do not affect the overall conclusions of the study. In the revised manuscript, we have described these potentially interesting observations briefly as a note in the corresponding figure legends (Fig. S4).

I recognise this is something considered in Brunner et al 2025 (JCB), but in their case they depleted SMC4 (so all condensins are lost or at least dismantled). Might bear further investigation.

Methods:

Data and methods are described in reasonable detail, and a decent number of replicates/statistical analyses have been. Documentation of the cell lines used could be improved. The actual cell line is not mentioned once in the manuscript. Although it is referenced, I'd recommend including the identity of the cell line (HCT116) in the main text when the cells are introduced and also in the relevant supplementary tables. Will make it easier for readers to contextualise the findings.

We apologize for the omission of important information regarding the parental cell line used in the current study. The information has been added to Materials and Methods as well as the resource table.

Minor comments:

Overall the manuscript is well-written and well presented. In the introduction it is suggested that no experiment has established a causal relationship between human condensin II and chromosome territories, but this is not correct, Hoencamp et al 2021 (cell) observed loss of CTs after condensin II depletion. Although that manuscript did not investigate it in as much detail as the present study, the fundamental relationship was previously established, so I would encourage the authors to revise this statement.

We are somewhat puzzled by this comment. In the original manuscript, we explicitly cited Hoencamp et al (2021) in support of the following sentences:

• *

(Lines 78-83 in the original manuscript)

*Moreover, high-throughput chromosome conformation capture (Hi-C) analysis revealed that, under such conditions, chromosomes retain a parallel arrangement of their arms, reminiscent of the so-called Rabl configuration (Hoencamp et al., 2021). These findings indicate that the loss or impairment of condensin II during mitosis results in defects in post-mitotic chromosome organization. *

• *

That said, to make the sentences even more precise, we have made the following revision in the manuscript.

• *

(Lines 78- 82 in the revised manuscript)

*Moreover, high-throughput chromosome conformation capture (Hi-C) analysis revealed that, under such conditions, chromosomes retain a parallel arrangement of their arms, reminiscent of the so-called Rabl configuration (Hoencamp et al., 2021). These findings,together with cytological analyses of centromere distributions, indicate that the loss or impairment of condensin II during mitosis results in defects in post-mitotic chromosome organization. *

• *

The following statement was intended to explain our current understanding of the maintenance of chromosome territories. Because Hoencamp et al (2021) did not address the maintenance of CTs, we have kept this sentence unchanged.

• *

(Lines 100-102 in the original manuscript)

Despite these findings, there is currently no evidence that either condensin II, cohesin, or their combined action contributes to the maintenance of CT morphology in mammalian interphase cells (Cremer et al., 2020).

• *

• *

Reviewer #2 (Significance (Required)):

General assessment:

Strengths: the multiscale investigation of genome architecture at different stages of interphase allow the authors to present convincing and well-analysed data that provide meaningful insight into local and global chromosome organisation across different scales.

Limitations:

As suggested in major comments.

Advance:

Although the role of condensin II in generating chromosome territories, and the roles of cohesin in interphase genome architecture are established, the interplay of the complexes and the stage specific roles of condensin II have not been investigated in human cells to the level presented here. This study provides meaningful new insight in particular into the role of condensin II in global genome organisation during interphase, which is much less well understood compared to its participation in mitosis.

Audience:

Will contribute meaningfully and be of interest to the general community of researchers investigating genome organisation and function at all stages of the cell cycle. Primary audience will be cell biologists, geneticists and structural biochemists. Importance of genome organisation in cell/organismal biology is such that within this grouping it will probably be of general interest.

My expertise is in genome organization by SMCs and chromosome segregation.

We appreciate the reviewer’s supportive comments. As the reviewer fully acknowledges, this study is the first systematic survey of the collaborative role of condensin II and cohesin in establishing and maintaining interphase chromosome territories. In particular, multi-scale FISH analyses have enabled us to clarify how the two SMC protein complexes contribute to the maintenance of G2 chromosome territories through their actions at different genomic scales. As the reviewer notes, we believe that the current study will appeal to a broad readership in cell and chromosome biology. The limitations of the current study mentioned by the reviewer are addressed in our reply above.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

Summary:

The manuscript “Condensin II collaborates with cohesin to establish and maintain interphase chromosome territories" investigates how condensin II and cohesin contribute to chromosome organization during the M-to-G1 transition and in G2 phase using published auxin-inducible degron (AID) cell lines which render the respective protein complexes nonfunctional after auxin addition. In this study, a novel degron cell line was established that enables the simultaneous depletion of both protein complexes, thereby facilitating the investigation of synergistic effects between the two SMC proteins. The chromosome architecture is studied using fluorescence in situ hybridization (FISH) and light microscopy. The authors reproduce a number of already published data and also show that double depletion causes during the M-to-G1 transition defects on chromosome territories, producing expanded, irregular shapes that obscure condensin II-specific phenotypes. Findings in G2 cells point to a new role of condensin II for chromosome conformation at a scale of ~20Mb. Although individual depletion has minimal effects on large-scale CT morphology in G2, combined loss of both complexes produces marked structural abnormalities, including irregular crescent-shaped CTs displaced toward the nucleolus and increased nucleolus-CT contact. The authors propose that condensin II and cohesin act sequentially and complementarily to ensure proper post-mitotic CT formation and maintain chromosome architecture across genomic scales.

We greatly appreciate the reviewer’s supportive comments. The reviewer has accurately recognized our new findings concerning the collaborative roles of condensin II and cohesin in the establishment and maintenance of interphase chromosome territories.

Concenrs about statistics:

• The authors provide the information on how many cells are analyzed but not the number of independent experiments. My concern is that there might variations in synchronization of the cell population and in the subsequent preparation (FISH) affecting the final result. We appreciate the reviewer’s important comment regarding the biological reproducibility of our experiments. As the reviewer correctly points out, variations in cell-cycle synchronization and FISH sample preparation can occur across experiments. To address this concern, we repeated the key experiments supporting our main conclusions (Figs. 3 and 6) two additional times, resulting in three independent biological replicas in total. All replicate experiments reproduced the major observations from the original analyses. These results further substantiated our original conclusion, despite the inevitable variability arising from cell synchronization or sample preparation in this type of experiments. In the revised manuscript, we have now explicitly indicated the number of biological replicates in the corresponding figures.

The analyses of chromosome-arm conformation shown in Fig. 5 were already performed in three independent rounds of experiments, as noted in the original submission. In addition, similar results were already obtained in other analyses reported in the manuscript. For example, centromere dispersion was quantified using an alternative centromere detection method (related to Fig. 1), and distances between specific chromosomal sites were measured using different locus-specific probes (related to Figs. 2 and 4). In both cases, the results were consistent with those presented in the manuscript.

• Statistically the authors analyze the effect of cells with induced degron vs. vehicle control (non-induced). However, the biologically relevant question is whether the data differ between cell lines when the degron system is induced. This is not tested here (cf. major concern 2 and 3). See our reply to major concerns 2 and 3.

• Some Journal ask for blinded analysis of the data which might make sense here as manual steps are involved in the data analysis (e.g. line 626 / 627the convex hull of the signals was manually delineated, line 635 / 636 Chromosome segmentation in FISH images was performed using individual thresholding). However personally I have no doubts on the correctness of the work. We thank the reviewer for pointing out that some steps in our data analysis were performed manually, such as delineating the convex hull of signals and segmenting chromosomes in FISH and IF images using individual thresholds. These manual steps were necessary because signal intensities vary among cells and chromosomes, making fully automated segmentation unreliable. To ensure objectivity, we confirmed that the results were consistent across two independently established double-depletion cell lines, which produced essentially identical findings. In addition, we repeated the key experiments underpinning our main conclusions (Figs. 3 and 6) two additional times, and the results were fully consistent with the original analyses. Therefore, we are confident that our current data analysis approach does not compromise the validity of our conclusions. Finally, we appreciate the reviewer’s kind remark that there is no doubt regarding the correctness of our work.

Major concerns:

• Degron induction appears to delay in Rad21-AID#1 and Double-AID#1 cells the transition from M to G1, as shown in Fig. S1. After auxin treatment, more cells exhibit a G2 phenotype than in an untreated population. What are the implications of this for the interpretation of the experiments? In our protocol shown in Fig. 1C, cells were released into mitosis after G2 arrest, and IAA was added 30 min after release. It is well established that cohesin depletion causes a prometaphase delay due to spindle checkpoint activation (e.g., Vass et al, 2003, Curr Biol; Toyoda and Yanagida, 2006, MBoC; Peters et al, 2008, Genes Dev), which explains why cells with 4C DNA content accumulated, as judged by FACS (Fig. S1). The same was true for doubly depleted cells. However, a fraction of cells that escaped this delay progressed through mitosis and enter the G1 phase of the next cell cycle. We selected these early G1 cells and used them for down-stream analyses. This experimental procedure was explicitly described in the legends of Fig. 1C and Fig. S1A as follows:

(Lines 934-937; Legend of Fig. 1C)

From the synchronized populations, early G1cells were selected based on their characteristic morphologies (i.e., pairs of small post-mitotic cells) and subjected to downstream analyses. Based on the measured nuclear sizes (Fig. S2 G), we confirmed that early G1 cells were appropriately selected.

(Lines 1114-1119; Legend of Fig. S1A)

In this protocol, ~60% of control and H2-depleted cells, and ~30% of Rad21-depleted and co-depleted cells, were successfully synchronized in G1 phase. The apparently lower synchronization efficiency in the latter two groups is attributable to the well documented mitotic delay caused by cohesin depletion (Hauf et al., 2005; Haarhuis et al., 2013; Perea-Resa et al., 2020). From these synchronized populations, early G1 cells were selected based on their characteristic morphologies (see the legend of Fig. 1 C).

• *

Thus, using this protocol, we analyzed an early G1 cell population that had completed mitosis without chromosome segregation defects. We acknowledge that this represents a technically challenging aspect of synchronizing cell-cycle progression from M to G1 in HCT116 cells, whose synchronization efficiency is limited compared with that of HeLa cells. Nevertheless, this approach constitutes the most practical strategy currently available.

• Line 178 "In contrast, cohesin depletion had a smaller effect on the distance between the two site-specific probes compared to condensin II depletion (Fig. 2, C and E)." The data in Fig. 2 E show both a significant effect of H2 and a significant effect of RAD21 depletion. Whether the absolute difference in effect size between the two conditions is truly relevant is difficult to determine, as the distribution of the respective control groups also appears to be different. This comment is well taken. Reviewer #1 has made a comment on the same issue. See our reply to Reviewer #1 (Other points, Figure 2E).

In brief, in the current study, we should focus on the differences between -IAA and +IAA within each cell line, rather than comparing the -IAA conditions across different cell lines. In this sense, a sentence in the original manuscript (lines 178-180) was misleading. In the revised manuscript, we have modified the corresponding and subsequent sentence as follows:

Although cohesin depletion had a marginal effect on the distance between the two site-specific probes (Fig.2, C and E), double depletion did not result in a significant change (Fig.2, D and E), consistent with the partial restoration of centromere dispersion (Fig. 1G).

• In Figures 3, S3 and related text in the manuscript I cannot follow the authors' argumentation, as H2 depletion alone leads to a significant increase in the CT area (Chr. 18, Chr. 19, Chr. 15). Similar to Fig. 2, the authors argue about the different magnitude of the effect (H2 depletion vs double depletion). Here, too, appropriate statistical tests or more suitable parameters describing the effect should be used. I also cannot fully follow the argumentation regarding chromosome elongation, as double depletion in Chr. 18 and Chr. 19 also leads to a significantly reduced circularity. Therefore, the schematic drawing Fig. 3 H (double depletion) seems very suggestive to me. This comment is related to the comment above (Major comment #2). See our reply to Reviewer #1 (Other points, Figure 2E).

It should be noted that, in Figure 3 (unlike in Figure 2), we did not compare the different magnitudes of the effect observed between H2 depletion and double depletion. Thus, the reviewer’s comment that “Similar to Fig. 2, the authors argue about the different magnitude of the effect (H2 depletion vs double depletion) ” does not accurately reflected our description.

Moreover, while the distance between two specific loci (Fig. 2E) and CT circularity (Fig. 3G) are intuitively related, they represent distinct parameters. Thus, it is not unexpected that double depletion resulted in apparently different outcomes for the two measurements. Thus, the reviewer’s counter-argument is not strictly applicable here.

That said, we agree with the reviewer that our descriptions here need to be clarified.

The differences between H2 depletion and double depletion are two-fold: (1) centromere dispersion is suppressed upon H2 depletion, but not upon double depletion (Fig 1G); (2) the distance between Cen 12 and 12q15 increased upon H2 depletion, but not upon double depletion (Fig 2E).

We have decided to remove the “homologous pair overlap” panel (formerly Fig. 3E) from the revised manuscript. Accordingly, the corresponding sentence has been deleted from the main text. Instead, we have added a new panel of “aspect ratio”, defined as the ratio of the major to the minor axis (new Fig. 3F). While this intuitive parameter was altered upon condensin II depletion and double depletion, again, we acknowledge that it is not sufficient to convincingly distinguish between the elongated and cloud-like phenotypes proposed in the original manuscript. For these reasons, in the revised manuscript, we have toned down our statements regarding the differences in CT morphology between the two conditions. Nonetheless, together with the data from Figs. 1 and 2, it is clear that the Rabl configuration observed upon condensin II depletion is further exacerbated in the absence of cohesin. Accordingly, we have modified the main text and the cartoon (Fig 3H) to more accurately depict the observations summarized above.

• 5 and accompanying text. I agree with the authors that this is a significant and very interesting effect. However, I believe the sharp bends is in most cases an artifact caused by the maximum intensity projection. I tried to illustrate this effect in two photographs: Reviewer Fig. 1, side view, and Reviewer Fig. 2, same situation top view (https://cloud.bio.lmu.de/index.php/s/77npeEK84towzJZ). As I said, in my opinion, there is a significant and important effect; the authors should simply adjust the description. This comment is well taken. We appreciate the reviewer’s effort to help clarify our original observations. We have therefore added a new section entitled “Limitations of the study” to explicitly describe the constrains of our current approach. That said, as the reviewer also acknowledges, our observations remain valid because all experiments were performed with appropriate controls.

Minor concerns:

• I would like to suggest proactively discussing possible artifacts that may arise from the harsh conditions during FISH sample preparation. We fully agree with the reviewer’s concerns. For FISH sample preparation, we used relatively harsh conditions, including (1) fixation under a hypotonic condition (0.3x PBS), (2) HCl treatment, and (3) a denaturation step. We recognize that these procedures inevitably affect the preservation of the original structure; however, they are unavoidable in the standard FISH protocol. We also acknowledge that our analyses were limited to 2D structures based on projected images, rather than full 3D reconstructions. These technical limitations are now explicitly described in a new section entitled “Limitations of the study”, and the technical details are provided in Materials and Methods.

• It would be helpful if the authors could provide the original data (microscopic image stacks) for download. We thank the reviewer for this suggestion and understand that providing the original image stacks could be of interest to readers. We agree that if the nuclei were perfectly spherical, as is the case for example in lymphocytes, 3D image stacks would contain much more information than 2D projections. However, as is typical for adherent cultured cells, including the HCT116-derived cells used in this study, the nuclei are flattened due to cell adhesion to the culture dish, with a thickness of only about one-tenth of the nuclear diameter (10–20 μm). Considering also the inevitable loss of structural preservation during FISH sample preparation, we were concerned that presenting 3D images might confuse rather than clarify. We therefore believe that representing the data as 2D projections, while explicitly acknowledging the technical limitations, provides the clearest and most interpretable presentation of our results. These limitations are now described in a new section of the manuscript.

• The authors use a blind deconvolution algorithm to improve image quality. It might be helpful to test other methods for this purpose (optional). We thank the reviewer for this valuable suggestion and fully agree that it is a valid point. We recognize that alternative image enhancement methods can offer advantages, particularly for smaller structures or when multiple probes are analyzed simultaneously. In our study, however, the focus was on detecting whole chromosome territories (CTs) and specific chromosomal loci, which can be visualized clearly with our current FISH protocol combined with blind deconvolution. We therefore believe that the image quality we obtained is sufficient to support the conclusions of this manuscript.

Reviewer #3 (Significance (Required)):

Advance:

Ono et al. addresses the important question on how the complex pattern of chromatin is reestablished after mitosis and maintained during interphase. In addition to affinity interactions (1,2), it is known that cohesin plays an important role in the formation and maintenance of chromosome organization interphase (3). However, current knowledge does not explain all known phenomena. Even with complete loss of cohesin, TAD-like structures can be recognized at the single-cell level (4), and higher structures such as chromosome territories are also retained (5). The function of condensin II during mitosis is another important factor that affects chromosome architecture in the following G1 phase (6). Although condensin II is present in the cell nucleus throughout interphase, very little is known about the role of this protein in this phase of the cell cycle. This is where the present publication comes in, with a new double degron cell line in which essential subunits of cohesin AND condensin can be degraded in a targeted manner. I find the data from the experiments in the G2 phase most interesting, as they suggest a previously unknown involvement of condensin II in the maintenance of larger chromatin structures such as chromosome territories.

The experiments regarding the M-G1 transition are less interesting to me, as it is known that condensin II deficiency in mitosis leads to elongated chromosomes (Rabl configuration)(6), and therefore the double degradation of condensin II and cohesin describes the effects of cohesin on an artificially disturbed chromosome structure.

For further clarification, we provide below a table summarizing previous studies relevant to the present work. We wish to emphasize three novel aspects of the present study. First, newly established cell lines designed for double depletion enabled us to address questions that had remained inaccessible in earlier studies. Second, to our knowledge, no study has previously reported condensin II depletion, cohesin depletion and double depletion in G2-arrested cells. Third, the present study represents the first systematic comparison of two different stages of the cell cycle using multiscale FISH under distinct depletion conditions. Although the M-to-G1 part of the present study partially overlaps with previous work, it serves as an important prelude to the subsequent investigations. We are confident that the reviewer will also acknowledge this point.

cell cycle

cond II depletion

cohesin depletion

double depletion

M-to-G1

Hoencamp et al (2021); Abramo et al (2019); Brunner et al (2025);

this study

Schwarzer et al (2017);

Wutz et al (2017);

this study

this study

G2

this study

this study

this study

Hoencamp et al (2021): Hi-C and imaging (CENP-A distribution)

Abramo et al (2019): Hi-C and imaging

Brunner et al (2025): mostly imaging (chromatin tracing)

Schwarzer et al (2017); Wutz et al (2017): Hi-C

this study: imaging (multi-scale FISH)

General limitations:

(1) Single cell imaging of chromatin structure typically shows only minor effects which are often obscured by the high (biological) variability. This holds also true for the current manuscript (cf. major concern 2 and 3).

See our reply above.

(2) A common concern are artefacts introduced by the harsh conditions of conventional FISH protocols (7). The authors use a method in which the cells are completely dehydrated, which probably leads to shrinking artifacts. However, differences between samples stained using the same FISH protocol are most likely due to experimental variation and not an artefact (cf. minor concern 1).

See our reply above.

• The anisotropic optical resolution (x-, y- vs. z-) of widefield microscopy (and most other light microscopic techniques) might lead to misinterpretation of the imaged 3D structures. This seems to be the cases in the current study (cf. major concern 4). See our reply above.

• In the present study, the cell cycle was synchronized. This requires the use of inhibitors such as the CDK1 inhibitor RO-3306. However, CDK1 has many very different functions (8), so unexpected effects on the experiments cannot be ruled out. The current approaches involving FISH inevitably require cell cycle synchronization. We believe that the use of the CDK1 inhibitor RO-3306 to arrest the cell cycle at G2 is a reasonable choice, although we cannot rule out unexpected effects arising from the use of the drug. This issue has now been addressed in the new section entitled “Limitations of the study”.

Audience:

The spatial arrangement of genomic elements in the nucleus and their (temporal) dynamics are of high general relevance, as they are important for answering fundamental questions, for example, in epigenetics or tumor biology (9,10). The manuscript from Ono et al. addresses specific questions, so its intended readership is more likely to be specialists in the field.

We are confident that, given the increasing interest in the 3D genome and its role in regulating diverse biological functions, the current manuscript will attract the broad readership of leading journals in cell biology.

About the reviewer:

By training I'm a biologist with strong background in fluorescence microscopy and fluorescence in situ hybridization. In recent years, I have been involved in research on the 3D organization of the cell nucleus, chromatin organization, and promoter-enhancer interactions.

We greatly appreciate the reviewer’s constructive comments on both the technical strengths and limitations of our fluorescence imaging approaches, which have been very helpful in revising the manuscript. As mentioned above, we have decided to add a special paragraph entitled “Limitations of the study” at the end of the Discussion section to discuss these issues.

All questions regarding the statistics of angularly distributed data are beyond my expertise. The authors do not correct their statistical analyses for "multiple testing". Whether this is necessary, I cannot judge.

We thank the reviewer for raising this important point. In our study, the primary comparisons were made between -IAA and +IAA conditions within the same cell line. Accordingly, the figures report P-values for these pairwise comparisons.

For the distance measurements, statistical evaluations were performed in PRISM using ANOVA (Kruskal–Wallis test), and the P-values shown in the figures are based on these analyses (Fig. 1, G and H; Fig. 2 E; Fig. 3 F and G; Fig. 4 F; Fig. 6 F [right]–H; Fig. S2 B and G; Fig. S3 D and H; Fig. S5 A [right] and B [right]; Fig. S8 B). While the manuscript focuses on pairwise comparisons between -IAA and +IAA conditions within the same cell line, we also considered potential differences across cell lines as part of the same ANOVA framework, thereby ensuring that multiple testing was properly addressed. Because cell line differences are not the focus of the present study, the corresponding results are not shown.

For the angular distribution analyses, we compared -IAA and +IAA conditions within the same cell line using the Mardia–Watson–Wheeler test; these analyses do not involve multiple testing (circular scatter plots; Fig. 5 C–E and Fig. S6 B, C, and E–H). In addition, to determine whether angular distributions exhibited directional bias under each condition, we applied the Rayleigh test to each dataset individually (Fig. 5 F and Fig. S6 I). As these tests were performed on a single condition, they are also not subject to the problem of multiple testing. Collectively, we consider that the statistical analyses presented in our manuscript appropriately account for potential multiple testing issues, and we remain confident in the robustness of the results.

Literature

Falk, M., Feodorova, Y., Naumova, N., Imakaev, M., Lajoie, B.R., Leonhardt, H., Joffe, B., Dekker, J., Fudenberg, G., Solovei, I. et al. (2019) Heterochromatin drives compartmentalization of inverted and conventional nuclei. Nature, 570, 395-399. Mirny, L.A., Imakaev, M. and Abdennur, N. (2019) Two major mechanisms of chromosome organization. Curr Opin Cell Biol, 58, 142-152. Rao, S.S.P., Huang, S.C., Glenn St Hilaire, B., Engreitz, J.M., Perez, E.M., Kieffer-Kwon, K.R., Sanborn, A.L., Johnstone, S.E., Bascom, G.D., Bochkov, I.D. et al. (2017) Cohesin Loss Eliminates All Loop Domains. Cell, 171, 305-320 e324. Bintu, B., Mateo, L.J., Su, J.H., Sinnott-Armstrong, N.A., Parker, M., Kinrot, S., Yamaya, K., Boettiger, A.N. and Zhuang, X. (2018) Super-resolution chromatin tracing reveals domains and cooperative interactions in single cells. Science, 362. Cremer, M., Brandstetter, K., Maiser, A., Rao, S.S.P., Schmid, V.J., Guirao-Ortiz, M., Mitra, N., Mamberti, S., Klein, K.N., Gilbert, D.M. et al. (2020) Cohesin depleted cells rebuild functional nuclear compartments after endomitosis. Nat Commun, 11, 6146. Hoencamp, C., Dudchenko, O., Elbatsh, A.M.O., Brahmachari, S., Raaijmakers, J.A., van Schaik, T., Sedeno Cacciatore, A., Contessoto, V.G., van Heesbeen, R., van den Broek, B. et al. (2021) 3D genomics across the tree of life reveals condensin II as a determinant of architecture type. Science, 372, 984-989. Beckwith, K.S., Ødegård-Fougner, Ø., Morero, N.R., Barton, C., Schueder, F., Tang, W., Alexander, S., Peters, J.-M., Jungmann, R., Birney, E. et al. (2023) Nanoscale 3D DNA tracing in single human cells visualizes loop extrusion directly in situ. BioRxiv 8 of 9https://doi.org/10.1101/2021.04.12.439407. Massacci, G., Perfetto, L. and Sacco, F. (2023) The Cyclin-dependent kinase 1: more than a cell cycle regulator. Br J Cancer, 129, 1707-1716. Bonev, B. and Cavalli, G. (2016) Organization and function of the 3D genome. Nat Rev Genet, 17, 661-678. Dekker, J., Belmont, A.S., Guttman, M., Leshyk, V.O., Lis, J.T., Lomvardas, S., Mirny, L.A., O'Shea, C.C., Park, P.J., Ren, B. et al. (2017) The 4D nucleome project. Nature, 549, 219-226.

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Reply to the reviewers

We will provide the revised manuscript as a PDF with highlighted changes, the Word file with tracked changes linked to reviewer comments, and all updated figures.

To address the reviewers' suggestions, we have conducted additional experiments that are now incorporated into new figures, or we have added new images to several existing figures where appropriate.

Please note that all figures have been renumbered to improve clarity and facilitate cross-referencing throughout the text. As recommended by Referee #3, all figure legends have been thoroughly revised to reflect these updates and are now labeled following the standard A-Z panel format, enhancing readability and ensuring easier identification. In addition, all figure legends now include the sample size for each statistical analysis.

For clarity and ease of reference, we provide below a comprehensive list of all figures included in the revised version. Figures that have undergone modifications are underlined.

Figure 1____. The first spermatogenesis wave in prepuberal mice.

This figure now includes amplified images of representative spermatocytes and a summary schematic illustrating the timeline of spermatogenesis. In addition, it now presents the statistical analysis of spermatocyte quantification to support the visual data.

__Figure 2.____ Cilia emerge across all stages of prophase I in spermatocytes during the first spermatogenesis wave. __

The images of this figure remain unchanged from the original submission, but all the graphs present now the statistical analysis of spermatocyte quantification.

Figure 3. Ultrastructure and markers of prepuberal meiotic cilia.

This figure remains unchanged from the original submission; however, we have replaced the ARL3-labelled spermatocyte image (A) with one displaying a clearer and more representative signal.

__Figure 4. Testicular tissue presents spermatocyte cysts in prepuberal mice and adult humans. __

This figure remains unchanged from the original submission.

__Figure 5. Cilia and flagella dynamics are correlated during prepuberal meiosis. __

This figure remains unchanged from the original submission.

__Figure 6. Comparative proteomics identifies potential regulators of ciliogenesis and flagellogenesis. __

This figure remains unchanged from the original submission.

Figure 7.____ Deciliation induces persistence of DNA damage in meiosis.

This figure has been substantially revised and now includes additional experiments analyzing chloral hydrate treatment, aimed at more accurately assessing DNA damage under both control and treated conditions. Images F-I and graph J are new.

Figure 8____. Aurora kinase A is a regulator of cilia disassembly in meiosis.

This figure is remodelled as the original version contained a mistake in previous panel II, for this, graph in new Fig.8 I has been corrected. In addition, it now contains additional data of αTubulin staining in arrested ciliated metaphases I after AURKA inhibition (new panel L1´).

__Figure 9. Schematic representation of the prepuberal versus adult seminiferous epithelium. __

This figure remains unchanged from the original submission.

__Supplementary Figure 1. Meiotic stages during the first meiotic wave. __

This figure remains unchanged from the original submission.

__Supplementary Figure 2 (new)____. __

This is a new figure that includes additional data requested by the reviewers. It includes additional markers of cilia in spermatocytes (glutamylated Tubulin/GT335), and the control data of cilia markers in non-ciliated spermatocytes. It also includes now the separated quantification of ciliated spermatocytes for each stage, as requested by reviewers, complementing graphs included in Figure 2.

Please note that with the inclusion of this new Supplementary Figure 2, the numbering of subsequent supplementary figures has been updated accordingly.

Supplementary Figure 3 (previously Suppl. Fig. 2)__. Ultrastructure of prophase I spermatocytes. __

This figure is equal in content to the original submission, but some annotations have been included.

Supplementary Figure 4 (previously Suppl. Fig. 3).__ Meiotic centrosome under the electron microscope. __

This figure remains unchanged from the original submission, but additional annotations have been included.

Supplementary Figure 5 (previously Suppl. Fig. 4)__. Human testis contains ciliated spermatocytes. __

This figure has been revised and now includes additional H2AX staining to better determine the stage of ciliated spermatocytes and improve their identification.

Supplementary Figure 6 (previously Suppl. Fig. 5). GLI1 and GLI3 readouts of Hedgehog signalling are not visibly affected in prepuberal mouse testes.

This figure has been remodeled and now includes the quantification of GLI1 and GLI3 and its corresponding statistical analysis. It also includes the control data for Tubulin, instead of GADPH.

Supplementary Figure 7 (previously Suppl. Fig. 6)__. CH and MLN8237 optimization protocol. __

This figure has been remodeled to incorporate control experiments using 1-hour organotypic culture treatment.

Supplementary Figure 8 (previously Suppl. Fig. 7)__. Tracking first meiosis wave with EdU pulse injection during prepubertal meiosis. __This figure remains unchanged from the original submission.

Supplementary Figure 9 (previously Suppl. Fig. 8)__. PLK1 and AURKA inhibition in cultured spermatocytes. __

This figure has been remodeled and now includes additional data on spindle detection in control and AURKA-inhibited spermatocytes (both ciliated and non ciliated).

__Response to the reviewers __

We will submit both the PDF version of the revised manuscript and the Word file with tracked changes relative to the original submission. Each modification made in response to reviewers' suggestions is annotated in the Word document within the corresponding section of the text.

A detailed, point-by-point response to each reviewer's comments is provided in the following section.

Response to the Referee #1

In this manuscript by Perez-Moreno et al., titled "The dynamics of ciliogenesis in prepubertal mouse meiosis reveal new clues about testicular maturation during puberty", the authors characterize the development of primary cilia during meiosis in juvenile male mice. The authors catalog a variety of testicular changes that occur as juvenile mice age, such as changes in testis weight and germ cell-type composition. They next show that meiotic prophase cells initially lack cilia, and ciliated meiotic prophase cells are detected after 20 days postpartum, coinciding with the time when post-meiotic spermatids within the developing testes acquire flagella. They describe that germ cells in juvenile mice harbor cilia at all substages of meiotic prophase, in contrast to adults where only zygotene stage meiotic cells harbor cilia. The authors also document that cilia in juvenile mice are longer than those in adults. They characterize cilia composition and structure by immunofluorescence and EM, highlighting that cilia polymerization may initially begin inside the cell, followed by extension beyond the cell membrane. Additionally, they demonstrate ciliated cells can be detected in adult human testes. The authors next perform proteomic analyses of whole testes from juvenile mice at multiple ages, which may not provide direct information about the extremely small numbers of ciliated meiotic cells in the testis, and is lacking follow up experiments, but does serve as a valuable resource for the community. Finally, the authors use a seminiferous tubule culturing system to show that chemical inhibition of Aurora kinase A likely inhibits cilia depolymerization upon meiotic prophase I exit and leads to an accumulation of metaphase-like cells harboring cilia. They also assess meiotic recombination progression using their culturing system, but this is less convincing.

Author response: We sincerely thank Ref #1 for the thorough and thoughtful evaluation of our manuscript. We are particularly grateful for the reviewer's careful reading and constructive feedback, which have helped us refine several sections of the text and strengthen our discussion. All comments and suggestions have been carefully considered and addressed, as detailed below.

__Major comments: __

1. There are a few issues with the experimental set up for assessing the effects of cilia depolymerization on DNA repair (Figure 7-II). First, how were mid pachytene cells identified and differentiated from early pachytene cells (which would have higher levels of gH2AX) in this experiment? I suggest either using H1t staining (to differentiate early/mid vs late pachytene) or the extent of sex chromosome synapsis. This would ensure that the authors are comparing similarly staged cells in control and treated samples. Second, what were the gH2AX levels at the starting point of this experiment? A more convincing set up would be if the authors measure gH2AX immediately after culturing in early and late cells (early would have higher gH2AX, late would have lower gH2AX), and then again after 24hrs in late cells (upon repair disruption the sampled late cells would have high gH2AX). This would allow them to compare the decline in gH2AX (i.e., repair progression) in control vs treated samples. Also, it would be informative to know the starting gH2AX levels in ciliated vs non-ciliated cells as they may vary.

Response:

We thank Ref #1 for this valuable comment, which significantly contributed to improving both the design and interpretation of the cilia depolymerization assay.

Following this suggestion, we repeated the experiment including 1-hour (immediately after culturing), and 24-hour cultures for both control and chloral hydrate (CH)-treated samples (n = 3 biological replicates). To ensure accurate staging, we now employ triple immunolabelling for γH2AX, SYCP3, and H1T, allowing clear distinction of zygotene (H1T−), early pachytene (H1T−), and late pachytene (H1T+) cells. The revised data (Figure 7) now provide a more complete and statistically robust analysis of DNA damage dynamics. These results confirm that CH-induced deciliation leads to persistence of the γH2AX signal at 24 hours, indicating impaired DNA repair progression in pachytene spermatocytes. The new images and graphs are included in the revised Figure 7.

Regarding the reviewer's final point about the comparison of γH2AX levels between ciliated and non-ciliated cells, we regret that direct comparison of γH2AX levels between ciliated and non-ciliated cells is not technically feasible. To preserve cilia integrity, all cilia-related imaging is performed using the squash technique, which maintains the three-dimensional structure of the cilia but does not allow reliable quantification of DNA damage markers due to nuclear distortion. Conversely, the nuclear spreading technique, used for DNA damage assessment, provides optimal visualization of repair foci but results in the loss of cilia due to cytoplasmic disruption during the hypotonic step. Given that spermatocytes in juvenile testes form developmentally synchronized cytoplasmic cysts, we consider that analyzing a statistically representative number of spermatocytes offers a valid and biologically meaningful measure of tissue-level effects.

In conclusion, we believe that the additional experiments and clarifications included in revised Figure 7 strengthen our conclusion that cilia depolymerization compromises DNA repair during meiosis. Further functional confirmation will be pursued in future works, since we are currently generating a conditional genetic model for a ciliopathy in our laboratory.

The authors analyze meiotic progression in cells cultured with/without AURKA inhibition in Figure 8-III and conclude that the distribution of prophase I cells does not change upon treatment. Is Figure 8-III A and B the same data? The legend text is incorrect, so it's hard to follow. Figure 8-III A shows a depletion of EdU-labelled pachytene cells upon treatment. Moreover, the conclusion that a higher proportion of ciliated zygotene cells upon treatment (Figure 8-II C) suggests that AURKA inhibition delays cilia depolymerization (page 13 line 444) does not make sense to me.

Response:

We thank Ref#1 for identifying this issue and for the careful examination of Figure 8. We discovered that the submitted version of Figure 8 contained a mismatch between the figure legend and the figure panels. The legend text was correct; however, the figure inadvertently included a non-corresponding graph (previously panel II-A), which actually belonged to Supplementary Figure 7 in the original submission. We apologize for this mistake.

This error has been corrected in the revised version. The updated Figure 8 now accurately presents the distribution of EdU-labelled spermatocytes across prophase I substages in control and AURKA-inhibited cultures (previously Figure 8-II B, now Figure 8-A). The corrected data show no significant differences in the proportions of EdU-labelled spermatocytes among prophase I substages after 24 hours of AURKA inhibition, confirming that meiotic progression is not delayed and that no accumulation of zygotene cells occurs under this treatment. Therefore, the observed increase in ciliated zygotene spermatocytes upon AURKA inhibition (new Figure 8 H-I) is best explained by a delay in cilia disassembly, rather than by an arrest or slowdown in meiotic progression. The figure legend and main text have been revised accordingly.

How do the authors know that there is a monopolar spindle in Figure 8-IV treated samples? Perhaps the authors can use a different Tubulin antibody (that does not detect only acetylated Tubulin) to show that there is a monopolar spindle.

Response:

We appreciate Ref#1 for this excellent suggestion. In the original submission (lines 446-447), we described that ciliated metaphase I spermatocytes in AURKA-inhibited samples exhibited monopolar spindle phenotypes. This description was based on previous reports showing that AURKA or PLK1 inhibition produces metaphases with monopolar spindles characterized by aberrant yet characteristic SYCP3 patterns, abnormal chromatin compaction, and circular bivalent alignment around non-migrated centrosomes (1). In our study, we observed SYCP3 staining consistent with these characteristic features of monopolar metaphases I.

However, we agree with Ref #1 that this could be better sustained with data. Following the reviewer's suggestion, we performed additional immunostaining using α-Tubulin, which labels total microtubules rather than only the acetylated fraction. For clarity purposes, the revised Figure 8 now includes α-Tubulin staining in the same ciliated metaphase I cells shown in the original submission, confirming the presence of defective microtubule polymerization and defective spindle organization. For clarity, we now refer to these ciliated metaphases I as "arrested MI". This new data further support our conclusion that AURKA inhibition disrupts spindle bipolarization and prevents cilia depolymerization, indicating that cilia maintenance and bipolar spindle organization are mechanistically incompatible events during male meiosis. The abstract, results, and discussion section has been expanded accordingly, emphasizing that the persistence of cilia may interfere with microtubule polymerization and centrosome separation under AURKA inhibition. The Discussion has been expanded to emphasize that persistence of cilia may interfere with centrosome separation and microtubule polymerization, contrasting with invertebrate systems -e.g. Drosophila (2) and P. brassicae (3)- in which meiotic cilia persist through metaphase I without impairing bipolar spindle assembly.

1. Alfaro, et al. EMBO Rep 22, (2021). DOI: 15252/embr.202051030 (PMID: 33615693)
2. Riparbelli et al . Dev Cell (2012) DOI: 1016/j.devcel.2012.05.024 (PMID: 22898783)
3. Gottardo et al, Cytoskeleton (Hoboken) (2023) DOI: 1002/cm.21755 (PMID: 37036073)

The authors state in the abstract that they provide evidence suggesting that centrosome migration and cilia depolymerization are mutually exclusive events during meiosis. This is not convincing with the data present in the current manuscript. I suggest amending this statement in the abstract.

Response:

We thank Ref#1 for this valuable observation, with which we fully agree. To avoid overstatement, the original statement has been removed from the Abstract, Results, and Discussion, and replaced with a more accurate formulation indicating that cilia maintenance and bipolar spindle formation are mutually exclusive events during mouse meiosis.

This revised statement is now directly supported by the new data presented in Figure 8, which demonstrate that AURKA inhibition prevents both spindle bipolarization and cilia depolymerization. We are grateful to the reviewer for highlighting this important clarification.

Minor comments:

The presence of cilia in all stages of meiotic prophase I in juvenile mice is intriguing. Why is the cellular distribution and length of cilia different in prepubertal mice compared to adults (where shorter cilia are present only in zygotene cells)? What is the relevance of these developmental differences? Do cilia serve prophase I functions in juvenile mice (in leptotene, pachytene etc.) that are perhaps absent in adults?

Related to the above point, what is the relevance of the absence of cilia during the first meiotic wave? If cilia serve a critical function during prophase I (for instance, facilitating DSB repair), does the lack of cilia during the first wave imply differing cilia (and repair) requirements during the first vs latter spermatogenesis waves?

In my opinion, these would be interesting points to discuss in the discussion section.

Response:

We thank the reviewer for these thoughtful observations, which we agree are indeed intriguing.

We believe that our findings likely reflect a developmental role for primary cilia during testicular maturation. We hypothesize that primary cilia at this stage might act as signaling organelles, receiving cues from Sertoli cells or neighboring spermatocytes and transmitting them through the cytoplasmic cysts shared by spermatocytes. Such intercellular communication could be essential for coordinating tissue maturation and meiotic entry during puberty. Although speculative, this hypothesis aligns with the established role of primary cilia as sensory and signaling hubs for GPCR and RTK pathways regulating cell differentiation and developmental patterning in multiple tissues (e.g., 1, 2). The Discussion section has been expanded to include these considerations.

1. Goetz et al, Nat Rev Genet (2010)- DOI: 1038/nrg2774 (PMID: 20395968)
2. Naturky et al , Cell (2019) DOI: 1038/s41580-019-0116-4 (PMID: 30948801) Our study focuses on the first spermatogenic wave, which represents the transition from the juvenile to the reproductive phase. It is therefore plausible that the transient presence of longer cilia during this period reflects a developmental requirement for external signaling that becomes dispensable in the mature testis. Given that this is only the second study to date examining mammalian meiotic cilia, there remains a vast area of research to explore. We plan to address potential signaling cascades involved in these processes in future studies.

On the other hand, while we cannot confirm that the cilia observed in zygotene spermatocytes persist until pachytene within the same cell, it is reasonable to speculate that they do, serving as longer-lasting signaling structures that facilitate testicular development during the critical pubertal window. In addition, the observation of ciliated spermatocytes at all prophase I substages at 20 dpp, together with our proteomic data, supports the idea that the emergence of meiotic cilia exerts a significant developmental impact on testicular maturation.

In summary, although we cannot yet define specific prophase I functions for meiotic cilia in juvenile spermatocytes, our data demonstrate that the first meiotic wave differs from later waves in cilia dynamics, suggesting distinct regulatory requirements between puberty and adulthood. These findings underscore the importance of considering developmental context when using the first meiotic wave as a model for studying spermatogenesis.

The authors state on page 9 lines 286-288 that the presence of cytoplasmic continuity via intercellular bridges (between developmentally synchronous spermatocytes) hints towards a mechanism that links cilia and flagella formation. Please clarify this statement. While the correlation between the timing of appearance of cilia and flagella in cells that are located within the same segment of the seminiferous tubule may be hinting towards some shared regulation, how would cytoplasmic continuity participate in this regulation? Especially since the cytoplasmic continuity is not between the developmentally distinct cells acquiring the cilia and flagella?

Response:

We thank Ref#1 for this excellent question and for the opportunity to clarify our statement.

The presence of intercellular bridges between spermatocytes is well known and has long been proposed to support germ cell communication and synchronization (1,2) as well as sharing mRNA (3) and organelles (4). A classic example is the Akap gene, located on the X chromosome and essential for the formation of the sperm fibrous sheath; cytoplasmic continuity through intercellular bridges allows Akap-derived products to be shared between X- and Y-bearing spermatids, thereby maintaining phenotypic balance despite transcriptional asymmetry (5). In addition, more recent work has further demonstrated that these bridges are critical for synchronizing meiotic progression and for processes such as synapsis, double-strand break repair, and transposon repression (6).

In this context, and considering our proteomic data (Figure 6), our statement did not intend to imply direct cytoplasmic exchange between ciliated and flagellated cells. Although our current methods do not allow comprehensive tracing of cytoplasmic continuity from the basal to the luminal compartment of the seminiferous epithelium, we plan to address this limitation using high-resolution 3D and ultrastructural imaging approaches in future studies.

Based on our current data, we propose that cytoplasmic continuity within developmentally synchronized spermatocyte cysts could facilitate the coordinated regulation of ciliogenesis, and similarly enable the sharing of regulatory factors controlling flagellogenesis within spermatid cysts. This coordination may occur through the diffusion of centrosomal or ciliary proteins, mRNAs, or signaling intermediates involved in the regulation of microtubule dynamics. However, we cannot exclude the possibility that such cytoplasmic continuity extends across all spermatocytes derived from the same spermatogonial clone, potentially providing a larger regulatory network.]] This mechanism could help explain the temporal correlation we observe between the appearance of meiotic cilia and the onset of flagella formation in adjacent spermatids within the same seminiferous segment.

We have revised the Discussion to explicitly clarify this interpretation and to note that, although hypothetical, it is consistent with established literature on cytoplasmic continuity and germ cell coordination.

1. Dym, et al. * Reprod.*(1971) DOI: 10.1093/biolreprod/4.2.195 (PMID: 4107186)
2. Braun et al. Nature. (1989) DOI: 1038/337373a0 (PMID: 2911388)
3. Greenbaum et al. * Natl. Acad. Sci. USA*(2006). DOI: 10.1073/pnas.0505123103 (PMID: 16549803)
4. Ventelä et al. Mol Biol Cell. (2003) DOI: 1091/mbc.e02-10-0647 (PMID: 12857863)
5. Turner et al. Journal of Biological Chemistry (1998). DOI: 1074/jbc.273.48.32135 (PMID: 9822690)
6. Sorkin, et al. Nat Commun (2025). DOI: 1038/s41467-025-56742-9 (PMID: 39929837)
7. *note: due to manuscript-length limitations, not all cited references can be included in the text; they are listed here to substantiate our response.*

Individual germ cells in H&E-stained testis sections in Figure 1-II are difficult to see. I suggest adding zoomed-in images where spermatocytes/round spermatids/elongated spermatids are clearly distinguishable.

Response:

Ref#1 is very right in this suggestion. We have revised Figure 1 to improve the quality of the H&E-stained testis sections and have added zoomed-in panels where spermatocytes, round spermatids, and elongated spermatids are clearly distinguishable. These additions significantly enhance the clarity and interpretability of the figure.

In Figure 2-II B, the authors document that most ciliated spermatocytes in juvenile mice are pachytene. Is this because most meiotic cells are pachytene? Please clarify. If the data are available (perhaps could be adapted from Figure 1-III), it would be informative to see a graph representing what proportions of each meiotic prophase substages have cilia.

Response:

We thank the reviewer for this valuable observation. Indeed, the predominance of ciliated pachytene spermatocytes reflects the fact that most meiotic cells in juvenile testes are at the pachytene stage (Figure 1). We have clarified this point in the text and have added a new supplementary figure (Supplementary Figure 2, new figure) presenting a graph showing the proportion of spermatocytes at each prophase I substage that possess primary cilia. This visualization provides a clearer quantitative overview of ciliation dynamics across meiotic substages.

I suggest annotating the EM images in Sup Figure 2 and 3 to make it easier to interpret.

Response:

We thank the reviewer for this helpful suggestion. We have now added annotations to the EM images in Supplementary Figures 3 and 4 to facilitate their interpretation. These visual guides help readers more easily identify the relevant ultrastructural features described in the text.

The authors claim that the ratio between GLI3-FL and GLI3-R is stable across their analyzed developmental window in whole testis immunoblots shown in Sup Figure 5. Quantifying the bands and normalizing to the loading control would help strengthen this claim as it hard to interpret the immunoblot in its current form.

Response:

We thank the reviewer for this valuable suggestion. Following this recommendation, Supplementary Figure 5 has been revised to include quantification of GLI1 and GLI3 protein levels, normalized to the loading control.

After quantification, we observed statistically significant differences across developmental stages. Specifically, GLI1 expression is slightly higher at 21 dpp compared to 8 dpp. For GLI3, we performed two complementary analyses:

• Total GLI3 protein (sum of full-length and repressor forms normalized to loading control) shows a progressive decrease during development, with the lowest levels at 60 dpp (Supplementary Figure 5D).
• GLI3 activation status, assessed as the GLI3-FL/GLI3-R ratio, is highest during the 19-21 dpp window, compared to 8 dpp and 60 dpp. Although these results suggest a possible transient activation of GLI3 during testicular maturation, we caution that this cannot automatically be attributed to increased Hedgehog signaling, as GLI3 processing can also be affected by other processes, such as changes in ciliogenesis. Furthermore, because the analysis was performed on whole-testis protein extracts, these changes cannot be specifically assigned to ciliated spermatocytes.

We have expanded the Discussion to address these findings and to highlight the potential involvement of the Desert Hedgehog (DHH) pathway, which plays key roles in testicular development, Sertoli-germ cell communication, and spermatogenesis (1, 2, 3). We plan to investigate these pathways further in future studies.

1. Bitgood et al. Curr Biol. (1996). DOI: 1016/s0960-9822(02)00480-3 (PMID: 8805249)
2. Clark et al. Biol Reprod. (2000) DOI: 1095/biolreprod63.6.1825 (PMID: 11090455)
3. O'Hara et al. BMC Dev Biol. (2011) DOI: 1186/1471-213X-11-72 (PMID: 22132805) *note: due to manuscript-length limitations, not all cited references can be included in the text; they are listed here to substantiate our response.

There are a few typos throughout the manuscript. Some examples: page 5 line 172, Figure 3-I legend text, Sup Figure 5-II callouts, Figure 8-III legend, page 15 line 508, page 17 line 580, page 18 line 611.

Response:

We thank the reviewer for detecting this. All typographical errors have been corrected, and figure callouts have been reviewed for consistency.

__ ____Response to the Referee #2__

__ __This study focuses on the dynamic changes of ciliogenesis during meiosis in prepubertal mice. It was found that primary cilia are not an intrinsic feature of the first wave of meiosis (initiating at 8 dpp); instead, they begin to polymerize at 20 dpp (after the completion of the first wave of meiosis) and are present in all stages of prophase I. Moreover, prepubertal cilia (with an average length of 21.96 μm) are significantly longer than adult cilia (10 μm). The emergence of cilia coincides temporally with flagellogenesis, suggesting a regulatory association in the formation of axonemes between the two. Functional experiments showed that disruption of cilia by chloral hydrate (CH) delays DNA repair, while the AURKA inhibitor (MLN8237) delays cilia disassembly, and centrosome migration and cilia depolymerization are mutually exclusive events. These findings represent the first detailed description of the spatiotemporal regulation and potential roles of cilia during early testicular maturation in mice. The discovery of this phenomenon is interesting; however, there are certain limitations in functional research.

We thank Ref#2 for taking the time to evaluate our manuscript and for summarizing its main findings. We regret that the reviewer did not find the study sufficiently compelling, but we respectfully clarify that the strength of our work lies precisely in addressing a largely unexplored aspect of mammalian meiosis for which virtually no prior data exist. Given the extremely limited number of studies addressing cilia in mammalian meiosis (only five to date, including our own previous publication on adult mouse spermatogenesis) (1-5), we consider that the present work provides the first robust and integrative evidence on the emergence, morphology, and potential roles of primary cilia during prepubertal testicular development. The study combines histology, high-resolution microscopy, proteomics, and pharmacological perturbations, supported by quantitative analyses, thereby establishing a solid and much-needed reference framework for future functional studies.

We emphasize that this manuscript constitutes the first comprehensive characterization of ciliogenesis during prepubertal mouse meiosis, complemented by functional in vitro assays that begin to address potential roles of these cilia. For this reason, we want to underscore the importance of this study in providing a solid framework that will support and guide future research

Major points:

1. The prepubertal cilia in spermatocytes discovered by the authors lack specific genetic ablation to block their formation, making it impossible to evaluate whether such cilia truly have functions. Because neither in the first wave of spermatogenesis nor in adult spermatogenesis does this type of cilium seem to be essential. In addition, the authors also imply that the formation of such cilia appears to be synchronized with the formation of sperm flagella. This suggests that the production of such cilia may merely be transient protein expression noise rather than a functionally meaningful cellular structure.

Response:

We agree that a genetic ablation model would represent the ideal approach to directly test cilia function in spermatogenesis. However, given the complete absence of prior data describing the dynamics of ciliogenesis during testis development, our priority in this study was to establish a rigorous structural and temporal characterization of this process in the main mammalian model organism, the mouse. This systematic and rigorous phenotypic characterization is a necessary first step before any functional genetics could be meaningfully interpreted.

To our knowledge, this study represents the first comprehensive analysis of ciliogenesis during prepubertal mouse meiosis, extending our previous work on adult spermatogenesis (1). Beyond these two contributions, only four additional studies have addressed meiotic cilia-two in zebrafish (2, 3), with Mytlys et al. also providing preliminary observations relevant to prepubertal male meiosis that we discuss in the present work, one in Drosophila (4) and a recent one in butterfly (5). No additional information exists for mammalian gametogenesis to date.

1. López-Jiménez et al. Cells (2022) DOI: 10.3390/cells12010142 (PMID: 36611937)
2. Mytlis et al. Science (2022) DOI: 10.1126/science.abh3104 (PMID: 35549308)
3. Xie et al. J Mol Cell Biol (2022) DOI: 10.1093/jmcb/mjac049 (PMID: 35981808)
4. Riparbelli et al . Dev Cell (2012) DOI: 10.1016/j.devcel.2012.05.024 (PMID: 22898783)
5. Gottardo et al, Cytoskeleton (Hoboken) (2023) DOI: 10.1002/cm.21755 (PMID: 37036073) We therefore consider this descriptive and analytical foundation to be essential before the development of functional genetic models. Indeed, we are currently generating a conditional genetic model for a ciliopathy in our laboratory. These studies are ongoing and will directly address the type of mechanistic questions raised here, but they extend well beyond the scope and feasible timeframe of the present manuscript.

We thus maintain that the present work constitutes a necessary and timely contribution, providing a robust reference dataset that will facilitate and guide future functional studies in the field of cilia and meiosis.

Taking this into account, we would be very pleased to address any additional, concrete suggestions from Ref#2 that could further strengthen the current version of the manuscript

The high expression of axoneme assembly regulators such as TRiC complex and IFT proteins identified by proteomic analysis is not particularly significant. This time point is precisely the critical period for spermatids to assemble flagella, and TRiC, as a newly discovered component of flagellar axonemes, is reasonably highly expressed at this time. No intrinsic connection with the argument of this paper is observed. In fact, this testicular proteomics has little significance.

Response:

We appreciate this comment but respectfully disagree with the reviewer's interpretation of our proteomic data. To our knowledge, this is the first proteomic study explicitly focused on identifying ciliary regulators during testicular development at the precise window (19-21 dpp) when both meiotic cilia and spermatid flagella first emerge.

While Piprek et al (1) analyzed the expression of primary cilia in developing gonads, proteomic data specifically covering the developmental transition at 19-21 dpp were not previously available. Furthermore, a recent cell-sorting study (2), detected expression of cilia proteins in pachytene spermatocytes compared to round spermatids, but did not explore their functional relevance or integrate these data with developmental timing or histological context.

In contrast, our dataset integrates histological staging, high-resolution microscopy, and quantitative proteomics, revealing a set of candidate regulators (including DCAF7, DYRK1A, TUBB3, TUBB4B, and TRiC) potentially involved in cilia-flagella coordination. We view this as a hypothesis-generating resource that outlines specific proteins and pathways for future mechanistic studies on both ciliogenesis and flagellogenesis in the testis.

Although we fully agree that proteomics alone cannot establish causal function, we believe that dismissing these data as having little significance overlooks their value as the first molecular map of the testis at the developmental window when axonemal structures arise. Our dataset provides, for the first time, an integrated view of proteins associated with ciliary and flagellar structures at the developmental stage when both axonemal organelles first appear. We thus believe that our proteomic dataset represents an important and novel contribution to the understanding of testicular development and ciliary biology.

Considering this, we would again welcome any specific suggestions from Ref#2 on additional analyses or clarifications that could make the relevance of this dataset even clearer to readers.

1. Piprek et al. Int J Dev Biol. (2019) doi: 10.1387/ijdb.190049rp (PMID: 32149371).
2. Fang et al. Chromosoma. (1981) doi: 10.1007/BF00285768 (PMID: 7227045).

Response to the Referee #3

In "The dynamics of ciliogenesis in prepubertal mouse meiosis reveals new clues about testicular development" Pérez-Moreno, et al. explore primary cilia in prepubertal mouse spermatocytes. Using a combination of microscopy, proteomics, and pharmacological perturbations, the authors carefully characterize prepubertal spermatocyte cilia, providing foundational work regarding meiotic cilia in the developing mammalian testis.

Response: We sincerely thank Ref#3 for their positive assessment of our work and for the thoughtful suggestions that have helped us strengthen the manuscript. We are pleased that the reviewer recognizes both the novelty and the relevance of our study in providing foundational insights into meiotic ciliogenesis during prepubertal testicular development. All specific comments have been carefully considered and addressed as detailed below.

Major concerns:

1. The authors provide evidence consistent with cilia not being present in a larger percentage of spermatocytes or in other cells in the testis. The combination of electron microscopy and acetylated tubulin antibody staining establishes the presence of cilia; however, proving a negative is challenging. While acetylated tubulin is certainly a common marker of cilia, it is not in some cilia such as those in neurons. The authors should use at least one additional cilia marker to better support their claim of cilia being absent.

Response:

We thank the reviewer for this helpful suggestion. In the revised version, we have strengthened the evidence for cilia identification by including an additional ciliary marker, glutamylated tubulin (GT335), in combination with acetylated tubulin and ARL13B (which were included in the original submission). These data are now presented in the new Supplementary Figure 2, which also includes an example of a non-ciliated spermatocyte showing absence of both ARL13B and AcTub signals.

Taken together, these markers provide a more comprehensive validation of cilia detection and confirm the absence of ciliary labelling in non-ciliated spermatocytes.

The conclusion that IFT88 localizes to centrosomes is premature as key controls for the IFT88 antibody staining are lacking. Centrosomes are notoriously "sticky", often sowing non-specific antibody staining. The authors must include controls to demonstrate the specificity of the staining they observe such as staining in a genetic mutant or an antigen competition assay.

Response:

We appreciate the reviewer's concern and fully agree that antibody specificity is critical when interpreting centrosomal localization. The IFT88 antibody used in our study is commercially available and has been extensively validated in the literature as both a cilia marker (1, 2), and a centrosome marker in somatic cells (3). Labelling of IFT88 in centrosomes has also been previously described using other antibodies (4, 5). In our material, the IFT88 signal consistently appears at one of the duplicated centrosomes and at both spindle poles-patterns identical to those reported in somatic cells. We therefore consider the reported meiotic IFT88 staining as specific and biologically reliable.

That said, we agree that genetic validation would provide the most definitive confirmation. We would like to inform that we are currently since we are currently generating a conditional genetic model for a ciliopathy in our laboratory that will directly assess both antibody specificity and functional consequences of cilia loss during meiosis. These experiments are in progress and will be reported in a follow-up study.

1. Wong et al. Science (2015). DOI: 1126/science.aaa5111 (PMID: 25931445)
2. Ocbina et al. Nat Genet (2011). DOI: 1038/ng.832 (PMID: 21552265)
3. Vitre et al. EMBO Rep (2020). DOI: 15252/embr.201949234 (PMID: 32270908)
4. Robert A. et al. J Cell Sci (2007). DOI: 1242/jcs.03366 (PMID: 17264151)
5. Singla et al, Developmental Cell (2010). DOI: 10.1016/j.devcel.2009.12.022 (PMID: 20230748) *note: due to manuscript-length limitations, not all cited references can be included in the text; they are listed here to substantiate our response.

There are many inconsistent statements throughout the paper regarding the timing of the first wave of spermatogenesis. For example, the authors state that round spermatids can be detected at 21dpp on line 161, but on line 180, say round spermatids can be detected a 19dpp. Not only does this lead to confusion, but such discrepancies undermine the validity of the rest of the paper. A summary graphic displaying key events and their timing in the first wave of spermatogenesis would be instrumental for reader comprehension and could be used by the authors to ensure consistent claims throughout the paper.

Response:

We thank the reviewer for identifying this inconsistency and apologize for the confusion. We confirm that early round spermatids first appear at 19 dpp, as shown in the quantitative data (Figure 1J). This can be detected in squashed spermatocyte preparations, where individual spermatocytes and spermatids can be accurately quantified. The original text contained an imprecise reference to the histological image of 21 dpp (previous line 161), since certain H&E sections did not clearly show all cell types simultaneously. However, we have now revised Figure 1, improving the image quality and adding a zoomed-in panel highlighting early round spermatids. Image for 19 dpp mice in Fig 1D shows early, yet still aflagellated spermatids. The first ciliated spermatocytes and the earliest flagellated spermatids are observed at 20 dpp. This has been clarified in the text.

In addition, we also thank the reviewer for the suggestion of adding a summary graphic, which we agree greatly facilitates reader comprehension. We have added a new schematic summary (Figure 1K) illustrating the key stages and timing of the first spermatogenic wave.

In the proteomics experiments, it is unclear why the authors assume that changes in protein expression are predominantly due to changes within the germ cells in the developing testis. The analysis is on whole testes including both the somatic and germ cells, which makes it possible that protein expression changes in somatic cells drive the results. The authors need to justify why and how the conclusions drawn from this analysis warrant such an assumption.

Response:

We agree with the reviewer that our proteomic analysis was performed on whole testis samples, which contain both germ and somatic cells. Although isolation of pure spermatocyte populations by FACS would provide higher resolution, obtaining sufficient prepubertal material for such analysis would require an extremely large number of animals. To remain compliant with the 3Rs principle for animal experimentation, we therefore used whole-testis samples from three biological replicates per age.

We acknowledge that our assumption-that the main differences arise from germ cells-is a simplification. However, germ cells constitute the vast majority of testicular cells during this developmental window and are the population undergoing major compositional changes between 15 dpp and adulthood. It is therefore reasonable to expect that a substantial fraction of the observed proteomic changes reflects alterations in germ cells. We have clarified this point in the revised text and have added a statement noting that changes in somatic cells could also contribute to the proteomic profiles.

The authors should provide details on how proteins were categorized as being involved in ciliogenesis or flagellogenesis, specifically in the distinction criteria. It is not clear how the categorizations were determined or whether they are valid. Thus, no one can repeat this analysis or perform this analysis on other datasets they might want to compare.

Response:

We thank the reviewer for this opportunity to clarify our approach. The categorization of protein as being involved in ciliogenesis or flagellogenesis was based on their Gene Ontology (GO) cellular component annotations obtained from the PANTHER database (Version 19.0), using the gene IDs of the Differentially Expressed Proteins (DEPs). Specifically, we used the GO terms cilium (GO:0005929) and motile cilium (GO:0031514). Since motile cilium is a subcategory of cilium, proteins annotated only with the general cilium term, but not included under motile cilium, were considered to be associated with primary cilia or with shared structural components common to different types of cilia. These GO terms are represented in the bottom panel of the Figure 6.

This information has been added to the Methods section and referenced in the Results for transparency and reproducibility.

In the pharmacological studies, the authors conclude that the phenotypes they observe (DNA damage and reduced pachytene spermatocytes) are due to loss of or persistence of cilia. This overinterprets the experiment. Chloral hydrate and MLN8237 certainly impact ciliation as claimed, but have additional cellular effects. Thus, it is possible that the observed phenotypes were not a direct result of cilia manipulation. Either additional controls must address this or the conclusions need to be more specific and toned down.

Response:

We thank the reviewer for this fair observation and have taken steps to strengthen and refine our interpretation. In the revised version, we now include data from 1-hour and 24-hour cultures for both control and chloral hydrate (CH)-treated samples (n = 3 biological replicates). The triple immunolabelling with γH2AX, SYCP3, and H1T allows accurate staging of zygotene (H1T⁻), early pachytene (H1T⁻), and late pachytene (H1T⁺) spermatocytes.

The revised Figure 7 now provides a more complete and statistically supported analysis of DNA damage dynamics, confirming that CH-induced deciliation leads to persistent γH2AX signal at 24 hours, indicative of delayed or defective DNA repair progression. We have also toned down our interpretation in the Discussion, acknowledging that CH could affect other cellular pathways.

As mentioned before, the conditional genetic model that we are currently generating will allow us to evaluate the role of cilia in meiotic DNA repair in a more direct and specific way.

Assuming the conclusions of the pharmacological studies hold true with the proper controls, the authors still conflate their findings with meiotic defects. Meiosis is not directly assayed, which makes this conclusion an overstatement of the data. The conclusions need to be rephrased to accurately reflect the data.

Response:

We agree that this aspect required clarification. As noted above, we have refined both the Results and Discussion sections to make clear that our assays specifically targeted meiotic spermatocytes.

We now present data for meiotic stages at zygotene, early pachytene and late pachytene. This is demonstrated with the labelling for SYCP3 and H1T, both specific marker for meiosis that are not detectable in non meiotic cells. We believe that this is indeed a way to assay the meiotic cells, however, we have specified now in the text that we are analysing potential defects in meiosis progression. We are sorry if this was not properly explained in the original manuscript: it is now rephrased in the new version both in the results and discussion section.

It is not clear why the authors chose not to use widely accepted assays of Hedgehog signaling. Traditionally, pathway activation is measured by transcriptional output, not GLI protein expression because transcription factor expression does not necessarily reflect transcription levels of target genes.

Response:

We agree with the reviewer that measuring mRNA levels of Hedgehog pathway target genes, typically GLI1 and PTCH1, is the most common method for measuring pathway activation, and is widely accepted by researchers in the field. However, the methods we use in this manuscript (GLI1 and GLI3 immunoblots) are also quite common and widely accepted:

Regarding GLI1 immunoblot, many articles have used this method to monitor Hedgehog signaling, since GLI1 protein levels have repeatedly been shown to also go up upon pathway activation, and down upon pathway inhibition, mirroring the behavior of GLI1 mRNA. Here are a few publications that exemplify this point:

• Banday et al. 2025 Nat Commun. DOI: 10.1038/s41467-025-56632-0 (PMID: 39894896)
• Shi et al 2022 JCI Insight DOI: 10.1172/jci.insight.149626 (PMID: 35041619)
• Deng et al. 2019 eLife, DOI: 10.7554/eLife.50208 (PMID: 31482846)
• Zhu et al. 2019 Nat Commun, DOI: 10.1038/s41467-019-10739-3 (PMID: 31253779)
• Caparros-Martin et al 2013 Hum Mol Genet, DOI: 10.1093/hmg/dds409 (PMID: 23026747) *note: due to manuscript-length limitations, not all cited references can be included in the text; they are listed here to substantiate our response.

As for GLI3 immunoblot, Hedgehog pathway activation is well known to inhibit GLI3 proteolytic processing from its full length form (GLI3-FL) to its transcriptional repressor (GLI3-R), and such processing is also commonly used to monitor Hedgehog signal transduction, of which the following are but a few examples:

• Pedraza et al 2025 eLife, DOI: 10.7554/eLife.100328 (PMID: 40956303)
• Somatilaka et al 2020 Dev Cell, DOI: 10.1016/j.devcel.2020.06.034 (PMID: 32702291)
• Infante et al 2018, Nat Commun, DOI: 10.1038/s41467-018-03339-0 (PMID: 29515120)
• Wang et al 2017 Dev Biol DOI: 10.1016/j.ydbio.2017.08.003 (PMID: 28800946)
• Singh et al 2015 J Biol Chem DOI: 10.1074/jbc.M115.665810 (PMID: 26451044)
• *note: due to manuscript-length limitations, not all cited references can be included in the text; they are listed here to substantiate our response.*

In summary, we think that we have used two well established markers to look at Hedgehog signaling (three, if we include the immunofluorescence analysis of SMO, which we could not detect in meiotic cilia).

These Hh pathway analyses did not provide any convincing evidence that the prepubertal cilia we describe here are actively involved in this pathway, even though Hh signaling is cilia-dependent and is known to be active in the male germline (Sahin et al 2014 Andrology PMID: 24574096; Mäkelä et al 2011 Reproduction PMID: 21893610; Bitgood et al 1996 Curr Biol. PMID: 8805249).

That said, we fully agree that our current analyses do not allow us to draw definitive conclusions regarding Hedgehog pathway activity in meiotic cilia, and we now state this explicitly in the revised Discussion.

Also in the Hedgehog pathway experiment, it is confusing that the authors report no detection of SMO yet detect little to no expression of GLIR in their western blot. Undetectable SMO indicates Hedgehog signaling is inactive, which results in high levels of GLIR. The impact of this is that it is not clear what is going on with Hh signaling in this system.

Response:

It is true that, when Hh signaling is inactive (and hence SMO not ciliary), the GLI3FL/GLI3R ratio tends to be low.

Although our data in prepuberal mouse testes show a strong reduction in total GLI3 protein levels (GLI3FL+GLI3R) as these mice grow older, this downregulation of total GLI3 occurs without any major changes in the GLI3FL/GLI3R ratio, which is only modestly affected (suppl. Figure 6).

Hence, since it is the ratio that correlates with Hh signaling rather than total levels, we do not think that the GLI3R reduction we see is incompatible with our non-detection of SMO in cilia: it seems more likely that overall GLI3 expression is being downregulated in developing testes via a Hh-independent mechanism.

Also potentially relevant here is the fact that some cell types depend more on GLI2 than on GLI3 for Hh signaling. For instance, in mouse embryos, Hh-mediated neural tube patterning relies more heavily on GLI2 processing into a transcriptional activator than on the inhibition of GLI3 processing into a repressor. In contrast, the opposite is true during Hh-mediated limb bud patterning (Nieuwenhuis and Hui 2005 Clin Genet. PMID: 15691355). We have not looked at GLI2, but it is conceivable that it could play a bigger role than GLI3 in our model.

Moreover, several forms of GLI-independent non-canonical Hh signaling have been described, and they could potentially play a role in our model, too (Robbins et al 2012 Sci Signal. PMID: 23074268).

We have revised the discussion to clarify some of these points.

All in all, we agree that our findings regarding Hh signaling are not conclusive, but we still think they add important pieces to the puzzle that will help guide future studies.

There are multiple instances where it is not clear whether the authors performed statistical analysis on their data, specifically when comparing the percent composition of a population. The authors need to include appropriate statistical tests to make claims regarding this data. While the authors state some impressive sample sizes, once evaluated in individual categories (eg specific cell type and age) the sample sizes of evaluated cilia are as low as 15, which is likely underpowered. The authors need to state the n for each analysis in the figures or legends.

We thank the reviewer for highlighting this important issue. We have now included the sample size (n) for every analysis directly in the figure legends. Although this adds length, it improves transparency and reproducibility.

Regarding the doubts of Ref#3 about the different sample sizes, the number of spermatocytes quantified in each stage is in agreement with their distribution in meiosis (example, pachytene lasts for 10 days this stage is widely represented in the preparations, while its is much difficult to quantify metaphases I that are less present because the stage itself lasts for less than 24hours). Taking this into account, we ensured that all analyses remain statistically valid and representative, applying the appropriate statistical tests for each dataset. These details are now clearly indicated in the revised figures and legends.

Minor concerns:

1. The phrase "lactating male" is used throughout the paper and is not correct. We assume this term to mean male pups that have yet to be weaned from their lactating mother, but "lactating male" suggests a rare disorder requiring medical intervention. Perhaps "pre-weaning males" is what the authors meant.

Response:

We thank the reviewer for noticing this terminology error. The expression has been corrected to "pre-weaning males" throughout the manuscript.

The convention used to label the figures in this paper is confusing and difficult to read as there are multiple panels with the same letter in the same figure (albeit distinct sections). Labeling panels in the standard A-Z format is preferred. "Panel Z" is easier to identify than "panel III-E".

Response:

We thank the reviewer for this suggestion. All figures have been relabelled using the standard A-Z panel format, ensuring consistency and easier readability across the manuscript.

Author Response:

We thank all reviewers for their time and effort to carefully review our paper and for the constructive comments on our manuscript. Below we outline our planned revisions to the public reviews of the three reviewers.

In our revision, we will include more details regarding our ABR measurements (including temperature, animal metadata), analysis (including filter settings) and lay out a much more detailed motivation for our ABR signal design. Furthermore, we will provide a more detailed discussion on the caveats of the technique and the interpretation of ABR data in general and our data specifically. Furthermore, we will add more discussion on differences between ABR based audiograms and behavioural data. The authors have extensive experience with the ABR technique and are well aware of its limitations, but also its strengths for use in animals that cannot be trained on behavioural tasks such as the very young zebra finches in this study. These additions will strengthen our paper. We think our conclusions remain justified by our data.

Reviewer #1 and #2:

We thank both reviewers for their positive words and suggested improvements. The planned general improvements listed above will take care of all suggestions and comments in the public review.

Reviewer #3:

We thank the reviewer for the detailed critique of our manuscript and many suggestions for improvement. The planned general improvements listed above will take care of many of the suggestions and comments listed in the public review. Here we will highlight a few first responses that we will address in detail in our resubmission.

The reviewer’s major critiques can be condensed to the following four points.

(1) ABR cannot be done in such small animals.

This critique is unfounded. ABR measures the summed activity in the auditory pathway, and with smaller distance from brainstem to electrodes in small animals, the ABR signals are expected to have higher amplitude and consequently better SNR.  Thus, smaller animals should lead to higher amplitude ABR signals. We have successfully recorded ABR in animals smaller than 2 DPH zebra finches to support this claim (zebrafish (Jørgensen et al., 2012), 10 mm froglets (Goutte et al., 2017) and 5 mm salamanders (Capshaw et al., 2020). It is more surprising the technique still provides robust signals even in very large animals such as Minke whales (Houser et al., 2024).

(2) The ABR methods used does not follow protocol for other published work in birds. Particularly the 25 ms long duration tone bursts may have underestimated high frequency hearing.

There is no fixed protocol for ABR measurements, and several studies of bird ABR have used as long or even longer durations. Longer-duration signals were chosen deliberately and are necessary to have a sufficient number of cycles and avoid frequency splatter at our lowest frequencies used (see Lauridsen et al., 2021).

(3) Sensitivity data should be corrected from ABR to behavioural data.

We present the results of our measurements on hearing sensitivity using ABR, and ABR based thresholds are generally less sensitive than thresholds based on behavioural studies (presented in Fig 2c). Correcting for these measurements to behavioural thresholds is of course possible, but presenting only the corrected thresholds would be a misrepresentation of our sensitivity data. Even so it should be done only within species and age group and such data is currently not available. In our revision, we will include elaborate discussion on this topic.

(4) Results are inconsistent with papers in developing songbirds.

We agree that our results do not support and even question the claims in earlier work. These papers however do either 1) not measure hearing physiology or 2) do so in different species. To our best knowledge there is presently no data published on the auditory physiology development in songbird embryos. Our data are consistent with what is known about the physiology of auditory development in all birds studied so far. We will provide a detailed discussion on this topic in our revision.

References

Capshaw et al. (2020) J Exp Biol 223: jeb236489

Goutte et al. (2017) Sci Rep 7: 12121, doi 10.1038/s41598-017-12145-5

Houser et al. (2024) Science 386, 902-906. DOI:10.1126/science.ado7580).

Jørgensen et al. (2012) Adv Exp Med Biol 730: 117-119

Lauridsen et al (2021) J Exp Biol 224: jeb237313. https://doi.org/10.1242/jeb.237313

Author response:

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

Reviewer #1 (Public review):

This Reviewer was positive about the study, stating ‘The findings are interesting and important to increase the understanding both of the synaptic transmissions in the main olfactory bulb and the DA neuron diversity.’ They provided a number of helpful suggestions for improving the paper, which we have incorporated as follows:

(1) It is known that there are two types of DA neurons in the glomerular layer with different diameters and capacitances (Kosaka and Kosaka, 2008; Pignatelli et al., 2005; Angela Pignatelli and Ottorino Belluzzi, 2017). In this manuscript, the authors need to articulate better which layer the imaging and ephys recordings took place, all glomerular layers or with an exception. Meanwhile, they have to report the electrophysiological properties of their recordings, including capacitances, input resistance, etc.

We thank the Reviewer for this clarification. Indeed, the two dopaminergic cell types we study here correspond directly to the subtypes previously identified based on cell size. Our previous work showed that axon-bearing OB DA neurons have significantly larger somas than their anaxonic neighbours (Galliano et al. 2018), and we replicate this important result in the present study (Figure 3D). In terms of electrophysiological correlates of cell size, we now provide full details of passive membrane properties in the new Supplementary Figure 4, as requested. Axon-bearing DA neurons have significantly lower input resistance and show a non-significant trend towards higher cell capacitance. Both features are entirely consistent with the larger soma size in this subtype. We apologise for the oversight in not fully describing previous categorisations of OB DA neurons, and have now added this information and the appropriate citations to the Introduction (lines 56 to 59 of the revised manuscript). 

In terms of cell location, all cells in this study were located in the OB glomerular layer. We sampled the entire glomerular layer in all experiments, including the glomerular/EPL border where the majority of axon-bearing neurons are located (Galliano et al. 2018). This is now clarified in the Materials and Methods section (lines 535 to 537 and 614 to 616 of the revised manuscript).

(2) It is understandable that recording the DA neurons in the glomerular layer is not easy. However, the authors still need to increase their n's and repeat the experiments at least three times to make their conclusion more solid. For example (but not limited to), Fig 3B, n=2 cells from 1 mouse. Fig.4G, the recording only has 3 cells.

Despite the acknowledged difficulty of these experiments, we have now added substantial extra data to the study as requested. We have increased the number of cells and animals to further support the following findings:

Fig 3B: we now have n=5 cells from N=3 mice. We have created a new Supplementary Figure 1 to show all the examples.

Figure 4G: we now have n=6 cells from N=4 mice.

Figure 5G: we now have n=3 cells from N=3 mice.

The new data now provide stronger support for our original conclusions. In the case of auto-evoked inhibition after the application of D1 and D2 receptor antagonists, a nonsignificant trend in the data suggests that, while dopamine is clearly not necessary for the response, it may play a small part in its strength. We have now included this consideration in the Results section (lines 256 to 264 of the revised manuscript).

(3) The statistics also use pseudoreplicates. It might be better to present the biology replicates, too.

Indeed, in a study focused on the structural and functional properties of individual neurons, we performed all comparisons with cell as the unit of analysis. This did often (though not always) involve obtaining multiple data points from individual mice, but in these low-throughput experiments n was never hugely bigger than N. The potential impact of pseudoreplicates and their associated within-animal correlations was therefore low. We checked this in response to the Reviewer’s comment by running parallel nested analyses for all comparisons that returned significant differences in the original submission. These are the cases in which we would be most concerned about potential false positive results arising from intra-animal correlations, which nested tests specifically take into account (Aarts et al., 2013). In every instance we found that the nested tests also reported significant differences between anaxonic and axonbearing cell types, thus fully validating our original statistical approach. We now report this in the relevant section of the Materials and Methods (lines 686 to 691 of the revised manuscript).

(4) In Figure 4D, the authors report the values in the manuscript. It is recommended to make a bar graph to be more intuitive.

This plot does already exist in the original manuscript. We originally describe these data to support the observation that an auto-evoked inhibition effect exists in anaxonic neurons (corresponding to now lines 240 to 245 of the revised manuscript). We then show them visually in their entirety when we compare them to the lack of response in axon-bearing neurons, depicted in Figure 5C. We still believe that this order of presentation is most appropriate for the flow of information in the paper, so have maintained it in our revised submission.

(5) In Figure 4F and G, although the data with three cells suggest no phenotype, the kinetics looked different. So, the authors might need to explore that aside from increasing the n.

We thank the Reviewer for this suggestion. To quantify potential changes in the autoevoked inhibition response kinetics, we fitted single exponential functions and compared changes in the rate constant (k; Methods, lines 650 to 652 of the revised manuscript). Overall, we observed no consistent or significant change in rate constant values after adding DA receptor antagonists. This finding is now reported in the Results section (lines 260 to 263 of the revised manuscript) and shown in a new Supplementary Figure 3.

(6) Similarly, for Figure 4I and J, L and M, it is better to present and analyze it like F and G, instead of showing only the after-antagonist effect.

We agree that the ideal scenario would have been to perform the experiments in Figure 4J and 4M the same way as those in Figure 4G, with a before vs after comparison. Unfortunately, however, this was not practically possible. 

When attempting to apply carbenoxelone to already-patched cells, we found that this drug highly disrupted the overall health and stability of our recordings immediately after its application. This is consistent with previous reports of similar issues with this compound (e.g. Connors 2012, Epilepsy Currents; Tovar et al., 2009, Journal of Neurophysiology). After many such attempts, the total yield of this experiment was one single cell from one animal. Even so, as shown in the traces below, we were able to show that the auto-evoked inhibition response was not eliminated in this specific case:

Author response image 1.

Traces of an AEI response recorded before (magenta) and after (green) the application of carbenoxolone (n=1 cell from N=1 mouse).

In light of these issues, we instead followed published protocols in applying the carbenoxolone directly in the bath without prior recording for 20 minutes (following Samailova et al., 2003, Journal of Neurochemistry) and ran the protocol after that time. Given that our main question was to ask whether gap junctions were strictly necessary for the presence of any auto-evoked inhibition response, our positive findings in these experiments still allowed us to draw clear conclusions.

In contrast, the issue with the NKCC1 antagonist bumetanide was time. As acknowledged by this Reviewer, obtaining and maintaining high-quality patch recordings from OB DA neurons is technically challenging. Bumetanide is a slow-acting drug when used to modify neuronal chloride concentrations, because in addition to the time it takes to reach the neurons and effectively block NKCC1, the intracellular levels of chloride subsequently change slowly. Studies using this drug in slice physiology experiments typically use an incubation time of at least 20 minutes (e.g. Huberfeld et al., 2007, Journal of Neuroscience), which was incompatible with productive data collection in OB DA neurons. Again, after many unsuccessful efforts, we were forced instead to include bumetanide in the bath without prior recording for 20-30 minutes. As with the carbenoxolone experiment, our goal here was to establish whether autoevoked inhibition was in any way retained in the presence of this drug, so our positive result again allowed us to draw clear conclusions.

Reviewer #1 (Recommendations for the authors):

(1) I suggest the authors reconsider the terminology. For example, they use "strikingly" in their title. The manuscript reported two different transmitter release strategies but not the mechanisms, and the word "strikingly" is not professional, either.

We appreciate the Reviewer’s attention to clarity and tone in the manuscript title, and have nevertheless decided to retain the original wording. The almost all-or-nothing differences between closely related cell types shown in structural and functional properties here (Figures 3F & 5C) are pronounced, extremely clear and easily spotted – all properties appropriate for the word ‘striking.’ In addition, we note that the use of this term is not at all unprofessional, with a PubMed search for ‘strikingly’ in the title of publications returning over 200 hits.

(2) Similarly, almost all confocal scopes are 3D because images can be taken at stacks. So "3D confocal" is misleading.

We understand that this is misleading. We have now replaced the sentence ‘Example snapshot of a 3D confocal stack of…’ by ‘Example confocal images of…’ in all the figure legends that apply.

(3) It is recommended to present the data in bar graphs with data dots instead of showing the numbers in the manuscript directly.

We agree entirely, and now present data plots for all comparisons reported in the study (Supplementary Figures 2, 4 and 5).

Reviewer #2 (Recommendations for the authors):

(1) Several experiments report notably small sample sizes, such as in Figures 3B and 5G, where data from only 2 cells derived from 1-2 mice are presented. Figures 4E-G also report the experimental result only from 3 cells derived from 3 mice. To enhance the statistical robustness and reliability of the findings, these experiments should be replicated with larger sample sizes.

As per our response to Reviewer 1’s comment #2 above, and to directly address the concern that some evidence was ‘incomplete’, we have now added significant extra data and analysis to this revised submission (Figures 4 and 5; and Supplementary Figure 1). We believe that this has further enhanced the robustness and reliability of our findings, as requested.

(2) The authors utilize vGAT-Cre for Figures 1-3 and DAT-tdTomato for Figures 4-5, raising concerns about consistency in targeting the same population of dopaminergic neurons. It remains unclear whether all OB DA neurons express vGAT and release GABA. Clarification and additional evidence are needed to confirm whether the same neuronal population was studied across these experiments.

Although we indeed used different mouse lines to investigate structural and functional aspects of transmitter release, we can be very confident that both approaches allowed us to study the same two distinct DA cell types being compared in this paper. Existing data to support this position are already clear and strong, so in this revision we have focused on the Reviewer’s suggestion to clarify the approaches we chose.

First, it is well characterised that in mouse and many other species all OB DA neurons are also GABAergic. This has been demonstrated comprehensively at the level of neurochemical identity and in terms of dopamine/GABA co-release, and is true across both small-soma/anaxonic and large-soma/axon-bearing subclasses (Kosaka & Kosaka 2008; 2016; Maher & Westbrook 2008; Borisovska et al., 2013; Vaaga et al., 2016; Liu et al. 2013). To specifically confirm vGAT expression, we have also now provided additional single-cell RNAseq data and immunohistochemical label in a revised Figure 1 (see also Panzanelli et al., 2007, now referenced in the paper, who confirmed endogenous vGAT colocalisation in TH-positive OB neurons). Most importantly, by using vGAT-cre mice here we were able to obtain sufficient numbers of both anaxonic and axon-bearing DA neurons among the vGAT-cre-expressing OB population. We could unambiguously identify these cells as dopaminergic because of their expression of TH protein which, due to the absence of noradrenergic neurons in the OB, is a specific and comprehensive marker for dopaminergic cells in this brain region (Hokfelt et al., 1975; Rosser et al., 1986; Kosaka & Kosaka 2016). Crucially, both axon-bearing and anaxonic OB DA subtypes strongly express TH (Galliano et al., 2018, 2021). We have now added additional text to the relevant Results section (lines 99 to 108 of the revised manuscript) to clarify these reasons for studying vGAT-cre mice here.

We were also able to clearly identify and sample both subtypes of OB DA neuron using DAT-tdT mice. Our previous published work has thoroughly characterised this exact mouse line at the exact ages studied in the present paper (Galliano et al., 2018; Byrne et al., 2022). We know that DAT-tdT mice provide rather specific label for TH-expressing OB DA neurons (75% co-localisation; Byrne et al., 2022), but most importantly we know which non-DA neurons are labelled in this mouse line and how to avoid them. All nonTH-expressing but tdT-positive cells in juvenile DAT-tdT mice are small, dimly fluorescent and weakly spiking neurons of the calretinin-expressing glomerular subtype (Byrne et al., 2022). These cells are easily detected during physiological recordings, and were excluded from our study here. This information is now provided in the relevant Methods section (lines 616 to 619 of the revised manuscript, also referenced in lines 236 to 240 of the results section), and we apologise for its previous omission. Finally, we have shown both structurally and functionally that both axon-bearing and anaxonic OB DA subtypes are labelled in DAT-tdT mice (Galliano et al., 2018, Tufo et al., 2025; present study). Overall, these additional clarifications firmly establish that the same neuronal populations were indeed studied across our experiments.

(3) The low TH+ signal in Figure 1D raises questions regarding the successful targeting of OB DA neurons. Further validation, such as additional staining, is required to ensure that the targeted neurons are accurately identified.

As noted in our response to the previous comment, TH is a specific marker for dopaminergic neurons in the mouse OB, and is widely used for this purpose. Labelling for TH in our tissue is extremely reliable, and in fact gives such strong signal that we were forced to reduce the primary antibody concentration to 1:50,000 to prevent bleedthrough into other acquisition channels. Even at this concentration it was extremely straightforward to unambiguously identify TH-positive cells based on somatic immunofluorescence. We recognise, however, that the original example image in Figure 1D was not sufficiently clear, and have now provided a new example which illustrates the TH-based identification of these cells much more effectively. 

(4) Estimating the total number of dopaminergic neurons in the olfactory bulb, along with the relative proportions of anaxonic and axon-bearing neuron subtypes, would provide valuable context for the study. Presenting such data is crucial to underscore the biological significance of the findings.

This information has already been well characterised in previous studies. Total dopaminergic cell number in the OB is ~90,000 (Maclean & Shipley, 1988; Panzanelli et al., 2007; Parrish-Aungst et al., 2007). In terms of proportions, anaxonic neurons make up the vast majority of these cells, with axon-bearing neurons representing only ~2.5% of all OB dopaminergic neurons at P28 (Galliano et al., 2018). Of course, the relatively low number of the axon-bearing subtype does not preclude its having a potentially large influence on glomerular networks and sensory processing, as demonstrated by multiple studies showing the functional effects of inter-glomerular inhibition (Kosaka & Kosaka, 2008; Liu et al., 2013; Whitesell et al., 2013; Banerjee et al., 2015). This information has now been added to the Introduction (line 47 and lines 59 to 62 of the revised manuscript).

(5) The authors report that in-utero injection was performed based on the premise that the two subclasses of dopaminergic neurons in the olfactory bulb are generated during embryonic development. However, it remains unclear whether in-utero injection is essential for distinguishing between these two subclasses. While the manuscript references a relevant study, the explanation provided is insufficient. A more detailed justification for employing in-utero injection would enhance the manuscript's clarity and methodological rigor.

We apologise for the lack of clarity in explaining the approach. In utero injection is not absolutely essential for distinguishing between the two subclasses, but it does have two major advantages. 1) Because infection happens before cells migrate to their final positions, it produces sparse labelling which permits later unambiguous identification of individual cells’ processes; and 2) Because both subclasses are generated embryonically (compared to the postnatal production of only anaxonic DA neurons), it allows effective targeting of both cell types. We have now expanded the relevant section of the Results to explain the rationale for our approach in more detail (lines 109 to 116 of the revised manuscript).

(6) In Figures 1A and 4A, it appears that data from previously published studies were utilized to illustrate the differential mRNA expression in dopaminergic neurons of the olfactory bulb. However, the Methods section and the manuscript lack a detailed description of how these dopaminergic neurons were classified or analyzed. Given that these figures contribute to the primary dataset, providing additional explanation and context is essential to ensure clarity of the findings.

We apologise for the lack of clarity. We have now extended the part of the methods referring to the RNAseq data analysis (lines 666 to 678 of the revised manuscript). 

(7) In Figure 2C, anaxonic dopamine neurons display considerable variability in the number of neurotransmitter release sites, with some neurons exhibiting sparse sites while others exhibit numerous sites. The authors should address the potential biological or methodological reasons for this variability and discuss its significance.

We thank the Reviewer for highlighting this feature of our data. We have now outlined potential methodological reasons for the variability, whilst also acknowledging that it is consistent with previous reports of presynaptic site distributions in these cells (Kiyokage et al., 2017; Results, lines 169 to 172 of the revised manuscript). We have also added a brief discussion of the potential biological significance (Discussion, lines 446 to 450).

(8) In the images used to differentiate anaxonic and axon-bearing neurons, the soma, axons, and dendrites are intermixed, making it difficult to distinguish structures specific to each subclass. Employing subclass-specific labeling or sparse labeling techniques could enhance clarity and accuracy in identifying these structures.

Distinguishing these structures is indeed difficult, and was the main reason we used viral label to produce sparse labelling (see response to comment #5 above). In all cases we were extremely careful, including cells only when we could be absolutely certain of their anaxonic or axon-bearing identity, and could also be certain of the continuity of all processes. Crucially, while the 2D representations we show in our figures may suggest a degree of intermixing, we performed all analyses on 3D image stacks, significantly improving our ability to accurately assign structures to individual cells. We have now added extra descriptions of this approach in the relevant Methods section (lines 546 to 548 of the revised manuscript).

(9) In Figure 3, the soma area and synaptophysin puncta density are compared between axon-bearing and anaxonic neurons. However, the figure only presents representative images of axon-bearing neurons. To ensure a fair and accurate comparison, representative images of both neuron subtypes should be included.

The original figures did include example images of puncta density (or lack of puncta) in both cell types (Figure 2B and Figure 3E). For soma area, we have now included representative images of axon-bearing and anaxonic neurons with an indication of soma area measurement in a new Supplementary Figure 2A.

(10) In Figure 4B, the authors state that gephyrin and synaptophysin puncta are in 'very close proximity.' However, it is unclear whether this proximity is sufficient to suggest the possibility of self-inhibition. Quantifying the distance between gephyrin and synaptophysin puncta would provide critical evidence to support this claim. Additionally, analyzing the distribution and proportion of gephyrinsynaptophysin pairs in close proximity would offer further clarity and strengthen the interpretation of these findings.

We thank the Reviewer for raising this issue. We entirely agree that the example image previously shown did not constitute sufficient evidence to claim either close proximity of gephyrin and synaptophysin puncta, nor the possibility of self-inhibition. We are not in a position to perform a full quantitative analysis of these spatial distributions, nor do we think this is necessary given previous direct evidence for auto-evoked inhibition in OB dopaminergic cells (Smith and Jahr, 2002; Murphy et al., 2005; Maher and Westbrook, 2008; Borisovska et al., 2013) and our own demonstration of this phenomenon in anaxonic neurons (Figure 4). We have therefore removed the image and the reference to it in the text. 

(11) In Figures 4J and 4M, the effects of the drugs are presented without a direct comparison to the control group (baseline control?). Including these baseline control data is essential to provide a clear context for interpreting the drug effects and to validate the conclusions drawn from these experiments.

We appreciate the Reviewer’s attention to this important point. As this concern was also raised by Reviewer 1 (their point #6), we have provided a detailed response fully addressing it in our replies to Reviewer 1 above. 

(12) In Lines 342-344, the authors claim that VMAT2 staining is notoriously difficult. However, several studies (e.g., Weihe et al., 2006; Cliburn et al., 2017) have successfully utilized VMAT2 staining. Moreover, Zhang et al., 2015 - a reference cited by the authors - demonstrates that a specific VMAT2 antibody effectively detects VMAT2. Providing evidence of VMAT2 expression in OB DA neurons would substantiate the claim that these neurons are GABA-co-releasing DA neurons and strengthen the study's conclusions.

As noted in response to this Reviewer’s comment #2 above, there is clear published evidence that OB DA neurons are GABA- and dopamine-releasing cells. These cells are also known to express VMAT2 (Cave et al., 2010; Borisovska et al., 2013; Vergaña-Vera et al., 2015). We do not therefore believe that additional evidence of VMAT2 expression is necessary to strengthen our study’s conclusions. We did make every effort to label VMAT2-positive release sites in our neurons, but unfortunately all commercially available antibodies were ineffective. The successful staining highlighted by the Reviewer was either performed in the context of virally driven overexpression (Zhang et al., 2015) or was obtained using custom-produced antibodies (Weihe et al., 2006; Cliburn et al., 2017). We have now modified the Discussion text to provide more clarification of these points (lines 393 to 395 of the revised manuscript).

Author response:

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

Reviewer #1 (Public review)

Summary:

This study by Park and colleagues uses longitudinal saliva viral load data from two cohorts (one in the US and one in Japan from a clinical trial) in the pre-vaccine era to subset viral shedding kinetics and then use machine learning to attempt to identify clinical correlates of different shedding patterns. The stratification method identifies three separate shedding patterns discriminated by peak viral load, shedding duration, and clearance slope. The authors also assess micro-RNAs as potential biomarkers of severity but do not identify any clear relationships with viral kinetics.

Strengths:

The cohorts are well developed, the mathematical model appears to capture shedding kinetics fairly well, the clustering seems generally appropriate, and the machine learning analysis is a sensible, albeit exploratory approach. The micro-RNA analysis is interesting and novel.

Weaknesses:

The conclusions of the paper are somewhat supported by the data but there are certain limitations that are notable and make the study's findings of only limited relevance to current COVID-19 epidemiology and clinical conditions.

We sincerely appreciate the reviewer’s thoughtful and constructive comments, which have been invaluable in improving the quality of our study. We have carefully revised the manuscript to address all points raised.

(1) The study only included previously uninfected, unvaccinated individuals without the omicron variant. It has been well documented that vaccination and prior infection both predict shorter duration shedding. Therefore, the study results are no longer relevant to current COVID-19 conditions. This is not at all the authors' fault but rather a difficult reality of much retrospective COVID research.

Thank you for your comment. We agree with the review’s comment that some of our results could not provide insight into the current COVID-19 conditions since most people have either already been infected with COVID-19 or have been vaccinated. We revised our manuscript to discuss this (page 22, lines 364-368). Nevertheless, we believe it is novel that we have extensively investigated the relationship between viral shedding patterns in saliva and a wide range of clinical and microRNA data, and that developing a method to do so remains important. This is important for providing insight into early responses to novel emerging viral diseases in the future. Therefore, we still believe that our findings are valuable.

(2) The target cell model, which appears to fit the data fairly well, has clear mechanistic limitations. Specifically, if such a high proportion of cells were to get infected, then the disease would be extremely severe in all cases. The authors could specify that this model was selected for ease of use and to allow clustering, rather than to provide mechanistic insight. It would be useful to list the AIC scores of this model when compared to the model by Ke.

Thank you for your feedback and suggestion regarding our mathematical model. As the reviewer pointed out, in this study, we adopted a simple model (target cell-limited model) to focus on reconstruction of viral dynamics and stratification of shedding patterns rather than exploring the mechanism of viral infection in detail. Nevertheless, we believe that the target cell-limited model provides reasonable reconstructed viral dynamics as it has been used in many previous studies. We revised manuscript to clarify this point (page 10, lines 139-144). Also, we revised our manuscript to provide more detailed description of the model comparison along with information about AIC (page 10, lines 130-135).

(3) Line 104: I don't follow why including both datasets would allow one model to work better than the other. This requires more explanation. I am also not convinced that non-linear mixed effects approaches can really be used to infer early model kinetics in individuals from one cohort by using late viral load kinetics in another (and vice versa). The approach seems better for making populationlevel estimates when there is such a high amount of missing data.

Thank you for your feedback. We recognized that our explanation was insufficient by your comment. We intended to describe that, rather than comparing performance of the two models, data fitting can be performed with same level for both models by including both datasets. We revised the manuscript to clarify this point (page 10, lines 135-139).

Additionally, we agree that nonlinear mixed effects models are a useful approach for performing population-level estimates of missing data. On the other hand, in addition, the nonlinear mixed effects model has the advantage of making the reasonable parameter estimation for each individual with not enough data points by considering the distribution of parameters of other individuals. Paying attention to these advantages, we adopted a nonlinear mixed effects model in our study. We also revised the manuscript to clarify this (page 27, lines 472-483).

(4) Along these lines, the three clusters appear to show uniform expansion slopes whereas the NBA cohort, a much larger cohort that captured early and late viral loads in most individuals, shows substantial variability in viral expansion slopes. In Figure 2D: the upslope seems extraordinarily rapid relative to other cohorts. I calculate a viral doubling time of roughly 1.5 hours. It would be helpful to understand how reliable of an estimate this is and also how much variability was observed among individuals.

We appreciate your detailed feedback on the estimated up-slope of viral dynamics. As the reviewer noted, the pattern differs from that observed in the NBA cohort, which may be due to their measurement of viral load from upper respiratory tract swabs. In our estimation, the mean and standard deviation of the doubling time (defined as ln2/(𝛽𝑇₀𝑝𝑐⁻¹ − 𝛿)) were 1.44 hours and 0.49 hours, respectively. Although direct validation of these values is challenging, several previous studies, including our own, have reported that viral loads in saliva increase more rapidly than in the upper respiratory tract swabs, reaching their peak sooner. Thus, we believe that our findings are consistent with those of previous studies. We revised our manuscript to discuss this point with additional references (page 20, lines 303-311).

(5) A key issue is that a lack of heterogeneity in the cohort may be driving a lack of differences between the groups. Table 1 shows that Sp02 values and lab values that all look normal. All infections were mild. This may make identifying biomarkers quite challenging.

Thank you for your comment regarding heterogeneity in the cohort. Although the NFV cohort was designed for COVID-19 patients who were either mild or asymptomatic, we have addressed this point and revised the manuscript to discuss it (page 21, lines 334-337).

(6) Figure 3A: many of the clinical variables such as basophil count, Cl, and protein have very low pre-test probability of correlating with virologic outcome.

Thank you for your comment regarding some clinical information we used in our study. We revised our manuscript to discuss this point (page 21, lines 337-338).

(7) A key omission appears to be micoRNA from pre and early-infection time points. It would be helpful to understand whether microRNA levels at least differed between the two collection timepoints and whether certain microRNAs are dynamic during infection.

Thank you for your comment regarding the collection of micro-RNA data. As suggested by the reviewer, we compared micro-RNA levels between two time points using pairwise t-tests and Mann-Whitney U tests with FDR correction. As a result, no micro-RNA showed a statistically significant difference. This suggests that micro-RNA levels remain relatively stable during the course of infection, at least for mild or asymptomatic infection, and may therefore serve as a biomarker independent of sampling time. We have revised the manuscript to include this information (page 17, lines 259-262).

(8) The discussion could use a more thorough description of how viral kinetics differ in saliva versus nasal swabs and how this work complements other modeling studies in the field.

We appreciate the reviewer’s thoughtful feedback. As suggested, we have added a discussion comparing our findings with studies that analyzed viral dynamics using nasal swabs, thereby highlighting the differences between viral dynamics in saliva and in the upper respiratory tract. To ensure a fair and rigorous comparison, we referred to studies that employed the same mathematical model (i.e., Eqs.(1-2)). Accordingly, we revised the manuscript and included additional references (page 20, lines 303-311).

Furthermore, we clarified the significance of our study in two key aspects. First, it provides a detailed analysis of viral dynamics in saliva, reinforcing our previous findings from a single cohort by extending them across multiple cohorts. Second, this study uniquely examines whether viral dynamics in saliva can be directly predicted by exploring diverse clinical data and micro-RNAs. Notably, cohorts that have simultaneously collected and reported both viral load and a broad spectrum of clinical data from the same individuals, as in our study, are exceedingly rare. We revised the manuscript to clarify this point (page 20, lines 302-311).

(9) The most predictive potential variables of shedding heterogeneity which pertain to the innate and adaptive immune responses (virus-specific antibody and T cell levels) are not measured or modeled.

Thank you for your comment. We agree that antibody and T cell related markers may serve as the most powerful predictors, as supported by our own study [S. Miyamoto et al., PNAS (2023), ref. 24] as well as previous reports. While this point was already discussed in the manuscript, we have revised the text to make it more explicit (page 21, lines 327-328).

(10) I am curious whether the models infer different peak viral loads, duration, expansion, and clearance slopes between the 2 cohorts based on fitting to different infection stage data.

Thank you for your comment. We compared features between 2 cohorts as reviewer suggested. As a result, a statistically significant difference between the two cohorts (i.e., p-value ≤ 0.05 from the t-test) was observed only at the peak viral load, with overall trends being largely similar. At the peak, the mean value was 7.5 log₁₀ (copies/mL) in the Japan cohort and 8.1 log₁₀ (copies/mL) in the Illinois cohort, with variances of 0.88 and 0.87, respectively, indicating comparable variability.

Reviewer #2 (Public review)

Summary:

This study argues it has found that it has stratified viral kinetics for saliva specimens into three groups by the duration of "viral shedding"; the authors could not identify clinical data or microRNAs that correlate with these three groups.

Strengths:

The question of whether there is a stratification of viral kinetics is interesting.

Weaknesses:

The data underlying this work are not treated rigorously. The work in this manuscript is based on PCR data from two studies, with most of the data coming from a trial of nelfinavir (NFV) that showed no effect on the duration of SARS-CoV-2 PCR positivity. This study had no PCR data before symptom onset, and thus exclusively evaluated viral kinetics at or after peak viral loads. The second study is from the University of Illinois; this data set had sampling prior to infection, so has some ability to report the rate of "upswing." Problems in the analysis here include:

We are grateful to the reviewer for the constructive feedback, which has greatly enhanced the quality of our study. In response, we have carefully revised the manuscript to address all comments.

The PCR Ct data from each study is treated as equivalent and referred to as viral load, without any reports of calibration of platforms or across platforms. Can the authors provide calibration data and justify the direct comparison as well as the use of "viral load" rather than "Ct value"? Can the authors also explain on what basis they treat Ct values in the two studies as identical?

Thank you for your comment regarding description of viral load data. We recognized the lack of explanation for the integration of viral load data by reviewer's comment. We calculated viral load from Ct value using linear regression equations between Ct and viral load for each study's measurement method, respectively. We revised the manuscript to clarify this point in the section of Saliva viral load data in Methods.

The limit of detection for the NFV PCR data was unclear, so the authors assumed it was the same as the University of Illinois study. This seems a big assumption, as PCR platforms can differ substantially. Could the authors do sensitivity analyses around this assumption?

Thank you for your comment regarding the detection limit for viral load data. As reviewer suggested, we conducted sensitivity analysis for assumption of detection limit for the NFV dataset. Specifically, we performed data fitting in the same manner for two scenarios: when the detection limit of NFV PCR was lower (0 log₁₀ copies/mL) or higher (2 log₁₀ copies/mL) than that of the Illinois data (1.08 log₁₀ copies/mL), and compared the results.

As a result, we obtained largely comparable viral dynamics in most cases (Supplementary Fig 6). When comparing the AIC values, we observed that the AIC for the same censoring threshold was 6836, whereas it increased to 7403 under the low censoring threshold and decreased to 6353 under the higher censoring threshold. However, this difference may be attributable to the varying number of data points treated as below the detection limit. Specifically, when the threshold is set higher, more data are treated as below the detection limit, which may result in a more favorable error calculation. To discuss this point, we have added a new figure (Supplementary Fig 6) and revised the manuscript accordingly (page 25, lines 415-418).

The authors refer to PCR positivity as viral shedding, but it is viral RNA detection (very different from shedding live/culturable virus, as shown in the Ke et al. paper). I suggest updating the language throughout the manuscript to be precise on this point.

We appreciate the reviewer’s feedback regarding the terminology used for viral shedding. In response, we have revised all instances of “viral shedding” to “viral RNA detection” throughout the manuscript as suggested.

Eyeballing extended data in Figure 1, a number of the putative long-duration infections appear to be likely cases of viral RNA rebound (for examples, see S01-16 and S01-27). What happens if all the samples that look like rebound are reanalyzed to exclude the late PCR detectable time points that appear after negative PCRs?

We sincerely thank the reviewer for the valuable suggestion. In response, we established a criterion to remove data that appeared to exhibit rebound and subsequently performed data fitting

(see Author response image 1 below). The criterion was defined as: “any data that increase again after reaching the detection limit in two measurements are considered rebound and removed.” As a result, 15 out of 144 cases were excluded due to insufficient usable data, leaving 129 cases for analysis. Using a single detection limit as the criterion would have excluded too many data points, while defining the criterion solely based on the magnitude of increase made it difficult to establish an appropriate “threshold for increase.”

The fitting result indicates that the removal of rebound data may influence the fitting results; however, direct comparison of subsequent analyses, such as clustering, is challenging due to the reduced sample size. Moreover, the results can vary substantially depending on the criterion used to define rebound, and establishing a consistent standard remains difficult. Accordingly, we retained the current analysis and have added a discussion of rebound phenomena in the Discussion section as a limitation (page 22, lines 355-359). We once again sincerely appreciate the reviewer’s insightful and constructive suggestion.

Author response image 1.

Comparison of model fits before and after removing data suspected of rebound. Black dots represent observed measurements, and the black and yellow curves show the fitted viral dynamics for the full dataset and the dataset with rebound data removed, respectively.

There's no report of uncertainty in the model fits. Given the paucity of data for the upslope, there must be large uncertainty in the up-slope and likely in the peak, too, for the NFV data. This uncertainty is ignored in the subsequent analyses. This calls into question the efforts to stratify by the components of the viral kinetics. Could the authors please include analyses of uncertainty in their model fits and propagate this uncertainty through their analyses?

We sincerely appreciate the reviewer’s detailed feedback on model uncertainty. To address this point, we revised Extended Fig 1 (now renumbered as Supplementary Fig 1) to include 95% credible intervals computed using a bootstrap approach. In addition, to examine the potential impact of model uncertainty on stratified analyses, we reconstructed the distance matrix underlying stratification by incorporating feature uncertainty. Specifically, for each individual, we sampled viral dynamics within the credible interval and averaged the resulting feature, and build the distance matrix using it. We then compared this uncertainty-adjusted matrix with the original one using the Mantel test, which showed a strong correlation (r = 0.72, p < 0.001). Given this result, we did not replace the current stratification but revised the manuscript to provide this information through Result and Methods sections (page 11, lines 159-162 and page 28, lines 512-519). Once again, we are deeply grateful for this insightful comment.

The clinical data are reported as a mean across the course of an infection; presumably vital signs and blood test results vary substantially, too, over this duration, so taking a mean without considering the timing of the tests or the dynamics of their results is perplexing. I'm not sure what to recommend here, as the timing and variation in the acquisition of these clinical data are not clear, and I do not have a strong understanding of the basis for the hypothesis the authors are testing.

We appreciate the reviewers' feedback on the clinical data. We recognized that the manuscript lacked description of the handling of clinical data by your comment. In this research, we focused on finding “early predictors” which could provide insight into viral shedding patterns. Thus, we used clinical data measured in the earliest time (date of admission) for each patient. Another reason is that the date of admission is the almost only time point at which complete clinical data without any missing values are available for all participants. We revised our manuscript to clarify this point (page 5, lines 90-95).

It's unclear why microRNAs matter. It would be helpful if the authors could provide more support for their claims that (1) microRNAs play such a substantial role in determining the kinetics of other viruses and (2) they play such an important role in modulating COVID-19 that it's worth exploring the impact of microRNAs on SARS-CoV-2 kinetics. A link to a single review paper seems insufficient justification. What strong experimental evidence is there to support this line of research?

We appreciate the reviewer’s comments regarding microRNA. Based on this feedback, we recognized the need to clarify our rationale for selecting microRNAs as the analyte. The primary reason was that our available specimens were saliva, and microRNAs are among the biomarkers that can be reliably measured in saliva. At the same time, previous studies have reported associations between microRNAs and various diseases, which led us to consider the potential relevance of microRNAs to viral dynamics, beyond their role as general health indicators. To better reflect this context, we have added supporting references (page 17, lines 240-243).

Reviewer #3 (Public review)

The article presents a comprehensive study on the stratification of viral shedding patterns in saliva among COVID-19 patients. The authors analyze longitudinal viral load data from 144 mildly symptomatic patients using a mathematical model, identifying three distinct groups based on the duration of viral shedding. Despite analyzing a wide range of clinical data and micro-RNA expression levels, the study could not find significant predictors for the stratified shedding patterns, highlighting the complexity of SARS-CoV-2 dynamics in saliva. The research underscores the need for identifying biomarkers to improve public health interventions and acknowledges several limitations, including the lack of consideration of recent variants, the sparsity of information before symptom onset, and the focus on symptomatic infections. 

The manuscript is well-written, with the potential for enhanced clarity in explaining statistical methodologies. This work could inform public health strategies and diagnostic testing approaches. However, there is a thorough development of new statistical analysis needed, with major revisions to address the following points:

We sincerely appreciate the thoughtful feedback provided by Reviewer #3, particularly regarding our methodology. In response, we conducted additional analyses and revised the manuscript accordingly. Below, we address the reviewer’s comments point by point.

(1) Patient characterization & selection: Patient immunological status at inclusion (and if it was accessible at the time of infection) may be the strongest predictor for viral shedding in saliva. The authors state that the patients were not previously infected by SARS-COV-2. Was Anti-N antibody testing performed? Were other humoral measurements performed or did everything rely on declaration? From Figure 1A, I do not understand the rationale for excluding asymptomatic patients. Moreover, the mechanistic model can handle patients with only three observations, why are they not included? Finally, the 54 patients without clinical data can be used for the viral dynamics fitting and then discarded for the descriptive analysis. Excluding them can create a bias. All the discarded patients can help the virus dynamics analysis as it is a population approach. Please clarify. In Table 1 the absence of sex covariate is surprising.

We appreciate the detailed feedback from the reviewer regarding patient selection. We relied on the patient's self-declaration to determine the patient's history of COVID-19 infection and revised the manuscript to specify this (page 6, lines 83-84).

In parameter estimation, we used the date of symptom onset for each patient so that we establish a baseline of the time axis as clearly as possible, as we did in our previous works. Accordingly, asymptomatic patients who do not have information on the date of symptom onset were excluded from the analysis. Additionally, in the cohort we analyzed, for patients excluded due to limited number of observations (i.e., less than 3 points), most patients already had a viral load close to the detection limit at the time of the first measurement. This is due to the design of clinical trial, as if a negative result was obtained twice in a row, no further follow-up sampling was performed. These patients were excluded from the analysis because it hard to get reasonable fitting results. Also, we used 54 patients for the viral dynamics fitting and then only used the NFV cohort for clinical data analysis. We acknowledge that our description may have confused readers. We revised our manuscript to clarify these points regarding patient selecting for data fitting (page 6, lines 96-102, page 24, lines 406-407, and page 7, lines 410-412). In addition, we realized, thanks to the reviewer’s comment, that gender information was missing in Table 1. We appreciate this observation and have revised the table to include gender (we used gender in our analysis). 

(2) Exact study timeline for explanatory covariates: I understand the idea of finding « early predictors » of long-lasting viral shedding. I believe it is key and a great question. However, some samples (Figure 4A) seem to be taken at the end of the viral shedding. I am not sure it is really easier to micro-RNA saliva samples than a PCR. So I need to be better convinced of the impact of the possible findings. Generally, the timeline of explanatory covariate is not described in a satisfactory manner in the actual manuscript. Also, the evaluation and inclusion of the daily symptoms in the analysis are unclear to me.

We appreciate the reviewer’s feedback regarding the collection of explanatory variables. As noted, of the two microRNA samples collected from each patient, one was obtained near the end of viral shedding. This was intended to examine potential differences in microRNA levels between the early and late phases of infection. No significant differences were observed between the two time points, and using microRNA from either phase alone or both together did not substantially affect predictive accuracy for stratified groups. Furthermore, microRNA collection was motivated primarily by the expectation that it would be more sensitive to immune responses, rather than by ease of sampling. We have revised the manuscript to clarify these points regarding microRNA (page 17, lines 243-245 and 259-262).

Furthermore, as suggested by the reviewer, we have also strengthened the explanation regarding the collection schedule of clinical information and the use of daily symptoms in the analysis (page 6, lines 90-95, page 14, lines 218-220,).

(3) Early Trajectory Differentiation: The model struggles to differentiate between patients' viral load trajectories in the early phase, with overlapping slopes and indistinguishable viral load peaks observed in Figures 2B, 2C, and 2D. The question arises whether this issue stems from the data, the nature of Covid-19, or the model itself. The authors discuss the scarcity of pre-symptom data, primarily relying on Illinois patients who underwent testing before symptom onset. This contrasts earlier statements on pages 5-6 & 23, where they claim the data captures the full infection dynamics, suggesting sufficient early data for pre-symptom kinetics estimation. The authors need to provide detailed information on the number or timing of patient sample collections during each period.

Thank you for the reviewer’s thoughtful comments. The model used in this study [Eqs.(1-2)] has been employed in numerous prior studies and has successfully identified viral dynamics at the individual level. In this context, we interpret the rapid viral increase observed across participants as attributable to characteristics of SARS-CoV-2 in saliva, an interpretation that has also been reported by multiple previous studies. We have added the relevant references and strengthened the corresponding discussion in the manuscript (page 20, lines 303-311).

We acknowledge that our explanation of how the complementary relationship between the two cohorts contributes to capturing infection dynamics was not sufficiently clear. As described in the manuscript, the Illinois cohort provides pre-symptomatic data, whereas the NFV cohort offers abundant end-phase data, thereby compensating for each other’s missing phases. By jointly analyzing the two cohorts with a nonlinear mixed-effects model, we estimated viral dynamics at the individual-level. This approach first estimates population-level parameters (fixed effects) using data from all participants and then incorporates random effects to account for individual variability, yielding the most plausible parameter values.

Thus, even when early-phase data are lacking in the NFV cohort, information from the Illinois cohort allows us to infer most reasonable dynamics, and the reverse holds true for the end phase. In this context, we argued that combining the two cohorts enables mathematical modeling to capture infection dynamics at the individual level. Recognizing that our earlier description could be misleading, we have carefully reinforced the relevant description (page 27, lines 472-483). In addition, as suggested by the reviewer, we have added information on the number of data samples available for each phase in both cohorts (page 7, lines 106-109).

(4) Conditioning on the future: Conditioning on the future in statistics refers to the problematic situation where an analysis inadvertently relies on information that would not have been available at the time decisions were made or data were collected. This seems to be the case when the authors create micro-RNA data (Figure 4A). First, when the sampling times are is something that needs to be clarified by the authors (for clinical outcomes as well). Second, proper causal inference relies on the assumption that the cause precedes the effect. This conditioning on the future may result in overestimating the model's accuracy. This happens because the model has been exposed to the outcome it's supposed to predict. This could question the - already weak - relation with mir-1846 level.

We appreciate the reviewer’s detailed feedback. As noted in Reply to Comments 2, we collected micro-RNA samples at two time points, near the peak of infection dynamics and at the end stage, and found no significant differences between them. This suggests that micro-RNA levels are not substantially affected by sampling time. Indeed, analyses conducted using samples from the peak, late stage, or both yielded nearly identical results in relation to infection dynamics. To clarify this point, we revised the manuscript by integrating this explanation with our response in Reply to Comments 2 (page 17, lines 259-262). In addition, now we also revised manuscript to clarify sampling times of clinical information and micro-RNA (page 6, lines 90-95).

(5) Mathematical Model Choice Justification and Performance: The paper lacks mention of the practical identifiability of the model (especially for tau regarding the lack of early data information). Moreover, it is expected that the immune effector model will be more useful at the beginning of the infection (for which data are the more parsimonious). Please provide AIC for comparison, saying that they have "equal performance" is not enough. Can you provide at least in a point-by-point response the VPC & convergence assessments?

We appreciate the reviewer’s detailed feedback regarding the mathematical model. We acknowledge the potential concern regarding the practical identifiability of tau (incubation period), particularly given the limited early-phase data. In our analysis, however, the nonlinear mixed-effects model yielded a population-level estimate of 4.13 days, which is similar with previously reported incubation periods for COVID-19. This concordance suggests that our estimate of tau is reasonable despite the scarcity of early data.

For model comparison, first, we have added information on the AIC of the two models to the manuscript as suggested by the reviewer (page 10, lines 130-135). One point we would like to emphasize is that we adopted a simple target cell-limited model in this study, aiming to focus on reconstruction of viral dynamics and stratification of shedding patterns rather than exploring the mechanism of viral infection in detail. Nevertheless, we believe that the target cell-limited model provides reasonable reconstructed viral dynamics as it has been used in many previous studies. We revised manuscript to clarify this (page 10, lines 135-144). 

Furthermore, as suggested, we have added the VPC and convergence assessment results for both models, together with explanatory text, to the manuscript (Supplementary Fig 2, Supplementary Fig 3, and page 10, lines 130-135). In the VPC, the observed 5th, 50th, and 95th percentiles were generally within the corresponding simulated prediction intervals across most time points. Although minor deviations were noted in certain intervals, the overall distribution of the observed data was well captured by the models, supporting their predictive performance (Supplementary Fig 2). In addition, the log-likelihood and SAEM parameter trajectories stabilized after the burn-in phase, confirming appropriate convergence (Supplementary Fig 3).

(6) Selected features of viral shedding: I wonder to what extent the viral shedding area under the curve (AUC) and normalized AUC should be added as selected features.

We sincerely appreciate the reviewer’s valuable suggestion regarding the inclusion of additional features. Following this recommendation, we considered AUC (or normalized AUC) as an additional feature when constructing the distance matrix used for stratification. We then evaluated the similarity between the resulting distance matrix and the original one using the Mantel test, which showed a very high correlation (r = 0.92, p < 0.001). This indicates that incorporating AUC as an additional feature does not substantially alter the distance matrix. Accordingly, we have decided to retain the current stratification analysis, and we sincerely thank the reviewer once again for this interesting suggestion.

(7) Two-step nature of the analysis: First you fit a mechanistic model, then you use the predictions of this model to perform clustering and prediction of groups (unsupervised then supervised). Thus you do not propagate the uncertainty intrinsic to your first estimation through the second step, ie. all the viral load selected features actually have a confidence bound which is ignored. Did you consider a one-step analysis in which your covariates of interest play a direct role in the parameters of the mechanistic model as covariates? To pursue this type of analysis SCM (Johnson et al. Pharm. Res. 1998), COSSAC (Ayral et al. 2021 CPT PsP), or SAMBA ( Prague et al. CPT PsP 2021) methods can be used. Did you consider sampling on the posterior distribution rather than using EBE to avoid shrinkage?

Thank you for the reviewer’s detailed suggestions regarding our analysis. We agree that the current approach does not adequately account for the impact of uncertainty in viral dynamics on the stratified analyses. As a first step, we have revised Extended Data Fig 1 (now renumbered as Supplementary Fig 1) to include 95% credible intervals computed using a bootstrap approach, to present the model-fitting uncertainty more explicitly. Then, to examine the potential impact of model uncertainty on stratified analyses, we reconstructed the distance matrix underlying stratification by incorporating feature uncertainty. Specifically, for each individual, we sampled viral dynamics within the credible interval and averaged the resulting feature, and build the distance matrix using it. We then compared this uncertainty-adjusted matrix with the original one using the Mantel test, which showed a strong correlation (r = 0.72, p < 0.001). Given this result, we did not replace the current stratification but revised the manuscript to provide this information (page 11, lines 159-162 and page 28, 512-519).

Furthermore, we carefully considered the reviewer’s proposed one-step analysis. However, implementation was constrained by data-fitting limitations. Concretely, clinical information is available only in the NFV cohort. Thus, if these variables are to be entered directly as covariates on the parameters, the Illinois cohort cannot be included in the data-fitting process. Yet the NFV cohort lacks any pre-symptomatic observations, so fitting the model to that cohort alone does not permit a reasonable (well-identified/robust) fitting result. While we were unable to implement the suggestion under the current data constraints, we sincerely appreciate the reviewer’s thoughtful and stimulating proposal.

(8) Need for advanced statistical methods: The analysis is characterized by a lack of power. This can indeed come from the sample size that is characterized by the number of data available in the study. However, I believe the power could be increased using more advanced statistical methods. At least it is worth a try. First considering the unsupervised clustering, summarizing the viral shedding trajectories with features collapses longitudinal information. I wonder if the R package « LongituRF » (and associated method) could help, see Capitaine et al. 2020 SMMR. Another interesting tool to investigate could be latent class models R package « lcmm » (and associated method), see ProustLima et al. 2017 J. Stat. Softwares. But the latter may be more far-reached.

Thank you for the reviewer’s thoughtful suggestions regarding our unsupervised clustering approach. The R package “LongitiRF” is designed for supervised analysis, requiring a target outcome to guide the calculation of distances between individuals (i.e., between viral dynamics). In our study, however, the goal was purely unsupervised clustering, without any outcome variable, making direct application of “LongitiRF” challenging.

Our current approach (summarizing each dynamic into several interpretable features and then using Random Forest proximities) allows us to construct a distance matrix in an unsupervised manner. Here, the Random Forest is applied in “proximity mode,” focusing on how often dynamics are grouped together in the trees, independent of any target variable. This provides a practical and principled way to capture overall patterns of dynamics while keeping the analysis fully unsupervised.

Regarding the suggestion to use latent class mixed models (R package “lcmm”), we also considered this approach. In our dataset, each subject has dense longitudinal measurements, and at many time points, trajectories are very similar across subjects, resulting in minimal inter-individual differences. Consequently, fitting multi-class latent class mixed models (ng ≥ 2) with random effects or mixture terms is numerically unstable, often producing errors such as non-positive definite covariance matrices or failure to generate valid initial values. Although one could consider using only the time points with the largest differences, this effectively reduces the analysis to a feature-based summary of dynamics. Such an approach closely resembles our current method and contradicts the goal of clustering based on full longitudinal information.

Taken together, although we acknowledge that incorporating more longitudinal information is important, we believe that our current approach provides a practical, stable, and informative solution for capturing heterogeneity in viral dynamics. We would like to once again express our sincere gratitude to the reviewer for this insightful suggestion.

(9) Study intrinsic limitation: All the results cannot be extended to asymptomatic patients and patients infected with recent VOCs. It definitively limits the impact of results and their applicability to public health. However, for me, the novelty of the data analysis techniques used should also be taken into consideration.

We appreciate your positive evaluation of our research approach and acknowledge that, as noted in the Discussion section as our first limitation, our analysis may not provide valid insights into recent VOCs or all populations, including asymptomatic individuals. Nonetheless, we believe it is novel that we extensively investigated the relationship between viral shedding patterns in saliva and a wide range of clinical and micro-RNA data. Our findings contribute to a deeper and more quantitative understanding of heterogeneity in viral dynamics, particularly in saliva samples. To discuss this point, we revised our manuscript (page 22, lines 364-368).

Strengths are:

Unique data and comprehensive analysis.

Novel results on viral shedding.

Weaknesses are:

Limitation of study design.

The need for advanced statistical methodology.

Reviewer #1 (Recommendations For The Authors):

Line 8: In the abstract, it would be helpful to state how stratification occurred.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 2, lines 8-11).

Line 31 and discussion: It is important to mention the challenges of using saliva as a specimen type for lab personnel.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 36-41).

Line 35: change to "upper respiratory tract".

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, line 35).

Line 37: "Saliva" is not a tissue. Please hazard a guess as to which tissue is responsible for saliva shedding and if it overlaps with oral and nasal swabs.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 42-45).

Line 42, 68: Please explain how understanding saliva shedding dynamics would impact isolation & screening, diagnostics, and treatments. This is not immediately intuitive to me.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 3, lines 48-50).

Line 50: It would be helpful to explain why shedding duration is the best stratification variable.

We thank the reviewer for the feedback. We acknowledge that our wording was ambiguous. The clear differences in the viral dynamics patterns pertain to findings observed following the stratification, and we have revised the manuscript to make this explicit (page 4, lines 59-61).

Line 71: Dates should be listed for these studies.

We thank the reviewer for the feedback, and have revised the manuscript accordingly (page 6, lines 85-86).

Reviewer #2 (Recommendations For The Authors):

Please make all code and data available for replication of the analyses.

We appreciate the suggestion. Due to ethical considerations, it is not possible to make all data and code publicly available. We have clearly stated in the manuscript about it (Data availability section in Methods).

Reviewer #3 (Recommendations For The Authors):

Here are minor comments / technical details:

(1) Figure 1B is difficult to understand.

Thank you for the comment. We updated Fig 1B to incorporate more information to aid interpretation.

(2) Did you analyse viral load or the log10 of viral load? The latter is more common. You should consider it. SI Figure 1 please plot in log10 and use a different point shape for censored data. The file quality of this figure should be improved. State in the material and methods if SE with moonlit are computed with linearization or importance sampling.

Thank you for the comment. We conducted our analyses using log10-transformed viral load. Also, we revised Supplementary Fig 1 (now renumbered as Supplementary Fig 4) as suggested. We also added Supplementary Fig 3 and clarified in the Methods that standard errors (SE) were obtained in Monolix from the Fisher information matrix using the linearization method (page 28, lines 498-499).

(3) Table 1 and Figure 3A could be collapsed.

Thank you for the comment, and we carefully considered this suggestion. Table 1 summarizes clinical variables by category, whereas Fig 3A visualizes them ordered by p-value of statistical analysis. Collapsing these into a single table would make it difficult to apprehend both the categorical summaries and the statistical ranking at a glance, thereby reducing readability. We therefore decided to retain the current layout. We appreciate the constructive feedback again. 

(4) Figure 3 legend could be clarified to understand what is 3B and 3C.

We thank the reviewer for the feedback and have reinforced the description accordingly.

(5) Why use AIC instead of BICc?

Thank you for your comment. We also think BICc is a reasonable alternative. However, because our objective is predictive adequacy (reconstruction of viral dynamics), we judged AIC more appropriate. In NLMEM settings, the effective sample size required by BICc is ambiguous, making the penalty somewhat arbitrary. Moreover, since the two models reconstruct very similar dynamics, our conclusions are not sensitive to the choice of criterion.

(6) Bibliography. Most articles are with et al. (which is not standard) and some are with an extended list of names. Provide DOI for all.

We thank the reviewer for the feedback, and have revised the manuscript accordingly.

(7) Extended Table 1&2 - maybe provide a color code to better highlight some lower p-values (if you find any interesting).

We thank the reviewer for the feedback. Since no clinical information and micro-RNAs other than mir-1846 showed low p-values, we highlighted only mir-1846 with color to make it easier to locate.

(8) Please make the replication code available.

We appreciate the suggestion. Due to ethical considerations, it is not possible to make all data and code publicly available. We have clearly stated in the manuscript about it (Data availability section in Methods).

Author response:

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

Reviewer #1 (Public review): 

Summary: 

In this work, van Paassen et al. have studied how CD8 T cell functionality and levels predict HIV DNA decline. The article touches on interesting facets of HIV DNA decay, but ultimately comes across as somewhat hastily done and not convincing due to the major issues. 

(1) The use of only 2 time points to make many claims about longitudinal dynamics is not convincing. For instance, the fact that raw data do not show decay in intact, but do for defective/total, suggests that the present data is underpowered. The authors speculate that rising intact levels could be due to patients who have reservoirs with many proviruses with survival advantages, but this is not the parsimonious explanation vs the data simply being noisy without sufficient longitudinal follow-up. n=12 is fine, or even reasonably good for HIV reservoir studies, but to mitigate these issues would likely require more time points measured per person. 

(1b) Relatedly, the timing of the first time point (6 months) could be causing a number of issues because this is in the ballpark for when the HIV DNA decay decelerates, as shown by many papers. This unfortunate study design means some of these participants may already have stabilized HIV DNA levels, so earlier measurements would help to observe early kinetics, but also later measurements would be critical to be confident about stability. 

The main goal of the present study was to understand the relationship of the HIV-specific CD8 T-cell responses early on ART with the reservoir changes across the subsequent 2.5-year period on suppressive therapy. We have revised the manuscript in order to clarify this.  We chose these time points because the 24 week time point is past the initial steep decline of HIV DNA, which takes place in the first weeks after ART initiation. It is known that HIV DNA continues to decay for years after (Besson, Lalama et al. 2014, Gandhi, McMahon et al. 2017). 

(2) Statistical analysis is frequently not sufficient for the claims being made, such that overinterpretation of the data is problematic in many places. 

(2a) First, though plausible that cd8s influence reservoir decay, much more rigorous statistical analysis would be needed to assert this directionality; this is an association, which could just as well be inverted (reservoir disappearance drives CD8 T cell disappearance). 

To correlate different reservoir measures between themselves and with CD8+ T-cell responses at 24 and 156 weeks, we now performed non-parametric (Spearman) correlation analyses, as they do not require any assumptions about the normal distribution of the independent and dependent variables. Benjamini-Hochberg corrections for multiple comparisons (false discovery rate, 0.25) were included in the analyses and did not change the results. 

Following this comment we would like to note that the association between the T-cell response at 24 weeks and the subsequent decrease in the reservoir cannot be bi-directional (that can only be the case when both variables are measured at the same time point). Therefore, to model the predictive value of T-cell responses measured at 24 weeks for the decrease in the reservoir between 24 and 156 weeks, we fitted generalized linear models (GLM), in which we included age and ART regimen, in addition to three different measures of HIV-specific CD8+ T-cell responses, as explanatory variables, and changes in total, intact, and total defective HIV DNA between 24 and 156 weeks ART as dependent variables.

(2b) Words like "strong" for correlations must be justified by correlation coefficients, and these heat maps indicate many comparisons were made, such that p-values must be corrected appropriately. 

We have now used Spearman correlation analysis, provided correlation coefficients to justify the wording, and adjusted the p-values for multiple comparisons (Fig. 1, Fig 3., Table 2). Benjamini-Hochberg corrections for multiple comparisons (false discovery rate, 0.25) were included in the analyses and did not change the results.  

(3) There is not enough introduction and references to put this work in the context of a large/mature field. The impacts of CD8s in HIV acute infection and HIV reservoirs are both deep fields with a lot of complexity. 

Following this comment we have revised and expanded the introduction to put our work more in the context of the field (CD8s in acute HIV and HIV reservoirs). 

Reviewer #2 (Public review): 

Summary: 

This study investigated the impact of early HIV specific CD8 T cell responses on the viral reservoir size after 24 weeks and 3 years of follow-up in individuals who started ART during acute infection. Viral reservoir quantification showed that total and defective HIV DNA, but not intact, declined significantly between 24 weeks and 3 years post-ART. The authors also showed that functional HIV-specific CD8⁺ T-cell responses persisted over three years and that early CD8⁺ T-cell proliferative capacity was linked to reservoir decline, supporting early immune intervention in the design of curative strategies. 

Strengths: 

The paper is well written, easy to read, and the findings are clearly presented. The study is novel as it demonstrates the effect of HIV specific CD8 T cell responses on different states of the HIV reservoir, that is HIV-DNA (intact and defective), the transcriptionally active and inducible reservoir. Although small, the study cohort was relevant and well-characterized as it included individuals who initiated ART during acute infection, 12 of whom were followed longitudinally for 3 years, providing unique insights into the beneficial effects of early treatment on both immune responses and the viral reservoir. The study uses advanced methodology. I enjoyed reading the paper. 

Weaknesses: 

All participants were male (acknowledged by the authors), potentially reducing the generalizability of the findings to broader populations. A control group receiving ART during chronic infection would have been an interesting comparison. 

We thank the reviewer for their appreciation of our study. Although we had indeed acknowledged the fact that all participants were male, we have clarified why this is a limitation of the study (Discussion, lines 296-298). The reviewer raises the point that it would be useful to compare our data to a control group. Unfortunately, these samples are not yet available, but our study protocol allows for a control group (chronic infection) to ensure we can include a control group in the future.

Reviewer #1 (Recommendations for the authors): 

Minor: 

On the introduction: 

(1) One large topic that is mostly missing completely is the emerging evidence of selection on HIV proviruses during ART from the groups of Xu Yu and Matthias Lichterfeld, and Ya Chi Ho, among others. 

Previously, it was only touched upon in the Discussion. Now we have also included this in the Introduction (lines 77-80).

(2) References 4 and 5 don't quite match with the statement here about reservoir seeding; we don't completely understand this process, and certainly, the tissue seeding aspect is not known. 

Line 61-62: references were changed and this paragraph was rewritten to clarify.

(3) Shelton et al. showed a strong relationship with HIV DNA size and timing of ART initiation across many studies. I believe Ananwaronich also has several key papers on this topic. 

References by Ananwaronich are included (lines 91-94).

(4) "the viral levels decline within weeks of AHI", this is imprecise, there is a peak and a decline, and an equilibrium. 

We agree and have rewritten the paragraph accordingly.

(5) The impact of CD8 cells on viral evolution during primary infection is complex and likely not relevant for this paper. 

We have left viral evolution out of the introduction in order to keep a focus on the current subject.

(6) The term "reservoir" is somewhat polarizing, so it might be worth mentioning somewhere exactly what you think the reservoir is, I think, as written, your definition is any HIV DNA in a person on ART? 

Indeed, we refer to the reservoir when we talk about the several aspects of the reservoir that we have quantified with our assays (total HIV DNA, unspliced RNA, intact and defective proviral DNA, and replication-competent virus). In most instances we try to specify which measurement we are referring to. We have added additional reservoir explanation to clarify our definition to the introduction (lines 55-58).

(7) I think US might be used before it is defined. 

We thank the reviewer for this notification, we have now also defined it in the Results section (line 131).

(8) In Figure 1 it's also not clear how statistics were done to deal with undetectable values, which can be tricky but important. 

We have now clarified this in the legend to Figure 2 (former Figure 1). Paired Wilcoxon tests were performed to test the significance of the differences between the time points. Pairs where both values were undetectable were always excluded from the analysis. Pairs where one value was undetectable and its detection limit was higher than the value of the detectable partner, were also excluded from the analysis. Pairs where one value was undetectable and its detection limit was lower than the value of the detectable partner, were retained in the analysis.

In the discussion: 

(1) "This confirms that the existence of a replication-competent viral reservoir is linked to the presence of intact HIV DNA." I think this statement is indicative of many of the overinterpretations without statistical justification. There are 4 of 12 individuals with QVOA+ detectable proviruses, which means there are 8 without. What are their intact HIV DNA levels? 

We thank the reviewer for the question that is raised here. We have now compared the intact DNA levels (measured by IPDA) between participants with positive vs. negative QVOA output, and observed a significant difference. We rephrased the wording as follows: “We compared the intact HIV DNA levels at the 24-week timepoint between the six participants, from whom we were able to isolate replicating virus, and the fourteen participants, from whom we could not. Participants with positive QVOA had significantly higher intact HIV DNA levels than those with negative QVOA (p=0.029, Mann-Whitney test; Suppl. Fig. 3). Five of six participants with positive QVOA had intact DNA levels above 100 copies/106 PBMC, while thirteen of fourteen participants with negative QVOA had intact HIV DNA below 100 copies/106 PBMC (p=0.0022, Fisher’s exact test). These findings indicate that recovery of replication-competent virus by QVOA is more likely in individuals with higher levels of intact HIV DNA in IPDA, reaffirming a link between the two measurements.”

(2) "To determine whether early HIV-specific CD8+ T-cell responses at 24 weeks were predictive for the change in reservoir size". This is a fundamental miss on correlation vs causation... it could be the inverse. 

We thank the reviewer for the remark. We have calculated the change in reservoir size (the difference between the reservoir size at 24 weeks and 156 weeks ART) and analyzed if the HIVspecific CD8+ T-cell response at 24 weeks ART are predictive for this change. We do not think it can be inverse, as we have a chronological relationship (CD8+ responses at week 24 predict the subsequent change in the reservoir).

(3) "This may suggest that active viral replication drives the CD8+ T-cell response." I think to be precise, you mean viral transcription drives CD8s, we don't know about the full replication cycle from these data. 

We agree with the reviewer and have changed “replication” to “transcription” (line 280).

(4) "Remarkably, we observed that the defective HIV DNA levels declined significantly between 24 weeks and 3 years on ART. This is in contrast to previous observations in chronic HIV infection (30)". I don't find this remarkable or in contrast: many studies have analyzed and/or modeled defective HIV DNA decay, most of which have shown some negative slope to defective HIV DNA, especially within the first year of ART. See White et al., Blankson et al., Golob et al., Besson et al., etc In addition, do you mean in long-term suppressed? 

The point we would like to make is that,  compared to other studies, we found a significant, prominent decrease in defective DNA (and not intact DNA) over the course of 3 years, which is in contrast to other studies (where usually the decrease in intact is significant and the decrease in defective less prominent). We have rephrased the wording (lines 227-230) as follows:

“We observed that the defective HIV DNA levels decreased significantly between 24 and 156 weeks of ART. This is different from studies in CHI, where no significant decrease during the first 7 years of ART (Peluso, Bacchetti et al. 2020, Gandhi, Cyktor et al. 2021), or only a significant decrease during the first 8 weeks on ART, but not in the 8 years thereafter, was observed (Nühn, Bosman et al. 2025).”

Reviewer #2 (Recommendations for the authors): 

(1) Page 4, paragraph 2 - will be informative to report the statistics here. 

(2) Page 4, paragraph 4 - "General phenotyping of CD4+ (Suppl. Fig. 3A) and CD8+ (Supplementary Figure 3B) T-cells showed no difference in frequencies of naïve, memory or effector CD8+ T-cells between 24 and 156 weeks." - What did the CD4+ phenotyping show? 

We thank the reviewer for the remark. Indeed, there were also no differences in frequencies of naïve, memory or effector CD4+ T-cells between 24 and 156 weeks. We have added this to the paragraph (now Suppl. Fig 4), lines 166-168.

(3) Page 5, paragraph 3 - "Similarly, a broad HIV-specific CD8+ T-cell proliferative response to at least three different viral proteins was observed in the majority of individuals at both time points" - should specify n=? for the majority of individuals. 

At time point 24 weeks, 6/11 individuals had a response to env, 10/11 to gag, 5/11 to nef, and 4/11 to pol. At 156 weeks, 8/11 to env, 10/11 to gag, 8/11 to nef and 9/11 to pol. We have added this to the text (lines 188-191).

(4) Seven of 22 participants had non-subtype B infection. Can the authors explain the use of the IPDA designed by Bruner et. al. for subtype B HIV, and how this may have affected the quantification in these participants? 

Intact HIV DNA was detectable in all 22 participants. We cannot completely exclude influence of primer/probe-template mismatches on the quantification results, however such mismatches could also have occurred in subtype B participants, and droplet digital PCR that IPDA is based on is generally much less sensitive to these mismatches than qPCR.

(5) Page 7, paragraph 2 - the authors report a difference in findings from a previous study ("a decline in CD8 T cell responses over 2 years" - reference 21), but only provide an explanation for this on page 9. The authors should consider moving the explanation to this paragraph for easier understanding. 

We agree with the reviewer that this causes confusion. Therefore, we have revised and changed the order in the Discussion.

(6) Page 7, paragraph 2 - Following from above, the previous study (21) reported this contradicting finding "a decline in CD8 T cell responses over 2 years" in a CHI (chronic HIV) treated cohort. The current study was in an acute HIV treated cohort. The authors should explain whether this may also have resulted in the different findings, in addition to the use of different readouts in each study.

We thank the reviewer for this attentiveness. Indeed, the study by Takata et al. investigates the reservoir and HIV-specific CD8+ T-cell responses in both the RV254/ SEARCH010 study who initiated ART during AHI and the RV304/ SEARCH013 who initiated ART during CHI. We had not realized that the findings of the decline in CD8 T cell responses were solely found in the RV304/ SEARCH013 (CHI cohort). It appears functional HIV specific immune responses were only measured in AHI at 96 weeks, so we have clarified this in the Discussion. 

Besson, G. J., C. M. Lalama, R. J. Bosch, R. T. Gandhi, M. A. Bedison, E. Aga, S. A. Riddler, D. K. McMahon, F. Hong and J. W. Mellors (2014). "HIV-1 DNA decay dynamics in blood during more than a decade of suppressive antiretroviral therapy." Clin Infect Dis 59(9): 1312-1321.

Gandhi, R. T., J. C. Cyktor, R. J. Bosch, H. Mar, G. M. Laird, A. Martin, A. C. Collier, S. A. Riddler, B. J. Macatangay, C. R. Rinaldo, J. J. Eron, J. D. Siliciano, D. K. McMahon and J. W. Mellors (2021). "Selective Decay of Intact HIV-1 Proviral DNA on Antiretroviral Therapy." J Infect Dis 223(2): 225-233.

Gandhi, R. T., D. K. McMahon, R. J. Bosch, C. M. Lalama, J. C. Cyktor, B. J. Macatangay, C. R. Rinaldo, S. A. Riddler, E. Hogg, C. Godfrey, A. C. Collier, J. J. Eron and J. W. Mellors (2017). "Levels of HIV-1 persistence on antiretroviral therapy are not associated with markers of inflammation or activation." PLoS Pathog 13(4): e1006285.

Nühn, M. M., K. Bosman, T. Huisman, W. H. A. Staring, L. Gharu, D. De Jong, T. M. De Kort, N. Buchholtz, K. Tesselaar, A. Pandit, J. Arends, S. A. Otto, E. Lucio De Esesarte, A. I. M. Hoepelman, R. J. De Boer, J. Symons, J. A. M. Borghans, A. M. J. Wensing and M. Nijhuis (2025). "Selective decline of intact HIV reservoirs during the first decade of ART followed by stabilization in memory T cell subsets." Aids 39(7): 798-811.

Peluso, M. J., P. Bacchetti, K. D. Ritter, S. Beg, J. Lai, J. N. Martin, P. W. Hunt, T. J. Henrich, J. D. Siliciano, R. F. Siliciano, G. M. Laird and S. G. Deeks (2020). "Differential decay of intact and defective proviral DNA in HIV-1-infected individuals on suppressive antiretroviral therapy." JCI Insight 5(4).

Author response:

Reviewer #1 (Public Review):

Summary

We thank the reviewer for the constructive and thoughtful evaluation of our work. We appreciate the recognition of the novelty and potential implications of our findings regarding UPR activation and proteasome activity in germ cells.

(1) The microscopy images look saturated, for example, Figure 1a, b, etc. Is this a normal way to present fluorescent microscopy?

The apparent saturation was not present in the original images, but likely arose from image compression during PDF generation. While the EMA granule was still apparent, in the revised submission, we will provide high-resolution TIFF files to ensure accurate representation of fluorescence intensity and will carefully optimize image display settings to avoid any saturation artifacts.

(2) The authors should ensure that all claims regarding enrichment/lower vs. lower values have indicated statistical tests.

We fully agree. In the revised version, we will correct any quantitative comparisons where statistical tests were not already indicated, with a clear statement of the statistical tests used, including p-values in figure legends and text.

(a) In Figure 2f, the authors should indicate which comparison is made for this test. Is it comparing 2 vs. 6 cyst numbers?

We acknowledge that the description was not sufficiently detailed. Indeed, the test was not between 2 vs 6 cyst numbers, but between all possible ways 8-cell cysts or the larger cysts studied could fragment randomly into two pieces, and produce by chance 6-cell cysts in 13 of 15 observed examples. We will expand the legend and main text to clarify that a binomial test was used to determine that the proportion of cysts producing 6-cell fragments differed very significantly from chance.

Revised text:

“A binomial test was used to assess whether the observed frequency of 6-cell cyst products differed from random cyst breakage. Production of 6-cell cysts was strongly preferred (13/15 cysts; ****p < 0.0001).”

(b) Figures 4d and 4e do not have a statistical test indicated.

We will include the specific statistical test used and report the corresponding p-values directly in the figure legends.

(3) Because the system is developmentally dynamic, the major conclusions of the work are somewhat unclear. Could the authors be more explicit about these and enumerate them more clearly in the abstract?

We will revise the abstract to better clarify the findings of this study. We will also replace the term Visham with mouse fusome to reflect its functional and structural analogy to the Drosophila and Xenopus fusomes, making the narrative more coherent and conclusive.

(4) The references for specific prior literature are mostly missing (lines 184-195, for example).

We appreciate this observation of a problem that occurred inadvertently when shortening an earlier version.  We will add 3–4 relevant references to appropriately support this section.

(5) The authors should define all acronyms when they are first used in the text (UPR, EGAD, etc).

We will ensure that all acronyms are spelled out at first mention (e.g., Unfolded Protein Response (UPR), Endosome and Golgi-Associated Degradation (EGAD)).

(6)  The jumping between topics (EMA, into microtubule fragmentation, polarization proteins, UPR/ERAD/EGAD, GCNA, ER, balbiani body, etc) makes the narrative of the paper very difficult to follow.

We are not jumping between topics, but following a narrative relevant to the central question of whether female mouse germ cells develop using a fusome.  EMA, microtubule fragmentation, polarization proteins, ER, and balbiani body are all topics with a known connection to fusomes. This is explained in the general introduction and in relevant subsections. We appreciate this feedback that further explanations of these connections would be helpful. In the revised manuscript, use of the unified term mouse fusome will also help connect the narrative across sections.  UPR/ERAD/EGAD are processes that have been studied in repair and maintenance of somatic cells and in yeast meiosis.  We show that the major regulator XbpI is found in the fusome, and that the fusome and these rejuvenation pathway genes are expressed and maintained throughout oogenesis, rather than only during limited late stages as suggested in previous literature.

(7) The heading title "Visham participates in organelle rejuvenation during meiosis" in line 241 is speculative and/or not supported. Drawing upon the extensive, highly rigorous Drosophila literature, it is safe to extrapolate, but the claim about regeneration is not adequately supported.

We believe this statement is accurate given the broad scope of the term "participates." It is supported by localization of the UPR regulator XbpI to the fusome. XbpI is the ortholog of HacI a key gene mediating UPR-mediated rejuvenation during yeast meiosis.  We also showed that rejuvenation pathway genes are expressed throughout most of meiosis (not previously known) and expanded cytological evidence of stage-specific organelle rejuvenation later in meiosis, such as mitochondrial-ER docking, in regions enriched in fusome antigens. However, we recognize the current limitations of this evidence in the mouse, and want to appropriately convey this, without going to what we believe would be an unjustified extreme of saying there is no evidence. 

Reviewer #2 (Public Review):

We thank the reviewer for the comprehensive summary and for highlighting both the technical achievement and biological relevance of our study. We greatly appreciate the thoughtful suggestions that have helped us refine our presentation and terminology.

(1) Some titles contain strong terms that do not fully match the conclusions of the corresponding sections.

(1a) Article title “Mouse germline cysts contain a fusome-like structure that mediates oocyte development”

We will change the statement to: “Mouse germline cysts contain a fusome that supports germline cyst polarity and rejuvenation.”

(1b) Result title “Visham overlaps centrosomes and moves on microtubules” We acknowledge that “moves” implies dynamics. We will include additional supplementary images showing small vesicular components of the mouse fusome on spindle-derived microtubule tracks.

(1c) Result title “Visham associates with Golgi genes involved in UPR beginning at the onset of cyst formation”

We will revise this title to: “The mouse fusome associates with the UPR regulatory protein Xbp1 beginning at the onset of cyst formation” to reflect the specific UPR protein that was immunolocalized. 

(1d) Result title “Visham participates in organelle rejuvenation during meiosis”

We will revise this to: “The mouse fusome persists during organelle rejuvenation in meiosis.”

(2) The authors aim to demonstrate that Visham is a fusome-like structure. I would suggest simply referring to it as a "fusome-like structure" rather than introducing a new term, which may confuse readers and does not necessarily help the authors' goal of showing the conservation of this structure in Drosophila and Xenopus germ cells. Interestingly, in a preprint from the same laboratory describing a similar structure in Xenopus germ cells, the authors refer to it as a "fusome-like structure (FLS)" (Davidian and Spradling, BioRxiv, 2025).

We appreciate the reviewer’s insightful comment. To maintain conceptual clarity and align with existing literature, we will refer to the structure as the mouse fusome throughout the manuscript, avoiding introduction of a new term.

Reviewer #3 (Public Review):

We thank the reviewer for emphasizing the importance of our study and for providing constructive feedback that will help us clarify and strengthen our conclusions.

(1) Line 86 - the heading for this section is "PGCs contain a Golgi-rich structure known as the EMA granule" 

We agree that the enrichment of Golgi within the EMA PGCs was not shown until the next section. We will revise this heading to:

“PGCs contain an asymmetric EMA granule.”

(2)  Line 105-106, how do we know if what's seen by EM corresponds to the EMA1 granule?

We will clarify that this identification is based on co-localization with Golgi markers (GM130 and GS28) and response to Brefeldin A treatment, which will be included as supplementary data. These findings support that the mouse fusome is Golgi-derived and can therefore be visualized by EM. The Golgi regions in E13.5 cyst cells move close together and associate with ring canals as visualized by EM (Figure 1E), the same as the mouse fusomes identified by EMA.

(3) Line 106-107-states "Visham co-stained with the Golgi protein Gm130 and the recycling endosomal protein Rab11a1". This is not convincing as there is only one example of each image, and both appear to be distorted.

Space is at a premium in these figures, but we have no limitation on data documenting this absolutely clear co-localization. We will replace the existing images with high-resolution, non-compressed versions for the final figures to clearly illustrate the co-staining patterns for GM130 and Rab11a1.

(4) Line 132-133---while visham formation is disrupted when microtubules are disrupted, I am not convinced that visham moves on microtubules as stated in the heading of this section.

We will include additional supplementary data showing small mouse fusome vesicles aligned along microtubules.

(5) Line 156 - the heading for this section states that Visham associates with polarity and microtubule genes, including pard3, but only evidence for pard3 is presented.

We agree and will revise the heading to: “Mouse fusome associates with the polarity protein Pard3.” We are adding data showing association of small fusome vesicles on microtubules.  

(6)  Lines 196-210 - it's strange to say that UPR genes depend on DAZ, as they are upregulated in the mutants. I think there are important observations here, but it's unclear what is being concluded.

UPR genes are not upregulated in DAZ in the sense we have never documented them increasing. We show that UPR genes during this time behave like pleuripotency genes and normally decline, but in DAZ mutants their decline is slowed.  We will rephrase the paragraph to clarify that Dazl mutation partially decouples developmental processes that are normally linked, which alters UPR gene expression relative to cyst development.

(7) Line 257-259-wave 1 and 2 follicles need to be explained in the introduction, and how these fits with the observations here clarified.

Follicle waves are too small a focus of the current study to explain in the introduction, but we will request readers to refer to the cited relevant literature (Yin and Spradling, 2025) for further details.

We sincerely thank all reviewers for their insightful and constructive feedback. We believe that the planned revisions—particularly the refined terminology, improved image quality, clarified statistics, and restructured abstract—will substantially strengthen the manuscript and enhance clarity for readers.

Author response:

Reviewer #1 (Public review):

Summary:

In this paper, the authors conduct both experiments and modeling of human cytomegalovirus (HCMV) infection in vitro to study how the infectivity of the virus (measured by cell infection) scales with the viral concentration in the inoculum. A naïve thought would be that this is linear in the sense that doubling the virus concentration (and thus the total virus) in the inoculum would lead to doubling the fraction of infected cells. However, the authors show convincingly that this is not the case for HCMV, using multiple strains, two different target cells, and repeated experiments. In fact, they find that for some regimens (inoculum concentration), infected cells increase faster than the concentration of the inoculum, which they term "apparent cooperativity". The authors then provided possible explanations for this phenomenon and constructed mathematical models and simulations to implement these explanations. They show that these ideas do help explain the cooperativity, but they can't be conclusive as to what the correct explanation is. In any case, this advances our knowledge of the system, and it is very important when quantitative experiments involving MOI are performed.

Strengths:

Careful experiments using state-of-the-art methodologies and advancing multiple competing models to explain the data.

Weaknesses:

There are minor weaknesses in explaining the implementation of the model. However, some specific assumptions, which to this reviewer were unclear, could have a substantial impact on the results. For example, whether cell infection is independent or not. This is expanded below.

Suggestions to clarify the study:

(1) Mathematically, it is clear what "increase linearly" or "increase faster than linearly" (e.g., line 94) means. However, it may be confusing for some readers to then look at plots such as in Figure 2, which appear linear (but on the log-log scale) and about which the authors also say (line 326) "data best matching the linear relationship on a log-log scale". 

This is a good point. In our revision, we will include a clarification to indicate that linear on the log-log scale relationship does not imply linear relationship on the linear-linear scale.

(2) One of the main issues that is unclear to me is whether the authors assume that cell infection is independent of other cells. This could be a very important issue affecting their results, both when analyzing the experimental data and running the simulations. One possible outcome of infection could be the generation of innate mediators that could protect (alter the resistance) of nearby cells. I can imagine two opposite results of this: i) one possibility is that resistance would lead to lower infection frequencies and this would result in apparent sub-linear infection (contrary to the observations); or ii) inoculums with more virus lead to faster infection, which doesn't allow enough time for the "resistance" (innate effect) to spread (potentially leading to results similar to the observations, supra-linear infection). 

In our models we assumed cells to be independent of each other (see also responses to other similar points). Because we measure infection in individual cells, assuming cells are independent is a reasonable first approximation. However, the reviewer makes an excellent point that there may be some between-cell signaling happening in the culture that “alerts” or “conditions” cells to change their “resistance”. It is also possible that at higher genome/cell numbers, exposure of cells to virions or virion debris may change the state of cells in the culture, and more cells become “susceptible” to infection. This is a good point that we will list in Limitations subsection of Discussion; it is a good hypothesis to test in our future experiments.

(3) Another unclear aspect of cell infection is whether each cell only has one chance to be infected or multiple chances, i.e., do the authors run the simulation once over all the cells or more times? 

Each cell has only one chance to be infected. Algorithm 1 clearly states that; we will add an extra sentence in “Agent-based simulations” to indicate this point.

(4) On the other hand, the authors address the complementary issue of the virus acting independently or not, with their clumping model (which includes nice experimental measurements). However, it was unclear to me what the assumption of the simulation is in this case. In the case of infection by a clump of virus or "viral compensation", when infection is successful (the cell becomes infected), how many viruses "disappear" and what happens to the rest? For example, one of the viruses of the clump is removed by infection, but the others are free to participate in another clump, or they also disappear. The only thing I found about this is the caption of Figure S10, and it seems to indicate that only the infected virus is removed. However, a typical assumption, I think, is that viruses aggregate to improve infection, but then the whole aggregate participates in infection of a single cell, and those viruses in the clump can't participate in other infections. Viral cooperativity with higher inocula in this case would be, perhaps, the result of larger numbers of clumps for higher inocula. This seems in agreement with Figure S8, but was a little unclear in the interpretation provided. 

This is a good point. We did not remove the clump if one of the virions in the clump manages to infect a cell, and indeed, this could be the reason why in some simulations we observe apparent cooperativity when modeling viral clumping. This is something we will explore in our revision.

(5) In algorithm 1, how does P_i, as defined, relate to equation 1? 

These are unrelated because eqn.(1) is a phenomenological model that links infection per cell to genomes per cell. P_i in algorithm 1 is “physics-inspired” potential barrier.

(6) In line 228, and several other places (e.g., caption of Table S2), the authors refer to the probability of a single genome infecting a cell p(1)=exp(-lambda), but shouldn't it be p(1)=1-exp(-lambda) according to equation 1?

Indeed, it was a typo, p(1)=1-exp(-lambda) per eqn 1. Thank you, it will be corrected in the revised paper.

(7) In line 304, the accrued damage hypothesis is defined, but it is stated as a triggering of an antiviral response; one would assume that exposure to a virion should increase the resistance to infection. Otherwise, the authors are saying that evolution has come up with intracellular viral resistance mechanisms that are detrimental to the cell. As I mentioned above, this could also be a mechanism for non-independent cell infection. For example, infected cells signal to neighboring cells to "become resistance" to infection. This would also provide a mechanism for saturation at high levels. 

We do not know how exposure of a cell to one virion would change its “antiviral state”, i.e., to become more or less resistant to the next infection. If a cell becomes more resistant, there is no possibility to observe apparent cooperativity in infection of cells, so this hypothesis cannot explain our observations with n>1. Whether this mechanism plays a role in saturation of cell infection rate at lower than 1 value when genome/cell is large is unclear but is a possibility. We will add this point to Discussion in revision.

(8) In Figure 3, and likely other places, t-tests are used for comparisons, but with only an n=5 (experiments). Many would prefer a non-parametric test. 

We repeated the analyses in Fig 3 with Mann-Whitney test, results were the same, so we would like to keep results from the t-test in the paper.

Reviewer #2 (Public review):

In their article, Peterson et al. wanted to show to what extent the classical "single hit" model of virion infection, where one virion is required to infect a cell, does not match empirical observations based on human cytomegalovirus in vitro infection model, and how this would have practical impacts in experimental protocols.

They first used a very simple experimental assay, where they infected cells with serially diluted virions and measured the proportion of infected cells with flow cytometry. From this, they could elegantly show how the proportion of infected cells differed from a "single hit" model, which they simulated using a simple mathematical model ("powerlaw model"), and better fit a model where virions need to cooperate to infect cells. They then explore which mechanism could explain this apparent cooperation:

(1) Stochasticity alone cannot explain the results, although I am unsure how generalizable the results are, because the mathematical model chosen cannot, by design, explain such observations only by stochasticity. 

Our null model simulations are not just about stochasticity; they also include variability in virion infectivity and cell resistance to infection. We agree that simulations cannot truly prove that such variability cannot result in apparent cooperativity; however, we also provide a mathematical proof that increase in frequency of infected cells should be linear with virion concentration at small genome/cell numbers.

(2) Virion clumping seemed not to be enough either to generally explain such a pattern. For that, they first use a mathematical model showing that the apparent cooperation would be small. However, I am unsure how extreme the scenario of simulated virion clumping is. They then used dynamic light scattering to measure the distribution of the sizes of clumps. From these estimates, they show that virion clumps cannot reproduce the observed virion cooperation in serial dilution assays. However, the authors remain unprecise on how the uncertainty of these clumps' size distribution would impact the results, as most clumps have a size smaller than a single virion, leaving therefore a limited number of clumps truly containing virions. 

As we stated in the paper, clumping may explain apparent cooperativity in simulations depending on how stock dilution impacts distribution of virions/clump. This could be explored further, however, better experimental measurements of virions/clump would be highly informative (but we do not have resources to do these experiments at present). Our point is that the degree of apparent cooperativity is dependent on the target cell used (n is smaller on epithelial cells than on fibroblasts) that is difficult to explain by clumping which is a virion property. Per comment by reviewer 1, we will do some more analyses of the clumping model to investigate importance of clump removal per successful infection on the detected degree of apparent cooperativity.

The two models remain unidentifiable from each other but could explain the apparent virion cooperativity: either due to an increase in susceptibility of the cell each time a virion tries to infect it, or due to viral compensation, where lesser fit viruses are able to infect cells in co-infection with a better fit virion. Unfortunately, the authors here do not attempt to fit their mathematical model to the experimental data but only show that theoretical models and experimental data generate similar patterns regarding virion apparent cooperation. 

In the revision we will provide examples of simulations that “match” experimental data with a relatively high degree of apparent cooperativity; we have done those before but excluded them from the current version since they are a bit messy. Fitting simulations to data may be an overkill.

Finally, the authors show that this virions cooperation could make the relationship between the estimated multiplicity of infection and viruses/cell deviate from the 1:1 relationship. Consequently, the dilution of a virion stock would lead to an even stronger decrease in infectivity, as more diluted virions can cooperate less for infection.

Overall, this work is very valuable as it raises the general question of how the estimate of infectivity can be biased if extrapolated from a single virus titer assay. The observation that HCMV virions often cooperate and that this cooperation varies between contexts seems robust. The putative biological explanations would require further exploration.

This topic is very well known in the case of segmented viruses and the semi-infectious particles, leading to the idea of studying "sociovirology", but to my knowledge, this is the first time that it was explored for a nonsegmented virus, and in the context of MOI estimation. 

Thank you.

Reviewer #3 (Public review): 

Summary:

The authors dilute fluorescent HCMV stocks in small steps (df ≈ 1.3-1.5) across 23 points, quantify infections by flow cytometry at 3 dpi, and fit a power-law model to estimate a cooperativity parameter n (n > 1 indicates apparent cooperativity). They compare fibroblasts vs epithelial cells and multiple strains/reporters, and explore alternative mechanisms (clumping, accrued damage, viral compensation) via analytical modeling and stochastic simulations. They discuss implications for titer/MOI estimation and suggest a method for detecting "apparent cooperativity," noting that for viruses showing this behavior, MOI estimation may be biased.

Strengths:

(1) High-resolution titration & rigor: The small-step dilution design (23 serial dilutions; tailored df) improves dose-response resolution beyond conventional 10× series.

(2) Clear quantitative signal: Multiple strain-cell pairs show n > 1, with appropriate model fitting and visualization of the linear regime on log-log axes.

(3) Mechanistic exploration: Side-by-side modeling of clumping vs accrued damage vs compensation frames testable hypotheses for cooperativity. 

Thank you.

Weaknesses:

(1) Secondary infection control: The authors argue that 3 dpi largely avoids progeny-mediated secondary infection; this claim should be strengthened (e.g., entry inhibitors/control infections) or add sensitivity checks showing results are robust to a small secondary-infection contribution. 

This is an important point. We do believe that the current knowledge about HCMV virion production time – it takes 3-4 days to make virions per multiple papers (see Fig 7 in Vonka and Benyesh-Melnick JB 1966; Fig 3B in Stanton et al JCI 2010; and Fig 1A in Li et al. PNAS 2015) – is sufficient to justify our experimental design but we do agree that an additional control to block novel infections with would be useful. We had previously performed experiments with a HCMV TB-gL-KO that cannot make infectious virions (but the stock virions can be made from complemented target cells). We will investigate if our titration experiments with this virus strain have sufficient resolution to detect apparent cooperativity. However, at present we do not have the resources to perform novel experiments.  

(2) Discriminating mechanisms: At present, simulations cannot distinguish between accrued damage and viral compensation. The authors should propose or add a decisive experiment (e.g., dual-color coinfection to quantify true coinfection rates versus "priming" without coinfection; timed sequential inocula) and outline expected signatures for each mechanism. 

Excellent suggestion. Because infection of a cell is a result of the joint viral infectivity and cell resistance, it may be hard to discriminate between these alternatives unless we specify them as particular molecular mechanisms. But we will try our best and list potential future experiments in the revised version of the paper.

(3) Decline at high genomes/cell: Several datasets show a downturn at high input. Hypotheses should be provided (cytotoxicity, receptor depletion, and measurement ceiling) and any supportive controls. 

Another good point. We do not have a good explanation, but we do not believe this is because of saturation of available target cells.  It seemed to only happen (or was most pronounced) with the ME stocks, which are typically lower in titer and so the higher MOI were nearly undiluted stock. It may be the effect of the conditioned medium.  Or perhaps there are non-infectious particles like dense bodies (enveloped particles that lack a capsid and genome) and non-infectious, enveloped particles (NIEPs) that compete for receptors or otherwise damage cells and these don’t get diluted out at the higher doses.  We plan to include these points in Discussion of the revised version of the paper.

(4) Include experimental data: In Figure 6, please include the experimentally measured titers (IU/mL), if available. 

This is a model-simulated scenario, and as such, there is no measured titers.

(5) MOI guidance: The practical guidance is important; please add a short "best-practice box" (how to determine titer at multiple genomes/cell and cell densities; when single-hit assumptions fail) for end-users. 

Good suggestion. We will include best-practice box using guidelines developed in Ryckman lab over the years in the revised version of the paper.

Overall note to all reviews: We have deposited our codes and the data on github; yet, none of the reviewers commented on it.

TEAR PIE

Author response:

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

Reviewer #1 (Public review): 

Summary: 

This study builds on previous work demonstrating that several beta connexins (Cx26, Cx30, and Cx32) have a carbamylation motif which renders them sensitive to CO₂. In response to CO₂, hemichannels composed of these connexins open, enabling diffusion of small molecules (such as ATP) between the cytosol and extracellular environment. Here, the authors have identified that an alpha connexin, Cx43, also contains a carbamylation motif, and they demonstrate that CO₂ opens Cx43 hemichannels. Most of the study involves using transfected cells expressing wildtype and mutant Cx43 to define amino acids required for CO₂ sensitivity. Hippocampal tissue slices in culture were used to show that CO₂-induced synaptic transmission was affected by Cx43 hemichannels, providing a physiological context. The authors point out that the Cx43 gene significantly diverges from the beta connexins that are CO₂ sensitive, suggesting that the conserved carbamylation motif was present before the alpha and beta connexin genes diverged. 

Strengths: 

(1) The molecular analysis defining the amino acids that contribute to the CO₂ sensitivity of Cx43 is a major strength of the study. The rigor of analysis was strengthened by using three independent assays for hemichannel opening: dye uptake, patch clamp channel measurements, and ATP secretion. The resulting analysis identified key lysines in Cx43 that were required for CO₂-mediated hemichannel opening. A double K to E Cx43 mutant produced a construct that produced hemichannels that were constitutively open, which further strengthened the analysis. 

(2) Using hippocampal tissue sections to demonstrate that CO₂ can influence field excitatory postsynaptic potentials (fEPSPs) provides a native context for CO₂ regulation of Cx43 hemichannels. Cx43 mutations associated with Oculodentodigital Dysplasia (ODDD) inhibited CO₂-induced hemichannel opening, although the mechanism by which this occurs was not elucidated. 

Weaknesses: 

(1) Cx43 channels are sensitive to cytosolic pH, which will be affected by CO₂. Cytosolic pH was not measured, and how this affects CO₂-induced Cx43 hemichannel activity was not addressed. 

We have now addressed this with intracellular pH measurements and removal of the C-terminal pH sensor from Cx43 -the hemichannel remains CO₂ sensitive.

(2) Cultured cells are typically grown in incubators containing 5% CO₂, which is ~40 mmHg. It is unclear how cells would be viable if Cx43 hemichannels are open at this PCO2. 

The cells look completely healthy with normal morphology and no sign of excessive cell death in the cultures. Presumably they have ways of compensating for the effects of partially open Cx43 hemichannels.

(3) Experiments using Gap26 to inhibit Cx43 hemichannels in fEPSP measurements used a scrambled peptide as a control. Analysis should also include Gap peptides specifically targeting Cx26, Cx30, and Cx32 as additional controls. 

We don’t feel this is necessary given the extensive prior literature in hippocampus showing the effect of ATP release via open Cx43 hemichannels on fEPSP amplitude that used astrocytic specific knockout of Cx43 and Gap26 (doi: 10.1523/jneurosci.0015-14.2014).

(4) The mechanism by which ODDD mutations impair CO2-mediated hemichannel opening was not addressed. Also, the potential roles for inhibiting Cx43 hemichannels in the pathology of ODDD are unclear. 

These pathological mutations that alter CO<SUB>2</SUB> sensitivity are similar to pathological mutation in Cx26 and Cx32, which also remove CO<SUB>2</SUB> sensitivity. Our cryo-EM studies on Cx26 give clues as to why these mutations have this effect -they alter conformational mobility of the channel (Brotherton et al 2022 doi: 10.1016/j.str.2022.02.010 and Brotherton et al 2024 doi: 10.7554/eLife.93686). We assume that similar considerations apply to Cx43, but this requires improved cryoEM structures of Cx43 hemichannels at differing levels of PCO<SUB>2</SUB>.

We agree that the link between loss of CO<SUB>2</SUB> sensitivity of Cx43 and ODDD is not established and have revised the text to make this clear.

(5) CO2 has no effect on Cx43-mediated gap junctional communication as opposed to Cx26 gap junctions, which are inhibited by CO2. The molecular basis for this difference was not determined. 

Cx26 gap junction channels are so far unique amongst CO<SUB>2</SUB> sensitive connexins in being closed by CO<SUB>2</SUB>. We have addressed the mechanism by which this occurs in Nijjar et al 2025 DOI: 10.1113/JP285885 -the requirement of carbamylation of K108 in Cx26 (in addition to K125) for GJC closure.

(6) Whether there are other non-beta connexins that have a putative carbamylation motif was not addressed. Additional discussion/analysis of how the evolutionary trajectory for Cx43 maintaining a carbamylation motif is unique for non-beta connexins would strengthen the study. 

We have performed a molecular phylogenetic survey to show that the carbamylation motif occurs across the alpha connexin clade and have shown that Cx50 is indeed CO<SUB>2</SUB> sensitive (doi: 10.1101/2025.01.23.634273). This is now in Fig 12.

Reviewer #2 (Public review): 

Summary: 

This paper examines the CO<SUB>2</SUB>  sensitivity of Cx43 hemichannels and gap junctional channels in transiently transfected Hela cells using several different assays, including ethidium dye uptake, ATP release, whole cell patch clamp recordings, and an imaging assay of gap junctional dye transfer. The results show that raising pCO₂ from 20 to 70 mmHg (at a constant pH of 7.3) causes an increase in opening of Cx43 hemichannels but does not block Cx43 gap junctions. This study also showed that raising pCO<SUB>2</SUB> from 20 to 35 mm Hg resulted in an increase in synaptic strength in hippocampal rat brain slices, presumably due to downstream ATP release, suggesting that the CO<SUB>2</SUB> sensitivity of Cx43 may be physiologically relevant. As a further test of the physiological relevance of the CO₂ sensitivity of Cx43, it was shown that two pathological mutations of Cx43 that are associated with ODDD caused loss of Cx43 CO₂-sensitivity. Cx43 has a potential carbamylation motif that is homologous to the motif in Cx26. To understand the structural changes involved in CO<SUB>2</SUB> sensitivity, a number of mutations were made in Cx43 sites thought to be the equivalent of those known to be involved in the CO<SUB>2</SUB> sensitivity of Cx26, and the CO<SUB>2</SUB> sensitivity of these mutants was investigated. 

Strengths: 

This study shows that the apparent lack of functional Cx43 hemichannels observed in a number of previous in vitro function studies may be due to the use of HEPES to buffer the external pH. When Cx43 hemichannels were studied in external solutions in which CO<SUB>2</SUB>/bicarbonate was used to buffer pH instead of HEPES, Cx43 hemichannels showed significantly higher levels of dye uptake, ATP release, and ionic conductance. These findings may have major physiological implications since Cx43 hemichannels are found in many organs throughout the body, including the brain, heart, and immune system. 

Weaknesses: 

(1) Interpretation of the site-directed mutation studies is complicated. Although Cx43 has a potential carbamylation motif that is homologous to the motif in Cx26, the results of site-directed mutation studies were inconsistent with a simple model in which K144 and K105 interact following carbamylation to cause the opening of Cx43 hemichannels. 

The mechanism of opening of Cx43 is more complex than that of Cx26, Cx32 and Cx50 and involves more Lys residues. The 4 Lys residues in Cx43 that are involved in opening the hemichannel have their equivalents in Cx26, but in Cx26 these additional residues seem to be involved in the closing of the GJC rather than opening of the hemichannel (see above). Cx50 is simpler and involves only two Lys residues (doi: 10.1101/2025.01.23.634273), which are equivalent to those in Cx26.

(2) Secondly, although it is shown that two Cx43 ODDD-associated mutations show a loss of CO₂ sensitivity, there is no evidence that the absence of CO2 sensitivity is involved in the pathology of ODD

We agree, but this is probably because this has not been directly tested by experiment, as the CO<Sub>2</sub> sensitivity of Cx43 was not previously known. As mentioned above we have revised the text to ensure that this is clear.

Reviewer #3 (Public review): 

In this paper, the authors aimed to investigate carbamylation effects on the function of Cx43-based hemichannels. Such effects have previously been characterized for other connexins, e.g., for Cx26, which display increased hemichannel (HC) opening and closure of gap junction channels upon exposure to increased CO₂ partial pressure (accompanied by increased bicarbonate to keep pH constant). 

The authors used HeLa cells transiently transfected with Cx43 to investigate CO₂ dependent carbamylation effects on Cx43 HC function. In contrast to Cx43-based gap junction channels that are reported here to be insensitive to PCO₂ alterations, they provide evidence that Cx43 HC opening is highly dependent on the PCO2 pressure in the bath solution, over a range of 20 up to 70 mmHg encompassing the physiologically normal resting level of around 40 mmHg. They furthermore identified several Cx43 residues involved in Cx43 HC sensitivity to PCO2: K105, K109, K144 & K234; mutation of 2 or more of these AAs is necessary to abolish CO₂ sensitivity. The subject is interesting and the results indicate that a fraction of HCs is open at a physiological 40 mmHg PCO₂, which differs from the situation under HEPES buffered solutions where HCs are mostly closed under resting conditions. The mechanism of HC opening with CO₂ gassing is linked to carbamylation, and the authors pinpointed several Lys residues involved in this process. 

Overall, the work is interesting as it shows that Cx43 HCs have a significant open probability under resting conditions of physiological levels of CO₂ gassing, probably applicable to the brain, heart, and other Cx43 expressing organs. The paper gives a detailed account of various experiments performed (dye uptake, electrophysiology, ATP release to assess HC function) and results concluded from those. They further consider many candidate carbamylation sites by mutating them to negatively charged Glu residues. The paper ends with hippocampal slice work showing evidence for connexin-dependent increases of the EPSP amplitude that could be inhibited by HC inhibition with Gap26 (Figure 10). Another line of evidence comes from the Cx43-linked ODDD genetic disease, whereby L90V as well as the A44V mutations of Cx43 prevented the CO₂-induced hemichannel opening response (Figure 11). Although the paper is interesting, in its present state, it suffers from (i) a problematic Figure 3, precluding interpretation of the data shown, and (ii) the poor use of hemichannel inhibitors that are necessary to strengthen the evidence in the crucial experiment of Figure 2 and others. 

The panels in Figure 3 were mislabelled in the accompanying legend possibly leading to some confusion. This has now been corrected.

We disagree that hemichannel blockers are needed to strengthen the evidence in Figure 2 and other figures. Our controls show that the CO₂-sensitive responses absolutely requires expression of Cx43 and was modified by mutations of Cx43. It is hard to see how this evidence would be strengthened by use of peptide inhibitors or other blockers of hemichannels that may not be completely selective.

Reviewing Editor Comments:

(1) Improve electrophysiological evidence, addressing concerns about the initial experiment and including peptide inhibitor data where applicable. 

We think the concerns about the electrophysiological evidence arise from a misunderstanding because we gave insufficient information about how we conducted the experiments. We have now provided a much more complete legend, added explanations in the text and given more detail in the Methods. We further respond to the reviewer below.

We do not agree on the necessity of the peptide inhibitor to demonstrate dependence on Cx43.  We have shown that parental HeLa cells do not release ATP to changes in PCO₂ or voltage (Fig 2D; Butler & Dale 2023, 10.3389/fncel.2023.1330983; Lovatt et al 2025, 10.1101/2025.03.12.642803, 10.1101/2025.01.23.634273). Our previous papers have shown many times that parental HeLa cells do not load with dye to CO₂ or zero Ca²⁺ (e.g. Huckstepp et al 2010, 10.1113/jphysiol.2010.192096; Meigh et al 2013, 10.7554/eLife.01213; Meigh et al 2014, 10.7554/eLife.04249), and we have shown that parental HeLa cells do not exhibit the same CO₂ dependent change in whole cell conductance that the Cx43-expressing cells do (Fig 2B). In addition, we shown that mutating key residues in Cx43 alters both CO₂-sensitive release of ATP and the CO₂-dependent dye loading without affecting the respective positive control. To bolster this, we have included data for the K144R mutation as a supplement to Fig 3. Given the expense of Gap26 it is impractical to include this as a standard control and unnecessary given the comprehensive controls outlined.

Collectively, these data show that the responses to CO₂ require expression of Cx43 and can be modified by mutation of Cx43.

(2) Strengthen the manuscript by measuring the effects of CO on cytosolic pH and Cx43 hemichannel opening. Consider using tail truncation mutants to assess the role of the C-terminal pH sensor in CO-mediated channel opening.

We agree and have performed the suggested experiments to address this issue.

(3) Investigate the effect of expressing the K105E/K109E Cx43 double mutant on cell viability.

In our experiments the cells look completely healthy based on their morphology in brightfield microscopy and growth rates. 

(4) Discuss and analyze the uniqueness of Cx43 among alpha connexins in maintaining the carbamylation motif.

now discuss this -Cx43 is not unique. We have added a molecular phylogenetic survey of the alpha connexin clade in Fig 12. Apart from Cx37, the carbamylation motif appears in all the other members of the clade (but not necessarily in the human orthologue). In a different MS, currently posted on bioRxiv, we have documented the CO₂ sensitivity of Cx50 and its dependence on the motif.

(5) Consider omitting data on ODDD-associated mutations unless there is evidence linking CO₂ sensitivity to disease pathology.

This experiment is observational, and we are not making claims that there is a direct causal link. Removing the ODDD mutant findings would lose potentially useful information for anyone studying how these mutations alter channel function. We have reworded the text to ensure that we say that the link between loss of CO₂ sensitivity and ODDD remains unproven.

(6) Justify the choice of high K^⁺ and low external calcium as a positive control in ATP release experiments.

These two manipulations can open the hemichannel independently of the CO₂ stimulus. Extracellular Ca²⁺ is well known to block all connexin hemichannels, and Cx43 is known to be voltage sensitive. The depolarisation from high K⁺ is effective at opening the hemichannel and we preferred this as a more physiological way of opening the Cx43 hemichannel. We have added some explanatory text.

(7) Clarify whether Cx43A44V or Cx43L90V mutations block gap junctional coupling.

This is an interesting point. Since Cx43 GJCs are not CO₂ sensitive we feel this is beyond the scope of our paper. 

(8) Discuss the potential implications of pCO₂ changes on myocardial function through alterations in intracellular pH.

We have modified the discussion to consider this point.

Reviewer #1 (Recommendations for the authors):

(1) Measurements of the effects of CO₂ on cytosolic pH/Cx43 hemichannel opening would strengthen the manuscript. Since the pH sensor of Cx43 is on the C terminus, the authors could consider making tail truncation mutants to see how this affects CO₂-mediated Cx43 channel opening.

We have done this (truncating after residue 256) -the channel remains highly CO₂ and voltage sensitive. We have also documented the effect of the  hypercapnic solutions on intracellular pH measured with BCECF. These new data are now included as figure supplements to Figure 2.

(2) What is the impact of expressing the K105E / K109E Cx43 double mutant on cell viability?

There was no obvious observed impact, cell density was as expected (no evidence of increased cell death), brightfield and fluorescence visualisation indicated normal healthy cells. We have added a movie (Fig 9, movie supplement 1) to show the effect of La³⁺ on the GRAB_ATP signal in cells expressing Cx43^{K105E, K109E} so readers can appreciate the morphology and its stability during the recording.

(3) A quick look at other alpha connexins suggested that Cx43 was unique among alpha connexins in maintaining the carbamylation motif. This merits additional discussion/ analysis.

This is an interesting point. Cx43 is not unique in the alpha clade in having the carbamylation motif as a number of other human alpha connexins also possess: Cx50, Cx59 and Cx62, and non-human alpha connexins (Cx40, Cx59, Cx46) also possess the motif. We have shown that Cx50 is CO₂ sensitive. We have performed a brief molecular phylogenetic analysis of the alpha connexon clade to highlight the occurrence of the carbamylation motif. This is now presented as Fig 12 to go with the accompanying discussion.

(4) There were some minor writing issues that should be addressed. For instance, fEPSP is not defined. Also, insets showing positive controls in some experiments were not described in the figure legends.

We have corrected these issues.

Reviewer #2 (Recommendations for the authors):

(1) I would omit the data on the ODDD-associated mutations since there is no evidence that loss of CO₂ sensitivity plays an important role in the underlying disease pathology.

We are not making the claim CO₂ loss leads to the underlying pathology and have reviewed the text to ensure that we clearly express that this is a correlation not a cause. We think this is worth retaining as many pathological mutations in other CO₂ sensitive connexins (Cx26, Cx32 and Cx50) cause loss of CO₂ sensitivity, and this information may be helpful to other researchers.

(2) Why is high K+ rather than low external calcium used as a positive control in ATP release experiments?

We used of high K⁺ and depolarisation as a positive control as regard this as a more physiological stimulus than the low external Ca²⁺.

(3) Does Cx43A44V or Cx43L90V block gap junctional coupling?

An interesting question but we have not examined this.

(4) Provide references for biophysical recordings of Cx43 hemichannels performed in HEPES-buffered salines, which document Cx43 hemichannels as being shut.

have added the original and some later references which examine Cx43 hemichannel gating in HEPES buffer and shows the need for substantial depolarisation to induce channel opening.

(5) In the heart muscle, changes in PCO₂ have long been hypothesized to cause changes in myocardial function by changing pHi.

This is true and we now add some discussion of this point. Now that we know that Cx43 is directly sensitive to CO₂ a direct action of CO₂ cannot be ruled out and careful experimentation is required to test this possibility. 

Reviewer #3 (Recommendations for the authors):

(1) Page 3: "... homologs of K125 and R104 ... ": the context is linked to Cx26, so Cx26 needs to be added here.

Done

(2) Page 4 text and related Figure 2:

(a) Figure 2A&B: PCO2-dependent Cx43 HC opening is clearly present in the carboxy-fluorescein dye uptake experiments (Figure 2A) as well as in the electrophysiological experiments (Figure 2B). The curves look quite different between these two distinct readouts: dye uptake doubles from 20 to 70 mmHg in Figure 2A while the electrophysiological data double from 45 to 70 mmHg in Figure 2B. These responses look quite distinct and may be linked to a non-linearity of the dye uptake assay or a problem in the electrophysiological measurements of Figure 2B discussed in the next point.

Different molecules/ions may have different permeabilities through the channel, which could explain the observed difference. Also, there is some contamination of the whole cell conductance change with another conductance (evident in recordings from parental HeLa cells). This is evident particularly at 70 mmHg. If this contaminating conductance were subtracted from the total conductance in the Cx43 expressing cells, then the dose response relations would be more similar. However, we are reluctant to add this additional data processing step to the paper.

(b) The traces in Figure 2B show that the HC current is inward at 20 mmHg PCO2, while it switches to an outward current at 55mmHg PCO2. HCs are non-selective channels, so their current should switch direction around 0 mV but not at -50 mV. As such, the -50 mV switching point indicates involvement of another channel distinct from non-selective Cx43 hemichannels.

We think that our incomplete description in the legend led to this misunderstanding. We used a baseline of 35 mmHg (where the channels will be slightly open) and changed to 20 mmHg to close them (or to higher PCO₂ to open them from this baseline), hence a decrease in conductance and loss of outward current for 20 mmHg. The holding potential for the recordings and voltage steps were the same in all recordings. We have now edited the legend and added more information into the methods to clarify this and how we constructed the dose response curve.

We agree that Cx43 hemichannels are relatively nonselective and would normally be expected to have a reversal potential around 0 mV, but we are using K-Gluconate and the lowered reversal potential (~-65 mV) is likely due to poor permeation of this anion via Cx43.

(c) A Hill slope of 6 is reported for this curve, which is extremely steep. The paper does not provide any further consideration, making this an isolated statement without any theoretical framework to understand the present finding in such context (i.e., in relation to the PCO2 dependency of Cx channels).

Yes, we agree -it seems to be the case with all CO₂ sensitive connexins that we have looked at that the Hill coefficient versus CO₂ is >4. Hemichannels are of course hexameric so there is potential for 6 CO₂ molecules to be bound and extensive cooperativity. We have modified the text to give greater context.

(d) A further remark to Figure 2 is that it does not contain any experiment showing the effect of Cx43 hemichannel inhibition with a reliable HC inhibitor such as Gap26, which is only used in the penultimate illustration of Figure 10. Gap26 should be used in Figure 2 and most of the other figures to show evidence of HC contribution. The lanthanum ions used in Figure 9 are a very non-specific hemichannel blocker and should be replaced by experiments with Gap26.

We have addressed the first part of this comment above.

We agree that La³⁺ blocks all hemichannels, but in the context of our experiments and the controls we have performed it is entirely adequate and supports our conclusions. Our controls show (mentioned above and below) show that the expression of Cx43 is absolutely required for CO₂-dependent ATP release (and dye loading). In Figure 9 our use of La³⁺ was to show the presence of a constitutively open Cx43 mutant hemichannel. Gap26 would add little to this. Our further controls show that with expression of Cx43^WT La³⁺ did nothing to the ATP signal under baseline conditions (20 mmHg) supporting our conclusion that the mutant channels are constitutively open.

(e) As the experiments of Figure 2 form the basis of what is to follow, the above remarks cast doubt on the robustness of the experiments and the data produced.

We disagree, our results are extremely robust: 1) we have used three independent assays confirm the presence of the response; 2) parental HeLa cells do not release ATP, dye load or show large conductance changes to CO₂ showing the absolute requirement for expression of Cx43; 3) mutations of Cx43 (in the carbamylation motif) alter the CO₂ evoked ATP release and dye loading giving further confirmation of Cx43 as the conduit for ATP release and dye loading; and 4) we use standard positive controls (0 Ca^², high K) to confirm cells still have functional channels for those mutations that modified CO₂ sensitivity.

(f) The sentence "Cells transfected with GRAB-ATP only, showed ... " should be

modified to "In contrast, cells not expressing Cx43 showed no responses to any applied CO2 concentration as concluded from GRAB-ATP experiments"

We have modified the text.

(3) Page 5 and Figures 3 & 4:

(a) Figure 3 illustrates results obtained with mutations of 4 distinct Lys residues. However, the corresponding legend indicates mutations that are different from the ones shown in the corresponding illustrations, making it impossible to reliably understand and interpret the results shown in panels A-E.

Thanks for pointing this out. Our apologies, we modified the figure so that the order of the images matched the order of the graph (and the legend) but then forgot to put the new version of the figure in the text. We have now corrected this so that Figure and legend match.

(b) Figure 4 lacks control WT traces!

The controls for this (showing that parental HeLa cells do not release ATP in response to CO₂ or depolarisation) are shown in Figure 2.

(c) Figure 4, Supplement 1: High Hill coefficients of 10 are shown here, but they are not discussed anywhere, as is also the case for the remark on p.4. A Hill steepness of 10 is huge and points to many processes potentially involved. As reported above, these data are floating around in the manuscript without any connection.

Yes, we agree this is very high and surprising. It may reflect as mentioned above the hexameric nature of the channel and that 4 Lys residues seem to be involved. We have used this equation to give some quantitative understanding of the effect of the mutations on CO₂ sensitivity and still think this is useful. We have no further evidence to interpret these values one way or the other.

(4) Page 6: Carbamate bridges are proposed to be formed between K105 and K144, and between K109 and K234. The first three of these Lysine residues are located in the 55aa long cytoplasmic loop of Cx43, while K234 is in the juxta membrane region involved in tubulin interactions. Both K144 and and K234 are involved in Cx43 HC inhibition: K144 is the last aa of the L2 peptide (D119-K144 sequence) that inhibits Cx43 hemichannels while K234 is the first aa of the TM2 peptide that reduces hemichannel presence in the membrane (sequence just after TM4, at the start of the C-tail). This context should be added to increase insight and understanding of the CO2 carbamylation effects on Cx43 hemichannel opening.

Thanks for suggesting this. We have added some discussion of CT to CL interactions in the context of regulation by pH and [Ca²⁺].

(5) Page 7: The Cx43 ODDD A44V and L90V mutations lead to loss of pCO2 sensitivity in dye loading and ATP assays. However, A44V located in EL1 is reportedly associated with Cx43 HC activation, while L90V in TM2 is associated with HC inhibition. Remarkably, these mutations are focused on non-Lys residues, which brings up the question of how to link this to the paper's main thread.

This follows the pattern that we have seen for other mutations such as A40V, A88V in Cx26 and several CMTX mutations of Cx32. Our cryoEM structures of Cx26 suggest that these mutations alter the flexibility of the molecule and hence abolish CO₂ sensitivity. We have reworded the text to avoid giving the impression that there is a demonstrated link between loss of CO₂ sensitivity of Cx43 and pathology.

(6) Page 8: HCs constitutively open - 'constutively' perhaps does not have the best connotation as it is not related to HC constitution but CO2 partial pressure.

Yes, we agree and have reworded this.

(7) Page 9: "in all subtypes" -> not clear what is meant - do you mean "in all cell types"?

We agree this is unclear -it refers to all astrocytic subtypes. We have amended the text.

(8) Page 10: Composition of hypocapnic recording solution: bubbling description is incomplete "95%O2/5%" and should be "95%O2/5%CO2".

Changed.

(9) Page 11: Composition of zero Ca^²⁺ hypocapnic recording solution: perhaps better to call this "nominally Ca^²⁺-free hypocapnic recording solution" as no Ca^²⁺ buffer is included in this solution

Thanks for pointing this out. We did in fact add 1 mM EGTA to the solutions but omitted this from the recipe, this has now been corrected.

(10) Page 11: in M&M I found that the NaHCO3- is lowered to 10 mM in the zero Ca^²⁺condition, while the control experimental condition has 26 mM NaHCO3-. The zero Ca condition should be kept at a physiologically normal 26 mM NaHCO3- concentration, so why was this done? Lowering NaHCO3- during hemichannel stimulation may result in smaller responses and introduce non-linearities.

For the dye loading we used 20 mmHg as the baseline condition and increased PCO₂ from this. Hence for the zero Ca²⁺ positive control we modified the 20 mmHg hypocapnic solution by substituting Mg²⁺ for Ca²⁺ and adding EGTA. We have modified the text in the Methods to clarify this.

Further remarks on the figures:

(1) Figure 2A: Add 20 & 70 mmHg to the images, to improve the readability of this illustration.

Done

(2) Figure 3: WT responses are shown in panel F, but experimental data (images and curves) are lacking and should be included in a revised version.

The wild type data is shown in Fig 2A. We have some sympathy for the comment, but we felt that Fig 2 should document CO₂ sensitivity, and then the subsequent Figs should analyse its basis. Hence the separation of Cx43^WT data from the mutant data. In panel F, we state that we have recalculated the WT data from Fig 2A to allow the comparison.

(3) Figures 4, 6, 8: Color codes for mmHg CO₂ pressure make reading these figures difficult; perhaps better to add mmHg values directly in relation to the traces.

We have considered this suggestion but feel that the figures would become very cluttered with the additional labelling.

(4) I wouldn't use colored lines when not necessary, e.g., Figure 9 100 µM La3+; Figure 10 (add 20->35 mmHg PCO2 switch; add scrGap26 above blue bars); Figure 11C & D.

We agree and can see that in Figs 9 and 10 this muddles our colour scheme in other figures so have modified these figures. There was not space to put the suggested labels.

(5) The mechanism of increased HC opening is not clear.

We agree and have discussed various options and the analogy with what we know about Cx26. Ultimately new cryo-EM data is required.

(6) Figure 10: 35G/35S are weird abbreviations for 35 mmHg Gap26 and scrambled Gap26.

Yes, but we used these to fit into the available space.

(7) Figure 11, legend: '20 mmHg PCO2 for each transfection for 70 mmHg PCO2'. It is not clear what is meant here.

Thanks for pointing this out, we have reworded this to ensure clarity.

Author response:

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

Reviewer #1 (Public review):

The manuscript by Choi and colleagues investigates the impact of variation in cortical geometry and growth on cortical surface morphology. Specifically, the study uses physical gel models and computational models to evaluate the impact of varying specific features/parameters of the cortical surface. The study makes use of this approach to address the topic of malformations of cortical development and finds that cortical thickness and cortical expansion rate are the drivers of differences in morphogenesis.

The study is composed of two main sections. First, the authors validate numerical simulation and gel model approaches against real cortical postnatal development in the ferret. Next, the study turns to modelling malformations in cortical development using modified tangential growth rate and cortical thickness parameters in numerical simulations. The findings investigate three genetically linked cortical malformations observed in the human brain to demonstrate the impact of the two physical parameters on folding in the ferret brain.

This is a tightly presented study that demonstrates a key insight into cortical morphogenesis and the impact of deviations from normal development. The dual physical and computational modeling approach offers the potential for unique insights into mechanisms driving malformations. This study establishes a strong foundation for further work directly probing the development of cortical folding in the ferret brain. One weakness of the current study is that the interpretation of the results in the context of human cortical development is at present indirect, as the modelling results are solely derived from the ferret. However, these modelling approaches demonstrate proof of concept for investigating related alterations more directly in future work through similar approaches to models of the human cerebral cortex.

We thank the reviewer for the very positive comments. While the current gel and organismal experiments focus on the ferret only, we want to emphasize that our analysis does consider previous observations of human brains and morphologies therein (Tallinen et al., Proc. Natl. Acad. Sci. 2014; Tallinen et al., Nat. Phys. 2016), which we compare and explain. This allows us to analyze the implications of our study broadly to understand the explanations of cortical malformations in humans using the ferret to motivate our study. Further analysis of normal human brain growth using computational and physical gel models can be found in our companion paper (Yin et al., 2025), now also published to eLife: S. Yin, C. Liu, G. P. T. Choi, Y. Jung, K. Heuer, R. Toro, L. Mahadevan, Morphogenesis and morphometry of brain folding patterns across species. eLife, 14, RP107138, 2025. doi:10.7554/eLife.107138

In future work, we plan to obtain malformed human cortical surface data, which would allow us to further investigate related alterations more directly. We have added a remark on this in the revised manuscript (please see page 8–9).

Reviewer 2 (Public review):

Summary:

Based on MRI data of the ferret (a gyrencephalic non-primate animal, in whom folding happens postnatally), the authors create in vitro physical gel models and in silico numerical simulations of typical cortical gyrification. They then use genetic manipulations of animal models to demonstrate that cortical thickness and expansion rate are primary drivers of atypical morphogenesis. These observations are then used to explain cortical malformations in humans.

Strengths:

The paper is very interesting and original, and combines physical gel experiments, numerical simulations, as well as observations in MCD. The figures are informative, and the results appear to have good overall face validity.

We thank the reviewer for the very positive comments.

Weaknesses:

On the other hand, I perceived some lack of quantitative analyses in the different experiments, and currently, there seems to be rather a visual/qualitative interpretation of the different processes and their similarities/differences. Ideally, the authors also quantify local/pointwise surface expansion in the physical and simulation experiments, to more directly compare these processes. Time courses of eg, cortical curvature changes, could also be plotted and compared for those experiments. I had a similar impression about the comparisons between simulation results and human MRI data. Again, face validity appears high, but the comparison appeared mainly qualitative.

We thank the reviewer for the comments. Besides the visual and qualitative comparisons between the models, we would like to point out that we have included the quantification of the shape difference between the real and simulated ferret brain models via spherical parameterization and the curvature-based shape index as detailed in main text Fig. 4 and SI Section 3. We have also utilized spherical harmonics representations for the comparison between the real and simulated ferret brains at different maximum order N. In our revision, we have included more calculations for the comparison between the real and simulated ferret brains at more time points in the SI (please see SI page 6). As for the comparison between the malformation simulation results and human MRI data in the current work, since the human MRI data are two-dimensional while our computational models are threedimensional, we focus on the qualitative comparison between them. In future work, we plan to obtain malformed human cortical surface data, from which we can then perform the parameterization-based and curvature-based shape analysis for a more quantitative assessment.

I felt that MCDs could have been better contextualized in the introduction.

We thank the reviewer for the comment. In our revision, we have revised the description of MCDs in the introduction (please see page 2).

Reviewer #1 (Recommendations for the authors):

The study is beautifully presented and offers an excellent complement to the work presented by Yin et al. In its current form, the malformation portion of the study appears predominantly reliant on the numerical simulations rather than the gel model. It might be helpful, therefore, to further incorporate the results presented in Figure S5 into the main text, as this seems to be a clear application of the physical gel model to modelling malformations. Any additional use of the gel models in the malformation portion of the study would help to further justify the necessity and complementarity of the dual methodological approaches.

We thank the reviewer for the suggestion. We have moved Fig. S5 and the associated description to the main text in the revised manuscript (please see the newly added Figure 5 on page 6 and the description on page 5–7). In particular, we have included a new section on the physical gel and computational models for ferret cortical malformations right before the section on the neurology of ferret and human cortical malformations.

One additional consideration is that the analyses in the current study focus entirely on the ferret cortex. Given the emphasis in the title on the human brain, it may be worthwhile to either consider adding additional modelling of the human cortex or to consider modifying the title to more accurately align with the focus of the methods/results.

We thank the reviewer for the suggestion. While the current gel and organismal experiments focus on the ferret only, we want to emphasize that our analysis does consider previous observations of human brains and morphologies therein (Tallinen et al., Proc. Natl. Acad. Sci. 2014; Tallinen et al., Nat. Phys. 2016), which we compare and explain. This allows us to analyze the implications of our study broadly to understand the explanations of cortical malformations in humans using the ferret to motivate our study. Therefore, we think that the title of the paper seems reasonable. To further highlight the connection between the ferret brain simulations and human brain growth, we have included an additional comparison between human brain surface reconstructions adapted from a prior study and the ferret simulation results in the SI (please see SI Section S4 and SI Fig. S5 on page 9–10).

Two additional minor points:

Table S1 seems sufficiently critical to the motivation for the study and organization of the results section to justify inclusion in the main text. Of course, I would leave any such minor changes to the discretion of the authors.

We thank the reviewer for the suggestion. We have moved Table S1 and the associated description to the main text in the revised manuscript (please see Table 1 on page 7).

Page 7, Column 1: “macacques” → “macaques”.

We thank the reviewer for pointing out the typo. We have fixed it in the revised manuscript (please see page 8).

Reviewer #2 (Recommendations for the authors):

The methods lack details on the human MRI data and patients.

We thank the reviewer for the comment. Note that the human MRI data and patients were from prior works (Smith et al., Neuron 2018; Johnson et al., Nature 2018; Akula et al., Proc. Natl. Acad. Sci. 2023) and were used for the discussion on cortical malformations in Fig. 6. In the revision, we have included a new subsection in the Methods section and provided more details and references of the MRI data and patients (please see page 9–10).

I think it is important to remember that religion and culture are not fixed. They have changed across history and will continue to change as society develops. Many ideas that were once seen as absolute were later reinterpreted or replaced. So when some people use tradition to justify strict beliefs about gender or sexuality, they may be holding on to only one version of that tradition. If we look at the past, we can see that many cultures and even some religious communities once accepted more diverse gender roles.

I am curious about how norms will change in the future. For a long time society has created fixed expectations for men and women and these ideas became so common that people often forget they are learned. As transgender people become more visible and more accepted I wonder if new expectations will slowly form around them too. It is possible that society will start creating its own image of what a transgender person should look like act like or live like even though the whole point of acceptance is to allow people to live freely. I think this shows how important it is to stay aware of how norms form so we do not turn one kind of freedom into another kind of pressure.

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Reply to the reviewers

Response to referee comments: ____RC-2025-03008

Reviewer #1 (Evidence, reproducibility and clarity (Required)):

Summary In this article, the authors used the synthetic TALE DNA binding proteins, tagged with YFP, which were designed to target five specific repeat elements in Trypanosoma brucei genome, including centromere and telomeres-associated repeats and those of a transposon element. This is in order to detect and identified, using YFP-pulldown, specific proteins that bind to these repetitive sequences in T. brucei chromatin. Validation of the approach was done using a TALE protein designed to target the telomere repeat (TelR-TALE) that detected many of the proteins that were previously implicated with telomeric functions. A TALE protein designed to target the 70 bp repeats that reside adjacent to the VSG genes (70R-TALE) detected proteins that function in DNA repair and the protein designed to target the 177 bp repeat arrays (177R-TALE) identified kinetochore proteins associated T. brucei mega base chromosomes, as well as in intermediate and mini-chromosomes, which imply that kinetochore assembly and segregation mechanisms are similar in all T. brucei chromosome.

Major comments: Are the key conclusions convincing? The authors reported that they have successfully used TALE-based affinity selection of protein-associated with repetitive sequences in the T. brucei genome. They claimed that this study has provided new information regarding the relevance of the repetitive region in the genome to chromosome integrity, telomere biology, chromosomal segregation and immune evasion strategies. These conclusions are based on high-quality research, and it is, basically, merits publication, provided that some major concerns, raised below, will be addressed before acceptance for publication. 1. The authors used TALE-YFP approach to examine the proteome associated with five different repetitive regions of the T. brucei genome and confirmed the binding of TALE-YFP with Chip-seq analyses. Ultimately, they got the list of proteins that bound to synthetic proteins, by affinity purification and LS-MS analysis and concluded that these proteins bind to different repetitive regions of the genome. There are two control proteins, one is TRF-YFP and the other KKT2-YFP, used to confirm the interactions. However, there are no experiment that confirms that the analysis gives some insight into the role of any putative or new protein in telomere biology, VSG gene regulation or chromosomal segregation. The proteins, which have already been reported by other studies, are mentioned. Although the author discovered many proteins in these repetitive regions, their role is yet unknown. It is recommended to take one or more of the new putative proteins from the repetitive elements and show whether or not they (1) bind directly to the specific repetitive sequence (e.g., by EMSA); (2) it is recommended that the authors will knockdown of one or a small sample of the new discovered proteins, which may shed light on their function at the repetitive region, as a proof of concept.

Response

The main request from Referee 1 is for individual evaluation of protein-DNA interaction for a few candidates identified in our TALE-YFP affinity purifications, particularly using EMSA to identify binding to the DNA repeats used for the TALE selection. In our opinion, such an approach would not actually provide the validation anticipated by the reviewer. The power of TALE-YFP affinity selection is that it enriches for protein complexes that associate with the chromatin that coats the target DNA repetitive elements rather than only identifying individual proteins or components of a complex that directly bind to DNA assembled in chromatin.

The referee suggests we express recombinant proteins and perform EMSA for selected candidates, but many of the identified proteins are unlikely to directly bind to DNA - they are more likely to associate with a combination of features present in DNA and/or chromatin (e.g. specific histone variants or histone post-translational modifications). Of course, a positive result would provide some validation but only IF the tested protein can bind DNA in isolation - thus, a negative result would be uninformative.

In fact, our finding that KKT proteins are enriched using the 177R-TALE (minichromosome repeat sequence) identifies components of the trypanosome kinetochore known (KKT2) or predicted (KKT3) to directly bind DNA (Marciano et al., 2021; PMID: 34081090), and likewise the TelR-TALE identifies the TRF component that is known to directly associate with telomeric (TTAGGG)n repeats (Reis et al 2018; PMID: 29385523). This provides reassurance on the specificity of the selection, as does the lack of cross selectivity between different TALEs used (see later point 3 below). The enrichment of the respective DNA repeats quantitated in Figure 2B (originally Figure S1) also provides strong evidence for TALE selectivity.

It is very likely that most of the components enriched on the repetitive elements targeted by our TALE-YFP proteins do not bind repetitive DNA directly. The TRF telomere binding protein is an exception - but it is the only obvious DNA binding protein amongst the many proteins identified as being enriched in our TelR-TALE-YFP and TRF-YFP affinity selections.

The referee also suggests that follow up experiments using knockdown of the identified proteins found to be enriched on repetitive DNA elements would be informative. In our opinion, this manuscript presents the development of a new methodology previously not applied to trypanosomes, and referee 2 highlights the value of this methodological development which will be relevant for a large community of kinetoplastid researchers. In-depth follow-up analyses would be beyond the scope of this current study but of course will be pursued in future. To be meaningful such knockdown analyses would need to be comprehensive in terms of their phenotypic characterisation (e.g. quantitative effects on chromosome biology and cell cycle progression, rates and mechanism of recombination underlying antigenic variation, etc) - simple RNAi knockdowns would provide information on fitness but little more. This information is already publicly available from genome-wide RNAi screens (www.tritrypDB.org), with further information on protein location available from the genome-wide protein localisation resource (Tryptag.org). Hence basic information is available on all targets selected by the TALEs after RNAi knock down but in-depth follow-up functional analysis of several proteins would require specific targeted assays beyond the scope of this study.

NonR-TALE-YFP does not have a binding site in the genome, but YFP protein should still be expressed by T. brucei clones with NLS. The authors have to explain why there is no signal detected in the nucleus, while a prominent signal was detected near kDNA (see Fig.2). Why is the expression of YFP in NonR-TALE almost not shown compared to other TALE clones?

Response

The NonR-TALE-YFP immunolocalisation signal indeed is apparently located close to the kDNA and away from the nucleus. We are not sure why this is so, but the construct is sequence validated and correct. However, we note that artefactual localisation of proteins fused to a globular eGFP tag, compared to a short linear epitope V5 tag, near to the kinetoplast has been previously reported (Pyrih et al, 2023; PMID: 37669165),

The expression of NonR-TALE-YFP is shown in Supplementary Fig. S2 in comparison to other TALE proteins. Although it is evident that NonR-TALE-YFP is expressed at lower levels than other TALEs (the different TALEs have different expression levels), it is likely that in each case the TALE proteins would be in relative excess.

It is possible that the absence of a target sequence for the NonR-TALE-YFP in the nucleus affects its stability and cellular location. Understanding these differences is tangential to the aim of this study.

However, importantly, NonR-TALE-YFP is not the only control for used for specificity in our affinity purifications. Instead, the lack of cross-selection of the same proteins by different TALEs (e.g. TelR-TALE-YFP, 177R-TALE-YFP) and the lack of enrichment of any proteins of interest by the well expressed ingiR-TALE-YFP or 147R-TALE-YFP proteins each provide strong evidence for the specificity of the selection using TALEs, as does the enrichment of similar protein sets following affinity purification of the TelR-TALE-YFP and TRF-YFP proteins which both bind telomeric (TTAGGG)n repeats. Moreover, control affinity purifications to assess background were performed using cells that completely lack an expressed YFP protein which further support specificity (Figure 6).

We have added text to highlight these important points in the revised manuscript:

Page 8:

"However, the expression level of NonR-TALE-YFP was lower than other TALE-YFP proteins; this may relate to the lack of DNA binding sites for NonR-TALE-YFP in the nucleus."

Page 8:

"NonR-TALE-YFP displayed a diffuse nuclear and cytoplasmic signal; unexpectedly the cytoplasmic signal appeared to be in the vicinity the kDNA of the kinetoplast (mitochrondria). We note that artefactual localisation of some proteins fused to an eGFP tag has previously been observed in T. brucei (Pyrih et al, 2023)."

Page 10:

Moreover, a similar set of enriched proteins was identified in TelR-TALE-YFP affinity purifications whether compared with cells expressing no YFP fusion protein (No-YFP), the NonR-TALE-YFP or the ingiR-TALE-YFP as controls (Fig. S7B, S8A; Tables S3, S4). Thus, the most enriched proteins are specific to TelR-TALE-YFP-associated chromatin rather than to the TALE-YFP synthetic protein module or other chromatin.

As a proof of concept, the author showed that the TALE method determined the same interacting partners enrichment in TelR-TALE as compared to TRF-YFP. And they show the same interacting partners for other TALE proteins, whether compared with WT cells or with the NonR-TALE parasites. It may be because NonR-TALE parasites have almost no (or very little) YFP expression (see Fig. S3) as compared to other TALE clones and the TRF-YFP clone. To address this concern, there should be a control included, with proper YFP expression.

Response

See response to point 2, but we reiterate that the ingi-TALE -YFP and 147R-TALE-YFP proteins are well expressed (western original Fig. S3 now Fig. S2) but few proteins are detected as being enriched or correspond to those enriched in TelR-TALE-YFP or TRF-YFP affinity purifications (see Fig. S9). Therefore, the ingi-TALE -YFP and 147R-TALE-YFP proteins provide good additional negative controls for specificity as requested. To further reassure the referee we have also included additional volcano plots which compare TelR-TALE-YFP, 70R-TALE-YFP or 177R-TALE-YFP to the ingiR-TALE-YFP affinity selection (new Figure S8). As with No-YFP or NonR-TALE-YFP controls, the use of ingiR-TALE-YFP as a negative control demonstrates that known telomere associated proteins are enriched in TelR-TALE-YFP affinity purification, RPA subunits enriched with 70R-TALE-YFP and Kinetochore KKT poroteins enriched with 177R-TALE-YFP. These analyses demonstrate specificity in the proteins enriched following affinity purification of our different TALE-YFPs and provide support to strengthen our original findings.

We now refer to use of No-YFP, NonR-TALE-YFP, and ingiR-TALE -YFP as controls for comparison to TelR-TALE-YFP, 70R-TALE-YFP or 177R-TALE-YFP in several places:

Page10:

"Moreover, a similar set of enriched proteins was identified in TelR-TALE-YFP affinity purifications whether compared with cells expressing no YFP fusion protein (No-YFP), the NonR-TALE-YFP or the ingiR-TALE-YFP as controls (Fig. S7B, S8A; Tables S3, S4)."

Page 11:

"Thus, the nuclear ingiR-TALE-YFP provides an additional chromatin-associated negative control for affinity purifications with the TelR-TALE-YFP, 70R-TALE-YFP and 177R-TALE-YFP proteins (Fig. S8)."

"Proteins identified as being enriched with 70R-TALE-YFP (Figure 6D) were similar in comparisons with either the No-YFP, NonR-TALE-YFP or ingiR-TALE-YFP as negative controls."

Top Page 12:

"The same kinetochore proteins were enriched regardless of whether the 177R-TALE proteomics data was compared with No-YFP, NonR-TALE or ingiR-TALE-YFP controls."

Discussion Page 13:

"Regardless, the 147R-TALE and ingiR-TALE proteins were well expressed in T. brucei cells, but their affinity selection did not significantly enrich for any relevant proteins. Thus, 147R-TALE and ingiR-TALE provide reassurance for the overall specificity for proteins enriched TelR-TALE, 70R-TALE and 177R-TALE affinity purifications."

After the artificial expression of repetitive sequence binding five-TALE proteins, the question is if there is any competition for the TALE proteins with the corresponding endogenous proteins? Is there any effect on parasite survival or health, compared to the control after the expression of these five TALEs YFP protein? It is recommended to add parasite growth curves, for all the TALE-proteins expressing cultures.

Response

Growth curves for cells expressing TelR-TALE-YFP, 177R-TALE-YFP and ingiR-TALE-YFP are now included (New Fig S3A). No deficit in growth was evident while passaging 70R-TALE-YFP, 147R-TALE-YFP, NonR-TALE-YFP cell lines (indeed they grew slightly better than controls).

The following text has been added page 8:

"Cell lines expressing representative TALE-YFP proteins displayed no fitness deficit (Fig. S3A)."

Since the experiments were performed using whole-cell extracts without prior nuclear fractionation, the authors should consider the possibility that some identified proteins may have originated from compartments other than the nucleus. Specifically, the detection of certain binding proteins might reflect sequence homology (or partial homology) between mitochondrial DNA (maxicircles and minicircles) and repetitive regions in the nuclear genome. Additionally, the lack of subcellular separation raises the concern that cytoplasmic proteins could have been co-purified due to whole cell lysis, making it challenging to discern whether the observed proteome truly represents the nuclear interactome.

Response

In our experimental design, we confirmed bioinformatically that the repeat sequences targeted were not represented elsewhere in the nuclear or mitochondrial genome (kDNA). The absence of subcellular fractionation could result in some cytoplasmic protein selection, but this is unlikely since each TALE targets a specific DNA sequence but is otherwise identical such that cross-selection of the same contaminating protein set would be anticipated if there was significant non-specific binding. We have previously successfully affinity selected 15 chromatin modifiers and identified associated proteins without major issues concerning cytoplasmic protein contamination (Staneva et al 2021 and 2022; PMID: 34407985 and 36169304). Of course, the possibility that some proteins are contaminants will need to be borne in mind in any future follow-up analysis of proteins of interest that we identified as being enriched on specific types of repetitive element in T. brucei. Proteins that are also detected in negative control, or negative affinity selections such as No-YFP, NoR-YFP, IngiR-TALE or 147R-TALE must be disregarded.

'6'. Should the authors qualify some of their claims as preliminary or speculative, or remove them altogether? As mentioned earlier, the author claimed that this study has provided new information concerning telomere biology, chromosomal segregation mechanisms, and immune evasion strategies. But there are no experiments that provides a role for any unknown or known protein in these processes. Thus, it is suggested to select one or two proteins of choice from the list and validate their direct binding to repetitive region(s), and their role in that region of interaction.

Response

As highlighted in response to point 1 the suggested validation and follow up experiments may well not be informative and are beyond the scope of the methodological development presented in this manuscript. Referee 2 describes the study in its current form as "a significant conceptual and technical advancement" and "This approach enhances our understanding of chromatin organization in these regions and provides a foundation for investigating the functional roles of associated proteins in parasite biology."

The Referee's phrase 'validate their direct binding to repetitive region(s)' here may also mean to test if any of the additional proteins that we identified as being enriched with a specific TALE protein actually display enrichment over the repeat regions when examined by an orthogonal method. A key unexpected finding was that kinetochore proteins including KKT2 are enriched in our affinity purifications of the 177R-TALE-YFP that targets 177bp repeats (Figure 6F). By conducting ChIP-seq for the kinetochore specific protein KKT2 using YFP-KKT2 we confirmed that KKT2 is indeed enriched on 177bp repeat DNA but not flanking DNA (Figure 7). Moreover, several known telomere-associated proteins are detected in our affinity selections of TelR-TALE-YFP (Figure 6B, FigS6; see also Reis et al, 2018 Nuc. Acids Res. PMID: 29385523; Weisert et al, 2024 Sci. Reports PMID: 39681615).

Would additional experiments be essential to support the claims of the paper? Request additional experiments only where necessary for the paper as it is, and do not ask authors to open new lines of experimentation. The answer for this question depends on what the authors want to present as the achievements of the present study. If the achievement of the paper was is the creation of a new tool for discovering new proteins, associated with the repeat regions, I recommend that they add a proof for direct interactions between a sample the newly discovered proteins and the relevant repeats, as a proof of concept discussed above, However, if the authors like to claim that the study achieved new functional insights for these interactions they will have to expand the study, as mentioned above, to support the proof of concept.

Response

See our response to point 1 and the point we labelled '6' above.

Are the suggested experiments realistic in terms of time and resources? It would help if you could add an estimated cost and time investment for substantial experiments. I think that they are realistic. If the authors decided to check the capacity of a small sample of proteins (which was unknown before as a repetitive region binding proteins) to interacts directly with the repeated sequence, it will substantially add of the study (e.g., by EMSA; estimated time: 1 months). If the authors will decide to check the also the function of one of at least one such a newly detected proteins (e.g., by KD), I estimate the will take 3-6 months.

Response

As highlighted previously the proposed EMSA experiment may well be uninformative for protein complex components identified in our study or for isolated proteins that directly bind DNA in the context of a complex and chromatin. RNAi knockdown data and cell location data (as well as developmental expression and orthology data) is already available through tritrypDB.org and trtyptag.org

Are the data and the methods presented in such a way that they can be reproduced? Yes

Are the experiments adequately replicated, and statistical analysis adequate? The authors did not mention replicates. There is no statistical analysis mentioned.

Response

The figure legends indicate that all volcano plots of TALE affinity selections were derived from three biological replicates. Cutoffs used for significance: PFor ChiP-seq two biological replicates were analysed for each cell line expressing the specific YFP tagged protein of interest (TALE or KKT2). This is now stated in the relevant figure legends - apologies for this oversight. The resulting data are available for scrutiny at GEO: GSE295698.

Minor comments: -Specific experimental issues that are easily addressable. The following suggestions can be incorporated: 1. Page 18, in the material method section author mentioned four drugs: Blasticidine, Phleomycin and G418, and hygromycin. It is recommended to mention the purpose of using these selective drugs for the parasite. If clonal selection has been done, then it should also be mentioned.

Response

We erroneously added information on several drugs used for selection in our labaoratory. In fact all TALE-YFP construct carry the Bleomycin resistance genes which we select for using Phleomycin. Also, clones were derived by limiting dilution immediately after transfection.

We have amended the text accordingly:

Page 17/18:

"Cell cultures were maintained below 3 x 106 cells/ml. Pleomycin 2.5 mg/ml was used to select transformants containing the TALE construct BleoR gene."

"Electroporated bloodstream cells were added to 30 ml HMI-9 medium and two 10-fold serial dilutions were performed in order to isolate clonal Pleomycin resistant populations from the transfection. 1 ml of transfected cells were plated per well on 24-well plates (1 plate per serial dilution) and incubated at 37{degree sign}C and 5% CO2 for a minimum of 6 h before adding 1 ml media containing 2X concentration Pleomycin (5 mg/ml) per well."

In the method section the authors mentioned that there is only one site for binding of NonR-TALE in the parasite genome. But in Fig. 1C, the authors showed zero binding site. So, there is one binding site for NonR-TALE-YFP in the genome or zero?

Response

We thank the reviewer for pointing out this discrepancy. We have checked the latest Tb427v12 genome assembly for predicted NonR-TALE binding sites and there are no exact matches. We have corrected the text accordingly.

Page 7:

"A control NonR-TALE protein was also designed which was predicted to have no target sequence in the T. bruceigenome."

Page 17:

"A control NonR-TALE predicted to have no recognised target in the T. brucei geneome was designed as follows: BLAST searches were used to identify exact matches in the TREU927 reference genome. Candidate sequences with one or more match were discarded."

The authors used two different anti-GFP antibodies, one from Roche and the other from Thermo Fisher. Why were two different antibodies used for the same protein?

Response

We have found that only some anti-GFP antibodies are effective for affinity selection of associated proteins, whereas others are better suited for immunolocalisation. The respective suppliers' antibodies were optimised for each application.

Page 6: in the introduction, the authors give the number of total VSG genes as 2,634. Is it known how many of them are pseudogenes?

Response

This value corresponds to the number reported by Consentino et al. 2021 (PMID: 34541528) for subtelomeric VSGs, which is similar to the value reported by Muller et al 2018 (PMID: 30333624) (2486), both in the same strain of trypanosomes as used by us. Based on the earlier analysis by Cross et al (PMID: 24992042), 80% of the identified VSGs in their study (2584) are pseudogenes. This approximates to the estimation by Consentino of 346/2634 (13%) being fully functional VSG genes at subtelomeres, or 17% when considering VSGs at all genomic locations (433/2872).

I found several typos throughout the manuscript.

Response

Thank you for raising this, we have read through the manuscipt several times and hopefully corrected all outstanding typos.

Fig. 1C: Table: below TOTAL 2nd line: the number should be 1838 (rather than 1828)

Corrected- thank you.

• Are prior studies referenced appropriately? Yes

• Are the text and figures clear and accurate? Yes

• Do you have suggestions that would help the authors improve the presentation of their data and conclusions? Suggested above

Reviewer #1 (Significance (Required)):

Describe the nature and significance of the advance (e.g., conceptual, technical, clinical) for the field: This study represents a significant conceptual and technical advancement by employing a synthetic TALE DNA-binding protein tagged with YFP to selectively identify proteins associated with five distinct repetitive regions of T. brucei chromatin. To the best of my knowledge, it is the first report to utilize TALE-YFP for affinity-based isolation of protein complexes bound to repetitive genomic sequences in T. brucei. This approach enhances our understanding of chromatin organization in these regions and provides a foundation for investigating the functional roles of associated proteins in parasite biology. Importantly, any essential or unique interacting partners identified could serve as potential targets for therapeutic intervention.

• Place the work in the context of the existing literature (provide references, where appropriate). I agree with the information that has already described in the submitted manuscript, regarding its potential addition of the data resulted and the technology established to the study of VSGs expression, kinetochore mechanism and telomere biology.

• State what audience might be interested in and influenced by the reported findings. These findings will be of particular interest to researchers studying the molecular biology of kinetoplastid parasites and other unicellular organisms, as well as scientists investigating chromatin structure and the functional roles of repetitive genomic elements in higher eukaryotes.

• 1Define your field of expertise with a few keywords to help the authors contextualize your point of view. 2Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate. (1) Protein-DNA interactions/ chromatin/ DNA replication/ Trypanosomes (2) None

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Summary

Carloni et al. comprehensively analyze which proteins bind repetitive genomic elements in Trypanosoma brucei. For this, they perform mass spectrometry on custom-designed, tagged programmable DNA-binding proteins. After extensively verifying their programmable DNA-binding proteins (using bioinformatic analysis to infer target sites, microscopy to measure localization, ChIP-seq to identify binding sites), they present, among others, two major findings: 1) 14 of the 25 known T. brucei kinetochore proteins are enriched at 177bp repeats. As T. brucei's 177bp repeat-containing intermediate-sized and mini-chromosomes lack centromere repeats but are stable over mitosis, Carloni et al. use their data to hypothesize that a 'rudimentary' kinetochore assembles at the 177bp repeats of these chromosomes to segregate them. 2) 70bp repeats are enriched with the Replication Protein A complex, which, notably, is required for homologous recombination. Homologous recombination is the pathway used for recombination-based antigenic variation of the 70bp-repeat-adjacent variant surface glycoproteins.

Major Comments

None. The experiments are well-controlled, claims well-supported, and methods clearly described. Conclusions are convincing.

Response Thank you for these positive comments.

Minor Comments

1) Fig. 2 - I couldn't find an uncropped version showing multiple cells. If it exists, it should be linked in the legend or main text; Otherwise, this should be added to the supplement.

Response

The images presented represent reproducible analyses, and independently verified by two of the authors. Although wider field of view images do not provide the resolution to be informative on cell location, as requested we have provided uncropped images in new Fig. S4 for all the cell lines shown in Figure 2A.

In addition, we have included as supplementary images (Fig. S3B) additional images of TelR-TALE-YFP, 177R-TALE-YFP and ingiR-TALE YFP localisation to provide additional support their observed locations presented in Figure 1. The set of cells and images presented in Figure 2A and in Fig S3B were prepared and obtained by a different authors, independently and reproducibly validating the location of the tagged protein.

2) I think Suppl. Fig. 1 is very valuable, as it is a quantification and summary of the ChIP-seq data. I think the authors could consider making this a panel of a main figure. For the main figure, I think the plot could be trimmed down to only show the background and the relevant repeat for each TALE protein, leaving out the non-target repeats. (This relates to minor comment 6.) Also, I believe, it was not explained how background enrichment was calculated.

Response

We are grateful for the reviewer's positive view of original Fig. S1 and appreciate the suggestion. We have now moved these analysis to part B of main Figure 2 in the revised manuscript - now Figure 2B. We have also provided additional details in the Methods section on the approaches used to assess background enrichment.

Page 19:

Background enrichment calculation

The genome was divided into 50 bp sliding windows, and each window was annotated based on overlapping genomic features, including CIR147, 177 bp repeats, 70 bp repeats, and telomeric (TTAGGG)n repeats. Windows that did not overlap with any of these annotated repeat elements were defined as "background" regions and used to establish the baseline ChIP-seq signal. Enrichment for each window was calculated using bamCompare, as log₂(IP/Input). To adjust for background signal amongst all samples, enrichment values for each sample were further normalized against the corresponding No-YFP ChIP-seq dataset.

Note: While revising the manuscript we also noticed that the script had a nomalization error. We have therefore included a corrected version of these analyses as Figure 2B (old Fig. S1)

3) Generally, I would plot enrichment on a log2 axis. This concerns several figures with ChIP-seq data.

Response

Our ChIP-seq enrichment is calculated by bamCompare. The resulting enrichment values are indeed log2 (IP/Input). We have made this clear in the updated figures/legends.

4) Fig. 4C - The violin plots are very hard to interpret, as the plots are very narrow compared to the line thickness, making it hard to judge the actual volume. For example, in Centromere 5, YFP-KKT2 is less enriched than 147R-TALE over most of the centromere with some peaks of much higher enrichment (as visible in panel B), however, in panel C, it is very hard to see this same information. I'm sure there is some way to present this better, either using a different type of plot or by improving the spacing of the existing plot.

Response

We thank the reviewer for this suggestion; we have elected to provide a Split-Violin plot instead. This improves the presentation of the data for each centromere. The original violin plot in Figure 4C has been replaced with this Split-Violin plot (still Figure 4C).

5) Fig. 6 - The panels are missing an x-axis label (although it is obvious from the plot what is displayed). Maybe the "WT NO-YFP vs" part that is repeated in all the plot titles could be removed from the title and only be part of the x-axis label?

Response

In fact, to save space the X axis was labelled inside each volcano plot but we neglected to indicate that values are a log2 scale indicating enrichment. This has been rectified - see Figure 6, and Fig. S7, S8 and S9.

6) Fig. 7 - I would like to have a quantification for the examples shown here. In fact, such a quantification already exists in Suppl. Figure 1. I think the relevant plots of that quantification (YFP-KKT2 over 177bp-repeats and centromere-repeats) with some control could be included in Fig. 7 as panel C. This opportunity could be used to show enrichment separated out for intermediate-sized, mini-, and megabase-chromosomes. (relates to minor comment 2 & 8)

Response

The CIR147 sequence is found exclusively on megabase-sized chromosomes, while the 177 bp repeats are located on intermediate- and mini-sized chromosomes. Due to limitations in the current genome assembly, it is not possible to reliably classify all chromosomes into intermediate- or mini- sized categories based on their length. Therefore, original Supplementary Fig. S1 presented the YFP-KKT2 enrichment over CIR147 and 177 bp repeats as a representative comparison between megabase chromosomes and the remaining chromosomes (corrected version now presented as main Figure 2B). Additionally, to allow direct comparison of YFP-KKT2 enrichment on CIR147 and 177 bp repeats we have included a new plot in Figure 7C which shows the relative enrichment of YFP-KKT2 on these two repeat types.

We have added the following text , page 12:

"Taking into account the relative to the number of CIR147 and 177 bp repeats in the current T.brucei genome (Cosentino et al., 2021; Rabuffo et al., 2024), comparative analyses demonstrated that YFP-KKT2 is enriched on both CIR147 and 177 bp repeats (Figure 7C)."

7) Suppl. Fig. 8 A - I believe there is a mistake here: KKT5 occurs twice in the plot, the one in the overlap region should be KKT1-4 instead, correct?

Response

Thanks for spotting this. It has been corrected

8) The way that the authors mapped ChIP-seq data is potentially problematic when analyzing the same repeat type in different regions of the genome. The authors assigned reads that had multiple equally good mapping positions to one of these mapping positions, randomly. This is perfectly fine when analysing repeats by their type, independent of their position on the genome, which is what the authors did for the main conclusions of the work. However, several figures show the same type of repeat at different positions in the genome. Here, the authors risk that enrichment in one region of the genome 'spills' over to all other regions with the same sequence. Particularly, where they show YFP-KKT2 enrichment over intermediate- and mini-chromosomes (Fig. 7) due to the spillover, one cannot be sure to have found KKT2 in both regions. Instead, the authors could analyze only uniquely mapping reads / read-pairs where at least one mate is uniquely mapping. I realize that with this strict filtering, data will be much more sparse. Hence, I would suggest keeping the original plots and adding one more quantification where the enrichment over the whole region (e.g., all 177bp repeats on intermediate-/mini-chromosomes) is plotted using the unique reads (this could even be supplementary). This also applies to Fig. 4 B & C.

Response

We thank the reviewer for their thoughtful comments. Repetitive sequences are indeed challenging to analyze accurately, particularly in the context of short read ChIP-seq data. In our study, we aimed to address YFP-KKT2 enrichment not only over CIR147 repeats but also on 177 bp repeats, using both ChIP-seq and proteomics using synthetic TALE proteins targeted to the different repeat types. We appreciate the referees suggestion to consider uniquely mapped reads, however, in the updated genome assembly, the 177 bp repeats are frequently immediately followed by long stretches of 70 bp repeats which can span several kilobases. The size and repetitive nature of these regions exceeds the resolution limits of ChIP-seq. It is therefore difficult to precisely quantify enrichment across all chromosomes.

Additionally, the repeat sequences are highly similar, and relying solely on uniquely mapped reads would result in the exclusion of most reads originating from these regions, significantly underestimating the relative signals. To address this, we used Bowtie2 with settings that allow multi-mapping, assigning reads randomly among equivalent mapping positions, but ensuring each read is counted only once. This approach is designed to evenly distribute signal across all repetitive regions and preserve a meaningful average.

Single molecule methods such as DiMeLo (Altemose et al. 2022; PMID: 35396487) will need to be developed for T. brucei to allow more accurate and chromosome specific mapping of kinetochore or telomere protein occupancy at repeat-unique sequence boundaries on individual chromosomes.

Reviewer #2 (Significance (Required)):

This work is of high significance for chromosome/centromere biology, parasitology, and the study of antigenic variation. For chromosome/centromere biology, the conceptual advancement of different types of kinetochores for different chromosomes is a novelty, as far as I know. It would certainly be interesting to apply this study as a technical blueprint for other organisms with mini-chromosomes or chromosomes without known centromeric repeats. I can imagine a broad range of labs studying other organisms with comparable chromosomes to take note of and build on this study. For parasitology and the study of antigenic variation, it is crucial to know how intermediate- and mini-chromosomes are stable through cell division, as these chromosomes harbor a large portion of the antigenic repertoire. Moreover, this study also found a novel link between the homologous repair pathway and variant surface glycoproteins, via the 70bp repeats. How and at which stages during the process, 70bp repeats are involved in antigenic variation is an unresolved, and very actively studied, question in the field. Of course, apart from the basic biological research audience, insights into antigenic variation always have the potential for clinical implications, as T. brucei causes sleeping sickness in humans and nagana in cattle. Due to antigenic variation, T. brucei infections can be chronic.

Response

Thank you for supporting the novelty and broad interest of our manuscript

My field of expertise / Point of view:

I'm a computer scientist by training and am now a postdoctoral bioinformatician in a molecular parasitology laboratory. The laboratory is working on antigenic variation in T. brucei. The focus of my work is on analyzing sequencing data (such as ChIP-seq data) and algorithmically improving bioinformatic tools.

Author response:

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

Reviewer #1 (Public review):

(1) The authors only report the quality of the classification considering the number of videos used for training, but not considering the number of mice represented or the mouse strain. Therefore, it is unclear if the classification model works equally well in data from all the mouse strains tested, and how many mice are represented in the classifier dataset and validation.

We agree that strain-level performance is critical for assessing generalizability. In the revision we now report per-strain accuracy and F1 for the grooming classifier, which was trained on videos spanning 60 genetically diverse strains (n = 1100 videos) and evaluated on the test set videos spanning 51 genetically diverse strains (n=153 videos). Performance is uniform across most strains (median F1 = 0.94, IQR = 0.899–0.956), with only modest declines in albino lines that lack contrast under infrared illumination; this limitation and potential remedies are discussed in the text. The new per-strain metrics are presented in the Supplementary figure (corresponding to Figure 4).

(2) The GUI requires pose tracking for classification, but the software provided in JABS does not do pose tracking, so users must do pose tracking using a separate tool. Currently, there is no guidance on the pose tracking recommendations and requirements for usage in JABS. The pose tracking quality directly impacts the classification quality, given that it is used for the feature calculation; therefore, this aspect of the data processing should be more carefully considered and described.

We have added a section to the methods describing how to use the pose estimation models used in JABS. The reviewer is correct that pose tracking quality will impact classification quality. We recommend that classifiers should only be re-used on pose files generated by the same pose models used in the behavior classifier training dataset. We hope that the combination of sharing classifier training data and making a more unified framework for developing and comparing classifiers will get us closer to having foundational behavior classification models that work in many environments. We also would like to emphasize that deviating from using our pose model will also likely hinder re-using our shared large datasets in JABS-AI (JABS1200, JABS600, JABS-BxD).

(3) Many statistical and methodological details are not described in the manuscript, limiting the interpretability of the data presented in Figures 4,7-8. There is no clear methods section describing many of the methods used and equations for the metrics used. As an example, there are no details of the CNN used to benchmark the JABS classifier in Figure 4, and no details of the methods used for the metrics reported in Figure 8.

We thank the reviewer for bringing this to our attention. We have added a methods section to the manuscript to address this concern. Specifically, we now provide: (1) improved citation visibility of the source of CNN experiments such that the reader can locate the architecture information, (2) mathematical formulations for all performance metrics (precision, recall, F1, …) with explicit equations;  (3) detailed statistical procedures including permutation testing methods, power analysis and multiple testing corrections used throughout Figures 7-8. These additions facilitate reproducibility and proper interpretation of all quantitative results presented in the manuscript.

Reviewer #2 (Public review):

(1) The manuscript as written lacks much-needed context in multiple areas: what are the commercially available solutions, and how do they compare to JABS (at least in terms of features offered, not necessarily performance)? What are other open-source options?

JABS adds to a list of commercial and open source animal tracking platforms. There are several reviews and resources that cover these technologies. JABS covers hardware, behavior prediction, a shared resource for classifiers, and genetic association studies. We’re not aware of another system that encompasses all these components. Commercial packages such as EthoVision XT and HomeCage Scan give users a ready-made camera-plus-software solution that automatically tracks each mouse and reports simple measures such as distance travelled or time spent in preset zones, but they do not provide open hardware designs, editable behavior classifiers, or any genetics workflow. At the open-source end, the >100 projects catalogued on OpenBehavior and summarised in recent reviews (Luxem et al., 2023; Işık & Ünal 2023) usually cover only one link in the chain—DIY rigs, pose-tracking libraries (e.g., DeepLabCut, SLEAP) or supervised and unsupervised behaviour-classifier pipelines (e.g., SimBA, MARS, JAABA, B-SOiD, DeepEthogram). JABS provides an open source ecosystem that integrates all four: (i) top-down arena hardware with parts list and assembly guide; (ii) an active-learning GUI that produces shareable classifiers; (iii) a public web service that enables sharing of the trained classifier and applies any uploaded classifier to a large and diverse strain survey; and (iv) built-in heritability, genetic-correlation and GWAS reporting. We have added a concise paragraph in the Discussion that cites these resources and makes this end-to-end distinction explicit.

(2) How does the supervised behavioral classification approach relate to the burgeoning field of unsupervised behavioral clustering (e.g., Keypoint-MoSeq, VAME, B-SOiD)? 

The reviewer raises an important point about the rapidly evolving landscape of automated behavioral analysis, where both supervised and unsupervised approaches offer complementary strengths for different experimental contexts. Unsupervised methods like Keypoint-MoSeq , VAME , and B-SOiD , which prioritize motif discovery from unlabeled data but may yield less precise alignments with expert annotations, as evidenced by lower F1 scores in comparative evaluations. Supervised approaches (like ours), by contrast, employ fully supervised classifiers to deliver frame-accurate, behavior-specific scores that align directly with experimental hypotheses. Ultimately, a pragmatic hybrid strategy, starting with unsupervised pilots to identify motifs and transitioning to supervised fine-tuning with minimal labels, can minimize annotation burdens and enhance both discovery and precision in ethological studies. This has been added in the discussion section of the manuscript.

(3) What kind of studies will this combination of open field + pose estimation + supervised classifier be suitable for? What kind of studies is it unsuited for? These are all relevant questions that potential users of this platform will be interested in.

This approach is suitable for a wide array of neuroscience, genetics, pharmacology, preclinical, and ethology studies. We have published in the domains of action detection for complex behaviors such as grooming, gait and posture, frailty, nociception, and sleep. We feel these tools are indispensable for modern behavior analysis. 

(4) Throughout the manuscript, I often find it unclear what is supported by the software/GUI and what is not. For example, does the GUI support uploading videos and running pose estimation, or does this need to be done separately? How many of the analyses in Figures 4-6 are accessible within the GUI?

We have now clarified these. The JABS framework comprises two distinct GUI applications with complementary functionalities. The JABS-AL (active learning) desktop application handles video upload, behavioral annotation, classifier training, and inference -- it does not perform pose estimation, which must be completed separately using our pose tracking pipeline (https://github.com/KumarLabJax/mouse-tracking-runtime). If a user does not want to use our pose tracking pipeline, we have provided conversions through SLEAP to convert to our JABS pose format.  The web-based GUI enables classifier sharing and cloud-based inference on our curated datasets (JABS600, JABS1200) and downstream behavioral statistics and genetic analyses (Figures 4-6). The JABS-AL application also supports CLI (command line interface) operation for batch processing.  We have clarified these distinctions and provided a comprehensive workflow diagram in the revised Methods section.

(5) While the manuscript does a good job of laying out best practices, there is an opportunity to further improve reproducibility for users of the platform. The software seems likely to perform well with perfect setups that adhere to the JABS criteria, but it is very likely that there will be users with suboptimal setups - poorly constructed rigs, insufficient camera quality, etc. It is important, in these cases, to give users feedback at each stage of the pipeline so they can understand if they have succeeded or not. Quality control (QC) metrics should be computed for raw video data (is the video too dark/bright? are there the expected number of frames? etc.), pose estimation outputs (do the tracked points maintain a reasonable skeleton structure; do they actually move around the arena?), and classifier outputs (what is the incidence rate of 1-3 frame behaviors? a high value could indicate issues). In cases where QC metrics are difficult to define (they are basically always difficult to define), diagnostic figures showing snippets of raw data or simple summary statistics (heatmaps of mouse location in the open field) could be utilized to allow users to catch glaring errors before proceeding to the next stage of the pipeline, or to remove data from their analyses if they observe critical issues.

These are excellent suggestions that align with our vision for improving user experience and data quality assessment. We recognize the critical importance of providing users with comprehensive feedback at each stage of the pipeline to ensure optimal performance across diverse experimental setups. Currently, we provide end-users with tools and recommendations to inspect their own data quality. In our released datasets (Strain Survey OFA and BXD OFA), we provide video-level quality summaries for coverage of our pose estimation models. 

For behavior classification quality control, we employ two primary strategies to ensure proper operation: (a) outlier manual validation and (b) leveraging known characteristics about behaviors. For each behavior that we predict on datasets, we manually inspect the highest and lowest expressions of this behavior to ensure that the new dataset we applied it to maintains sufficient similarity. For specific behavior classifiers, we utilize known behavioral characteristics to identify potentially compromised predictions. As the reviewer suggested, high incidence rates of 1-3 frame bouts for behaviors that typically last multiple seconds would indicate performance issues.

We currently maintain in-house post-processing scripts that handle quality control according to our specific use cases. Future releases of JABS will incorporate generalized versions of these scripts, integrating comprehensive QC capabilities directly into the platform. This will provide users with automated feedback on video quality, pose estimation accuracy, and classifier performance, along with diagnostic visualizations such as movement heatmaps and behavioral summary statistics.

Reviewer #1 (Recommendations for the authors):

(1) A weakness of this tool is that it requires pose tracking, but the manuscript does not detail how pose tracking should be done and whether users should expect that the data deposited will help their pose tracking models. There is no specification on how to generate pose tracking that will be compatible with JABS. The classification quality is directly linked to the quality of the pose tracking. The authors should provide more details of the requirements of the pose tracking (skeleton used) and what pose tracking tools are compatible with JABS. In the user website link, I found no such information. Ideally, JABS would be integrated with the pose tracking tool into a single pipeline. If that is not possible, then the utility of this tool relies on more clarity on which pose tracking tools are compatible with JABS.

The JABS ecosystem was deliberately designed with modularity in mind, separating the pose estimation pipeline from the active learning and classification app (JABS-AL) to offer greater flexibility and scalability for users working across diverse experimental setups. Our pose estimation pipeline is documented in detail within the new Methods subsection, outlining the steps to obtain JABS-compatible keypoints with our recommended runtime (https://github.com/KumarLabJax/mouse-tracking-runtime) and frozen inference models (https://github.com/KumarLabJax/deep-hrnet-mouse). This pipeline is an independent component within the broader JABS workflow, generating skeletonized keypoint data that are then fed into the JABS-AL application for behavior annotation and classifier training.

By maintaining this separation, users have the option to use their preferred pose tracking tools— such as SLEAP —while ensuring compatibility through provided conversion utilities to the JABS skeleton format. These details, including usage instructions and compatibility guidance, are now thoroughly explained in the newly added pose estimation subsection of our Methods section. This modular design approach ensures that users benefit from best-in-class tracking while retaining the full power and reproducibility of our active learning pipeline.

(2) The authors should justify why JAABA was chosen to benchmark their classifier. This tool was published in 2013, and there have been other classification tools (e.g., SIMBA) published since then.  

We appreciate the reviewer’s suggestion regarding SIMBA. However, our comparisons to JAABA and a CNN are based on results from prior work (Geuther, Brian Q., et al. "Action detection using a neural network elucidates the genetics of mouse grooming behavior." Elife 10 (2021): e63207.), where both were used to benchmark performance on our publicly released dataset. In this study, we introduce JABS as a new approach and compare it against those established baselines. While SIMBA may indeed offer competitive performance, we believe the responsibility to demonstrate this lies with SIMBA’s authors, especially given the availability of our dataset for benchmarking.

(3) I had a lot of trouble understanding the elements of the data calculated in JABS vs outside of JABS. This should be clarified in the manuscript.

(a) For example, it was not intuitive that pose tracking was required and had to be done separately from the JABS pipeline. The diagrams and figures should more clearly indicate that.

(b) In section 2.5, are any of those metrics calculated by JABS? Another software GEMMA, but no citation is provided for this tool. This created ambiguity regarding whether this is an analysis that is separate from JABS or integrated into the pipeline.  

We acknowledge the confusion regarding the delineation between JABS components and external tools, and we have comprehensively addressed this throughout the manuscript. The JABS ecosystem consists of three integrated modules: JABS-DA (data acquisition), JABS-AL (active learning for behavior annotation and classifier training), and JABS-AI (analysis and integration via web application). Pose estimation, while developed by our laboratory, operates as a preprocessing pipeline that generates the keypoint coordinates required for subsequent JABS classifier training and annotation workflows. We have now added a dedicated Methods subsection that explicitly maps each analytical step to its corresponding software component, clearly distinguishing between core JABS modules and external tools (such as GEMMA for genetic analysis). Additionally, we have provided proper citations and code repositories for all external pipelines to ensure complete transparency regarding the computational workflow and enable full reproducibility of our analyses.

(4) There needs to be clearer explanations of all metrics, methods, and transformations of the data reported.

(a) There is very little information about the architecture of the classification model that JABS uses.

(b) There are no details on the CNN used for comparing and benchmarking the classifier in JABS.

(c) Unclear how the z-scoring of the behavioral data in Figure 7 was implemented.

(d) There is currently no information on how the metrics in Figure 8 are calculated.

We have added a comprehensive Methods section that not only addresses the specific concerns raised above but provides complete methodological transparency throughout our study. This expanded section includes detailed descriptions of all computational architectures (including the JABS classifier and grooming benchmark models and metrics), statistical procedures and data transformations (including the z-scoring methodology for Figure 7), downstream genetic analysis (including all measures presented in Figure 8), and preprocessing pipelines. 

(5) The authors talk about their datasets having visual diversity, but without seeing examples, it is hard to know what they mean by this visual diversity. Ideally, the manuscript would have a supplementary figure with a representation of the variety of setups and visual diversity represented in the datasets used to train the model. This is important so that readers can quickly assess from reading the manuscript if the pre-trained classifier models could be used with the experimental data they have collected.

The visual diversity of our training datasets has been comprehensively documented in our previous tracking work (https://www.nature.com/articles/s42003-019-0362-1), which systematically demonstrates tracking performance across mice with diverse coat colors (black, agouti, albino, gray, brown, nude, piebald), body sizes including obese mice, and challenging recording conditions with dynamic lighting and complex environments. Notably, Figure 3B in that publication specifically illustrates the robustness across coat colors and body shapes that characterize the visual diversity in our current classifier training data. To address the reviewer's concern and enable readers to quickly assess the applicability of our pre-trained models to their experimental data, we have now added this reference to the manuscript to ground our claims of visual diversity in published evidence.

(6) All figures have a lot of acronyms used that are not defined in the figure legend. This makes the figures really hard to follow. The figure legends for Figures 1,2, 7, and 9 did not have sufficient information for me to comprehend the figure shown.

We have fixed this in the manuscript. 

(7) In the introduction, the authors talk about compression artifacts that can be introduced in camera software defaults. This is very vague without specific examples.

This is a complex topic that balances the size and quality of video data and is beyond the scope of this paper. We have carefully optimized this parameter and given the user a balanced solution. A more detailed blog post on compression artifacts can be found at our lab’s webpage (https://www.kumarlab.org/2018/11/06/brians-video-compression-tests/). We have also added a comment about keyframes shifting temporal features in the main manuscript. 

(8) More visuals of the inside of the apparatus should be included as supplementary figures. For example, to see the IR LEDs surrounding the camera.

We have shared data from JABS as part of several papers including the tracking paper (Geuther et al 2019), grooming, gait and posture, mouse mass. We have also released entire datasets that as part of this paper (JABS1800, JABS-BXD). We also have step by step assembly guide that shows the location of the lights/cameras and other parts (see Methods, JABS workflow guide, and this PowerPoint file in the GitHub repository (https://github.com/KumarLabJax/JABS-datapipeline/blob/main/Multi-day%20setup%20PowerPoint%20V3.pptx).

(9) Figure 2 suggests that you could have multiple data acquisition systems simultaneously. Do each require a separate computer? And then these are not synchronized data across all boxes?

Each JABS-DA unit has its own edge device (Nvidia Jetson). Each system (which we define as multiple JABS-DA areas associated with one lab/group) can have multiple recording devices (arenas). The system requires only 1 control portal (RPi computer) and can handle as many recording devices as needed (Nvidia computer w/ camera associated with each JABS-DA arena). To collect data, 1 additional computer is needed to visit the web control portal and initiate a recording session. Since this is a web portal, users can use any computer or a tablet. The recording devices are not strictly synchronized but can be controlled in a unified manner.

(10) The list of parts on GitHub seems incomplete; many part names are not there.

We thank referee for bringing this to our attention. We have updated the GitHub repository (and its README) which now links out to the design files. 

(11) The authors should consider adding guidance on how tethers and headstages are expected to impact the use of JABS, as many labs would be doing behavioral experiments combined with brain measurements.

While our pose estimation model was not specifically trained on tethered animals, published research demonstrates that keypoint detection models maintain robust performance despite the presence of headstages and recording equipment. Once accurate pose coordinates are extracted, the downstream behavior classification pipeline operates independently of the pose estimation method and would remain fully functional. We recommend users validate pose estimation accuracy in their specific experimental setup, as the behavior classification component itself is agnostic to the source of pose coordinates.

Reviewer #2 (Recommendations for the authors):

(1) "Using software-defaults will introduce compression artifacts into the video and will affect algorithm performance." Can this be quantified? I imagine most of the performance hit comes from a decrease in pose estimation quality. How does a decrease in pose estimation quality translate to action segmentation? Providing guidelines to potential users (e.g., showing plots of video compression vs classifier performance) would provide valuable information for anyone looking to use this system (and could save many labs countless hours replicating this experiment themselves). A relevant reference for the effect of compression on pose estimation is Mathis, Warren 2018 (bioRxiv): On the inference speed and video-compression robustness of DeepLabCut.

Since our behavior classification approach depends on features derived from keypoint, changes in keypoint accuracy will affect behavior segmentation accuracy. We agree that it is important to try and understand this further, particularly with the shared bioRxiv paper investigating the effect of compression on pose estimation accuracy. Measuring the effect of compression on keypoint and behavior classification is a complex task to evaluate concisely, given the number of potential variables to inspect. To list a few variables that should be investigated are: discrete cosine transform quality (Mathis, Warren experiment), Frame Size (Mathis, Warren experiment), Keyframe Interval (new, unique to video data), inter-frame settings (new, unique to video data), behavior of interest, Pose models with compression-augmentation used in training ( https://arxiv.org/pdf/1506.08316?) and type of CNN used (under active development). The simplest recommendation that we can make at this time is that we know compression will affect behavior predictions and that users should be cautious about using our shared classifiers on compressed video data. To show that we are dedicated in sharing these results as we run those experiments, in a related work ( CV4Animals conference accepted paper (https://www.cv4animals.com/) and can be downloaded here https://drive.google.com/file/d/1UNQIgCUOqXQh3vcJbM4QuQrq02HudBLD/view) we have already begun to inspect how changing some factors affect behavior segmentation performance. In this work, we investigate the robustness of behavior classification across multiple behaviors using different keypoint subsets. Our findings in this work is that classifiers are relatively stable across different keypoint subsets. We are actively working on follow-up effort to investigate the effect of keypoint noise, CNN model architecture, and other factors we've listed above on behavior segmentation tasks.

(2) The analysis of inter-annotator variability is very interesting. I'm curious how these differences compare to two other types of variability:

(a) intra-annotator variability; I think this is actually hard to quantify with the presented annotation workflow. If a given annotator re-annotated a set of videos, but using different sparse subsets of the data, it is not possible to disentangle annotator variability versus the effect of training models on different subsets of data. This can only be rigorously quantified if all frames are labeled in each video.

We propose an alternative approach to behavior classifier development in the text associated with Figure 3C. We do not advocate for high inter-annotator agreement since individual behavior experts have differing labeling style (an intuitive understanding of the behavior). Rather, we allow multiple classifiers for the same behavior and allow the end user to prioritize classifiers based on heritability of the behavior from a classifier.  

(b) In lieu of this, I'd be curious to see the variability in model outputs trained on data from a single annotator, but using different random seeds or train/val splits of the data. This analysis would provide useful null distributions for each annotator and allow for more rigorous statistical arguments about inter-annotator variability. 

JABS allows the user to use multiple classifiers (random forest, XGBoost). We do not expect the user to carry out hyperparameter tuning or other forms of optimization. We find that the major increase in performance comes from optimizing the size of the window features and folds of cross validation. However, future versions of JABS-AL could enable a complete hyper-parameter scan across seeds and data splits to obtain a null distribution for each annotator. 

(c) I appreciate the open-sourcing of the video/pose datasets. The authors might also consider publicly releasing their pose estimation and classifier training datasets (i.e., data plus annotations) for use by method developers.

We thank the referee for acknowledging our commitment to open data sharing practices. Building upon our previously released strain survey dataset, we have now also made our complete classifier training resources publicly available, including the experimental videos, extracted pose coordinates, and behavioral annotations. The repository link has been added to the manuscript to ensure full reproducibility and facilitate community adoption of our methods.  

(3) More thorough discussion on the limitations of the top-down vs bottom-up camera viewpoint; are there particular scientific questions that are much better suited to bottomup videos (e.g., questions about paw tremors, etc.).

Top-down imaging, bottom-up, and multi-view imaging have a variety of pros and cons. Generally speaking, multi-view imaging will provide the most accurate pose models but requires increased resources on both hardware setup as well as processing of data. Top-down provides the advantage of flexibility for materials, since the floor doesn’t need to be transparent. Additionally lighting and potential reflection with the bottom-up perspective. Since the paws are not occluded from the bottom-up perspective, models should have improved paw keypoint precision allowing the model to observe more subtle behaviors. However, the appearance of the arena floor will change over time as the mice defecate and urinate. Care must be taken to clean the arena between recordings to ensure transparency is maintained. This doesn’t impact top-down imaging that much but will occlude or distort from the bottom-up perspective. Additionally, the inclusion of bedding for longer recordings, which is required by IACUC, will essentially render bottom-up imaging useless because the bedding will completely obscure the mouse. Overall, while bottomup may provide a precision benefit that will greatly enhance subtle motion, top-down imaging is overall more robust for obtaining consistent imaging across large experiments for longer periods of time.

(4) More thorough discussion on what kind of experiments would warrant higher spatial or temporal resolution (e.g., investigating slight tremors in a mouse model of neurodegenerative disease might require this greater resolution).

This is an important topic that deserves its own perspective guide. We try to capture some of this in the paper on specifications. However, we only scratch the surface. Overall, there are tradeoffs between frame rate, resolution, color/monochrome, and compression. Labs have collected data at hundreds of frames per second to capture the kinetics of reflexive behavior for pain (AbdoosSaboor lab) or whisking behavior. Labs have also collected data a low 2.5 frames per second for tracking activity or centroid tracking (see Kumar et al PNAS). The data collection specifications are largely dependent on the behaviors being captured. Our rule of thumb is the Nyquist Limit, which states that the data capture rate needs to be twice that of the frequency of the event. For example, certain syntaxes of grooming occur at 7Hz and we need 14FPS to capture this data. JABS collects data at 30FPS, which is a good compromise between data load and behavior rate. We use 800x800 pixel resolution which is a good compromise to capture animal body parts while limiting data size. Thank you for providing the feedback that the field needs guidance on this topic. We will work on creating such guidance documents for video data acquisition parameters to capture animal behavior data for the community as a separate publication.

(5) References 

(a) Should add the following ref when JAABA/MARS are referenced: Goodwin et al.2024, Nat Neuro (SimBA)

(b) Could also add Bohnslav et al. 2021, eLife (DeepEthogram).

(c) The SuperAnimal DLC paper (Ye et al. 2024, Nature Comms) is relevant to the introduction/discussion as well.

We thank the referee for the suggestions. We have added these references.  

(6) Section 2.2:

While I appreciate the thoroughness with which the authors investigated environmental differences in the JABS arena vs standard wean cage, this section is quite long and eventually distracted me from the overall flow of the exposition; might be worth considering putting some of the more technical details in the methods/appendix.

These are important data for adopters of JABS to gain IACUC approval in their home institution. These committees require evidence that any new animal housing environment has been shown to be safe for the animals. In the development of JABS, we spent a significant amount of time addressing the JAX veterinary and IACUC concerns. Therefore, we propose that these data deserve to be in the main text. 

(7) Section 2.3.1:

(a) Should again add the DeepEthogram reference here

(b) Should reference some pose estimation papers: DeepLabCut, SLEAP, Lightning Pose. 

We thank the referee for the suggestions. We have added these references.  

(c) "Pose based approach offers the flexibility to use the identified poses for training classifiers for multiple behaviors" - I'm not sure I understand why this wouldn't be possible with the pixel-based approach. Is the concern about the speed of model training? If so, please make this clearer.

The advantage lies not just in training speed, but in the transferability and generalization of the learned representations. Pose-based approaches create structured, low-dimensional latent embeddings that capture behaviorally relevant features which can be readily repurposed across different behavioral classification tasks, whereas pixel-based methods require retraining the entire feature extraction pipeline for each new behavior. Recent work demonstrates that pose-based models achieve greater data efficiency when fine-tuned for new tasks compared to pixel-based transfer learning approaches [1], and latent behavioral representations can be partitioned into interpretable subspaces that generalize across different experimental contexts [2]. While pixel-based approaches can achieve higher accuracy on specific tasks, they suffer from the "curse of dimensionality" (requiring thousands of pixels vs. 12 pose coordinates per frame) and lack the semantic structure that makes pose-based features inherently reusable for downstream behavioral analysis.

(1) Ye, Shaokai, et al. "SuperAnimal pretrained pose estimation models for behavioral analysis." Nature communications 15.1 (2024): 5165.

(2) Whiteway, Matthew R., et al. "Partitioning variability in animal behavioral videos using semi-supervised variational autoencoders." PLoS computational biology 17.9 (2021): e1009439.  

(d) The pose estimation portion of the pipeline needs more detail. Do users use a pretrained network, or do they need to label their own frames and train their own pose estimator? If the former, does that pre-trained network ship with the software? Is it easy to run inference on new videos from a GUI or scripts? How accurate is it in compliant setups built outside of JAX? How long does it take to process videos?

We have added the guidance on pose estimation in the manuscript (section “2.3.1 Behavior annotation and classifier training” and in the methods section titled “Pose tracking pipeline”)

(e) The final paragraph describing how to arrive at an optimal classifier is a bit confusing - is this the process that is facilitated by the app, or is this merely a recommendation for best practices? If this is the process the app requires, is it indeed true that multiple annotators are required? While obviously good practice, I imagine there will be many labs that just want a single person to annotate, at least in the beginning prototyping stages. Will the app allow training a model with just a single annotator?

We have clarified this in the text. 

(8) Section 2.5:

(a) This section contained a lot of technical details that I found confusing/opaque, and didn't add much to my overall understanding of the system; sec 2.6 did a good job of clarifying why 2.5 is important. It might be worth motivating 2.5 by including the content of 2.6 first, and moving some of the details of 2.5 to the method/appendix.

We moved some of the technical details in section 2.5 to the methods section titled “Genetic analysis”. Furthermore, we have added few statements to motivate the need of genetic analysis and how the webapp can facilitate this (which is introduced in the section 2.6)    

(9) Minor corrections:

(a) Bottom of first page, "always been behavior quantification task" missing "a".

(b) "Type" column in Table S2 is undocumented and unused (i.e., all values are the same); consider removing.

(c) Figure 4B, x-axis: add units.

(d) Page 8/9: all panel references to Figure S1 are off by one

We have fixed them in the updated manuscript.

Author response:

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

Reviewer #1 (Public review):

Circannual timing is a phylogenetically widespread phenomenon in long-lived organisms and is central to the seasonal regulation of reproduction, hibernation, migration, fur color changes, body weight, and fat deposition in response to photoperiodic changes. Photoperiodic control of thyroid hormone T3 levels in the hypothalamus dictates this timing. However, the mechanisms that regulate these changes are not fully understood. The study by Stewart et al. reports that hypothalamic iodothyronine deiodinase 3 (Dio3), the major inactivator of the biologically active thyroid hormone T3, plays a critical role in circannual timing in the Djungarian hamster. Overall, the study yields important results for the field and is well-conducted, with the exception of the CRISPR/Cas9 manipulation.

We appreciate the positive and supportive comment from the Reviewer. We have clarified the oversight in the Crispr/Cas9 data representation below. Our correction should alleviate any concern raised.

Figure 1 lays the foundation for examining circannual timing by establishing the timing of induction, maintenance, and recovery phases of the circannual timer upon exposure of hamsters to short photoperiod (SP) by monitoring morphological and physiological markers. Measures of pelage color, torpor, body mass, plasma glucose, etc, established that the initiation phase occurred by weeks 4-8 in SP, the maintenance by weeks 12-20, and the recovery after week 20, where all morphological and physiological changes started to reverse back to long photoperiod phenotypes.

The statistical analyses look fine, and the results are unambiguous.

We thank the Reviewer for recognizing our attempts to highlight the phenomenon of circannual interval timing.

Their representation could, however, be improved. In Figures 1d and 1e, two different measures are plotted on each graph and differentiated by dots and upward or downward arrowheads. The plots are so small, though, that distinguishing between the direction of the arrows is difficult. Some color coding would make it more reader-friendly. The same comment applies to Figure S4. 

We have increased the panel size for Figure 1d and 1e. We have also changed the colour of the graphs in Figure 1d and 1e to facilitate the differentiation of the two dependent variables. For the circos plots, we attempted different ways to represent the data. We have opted to keep the figures in their current stage. The overall aim is to provide a ‘gestalt’ view of the timing of changes in transcript expression and highlighted only a few key genes. The whole dataset is provided in the supplementary materials for Reviewer/Reader interrogation.

The authors went on to profile the transcriptome of the mediobasal and dorsomedial hypothalamus, paraventricular nucleus, and pituitary gland (all known to be involved in seasonal timing) every 4 weeks over the different phases of the circannual interval timer. A number of transcripts displaying seasonal rhythms in expression levels in each of the investigated structures were identified, including transcripts whose expression peaks during each phase. This included two genes of particular interest due to their known modulation of expression in response to photoperiod, Dio3 and Sst, found among the transcripts upregulated during the induction and maintenance phases, respectively. The experiments are technically sound and properly analyzed, revealing interesting candidates. Again, my main issues lie with the representation in the figure. In particular, the authors should clarify what the heatmaps on the right of Figures 1f and 1g represent. I suspect they are simply heatmaps of averaged expression of all genes within a defined category, but a description is missing in the legend, as well as a scale for color coding near the figure.

We have clarified the heatmap and density maps in the Figure legend. We apologise for the lack of information to describe the figure panels. (see lines 644-648)

Figure 2 reveals that SP-programmed body mass loss is correlated to increased Dio3-dependent somatostatin (Sst) expression. First, to distinguish whether the body mass loss was controlled by rheostatic mechanisms and not just acute homeostatic changes in energy balance, experiments from hamsters fed ad lib or experiencing an acute food restriction in both LP and SP were tested. Unlike plasma insulin, food restriction had no additional effect on SP-driven epididymal fat mass loss (Figure S7). This clearly establishes a rheostatic control of body mass loss across weeks in SP conditions. Importantly, Sst expression in the mediobasal hypothalamus increased in both ad lib fed or restriction fed SP hamsters and this increase in expression could be reduced by a single subcutaneous injection of active T3, clearly suggesting that increase in Sst expression in SP is due to a decrease of active T3 likely via Dio3 increase in expression in the hypothalamus. The results are unambiguous

We thank the Reviewer for the supportive and affirmative feedback.

Figure 3 provides a functional test of Dio3's role in the circannual timer. Mediobasal hypothalamic injections of CRISPR-Cas9 lentiviral vectors expressing two guide RNAs targeting the hamster Dio3 led to a significant reduction in the interval between induction and recovery phases seen in SP as measured by body mass, and diminished the extent of pelage color change by weeks 15-20. In addition, hamsters that failed to respond to SP exposure by decreasing their body mass also had undetectable Dio3 expression in the mediobasal hypothalamus. Together, these data provide strong evidence that Dio3 functions in the circannual timer. I noted, however, a few problems in the way the CRISPR modification of Dio3 in the mediobasal hypothalamus was reported in Figure S8. One is in Figure S8b, where the PAM sites are reported to be 9bp and 11bp downstream of sgRNA1 and sgRNA2, respectively. Is this really the case? If so, I would have expected the experiment to fail to show any effect as PAM sites need to immediately follow the target genomic sequence recognized by the sgRNA for Cas9 to induce a DNA double-stranded break. It seems that each guide contains a 3' NGG sequence that is currently underlined as part of sgRNAs in both Fig S8b and in the method section. If this is not a mistake in reporting the experimental design, I believe that the design is less than optimal and the efficiencies of sgRNAs are rather low, if at all functional.

We apologize for the oversight and indeed the reporting in Figure S8b was a mistake. The PAM site previously indicated was the ‘secondary PAM site’ (which as the Reviewer notes would likely have low efficiency). The PAM site is described within the gRNA in the figure. We use Adobe Illustrator to generate figures, and during the editing process, the layer for PAM text was accidentally moved ‘back’ to a lower level. The oversight was not rectified before submission. We apologise for this unreservedly. The PAM site text has been moved forward, to highlight the location of the primary site (ie immediately following gRNA) and labelled the gRNA and PAM site in the ‘Target region’. The secondary PAM site text was removed to eliminate any confusion.

The authors report efficiencies around 60% (line 325), but how these were obtained is not specified. 

The efficiency provided are based on bioinformatic analyses and not in vivo assays. To reduce any confusion, we have removed the text. The gRNA were clearly effective to induce mutations based on the sequencing analyses.

Another unclear point is the degree to which the mediobasal hypothalamus was actually mutated. Only one mutated (truncated) sequence in Figure S8c is reported, but I would have expected a range of mutations in different cells of the tissue of interest.

The tissue punch would include multiple different cells (e.g., neuronal, glial, etc). We agree with the Reviewer that genomic samples from different cells would be included in the sequencing analyses. Given the large mutation in the target region, the gRNA was effective. We have only shown one representative sequence. If the Reviewer would like to see all mutations, we can easily show the other samples.

Although the authors clearly find a phenotypic effect with their CRISPR manipulation, I suspect that they may have uncovered greater effects with better sgRNA design. These points need some clarification. I would also argue that repeating this experiment with properly designed sgRNAs would provide much stronger support for causally linking Dio3 in circannual timing.

The gRNA was designed using the Gold-standard approach – ChopChop [citation Labon et al., 2019]. If the Reviewer’s concern re design is due to the comment above re PAM site; this issue was clarified and there are no concerns for the gRNA design. The major challenge with the Dio3 gene (single exon) with a very short sequence length (approx.. 412bp). There is limited scope within this sequence length to generate gRNA.

A proposed schematic model for mechanisms of circannual interval timing is presented in Figure S9. I think this represents a nice summary of the findings put in a broader context and should be presented as a main figure in the manuscript itself rather than being relayed in supplementary materials.

We agree with the Reviewer position and moved the figure to the main manuscript. The figure is now Figure 4.

Reviewer #2 (Public review):

Several animals and plants adjust their physiology and behavior to seasons. These changes are timed to precede the seasonal transitions, maximizing chances of survival and reproduction. The molecular mechanisms used for this process are still unclear. Studies in mammals and birds have shown that the expression of deiodinase type-1, 2, and 3 (Dio1, 2, 3) in the hypothalamus spikes right before the transition to winter phenotypes. Yet, whether this change is required or an unrelated product of the seasonal changes has not been shown, particularly because of the genetic intractability of the animal models used to study seasonality. Here, the authors show for the first time a direct link between Dio3 expression and the modulation of circannual rhythms.

We appreciate the clear synthesis and support for the manuscript.

Strengths:

The work is concise and presents the data in a clear manner. The data is, for the most part, solid and supports the author's main claims. The use of CRISPR is a clear advancement in the field. This is, to my knowledge, the first study showing a clear (i.e., causal) role of Dio3 in the circannual rhythms in mammals. Having established a clear component of the circannual timing and a clean approach to address causality, this study could serve as a blueprint to decipher other components of the timing mechanism. It could also help to enlighten the elusive nature of the upstream regulators, in particular, on how the integration of day length takes place, maybe within the components in the Pars tuberalis, and the regulation of tanycytes.

We thank the Reviewer for this positive summary.

Weaknesses:

Due to the nature of the CRISPR manipulation, the low N number is a clear weakness. This is compensated by the fact that the phenotypes shown here are strong enough. Also, this is the only causal evidence of Dio3's role; thus, additional evidence would have significantly strengthened the author's claims. The use of the non-responsive population of hamsters also helps, but it falls within the realm of correlations.

We would also like to remind the Reviewer that one Crispr-Cas9 Dio3^cc treated hamster did not show any mutation in the genome. This hamster was observed to have a change in body mass and pelage colour like controls. This animal provides another positive control.

We also conducted a statistical power analysis to examine whether n=3 is sufficient for the Dio3^cc treatment group. Using the appropriate expected difference in means and standard deviations for an alpha of 0.05; we regularly observed beta >0.8 across the dependent variables. 

Additionally, the consequences of the mutations generated by CRISPR are not detailed; it is not clear if the mutations affect the expression of Dio3 or generate a truncation or deletion, resulting in a shorter protein.

We agree with the Reviewer that transcript and protein assays would strengthen the genome mutation data. Due to the small brain region under investigation, we are limited in the amount of biological material to extract. Dio3 is an intronless gene and very short – approximately 412 base pairs in length. We opted to maximize resources into sequencing the gene as the confirmation of genetic mutation is paramount. Given the large size of the mutation in the treated hamsters, there would be no amplification of transcript or protein translated.

Reviewer #3 (Public review):

The authors investigated SP-induced physiological and molecular changes in Djungarian hamsters and the endogenous recovery from it after circa half a year. The study aimed to elucidate the intrinsic mechanism and included nice experiments to distinguish between rheostatic effects on energy state and homeostatic cues driven by an interval timer. It also aimed to elucidate the role of Dio3 by introducing a targeted mutation in the MBH by ICV. The experiments and analyses are sound, and the amount of work is impressive. The impact of this study on the field of seasonal chronobiology is probably high.

We thank the Reviewer for their positive comments and support for our work.

Even though the general conclusions are well-founded, I have fundamental criticism concerning 3 points, which I recommend revising:

(1) The authors talk about a circannual interval timer, but this is no circannual timer. This is a circasemiannual timer. It is important that the authors use precise wording throughout the manuscript.

We agree with the Reviewer that the change in physiology and behaviour does not approximate a full year (e.g. annual) and only a half of the year. We opted to use circannual timer as this term is established in the field (see doi: 10.1177/0748730404266626; doi: 10.1098/rstb.2007.2143). We cannot identify any publication that has used the term ‘semiannual timer’. We do not feel this manuscript is the appropriate time to introduce a new term to the field; we will endeavour to push the field to consider the use of ‘semiannual timer’. A Review or Opinion paper is best place for this discussion. We hope the Reviewer will understand our position.

(2) The authors put their results in the context of clocks. For example, line 180/181 seasonal clock. But they have described and investigated an interval timer. A clock must be able to complete a full cycle endogenously (and ideally repeatedly) and not only half of it. In contrast, a timer steers a duration. Thus, it is well possible that a circannual clock mechanism and this circa-semiannual timer of photoperiodic species are 2 completely different mechanisms. The argumentation should be changed accordingly.

We agree with the Reviewers definitions of circannual ‘clock’ and ‘timer’. We were careful to distinguish between the two concepts early in the manuscript (lines 41-46). We have added italics to emphasis the different terms. The use of seasonal clock on line 180/191 was imprecise and we appreciate the Reviewer highlighting our oversight and the text was revised. We have also revised the Abstract accordingly.

(3) The authors chose as animal model the Djungarian hamster, which is a predominantly photoperiodic species and not a circannual species. A photoperiodic species has no circannual clock. That is another reason why it is difficult to draw conclusions from the experiment for circannual clocks. However, the Djungarian hamster is kind of "indifferent" concerning its seasonal timing, since a small fraction of them are indeed able to cycle (Anchordoquy HC, Lynch GR (2000), Evidence of an annual rhythm in a small proportion of Siberian hamsters exposed to chronic short days. J Biol Rhythms 15:122-125.). Nevertheless, the proportion is too small to suggest that the findings in the current study might reflect part of the circannual timing. Therefore, the authors should make a clear distinction between timers and clocks, as well as between circa-annual and circa-semiannual durations/periods.

This comment is not clear to us. The Reviewer states the hamsters are not a circannual species, but then highlight one study that shows circannual rhythmicity. We agree that circannual rhythmicity in Djungarian hamsters is dependent on the physiological process under investigation (e.g. body mass versus reproduction) and that photoperiodic response system either dampen or mask robust cycles. We have corrected the text oversight highlighted above and the manuscript is focused on interval timers. We have kept the term circannual over semicircannual due to the prior use in the scientific literature.

Reviewing Editor Comments:

The detailed suggestions of the reviewers are outlined below (or above in case of reviewer 1). In light of the criticism, we ask the authors to especially pay attention to the comments on the Cas9/Crisp experiment, raised by Reviewers 1 and 2. As currently described, there are serious questions on the design of the sgRNAs, and also missing critical methodological details. If the latter are diligently taken care of, they may resolve the questions on the sgRNA design. Please also reconsider the wording along the suggestions of Reviewer 3.

We appreciate the Editors time and support for the manuscript. We have clarified and corrected our oversight for the PAM site. This correction confirms the strength of the Crispr-cas9 gRNA used in the study. The correction should remove all concerns. We have also considered using semicircannual in the text. As there is existing scientific literature using circannual interval timer, and there is no publication to our knowledge for using ‘semicircannual; we have opted to keep with the current approach and use circannual. We feel a subsequent Opinion paper is more suitable to introduce a new term.

Reviewer #2 (Recommendations for the authors):

First, I want to commend the authors for their work. It is a clear advancement for our field. Below are a couple of comments and suggestions I have:

we thank the Review for the positive comment and support. We have endeavoured to incorporate their suggested improvements to the manuscript.

(1) Looking at the results of Figure 1A and Figure S8, the control in S8 showed a lower pelage color score as compared to the hamsters in 1A. Is this a byproduct of the ICV injection?

The difference between Figure 1 and 3 is likely due to the smaller sample sizes. The controls in Figure 1 had a higher proportion of hamsters show complete white fur (score =3) at 1618 weeks compared to controls in Figure 3. It is possible, although unlikely that the ICV injection would reduce the development of winter phenotype. There was no substance in the ICV injection that would impact the prolactin signalling pathway. Our perspective is that the difference between the two figures is due to the different sampling population. Overall, the timing of the change in pelage colour is the same between the figures and suggest that the mechanisms of interval timer were unaffected.

(2) Is there a particular reason why the pelage color for the CRISPR mutants is relegated to the supplemental information? In my opinion, this is also important, even though the results might be difficult to explain. Additionally, did the authors check for food intake and adipose mass in these animals?

We agree with the Reviewer the pelage change is very interesting. We decided to have Figure 3 focus on body mass. The rationale was due to the robust nature of the data collection from Crispr-cas9 study (Fig.3b), in addition to the non-responsive hamsters (Fig.3e). We disagree that the data patterns are hard to explain, as pelage changes was similar to the photoperiodic induced change in body mass. No differences were observed for food intake or adipose tissue. We have added this information in the text (see lines 162-163).

(3) I might have missed it, but did the authors check for the expression of Dio3 on the CRISPR mutants? Does the deletion cause reduced expression or any other mRNA effect, such as those resulting in the truncation of a protein?

Due to the limited biological material extracted from the anatomical punches, we decided to focus on genomic mutations. Dio3 has a very short sequence length and the size of the mutations identified indicate that no RNA could be transcribed.

(4) Could the authors clarify which reference genome or partial CDS (i.e., accession numbers) they used to align the gRNA? Did they use the SSSS strain or the Psun_Stras_1 isolate?

The gRNAs were designed using the online tool CHOPCHOP, using the Mus musculus

Dio3 gene. The generated gRNAs were subsequently aligned via blast with the Phodopus sungorus Dio3 partial cds (GenBank: MF662622.1), to ensure alignment with the species. We are confident that the gRNA designed align 100% in hamsters. Furthermore, we conducted BLAST to ensure there were no off-targets. The only gene identified in the BLAST was the rodent (i.e. hamster, mouse) Dio3 sequence.

(5) Figure 3b. I do agree with the authors in pointing out that the decrease in body mass is occurring earlier in Dio3wt hamsters; however, the shape of the body mass dynamic is also different. Do the authors have any comments on the possible role of Dio3 in the process of exist of overwintering?

This is a very interesting question. We do not have the data to evaluate the role of Dio3 for overwintering. We argue that disruption in Dio3 reduced the circannual interval period. For this interpretation, yes, Dio3 is necessary for overwintering. However, we would need to show the sufficiency of Dio3 to induce the winter phenotype in hamsters housed in long photoperiod. At this time, we do not have the technical ability to conduct this experiment.

(6) In Figure 3d, the Dio3wt group does not show any dispersion. Is this correct? If that's true, and no dispersion is observed, no normality can be assumed, and a t-test can't be performed (Line 692).The Mann-Whitney test might be better suited.

We conducted a Welch’s t-test to compare the difference in body mass period. We used the Welch’s test as the variance were not equal; Mann-Whitney test is best for skewed distributions. To clarify the test used, we have added ‘Welch’s test’ to the Figure legend.

(9) Figure 1 h. It might be convenient to add the words "Induction", "maintenance", and "recovery" over each respective line on the polar graph for easier reading.

We have added the text as suggested by the Reviewer.

Reviewer #3 (Recommendations for the authors):

(1) Figure 1: Please enlarge all partial graphics at least to the size of Figure 2. In the print version, labels are barely readable

we have increased the panels in Figure 1 and 3 by 20% to accommodate the Reviewers suggestion.

(2) Legend Figure 2: Add that the food restriction was 16h.

We have added 16h to the text.

(3) Figure 3b: enlarge font size. In the legend: Dio3cc hamsters delayed.... The delay might have been a week or so, but not more (and even that is unclear since the rise in body mass in that week seems to be rather a disturbance of the curve). Thus 'delay' might not be the most appropriate wording. Instead, the initial decline is slower, but both started at nearly the same week (=> no delay). Minimum body mass is reached at the identical week as in wt (=> no delay). Also, the increase started at the same week but was much faster in Dio3cc than in wt. Figure 3c: How can there be a period when there is no repeated cycle (rhythm)? This is rather a duration. Moreover, according to the displayed data, I am wondering which start point and which endpoint is used. The first and last values are the highest of the graph, but have they been the maximum? Especially for Dio3wt, it can be assumed that animals haven't reached the maximum at the end of the graph.

We have increased the font size in Figure 3b. We have changed ‘delayed’ to ‘slower’ in the text. Period analyses, such as the Lomb-Scargle measure the duration of a cycle (and multiple cycles). The start point and end point used in the analyses were the initial data collection date (week 0) and the final data collection date (week 32). The Lomb-Scargle analyses determines the duration of the period that occurs within these phases of the cycle. We believe the period analyses conducted by the Lomb-Scargle is the most suitable for the scientific question.

(4) Figure S9: This is a very nice graph and summarises your main results. It should appear in the main manuscript and not in the supplements.

We appreciate the positive comment and suggestion. We agree with the Reviewer and have move the graph to the main figure. The revised manuscript indicates the graph as Figure 4.

Reviewer #2 (Public review):

This study aims to disentangle the contribution of sensory and motor processes (mapped onto the inverse and forward components of speech motor control models like DIVA) to production changes as a result of altered auditory feedback. After five experiments, the authors conclude that it is the motor compensation on the previous trial, and not the sensory error, that drives compensatory responses in subsequent trials.

Assessment:

The goal of this paper is great, and the question is timely. Quite a bit of work has gone into the study, and the technical aspects are sound. That said, I just don't understand how the current design can accomplish what the authors have set as their goal. This may, of course, be a misunderstanding on my part, so I'll try to explain my confusion below. If it is indeed my mistake, then I encourage the authors to dedicate some space to unpacking the logic in the Introduction, which is currently barely over a page long. They should take some time to lay out the logic of the experimental design and the dependent and independent variables, and how this design disentangles sensory and motor influences. Then clearly discuss the opposing predictions supporting sensory-driven vs. motor-driven changes. Given that I currently don't understand the logic and, consequently, the claims, I will focus my review on major points for now.

Main issues

(1) Measuring sensory change. As acknowledged by the authors, making a motor correction as a function of altered auditory feedback is an interactive process between sensory and motor systems. However, one could still ask whether it is primarily a change to perception vs. a change to production that is driving the motor correction. But to do this, one has to have two sets of measurements: (a) perceptual change, and (b) motor change. As far as I understand, the study has the latter (i.e., C), but not the former. Instead, the magnitude of perceptual change is estimated through the proxy of the magnitude of perturbation (P), but the two are not the same; P is a physical manipulation; perceptual change is a psychological response to that physical manipulation. It is theoretically possible that a physical change does not cause a psychological change, or that the magnitude of the two does not match. So my first confusion centers on the absence of any measure of sensory change in this study.

To give an explicit example of what I mean, consider a study like Murphy, Nozari, and Holt (2024; Psychonomic Bulletin & Review). This work is about changes to production as a function of exposure to other talkers' acoustic properties - rather than your own altered feedback - but the idea is that the same sensory-motor loop is involved in both. When changing the acoustic properties of the input, the authors obtain two separate measures: (a) how listeners' perception changes as a function of this physical change in the acoustics of the auditory signal, and (b) how their production changes. This allows the authors to identify motor changes above and beyond perceptual changes. Perhaps making a direct comparison with this study would help the reader understand the parallels better.

(2) A more fundamental issue for me is a theoretical one: Isn't a compensatory motor change ALWAYS a consequence of a perceptual change? I think it makes sense to ask, "Does a motor compensation hinge on a previous motor action or is sensory change enough to drive motor compensation?" This question has been asked for changed acoustics for self-produced speech (e.g., Hantzsch, Parrell, & Niziolek, 2022) and other-produced speech (Murphy, Holt, & Nozari, 2025), and in both cases, the answer has been that sensory changes alone are, in fact, sufficient to drive motor changes. A similar finding has been reported for the role of cerebellum in limb movements (Tseng et al., 2007), with a similar answer (note that in that study, the authors explicitly talk about "the addition" of motor corrections to sensory error, not one vs. the other as two independent factors. So I don't understand a sentence like "We found that motor compensation, rather than sensory errors, predicted the compensatory responses in the subsequent trials", which views motor compensations and sensory errors as orthogonal variables affecting future motor adjustments.

In other words, there is a certain degree of seriality to the compensation process, with sensory changes preceding motor corrections. If the authors disagree with this, they should explain how an alternative is possible. If they mean something else, a comparison with the above studies and explaining the differences in positions would greatly help.

(3) Clash with previous findings. I used the examples in point 2 to bring up a theoretical issue, but those examples are also important in that all three of them reach a conclusion compatible with one another and different from the current study. The authors do discuss Tseng et al.'s findings, which oppose their own, but dismiss the opposition based on limb vs. articulator differences. I don't find the authors reasoning theoretically convincing here, but more importantly, the current claims also oppose findings from speech motor studies (see citations in point 2), to which the authors' arguments simply don't apply. Strangely, Hantzsch et al.'s study has been cited a few times, but never in its most important capacity, which is to show that speech motor adaptation can take place after a single exposure to auditory error. Murphy et al. report a similar finding in the context of exposure to other talkers' speech.

If the authors can convincingly justify their theoretical position in 2, the next step would be to present a thorough comparison with the results of the three studies above. If indeed there is no discrepancy, this comparison would help clarify it.

References

Hantzsch, L., Parrell, B., & Niziolek, C. A. (2022). A single exposure to altered auditory feedback causes observable sensorimotor adaptation in speech. eLife, 11, e73694.

Murphy, T. K., Nozari, N., & Holt, L. L. (2024). Transfer of statistical learning from passive speech perception to speech production. Psychonomic Bulletin & Review, 31(3), 1193-1205.

Murphy, T. K., Holt, L. L. & Nozari, N. (2025). Exposure to an Accent Transfers to Speech Production in a Single Shot. Preprint available at: https://papers.ssrn.com/sol3/papers.cfm?abstract_id=5196109.

Tseng, Y. W., Diedrichsen, J., Krakauer, J. W., Shadmehr, R., & Bastian, A. J. (2007). Sensory prediction errors drive cerebellum-dependent adaptation of reaching. Journal of neurophysiology, 98(1), 54-62.

Author response:

Reviewer 1 (Public review):

(1) Figure 1B shows the PREDICTED force-extension curve for DNA based on a worm-like chain model. Where is the experimental evidence for this curve? This issue is crucial because the F-E curve will decide how and when a catch-bond is induced (if at all it is) as the motor moves against the tensiometer. Unless this is actually measured by some other means, I find it hard to accept all the results based on Figure 1B.

The Worm-Like-Chain model for the elasticity of DNA was established by early work from the Bustamante lab (Smith et al., 1992)  and Marko and Siggia (Marko and Siggia, 1995), and was further validated and refined by the Block lab (Bouchiat et al., 1999; Wang et al., 1997). The 50 nm persistence length is the consensus value, and was shown to be independent of force and extension in Figure 3 of Bouchiat et al (Bouchiat et al., 1999). However, we would like to stress that for our conclusions, the precise details of the Force-Extension relationship of our dsDNA are immaterial. The key point is that the motor stretches the DNA and stalls when it reaches its stall force. Our claim of the catch-bond character of kinesin is based on the longer duration at stall compared to the run duration in the absence of load. Provided that the motor is indeed stalling because it has stretched out the DNA (which is strongly supported by the repeated stalling around the predicted extension corresponding to ~6 pN of force), then the stall duration depends on neither the precise value for the extension nor the precise value of the force at stall.

(2) The authors can correct me on this, but I believe that all the catch-bond studies using optical traps have exerted a load force that exceeds the actual force generated by the motor. For example, see Figure 2 in reference 42 (Kunwar et al). It is in this regime (load force > force from motor) that the dissociation rate is reduced (catch-bond is activated). Such a regime is never reached in the DNA tensiometer study because of the very construction of the experiment. I am very surprised that this point is overlooked in this manuscript. I am therefore not even sure that the present experiments even induce a catch-bond (in the sense reported for earlier papers).

It is true that Kunwar et al measured binding durations at super-stall loads and used that to conclude that dynein does act as a catch-bond (but kinesin does not) (Kunwar et al., 2011). However, we would like to correct the reviewer on this one. This approach of exerting super-stall forces and measuring binding durations is in fact less common than the approach of allowing the motor to walk up to stall and measuring the binding duration. This ‘fixed trap’ approach has been used to show catch-bond behavior of dynein (Leidel et al., 2012; Rai et al., 2013) and kinesin (Kuo et al., 2022; Pyrpassopoulos et al., 2020). For the non-processive motor Myosin I, a dynamic force clamp was used to keep the actin filament in place while the myosin generated a single step (Laakso et al., 2008). Because the motor generates the force, these are not superstall forces either.

(3) I appreciate the concerns about the Vertical force from the optical trap. But that leads to the following questions that have not at all been addressed in this paper:

(i) Why is the Vertical force only a problem for Kinesins, and not a problem for the dynein studies?

Actually, we do not claim that vertical force is not a problem for dynein; our data do not speak to this question. There is debate in the literature as to whether dynein has catch bond behavior in the traditional single-bead optical trap geometry - while some studies have measured dynein catch bond behavior (Kunwar et al., 2011; Leidel et al., 2012; Rai et al., 2013), others have found that dynein has slip-bond or ideal-bond behavior (Ezber et al., 2020; Nicholas et al., 2015; Rao et al., 2019). This discrepancy may relate to vertical forces, but not in an obvious way.

(ii) The authors state that "With this geometry, a kinesin motor pulls against the elastic force of a stretched DNA solely in a direction parallel to the microtubule". Is this really true? What matters is not just how the kinesin pulls the DNA, but also how the DNA pulls on the kinesin. In Figure 1A, what is the guarantee that the DNA is oriented only in the plane of the paper? In fact, the DNA could even be bending transiently in a manner that it pulls the kinesin motor UPWARDS (Vertical force). How are the authors sure that the reaction force between DNA and kinesin is oriented SOLELY along the microtubule?

We acknowledge that “solely” is an absolute term that is too strong to describe our geometry. We will soften this term in our revision to “nearly parallel to the microtubule”. In the Geometry Calculations section of Supplementary Methods, we calculate that if the motor and streptavidin are on the same protofilament, the vertical force will be <1% of the horizontal force. We also note that if the motor is on a different protofilament, there will be lateral forces and forces perpendicular to the microtubule surface, except they are oriented toward rather than away from the microtubule. The DNA can surely bend due to thermal forces, but because inertia plays a negligible role at the nanoscale (Howard, 2001; Purcell, 1977), any resulting upward forces will only be thermal forces, which the motor is already subjected to at all times.

(4) For this study to be really impactful and for some of the above concerns to be addressed, the data should also have included DNA tensiometer experiments with Dynein. I wonder why this was not done?

As much as we would love to fully characterize dynein here, this paper is about kinesin and it took a substantial effort. The dynein work merits a stand-alone paper.

While I do like several aspects of the paper, I do not believe that the conclusions are supported by the data presented in this paper for the reasons stated above.

The three key points the reviewer makes are the validity of the worm-like-chain model, the question of superstall loads, and the role of DNA bending in generating vertical forces. We hope that we have fully addressed these concerns in our responses above.

Reviewer #2 (Public review):

Major comments:

(1) The use of the term "catch bond" is misleading, as the authors do not really mean consistently a catch bond in the classical sense (i.e., a protein-protein interaction having a dissociation rate that decreases with load). Instead, what they mean is that after motor detachment (i.e., after a motor protein dissociating from a tubulin protein), there is a slip state during which the reattachment rate is higher as compared to a motor diffusing in solution. While this may indeed influence the dynamics of bidirectional cargo transport (e.g., during tug-of-war events), the used terms (detachment (with or without slip?), dissociation, rescue, ...) need to be better defined and the results discussed in the context of these definitions. It is very unsatisfactory at the moment, for example, that kinesin-3 is at first not classified as a catch bond, but later on (after tweaking the definitions) it is. In essence, the typical slip/catch bond nomenclature used for protein-protein interaction is not readily applicable for motors with slippage.

We appreciate the reviewer’s point and we will work to streamline and define terms in our revision.

(2) The authors define the stall duration as the time at full load, terminated by >60 nm slips/detachments. Isn't that a problem? Smaller slips are not detected/considered... but are also indicative of a motor dissociation event, i.e., the end of a stall. What is the distribution of the slip distances? If the slip distances follow an exponential decay, a large number of short slips are expected, and the presented data (neglecting those short slips) would be highly distorted.

The reviewer brings up a good point that there may be undetected slips. To address this question, we plotted the distribution of slip distances for kinesin-3, which by far had the most slip events. As the reviewer suggested, it is indeed an exponential distribution. Our preliminary analysis suggests that roughly 20% of events are missed due to this 60 nm cutoff. This will change our unloaded duration numbers slightly, but this will not alter our conclusions.\

(3) Along the same line: Why do the authors compare the stall duration (without including the time it took the motor to reach stall) to the unloaded single motor run durations? Shouldn't the times of the runs be included?

The elastic force of the DNA spring is variable as the motor steps up to stall, and so if we included the entire run duration then it would be difficult to specify what force we were comparing to unloaded. More importantly, if we assume that any stepping and detachment behavior is history independent, then it is mathematically proper to take any arbitrary starting point (such as when the motor reaches stall), start the clock there, and measure the distribution of detachments durations relative to that starting point.

More importantly, what we do in Fig. 3 is to separate out the ramps from the stalls and, using a statistical model, we compute a separate duration parameter (which is the inverse of the off-rate) for the ramp and the stall. What we find is that the relationship between ramp, stall, and unloaded durations is different for the three motors, which is interesting in itself.

(4) At many places, it appears too simple that for the biologically relevant processes, mainly/only the load-dependent off-rates of the motors matter. The stall forces and the kind of motor-cargo linkage (e.g., rigid vs. diffusive) do likely also matter. For example: "In the context of pulling a large cargo through the viscous cytoplasm or competing against dynein in a tug-of-war, these slip events enable the motor to maintain force generation and, hence, are distinct from true detachment events." I disagree. The kinesin force at reattachment (after slippage) is much smaller than at stall. What helps, however, is that due to the geometry of being held close to the microtubule (either by the DNA in the present case or by the cargo in vivo) the attachment rate is much higher. Note also that upon DNA relaxation, the motor is likely kept close to the microtubule surface, while, for example, when bound to a vesicle, the motor may diffuse away from the microtubule quickly (e.g., reference 20).

We appreciate the reviewer’s detailed thinking here, and we offer our perspective. As to the first point, we agree that the stall force is relevant and that the rigidity of the motor-cargo linkage will play a role. The goal of the sentence on pulling cargo that the reviewer highlights is to set up our analysis of slips, which we define as rearward displacements that don’t return to the baseline before force generation resumes. We agree that force after slippage is much smaller than at stall, and we plan to clarify that section of text. However, as shown in the model diagram in Fig. 5, we differentiate between the slip state (and recovery from this slip state) and the detached state (and reattachment from this detached state). This delineation is important because, as the reviewer points out, if we are measuring detachment and reattachment with our DNA tensiometer, then the geometry of a vesicle in a cell will be different and diffusion away from the microtubule or elastic recoil perpendicular to the microtubule will suppress this reattachment.

Our evidence for a slip state in which the motor maintains association with the microtubule comes from optical trapping work by Tokelis et al (Toleikis et al., 2020) and Sudhakar et al (Sudhakar et al., 2021). In particular, Sudhakar used small, high index Germanium microspheres that had a low drag coefficient. They showed that during ‘slip’ events, the relaxation time constant of the bead back to the center of the trap was nearly 10-fold slower than the trap response time, consistent with the motor exerting drag on the microtubule. (With larger beads, the drag of the bead swamps the motor-microtubule friction.) Another piece of support for the motor maintaining association during a slip is work by Ramaiya et al. who used birefringent microspheres to exert and measure rotational torque during kinesin stepping (Ramaiya et al., 2017). In most traces, when the motor returned to baseline following a stall, the torque was dissipated as well, consistent with a ‘detached’ state. However, a slip event is shown in S18a where the motor slips backward while maintaining torque. This is best explained by the motor slipping backward in a state where the heads are associated with the microtubule (at least sufficiently to resist rotational forces). Thus, we term the resumption after slip to be a rescue from the slip state rather than a reattachment from the detached state.

To finish the point, with the complex geometry of a vesicle, during slip events the motor remains associated with the microtubule and hence primed for recovery. This recovery rate is expected to be the same as for the DNA tensiometer. Following a detachment, however, we agree that there will likely be a higher probability of reattachment in the DNA tensiometer due to proximity effects, whereas with a vesicle any elastic recoil or ‘rolling’ will pull the detached motor away from the microtubule, suppressing reattachment. We plan to clarify these points in the text of the revision.

(5) Why were all motors linked to the neck-coil domain of kinesin-1? Couldn't it be that for normal function, the different coils matter? Autoinhibition can also be circumvented by consistently shortening the constructs.

We chose this dimerization approach to focus on how the mechoanochemical properties of kinesins vary between the three dominant transport families. We agree that in cells, autoinhibition of both kinesins and dynein likely play roles in regulating bidirectional transport, as will the activity of other regulatory proteins. The native coiled-coils may act as as ‘shock absorbers’ due to their compliance, or they might slow the motor reattachment rate due to the relatively large search volumes created by their long lengths (10s of nm). These are topics for future work. By using the neck-coil domain of kinesin-1 for all three motors, we eliminate any differences in autoinhibition or other regulation between the three kinesin families and focus solely on differences in the mechanochemistry of their motor domains.

(6) I am worried about the neutravidin on the microtubules, which may act as roadblocks (e.g. DOI: 10.1039/b803585g), slip termination sites (maybe without the neutravidin, the rescue rate would be much lower?), and potentially also DNA-interaction sites? At 8 nM neutravidin and the given level of biotinylation, what density of neutravidin do the authors expect on their microtubules? Can the authors rule out that the observed stall events are predominantly the result of a kinesin motor being stopped after a short slippage event at a neutravidin molecule?

We will address these points in our revision.

(7) Also, the unloaded runs should be performed on the same microtubules as in the DNA experiments, i.e., with neutravidin. Otherwise, I do not see how the values can be compared.

We will address this point in our revision.

(8) If, as stated, "a portion of kinesin-3 unloaded run durations were limited by the length of the microtubules, meaning the unloaded duration is a lower limit." corrections (such as Kaplan-Meier) should be applied, DOI: 10.1016/j.bpj.2017.09.024.

(9) Shouldn't Kaplan-Meier also be applied to the ramp durations ... as a ramp may also artificially end upon stall? Also, doesn't the comparison between ramp and stall duration have a problem, as each stall is preceded by a ramp ...and the (maximum) ramp times will depend on the speed of the motor? Kinesin-3 is the fastest motor and will reach stall much faster than kinesin-1. Isn't it obvious that the stall durations are longer than the ramp duration (as seen for all three motors in Figure 3)?

The reviewer rightly notes the many challenges in estimating the motor off-rates during ramps. To estimate ramp off-rates and as an independent approach to calculating the unloaded and stall durations, we developed a Markov model coupled with Bayesian inference methods to estimate a duration parameter (equivalent to the inverse of the off-rate) for the unloaded, ramp, and stall duration distributions. With the ramps, we have left censoring due to the difficulty in detecting the start of the ramps in the fluctuating baseline, and we have right censoring due to reaching stall (with different censoring of the ramp duration for the three motors due to their different speeds). The Markov model assumes a constant detachment probability and history independence, and thus is robust even in the face of left and right censoring (details in the Supplementary section). This approach is preferred over Kaplan-Meier because, although these non-parametric methods make no assumptions for the distribution, they require the user to know exactly where the start time is.

Regarding the potential underestimate of the kinesin-3 unloaded run duration due to finite microtubule lengths. The first point is that the unloaded duration data in Fig. 2C are quite linear up to 6 s and are well fit by the single-exponential fit (the points above 6s don’t affect the fit very much). The second point is that when we used our Markov model (which is robust against right censoring) to estimate the unloaded and stall durations, the results agreed with the single-exponential fits very well (Table S2). For instance, the single-exponential fit for the kinesin-3 unloaded duration was 2.74 s (2.33 – 3.17 s 95% CI) and the estimate from the Markov model was 2.76 (2.28 – 3.34 s 95% CI). Thus, we chose not to make any corrections due to finite microtubule lengths.

(10) It is not clear what is seen in Figure S6A: It looks like only single motors (green, w/o a DNA molecule) are walking ... Note: the influence of the attached DNA onto the stepping duration of a motor may depend on the DNA conformation (stretched and near to the microtubule (with neutravidin!) in the tethered case and spherically coiled in the untethered case).

In Figure S6A kymograph, the green traces are GFP-labeled kinesin-1 without DNA attached (which are in excess) and the red diagonal trace is a motor with DNA attached. There are also two faint horizontal red traces, which are labeled DNA diffusing by (smearing over a large area during a single frame). Panel S6B shows run durations of motors with DNA attached. We agree that the DNA conformation will differ if it is attached and stretched (more linear) versus simply being transported (random coil), but by its nature this control experiment is only addressing random coil DNA.

(11) Along this line: While the run time of kinesin-1 with DNA (1.4 s) is significantly shorter than the stall time (3.0 s), it is still larger than the unloaded run time (1.0 s). What do the authors think is the origin of this increase?

Our interpretation of the unloaded kinesin-DNA result is that the much slower diffusion constant of the DNA relative to the motor alone enables motors to transiently detach and rebind before the DNA cargo has diffused away, thus extending the run duration. In contrast, such detachment events for motors alone normally result in the motor diffusing away from the microtubule, terminating the run. This argument has been used to reconcile the longer single-motor run lengths in the gliding assay versus the bead assay (Block et al., 1990). Notably, this slower diffusion constant should not play a role in the DNA tensiometer geometry because if the motor transiently detaches, then it will be pulled backward by the elastic forces of the DNA and detected as a slip or detachment event. We will address this point in the revision.

(12) "The simplest prediction is that against the low loads experienced during ramps, the detachment rate should match the unloaded detachment rate." I disagree. I would already expect a slight increase.

Agreed. We will change this text to: “The prediction for a slip bond is that against the low loads experienced during ramps, the detachment rate should be equal to or faster than the unloaded detachment rate.”

(13) Isn't the model over-defined by fitting the values for the load-dependence of the strong-to-weak transition and fitting the load dependence into the transition to the slip state?

Essentially, yes, it is overdefined, but that is essentially by design and it is still very useful. Our goal here was to make as simple a model as possible that could account for the data and use it to compare model parameters for the different motor families. Ignoring the complexity of the slip and detached states, a model with a strong and weak state in the stepping cycle and a single transition out of the stepping cycle is the simplest formulation possible. And having rate constants (k_S-W and k_slip in our case) that vary exponentially with load makes thermodynamic sense for modeling mechanochemistry (Howard, 2001). Thus, we were pleasantly surprised that this bare-bones model could recapitulate the unloaded and stall durations for all three motors (Fig. 5C-E).

(14) "When kinesin-1 was tethered to a glass coverslip via a DNA linker and hydrodynamic forces were imposed on an associated microtubule, kinesin-1 dissociation rates were relatively insensitive to loads up to ~3 pN, inconsistent with slip-bond characteristics (37)." This statement appears not to be true. In reference 37, very similar to the geometry reported here, the microtubules were fixed on the surface, and the stepping of single kinesin motors attached to large beads (to which defined forces were applied by hydrodynamics) via long DNA linkers was studied. In fact, quite a number of statements made in the present manuscript have been made already in ref. 37 (see in particular sections 2.6 and 2.7), and the authors may consider putting their results better into this context in the Introduction and Discussion. It is also noteworthy to discuss that the (admittedly limited) data in ref. 37 does not indicate a "catch-bond" behavior but rather an insensitivity to force over a defined range of forces.

The reviewer misquoted our sentence. The actual wording of the sentence was: “When kinesin-1 was connected to micron-scale beads through a DNA linker and hydrodynamic forces parallel to the microtubule imposed, dissociation rates were relatively insensitive to loads up to ~3 pN, inconsistent with slip-bond characteristics (Urbanska et al., 2021).” The sentence the reviewer quoted was in a previous version that is available on BioRxiv and perhaps they were reading that version. Nonetheless, in the revision we will note in the Discussion that this behavior was indicative of an ideal bond (not a catch-bond), and we will also add a sentence in the Introduction highlighting this work.

Reviewer #3 (Public review):

The authors attribute the differences in the behaviour of kinesins when pulling against a DNA tether compared to an optical trap to the differences in the perpendicular forces. However, the compliance is also much different in these two experiments. The optical trap acts like a ~ linear spring with stiffness ~ 0.05 pN/nm. The dsDNA tether is an entropic spring, with negligible stiffness at low extensions and very high compliance once the tether is extended to its contour length (Fig. 1B). The effect of the compliance on the results should be addressed in the manuscript.

This is an interesting point. To address it, we calculated the predicted stiffness of the dsDNA by taking the slope of theoretical force-extension curve in Fig. 1B. Below 650 nm extension, the stiffness is <0.001 pN/nM; it reaches 0.01 pN/nM at 855 nm, and at 960 nm where the force is 6 pN the stiffness is roughly 0.2 pN/nm. That value is higher than the quoted 0.05 pN/nm trap stiffness, but for reference, at this stiffness, an 8 nm step leads to a 1.6 pN jump in force, which is reasonable. Importantly, the stiffness of kinesin motors has been estimated to be in the range of 0.3 pN (Coppin et al., 1996; Coppin et al., 1997). Granted, this stiffness is also nonlinear, but what this means is that even at stall, our dsDNA tether has a similar predicted compliance to the motor that is pulling on it. We will address this point in our revision.  

Compared to an optical trapping assay, the motors are also tethered closer to the microtubule in this geometry. In an optical trap assay, the bead could rotate when the kinesin is not bound. The authors should discuss how this tethering is expected to affect the kinesin reattachment and slipping. While likely outside the scope of this study, it would be interesting to compare the static tether used here with a dynamic tether like MAP7 or the CAP-GLY domain of p150glued.

Please see our response to Reviewer #2 Major Comment #4 above, which asks this same question in the context of intracellular cargo. We plan to address this in our revision. Regarding a dynamic tether, we agree that’s interesting – there are kinesins that have a second, non-canonical binding site that achieves this tethering (ncd and Cin8); p150glued likely does this naturally for dynein-dynactin-activator complexes; and we speculated in a review some years ago (Hancock, 2014) that during bidirectional transport kinesin and dynein may act as dynamic tethers for one another when not engaged, enhancing the activity of the opposing motor.

In the single-molecule extension traces (Figure 1F-H; S3), the kinesin-2 traces often show jumps in position at the beginning of runs (e.g., the four runs from ~4-13 s in Fig. 1G). These jumps are not apparent in the kinesin-1 and -3 traces. What is the explanation? Is kinesin-2 binding accelerated by resisting loads more strongly than kinesin-1 and -3?

Due to the compliance of the dsDNA, the 95% limits for the initial attachment position are +/- 290 nm (Fig. S2). Thus, some apparent ‘jumps’ from the detached state are expected. We will take a closer look at why there are jumps for kinesin-2 that aren’t apparent for kinesin-1 or -3.

When comparing the durations of unloaded and stall events (Fig. 2), there is a potential for bias in the measurement, where very long unloaded runs cannot be observed due to the limited length of the microtubule (Thompson, Hoeprich, and Berger, 2013), while the duration of tethered runs is only limited by photobleaching. Was the possible censoring of the results addressed in the analysis?

Yes. Please see response to Reviewer #2 points (8) and (9) above.

The mathematical model is helpful in interpreting the data. To assess how the "slip" state contributes to the association kinetics, it would be helpful to compare the proposed model with a similar model with no slip state. Could the slips be explained by fast reattachments from the detached state?

In the model, the slip state and the detached states are conceptually similar; they only differ in the sequence (slip to detached) and the transition rates into and out of them. The simple answer is: yes, the slips could be explained by fast reattachments from the detached state. In that case, the slip state and recovery could be called a “detached state with fast reattachment kinetics”. However, the key data for defining the kinetics of the slip and detached states is the distribution of Recovery times shown in Fig. 4D-F, which required a triple exponential to account for all of the data. If we simplified the model by eliminating the slip state and incorporating fast reattachment from a single detached state, then the distribution of Recovery times would be a single-exponential with a time constant equivalent to t₁, which would be a poor fit to the experimental distributions in Fig. 4D-F.

We appreciate the efforts and helpful suggestions of all three reviewers and the Editor.

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Author response:

Reviewer #1 (Public review):

Fombellida-Lopez and colleagues describe the results of an ART intensification trial in people with HIV infection (PWH) on suppressive ART to determine the effect of increasing the dose of one ART drug, dolutegravir, on viral reservoirs, immune activation, exhaustion, and circulating inflammatory markers. The authors hypothesize that ART intensification will provide clues about the degree to which low-level viral replication is occurring in circulation and in tissues despite ongoing ART, which could be identified if reservoirs decrease and/or if immune biomarkers change. The trial design is straightforward and well-described, and the intervention appears to have been well tolerated. The investigators observed an increase in dolutegravir concentrations in circulation, and to a lesser degree in tissues, in the intervention group, indicating that the intervention has functioned as expected (ART has been intensified in vivo). Several outcome measures changed during the trial period in the intervention group, leading the investigators to conclude that their results provide strong evidence of ongoing replication on standard ART. The results of this small trial are intriguing, and a few observations in particular are hypothesis-generating and potentially justify further clinical trials to explore them in depth. However, I am concerned about over-interpretation of results that do not fully justify the authors' conclusions.

We thank Reviewer #1 for their thoughtful and constructive comments, which helped us clarify and improve the manuscript. Below, we address each of the reviewer’s points and describe the changes that we implemented in the revised version. We acknowledge the reviewer’s concern regarding potential overinterpretation of certain findings, and in the revised version we took particular care to ensure that all conclusions are supported by the data and framed within the exploratory nature of the study.

(1) Trial objectives: What was the primary objective of the trial? This is not clearly stated. The authors describe changes in some reservoir parameters and no changes in others. Which of these was the primary outcome? No a priori hypothesis / primary objective is stated, nor is there explicit justification (power calculations, prior in vivo evidence) for the small n, unblinded design, and lack of placebo control. In the abstract (line 36, "significant decreases in total HIV DNA") and conclusion (lines 244-246), the authors state that total proviral DNA decreased as a result of ART intensification. However, in Figures 2A and 2E (and in line 251), the authors indicate that total proviral DNA did not change. These statements are confusing and appear to be contradictory. Regarding the decrease in total proviral DNA, I believe the authors may mean that they observed transient decrease in total proviral DNA during the intensification period (day 28 in particular, Figure 2A), however this level increases at Day 56 and then returns to baseline at Day 84, which is the source of the negative observation. Stating that total proviral DNA decreased as a result of the intervention when it ultimately did not is misleading, unless the investigators intended the day 28 timepoint as a primary endpoint for reservoir reduction - if so, this is never stated, and it is unclear why the intervention would then be continued until day 84? If, instead, reservoir reduction at the end of the intervention was the primary endpoint (again, unstated by the authors), then it is not appropriate to state that the total proviral reservoir decreased significantly when it did not.

We agree with the reviewer that the primary objective of the study was not explicitly stated in the submitted manuscript. We clarified this in the revised manuscript (lines 361-364). As registered on ClinicalTrials.gov (NCT05351684), the primary outcome was defined as “To evaluate the impact of treatment intensification at the level of total and replication-competent reservoir (RCR) in blood and in tissues”, with a time frame of 3 months. Accordingly, our aim was to explore whether any measurable reduction in the HIV reservoir (total or replication-competent) occurred during the intensification period, including at day 28, 56, or 84. The protocol did not prespecify a single time point for this effect to occur, and the exploratory design allowed for detection of transient or sustained changes within the intensification window.

We recognize that this scope was not clearly articulated in the original text and may have led to confusion in interpreting the transient drop in total HIV DNA observed at day 28. While total DNA ultimately returned to baseline by the end of intensification, the presence of a transient reduction during this 3-month window still fits within the framework of the study’s registered objective. Moreover, although the change in total HIV DNA was transient, it aligns with the consistent direction of changes observed across the multiple independent measures, including CA HIV RNA, RNA/DNA ratio and intact HIV DNA, collectively supporting a biological effect of intensification.

We would also like to stress that this is the first clinical trial ever, in which an ART intensification is performed not by adding an extra drug but by increasing the dosage of an existing drug. Therefore, we were more interested in the overall, cumulative, effect of intensification throughout the entire trial period, than in differences between groups at individual time points. We clarified in the revised manuscript that this was a proof-of-concept phase 2 study, designed to reveal biological effects of ART intensification rather than confirm efficacy in a powered comparison. The absence of a prespecified statistical endpoint or sample size calculation reflects the exploratory nature of the trial.

(2) Intervention safety and tolerability: The results section lacks a specific heading for participant safety and tolerability of the intervention. I was wondering about clinically detectable viremia in the study. Were there any viral blips? Was the increased DTG well tolerated? This drug is known to cause myositis, headache, CPK elevation, hepatotoxicity, and headache. Were any of these observed? What is the authors' interpretation of the CD4:8 ratio change (line 198)? Is this a significant safety concern for a longer duration of intensification? Was there also a change in CD4% or only in absolute counts? Was there relative CD4 depletion observed in the rectal biopsy samples between days 0 and 84? Interestingly, T cells dropped at the same timepoints that reservoirs declined... how do the authors rule out that reservoir decline reflects transient T cell decline that is non-specific (not due to additional blockade of replication)?

We improved the Methods section to clarify how safety and tolerability were assessed during the study (lines 389-396). Safety evaluations were conducted on day 28 and day 84 and included a clinical examination and routine laboratory testing (liver function tests, kidney function, and complete blood count). Medication adherence was also monitored through pill counts performed by the study nurses.

No virological blips above 50 copies/mL were observed and no adverse events were reported by participants during the 3-month intensification period. Although CPK levels were not included in the routine biological monitoring, no participant reported muscle pain or other symptoms suggestive of muscle toxicity.

The CD4:CD8 ratio decrease noted during intensification was not associated with significant changes in absolute CD4 or CD8 counts, as shown in Figure 5. We interpret this ratio change as a transient redistribution rather than an immunological risk, therefore we do not consider it to represent a safety concern.

We would like to clarify that CD4⁺ T-cell counts did not significantly decrease in any of the treatment groups, as shown in Figure 5. The apparent decline observed concerns the CD4/CD8 ratio, which transiently dropped, but not the absolute number of CD4⁺ T cells. Moreover, although the dynamics of total HIV DNA is indeed similar to that of CD4/CD8 ratio (both declined transiently and then returned to baseline by day 84), the dynamics of unspliced RNA and unspliced RNA/total DNA ratio are clearly different, as these markers demonstrated a sustained decrease that was maintained throughout the trial period, even when the CD4/CD8 ratio already returned to baseline. Also, we observed a significant decrease in intact HIV DNA at day 84 compared to day 0. These effects cannot be easily explained by a transient decline in CD4+ cells.

(3) The investigators describe a decrease in intact proviral DNA after 84 days of ART intensification in circulating cells (Figure 2D), but no changes to total proviral DNA in blood or tissue (Figures 2A and 2E; IPDA does not appear to have been done on tissue samples). It is not clear why ART intensification would result in a selective decrease in intact proviruses and not in total proviruses if the source of these reservoir cells is due to ongoing replication. These reservoir results have multiple interpretations, including (but not limited to) the investigators' contention that this provides strong evidence of ongoing replication. However, ongoing replication results in the production of both intact and mutated/defective proviruses that both contribute to reservoir size (with defective proviruses vastly outnumbering intact proviruses). The small sample size and well-described heterogeneity of the HIV reservoir (with regard to overall size and composition) raise the possibility that the study was underpowered to detect differences over the 84-day intervention period. No power calculations or prior studies were described to justify the trial size or the duration of the intervention. Readers would benefit from a more nuanced discussion of reservoir changes observed here.

We sincerely thank the reviewer for this insightful comment. We fully agree that the reservoir dynamics observed in our study might raise several possible interpretations, and that its complexity, resulting from continuous cycles of expansion and contraction, reflects the heterogeneity of the latent reservoir. 

Total HIV DNA in PBMCs showed a transient decline during intensification (notably at day 28), ultimately returning to baseline by day 84. This biphasic pattern likely reflects the combined effects of suppression of ongoing low-level replication by an increased DTG dosage, followed by the expansion of infected cell clones (mostly harbouring defective proviruses). In other words, the transient decrease in total (intact + defective) DNA at day 28 may be due to an initial decrease in newly infected cells upon ART intensification, however at the subsequent time points this effect was masked by proliferation (clonal expansion) of infected cells with defective proviruses. Recent studies suggest that intact and defective proviruses are subjected to different selection pressures by the immune system on ART (PMID: 38337034) and their decay on therapy is different (intact proviruses are cleared much more rapidly than defectives). In addition, defective proviruses can be preferentially expanded as they can reprogram the host cell proliferation machinery (https://doi.org/10.1101/2025.09.22.676989). This explains why in our study the intact proviruses decreased, but the total proviruses did not change, between days 0 and 84, in the intensification group. Interestingly, in the control group, we observed a significant increase in total DNA at day 84 compared to day 0, with no difference for the intact DNA, which is also in line with the clonal expansion of defective proviruses.

Importantly, we observed a significant decrease in intact proviral DNA between day 0 and day 84 in the intensification group (Figure 2D). This result directly addresses the study’s primary objective: assessing the impact of intensification on the replication-competent reservoir. In comparison, as the reviewer rightly points out, total HIV DNA includes over 90% defective genomes, which limits its interpretability as a biomarker of biologically relevant reservoir changes. In addition, other reservoir markers, such as cell-associated unspliced RNA and RNA/DNA ratios, also showed consistent trends supporting a biologically relevant effect of intensification. Even in the absence of sustained changes in total HIV DNA, the coherence across the different independent measures of the reservoir (intact DNA, unspliced RNA), suggests an effect indicative of ongoing replication pre-intensification.

Regarding tissue reservoirs, the lack of substantial change in total HIV DNA between days 0 and 84 is also in line with the predominance of defective sequences in these compartments. Moreover, the limited increase in rectal tissue dolutegravir levels during intensification (from 16.7% to 20% of plasma concentrations) may have limited the efficacy of the intervention in this site.

As for the IPDA on rectal biopsies, we attempted the assay using two independent DNA extraction methods (Promega Reliaprep and Qiagen Puregene), but both yielded high DNA shearing index values, and intact proviral detection was successful in only 3 of 40 samples. Given the poor DNA integrity, these results were not interpretable.

That said, we fully acknowledge the limitations of our study, especially the small sample size, and we agree with the reviewer that caution is needed when interpreting these findings. In the revised manuscript, we adopted a more measured tone in the discussion (lines 340-346), stating that these observations are exploratory and hypothesis-generating, and require confirmation in larger, more powered studies. Nonetheless, we believe that the convergence of multiple reservoir markers pointing in the same direction constitutes a meaningful biological effect that deserves further investigation.

(4) While a few statistically significant changes occurred in immune activation markers, it is not clear that these are biologically significant. Lines 175-186 and Figure 3: The change in CD4 cells + for TIGIT looks as though it declined by only 1-2%, and at day 84, the confidence interval appears to widen significantly at this timepoint, spanning an interquartile range of 4%. The only other immune activation/exhaustion marker change that reached statistical significance appears to be CD8 cells + for CD38 and HLA-DR, however, the decline appears to be a fraction of a percent, with the control group trending in the same direction. Despite marginal statistical significance, it is not clear there is any biological significance to these findings; Figure S6 supports the contention that there is no significant change in these parameters over time or between groups. With most markers showing no change and these two showing very small changes (and the latter moving in the same direction as the control group), these results do not justify the statement that intensifying DTG decreases immune activation and exhaustion (lines 38-40 in the abstract and elsewhere).

We agree with the reviewer that the observed changes in immune activation and exhaustion markers were modest. We revised the abstract and the manuscript text (including a section header) to reflect this more accurately (lines 39, 175, 185, 253). We noted that these differences, while statistically significant (e.g., in TIGIT+ CD4+ T cells and CD38+HLA-DR+ CD8+ T cells), were limited in magnitude. We explicitly acknowledged these limitations and interpreted the findings with appropriate caution.

(5) There are several limitations of the study design that deserve consideration beyond those discussed at line 327. The study was open-label and not placebo-controlled, which may have led to some medication adherence changes that confound results (authors describe one observation that may be evidence of this; lines 146-148). Randomized/blinded / cross-over design would be more robust and help determine signal from noise, given relatively small changes observed in the intervention arm.There does not seem to be a measurement of key outcome variables after treatment intensification ceased - evidence of an effect on replication through ART intensification would be enhanced by observing changes once intensification was stopped. Why was intensification maintained for 84 days? More information about the study duration would be helpful. Table 1 indicates that participants were 95% male. Sex is known to be a biological variable, particularly with regard to HIV reservoir size and chronic immune activation in PWH. Worldwide, 50% of PWH are women. Research into improving management/understanding of disease should reflect this, and equal participation should be sought in trials. Table 1 shows differing baseline reservoir sizes between the control and intervention groups. This may have important implications, particularly for outcomes where reservoir size is used as the denominator.

We expanded the limitations section to address several key aspects raised by the reviewer: the absence of blinding and placebo control, the predominantly male study population, and the lack of postintervention follow-up. While we acknowledge that open-label designs can introduce behavioural biases, including potential changes in adherence, we now explicitly state that placebo-controlled, blinded trials would provide a more robust assessment and are warranted in future research (lines 340346). 

The 84-day duration of intensification was chosen based on previous studies and provided sufficient time for observing potential changes in viral transcription and reservoir dynamics. However, we agree that including post-intervention follow-up would have strengthened the conclusions, and we highlighted this limitation and future direction in the revised manuscript (lines 340-346). 

The sex imbalance is now clearly acknowledged as a limitation in the revised manuscript, and we fully support ongoing efforts to promote equitable recruitment in HIV research. We would like to add that, in our study, rectal biopsies were coupled with anal cancer screening through HPV testing. This screening is specifically recommended for younger men who have sex with men (MSM), as outlined in the current EACS guidelines (see: https://eacs.sanfordguide.com/eacs part2/cancer/cancerscreening-methods). As a result, MSM participants had both a clinical incentive and medical interest to undergo this procedure, which likely contributed to the higher proportion of male participants in the study.

Lastly, although baseline total HIV DNA was higher in the intensified group, our statistical approach is based on a within-subject (repeated-measures) design, in which the longitudinal change of a parameter within the same participant during the study was the main outcome. In other words, we are not comparing absolute values of any marker between the groups, we are looking at changes of parameters from baseline within participants, and these are not expected to be affected by baseline imbalances.

(6) Figure 1: the increase in DTG levels is interesting - it is not uniform across participants. Several participants had lower levels of DTG at the end of the intervention. Though unlikely to be statistically significant, it would be interesting to evaluate if there is a correlation between change in DTG concentrations and virologic / reservoir / inflammatory parameters. A positive relationship between increasing DTG concentration and decreased cell-associated RNA, for example, would help support the hypothesis that ongoing replication is occurring.

We agree with the reviewer that assessing correlations between DTG concentrations and virological, immunological, or inflammatory markers would be highly informative. In fact, we initially explored this question in a preliminary way by examining whether individuals who showed a marked increase in DTG levels after intensification also demonstrated stronger changes in the viral reservoir. While this exploratory analysis did not reveal any clear associations, we would like to emphasize that correlating biological effects with DTG concentrations measured at a single timepoint may have limited interpretability. A more comprehensive understanding of the relationship between drug exposure and reservoir dynamics would ideally require multiple pharmacokinetic measurements over time, including pre-intensification baselines. This is particularly important given that DTG concentrations vary across individuals and over time, depending on adherence, metabolism, and other individual factors.

(7) Figure 2: IPDA in tissue- was this done? scRNA in blood (single copy assay) - would this be expected to correlate with usCaRNA? The most unambiguous result is the decrease in cell-associated RNA - accompanying results using single-copy assay in plasma would be helpful to bolster this result.

As mentioned in our response to point 3, we attempted IPDA on tissue samples, but technical limitations prevented reliable detection of intact proviruses. Regarding residual viremia, we did perform ultra-sensitive plasma HIV RNA quantification but due to a technical issue (an inadvertent PBMC contamination during plasma separation) that affected the reliability of the results we felt uncomfortable including these data in the manuscript.

The use of the US RNA / Total DNA ratio is not helpful/difficult to interpret since the control and intervention arms were unmatched for total DNA reservoir size at study entry.

We respectfully disagree with this comment. The US RNA/total DNA ratio is commonly used to assess the relative transcriptional activity of the viral reservoir, rather than its absolute size. While we acknowledge that the total HIV-1 DNA levels differed at baseline between the two groups, the US RNA/total DNA ratio specifically reflects the relationship between transcriptional activity and reservoir size within each individual, and is therefore not directly confounded by baseline differences in total DNA alone.

Moreover, our analyses focus on within-subject longitudinal changes from baseline, not on direct between-group comparisons of absolute marker values. As such, the observed changes in the US RNA/total DNA ratio over time are interpreted relative to each participant's baseline, mitigating concerns related to baseline imbalances between groups.

Reviewer #2 (Public review):

Summary:

An intensification study with a double dose of 2nd generation integrase inhibitor with a background of nucleoside analog inhibitors of the HIV retrotranscriptase in 2, and inflammation is associated with the development of co-morbidities in 20 individuals randomized with controls, with an impact on the levels of viral reservoirs and inflammation markers. Viral reservoirs in HIV are the main impediment to an HIV cure, and inflammation is associated with co-morbidities.

Strengths:

The intervention that leads to a decrease of viral reservoirs and inflammation is quite straightforward forward as a doubling of the INSTI is used in some individuals with INSTI resistance, with good tolerability.

This is a very well documented study, both in blood and tissues, which is a great achievement due to the difficulty of body sampling in well-controlled individuals on antiretroviral therapy. The laboratory assays are performed by specialists in the field with state-of-the art quantification assays. Both the introduction and the discussion are remarkably well presented and documented.

The findings also have a potential impact on the management of chronic HIV infection.

Weaknesses:

I do not think that the size of the study can be considered a weakness, nor the fact that it is open-label either.

We thank Reviewer #2 for their constructive and supportive comments. We appreciate their positive assessment of the study design, the translational relevance of the intervention, and the technical quality of the assays. We also take note of their perspective regarding sample size and study design, which supports our positioning of this trial as an exploratory, hypothesis-generating phase 2 study.

Reviewer #3 (Public review):

The introduction does a very good job of discussing the issue around whether there is ongoing replication in people with HIV on antiretroviral therapy. Sporadic, non-sustained replication likely occurs in many PWH on ART related to adherence, drug-drug interactions and possibly penetration of antivirals into sanctuary areas of replication and as the authors point out proving it does not occur is likely not possible and proving it does occur is likely very dependent on the population studied and the design of the intervention. Whether the consequences of this replication in the absence of evolution toward resistance have clinical significance challenging question to address.

It is important to note that INSTI-based therapy may have a different impact on HIV replication events that results in differences in virus release for specific cell type (those responsible for "second phase" decay) by blocking integration in cells that have completed reverse transcription prior to ART initiation but have yet to be fully activated. In a PI or NNRTI-based regimen, those cells will release virus, whereas with an INSTI-based regimen, they will not.

Given the very small sample size, there is a substantial risk of imbalance between the groups in important baseline measures. Unfortunately, with the small sample size, a non-significant P value is not helpful when comparing baseline measures between groups. One suggestion would be to provide the full range as opposed to the inter-quartile range (essentially only 5 or 6 values). The authors could also report the proportion of participants with baseline HIV RNA target not detected in the two groups.

We thank Reviewer #3 for their thoughtful and balanced review. We are grateful for the recognition of the strength of the Introduction, the complexity of evaluating residual replication, and the technical execution of the assays. We also appreciate the insightful suggestions for improving the clarity and transparency of our results and discussion.

We revised the manuscript to address several of the reviewer’s key concerns. We agree that the small sample size increases the risk of baseline imbalances. We acknowledged these limitations in the manuscript (lines 327-330). For transparency, we now provide both the full range and the IQR for all parameters in Table 1. However, we would like to stress that our statistical approach is based on a within-subject (repeated-measures) design, in which the longitudinal change of a parameter within the same participant during the study was the main outcome. In other words, we are not comparing absolute values of any marker between the groups, we are looking at changes of parameters from baseline within participants, and these are not expected to be affected by baseline imbalances.

A suggestion that there is a critical imbalance between groups is that the control group has significantly lower total HIV DNA in PBMC, despite the small sample size. The control group also has numerically longer time of continuous suppression, lower unspliced RNA, and lower intact proviral DNA. These differences may have biased the ability to see changes in DNA and US RNA in the control group.

We acknowledge the significant baseline difference in total HIV DNA between groups, which we have clearly reported. However, the other variables mentioned, such as duration of continuous viral suppression, unspliced RNA levels, and intact proviral DNA, did not differ significantly between groups at baseline, despite differences in the median values (that are always present). These numerical differences do not necessarily indicate a critical imbalance.

Notably, there was no significant difference in the change in US RNA/DNA between groups (Figure 2C).

The nonsignificant difference in the change in US RNA/total DNA between groups is not unexpected, given the significant between-group differences for both US RNA and total DNA changes. Since the ratio combines both markers, it is likely to show attenuated between-group differences compared to the individual components. However, while the difference did not reach statistical significance (p = 0.09), we still observed a trend towards a greater reduction in the US RNA/total DNA ratio in the intervention group.

The fact that the median relative change appears very similar in Figure 2C, yet there is a substantial difference in P values, is also a comment on the limits of the current sample size. 

Although we surely agree that in general, the limited sample size impacts statistical power, we would like to point out that in Figure 2C, while the medians may appear similar, the ranges do differ between groups. At days 56 and 84, the median fold changes from baseline are indeed close but the full interquartile range in the DTG group stays below 1, while in the control group, the interquartile range is wider and covers approximately equal distance above and below 1. This explains the difference in p values between the groups.

The text should report the median change in US RNA and US RNA/DNA when describing Figures 2A-2C.

These data are already reported in the Results section (lines 164–166): "By day 84, US RNA and US RNA/total DNA ratio had decreased from day 0 by medians (IQRs) of 5.1 (3.3–6.4) and 4.6 (3.1–5.3) fold, respectively (p = 0.016 for both markers)."

This statistical comparison of changes in IPDA results between groups should be reported. The presentation of the absolute values of all the comparisons in the supplemental figures is a strength of the manuscript.

In the assessment of ART intensification on immune activation and exhaustion, the fact that none of the comparisons between randomized groups were significant should be noted and discussed.

We would like to point out that a statistically significant difference between the randomized groups was observed for the frequency of CD4⁺ T cells expressing TIGIT, as shown in Figure 3A and reported in the Results section (p = 0.048).

The changes in CD4:CD8 ratio and sCD14 levels appear counterintuitive to the hypothesis and are commented on in the discussion.

Overall, the discussion highlights the significant changes in the intensified group, which are suggestive. There is limited discussion of the comparisons between groups where the results are less convincing.

We observed statistically significant differences between the randomized groups for total DNA (p<0.001) and US RNA (p=0.01), as well as for the frequency of CD4⁺ T cells expressing TIGIT (p=0.048). We would like to stress that US RNA is a key marker of residual replication as it is very sensitive to de novo infection events. As discussed in the manuscript (lines 291-294), a newly infected CD4+ T lymphocyte can contain hundreds to thousands of US HIV RNA copies at the peak of infection. Therefore, a change in the US RNA level upon ART intensification is a very sensitive indicator of new infections. The fact that for US RNA we observed both a significant reduction in the intensified group and a significant difference between the groups is a strong indicator that some new infections had been occurring prior to intensification.

The limitations of the study should be more clearly discussed. The small sample size raises the possibility of imbalance at baseline. The supplemental figures (S3-S5) are helpful in showing the differences between groups at baseline, and the variability of measurements is more apparent. The lack of blinding is also a weakness, though the PK assessments do help (note 3TC levels rise substantially in both groups for most of the time on study (Figure S2).

The many assays and comparisons are listed as a strength. The many comparisons raise the possibility of finding significance by chance. In addition, if there is an imbalance at baseline outcomes, measuring related parameters will move in the same direction.

We agree that the multiple comparisons raise the possibility of chance findings but would like to stress that in an exploratory study like this it is very important to avoid a type II error. In addition, the consistent directionality of the most relevant outcomes (US RNA and intact DNA) lends biological plausibility to the observed effects.

The limited impact on activation and inflammation should be addressed in the discussion, as they are highlighted as a potentially important consequence of intermittent, not sustained replication in the introduction.

The study is provocative and well executed, with the limitations listed above. Pharmacokinetic analyses help mitigate the lack of blinding. The major impact of this work is if it leads to a much larger randomized, controlled, blinded study of a longer duration, as the authors point out.

Finally, we fully endorse the reviewer’s suggestion that the primary contribution of this study lies in its value as a proof-of-concept and foundation for future randomized, blinded trials of greater scale and duration. We highlighted this more clearly in the revised Discussion (lines 340-346).

Reviewer #1 (Recommendations for the authors):

(1) Lines 84-87: How would chronic immune activation/inflammation be expected to differ if viral antigen is being released from stable reservoirs rather than low-level replication?

This is a very insightful question. Although release of viral antigens from stable reservoirs could certainly also trigger immune activation/inflammation, the reservoir cells in PWH on long-term ART are constantly being negatively selected by the immune system (PMID: 38337034; PMID: 36596305) so that after a number of years on therapy, most proviruses are either transcriptionally silent or express only a low amount of viral RNA/antigen. Recent evidence suggests that these selected cells possess specific biological properties that include mechanisms that limit proviral gene expression (PMID: 36599977; PMID: 36599978). In comparison, low-level replication would result in de novo infection of unselected, activated CD4+ cells that are expected to produce much more viral antigen than preselected reservoir cells.

(2) Lines 249-253: There are multiple ways to explain this observation - alternatively, the total proviral DNA declined due to transient CD4 depletion.

As discussed above, CD4⁺ T-cell counts did not significantly decrease in any of the treatment groups, as shown in Figure 5. The apparent decline observed concerns the CD4/CD8 ratio, which transiently dropped, but not the absolute number of CD4⁺ T cells. Moreover, although the dynamics of total HIV DNA is indeed similar to that of CD4/CD8 ratio (both declined transiently and then returned to baseline by day 84), the dynamics of unspliced RNA and unspliced RNA/total DNA ratio is clearly different, as these markers demonstrated a sustained decrease that was maintained throughout the trial period. Also, we observed a significant decrease in intact HIV DNA at day 84 compared to day 0. These effects cannot be easily explained by a transient decline in CD4+ cells.

(3) Lines 301-305: This is a confusing explanation for not seeing an effect in tissue. Overall, there was no change in total proviral DNA in blood between days 0 and 84 either - yet the explanation for this observation is different (249-253). Was IPDA not performed on the tissue? Wouldn't this be the preferred test for reservoir depletion?

We thank the reviewer for bringing this point to our attention. We modified the Discussion to prevent the confusion (lines 303-305). As for the IPDA on tissue, we attempted this assay on the tissue samples using two independent DNA extraction methods (Promega Reliaprep and Qiagen Puregene), but both yielded high DNA shearing index values, and intact proviral detection was successful in only 3 of 40 samples. Given the poor DNA integrity, these results were not interpretable.

Author response:

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

Reviewer #1 (Public review):

Weaknesses:

Only 1 gene (katG) gave a strong and 1 (Mab_1456c) exhibited a minor defect. Two of the clones did not show any persistence phenotype (blaR and recR) and one (pafA) showed a minor phenotype,

We have now carried out more detailed validation studies on the Tn-Seq, with analysis of timedependent killing over 14 d. This more comprehensive analysis shows that 4 of 5 genes analyzed do indeed have antibiotic tolerance defects under the conditions that Tn-Seq predicted a survival defect (Revised Figure 3). In addition, we found that even before actual cell death, several mutants had delayed resumption of growth after antibiotic removal (Figure 3 Supplemental).

Fig 3 - Why is there such a huge difference in the extent of killing of the control strain in media, when exposed to TIG/LZD, when compared to Fig. 1C and Fig. 4. In Fig. 1C, M. abs grown in media decreases by >1 log by Day 3 and >4 log by Day 6, whereas in Fig. 3, the bacterial load decreases by <1 log by Day 3 and <2 log by Day 6. This needs to be clarified, if the experimental conditions were different, because if comparing to Fig. 1C data then the katG mutant strain phenotype is not very different.

We agree with the reviewer that there is variability in the timing and extent of cell death from experiment to experiment. As noted by the reviewer, in Figure 1C the largest decrement in survival is between day 1 - day 3 (also seen in Figure 6A). As they noted in Figure 4 the largest decrement is between day 3 – day 6 (also seen in Figure 3A, Figure 5F). In each experiment with katG mutants we carefully compare the mutant vs. the control strain within that experiment, which is more accurate than comparing the behavior of mutant in one experiment to a control in another experiment.

Reviewer #2 (Public review):

Weaknesses:

.First, word-choice decisions could better conform to the published literature. Alternatively, novel definitions could be included. In particular, the data support the concept of phenotypic tolerance, not persistence. 

We appreciate the reviewers comments, text modified.

Second, two of the novel observations could be explored more extensively to provide mechanistic explanations for the phenomena. 

We have added several additional experiments, these are detailed below in response to specific comments.

Reviewer #3 (Public review):

Weaknesses:

The findings could not be validated in clinical strains.

We understand the reviewer’s concern that the katG phenotype was only observed in one of the two clinical strains we studied. We feel that our findings are relevant beyond the ATCC 19977 strain for two reasons

(1) We have performed additional analyses of the two clinical isolates and indeed find significant accumulation of ROS following antibiotic exposure in both of these strains (revised Figure 6A).

(2) We do in fact see a role for katG in starvation-induced antibiotic tolerance in Mabs clinical strain-2. It is not surprising that different strains from a particular species may have some different responses to stresses – for example, there is wide strain-specific variability in susceptibility to different phages within a species based on which particular phage defense modules a given strain carries (for example PMID: 37160116). We speculate that different Mabs strains may express varying levels of other antioxidant factors and note that the genes encoding several such factors were identified by our Tn-Seq screen including the peroxidases ahpC, ahpD, and ahpE. Our analysis of the genetic interactions between katG and these other factors is ongoing. 

Comments/Suggestions

(1) In Fig1E, the authors show no difference in killing Mtb with or without adaptation in PBS. These data are contrary to the data presented in Figure 1B. These also do not align with the data of M. smegmatis and M. abscesses. Please discuss these observations in light of the Duncan model of persistence (Mol Microbiol. 2002 Feb;43(3):717-31.).’

The above referenced Duncan laboratory study found tolerance after prolonged starvation but did not actually examine tolerance at early time points. While some of the transcriptional and metabolic changes seen by Duncan and others are slow, other groups have described starvation responses in Mtb that are quite rapid. For example, the stringent response mediator ppGpp accumulates within a few hours after onset of starvation in Mtb (PMID: 30906866). We suspect that a rapid signaling response such as this underlies the phenotype we observe. Regarding the difference between Mtb and other mycobacterial species we also find it surprising that Mtb had a much more rapid starvation response. This is a clear species-specific difference that may reflect an adaptation of Mtb to the nutrient-limited physiologic niche within host macrophages.

(2) Line 151, the authors state that they have used an M. abscesses Tn mutant library of ~ 55,000 mutant strains. The manuscript will benefit from the description of the coverage of total TA sites covered by the mutants.

Text modified to add this detail. There are 91,559 TA sites in the abscessus genome. Thus, our Tn density is ~60%.

(3) Line 155: Please explain how long the cells were kept in an Antibiotic medium.

This technical detail was noted above on line 153 in the original text: “…and then exposed them to TIG/LZD for 6 days”. To clarify the overall conditions, we have also revised the text of the manuscript and added the detail of how long cells were passaged after removal of antibiotics.

(4) Line 201: data not shown. Delayed resumption of growth after removal of antibiotic would be helpful in indicating drug resilience. This data could enhance the manuscript.

Data now provided in Figure 3 Supplemental

(5) Figures 4C and 4F represent the kill curve. It will be good to show the date with CFU against the drug concentration in place of OD600. CFU rather than OD600 best reflects growth inhibition.

Figures 4C and 4F are measuring the minimum inhibitory concentration (MIC) to stop the overall growth of the bacterial population. While we agree that CFU could be analyzed, this would be measuring a different outcome – cell death and the minimum bactericidal concentration (MBC). In these experiments we sought to specifically examine the MIC so as to separate growth inhibition from cell death. For this we used the standard method employed by clinical microbiology laboratories for MIC, which is optical density of the culture (PMID: 10325306).

(6) Figure 5C. The authors shall show the effect of TIG/LZD on M. abscesses ROS production without the PBS adaptation. It is important to conclude that TIG/LZD induces ROS in cells. Authors should utilize ROS scavengers such as Thiourea, DFO, etc., to conclude ROS's contribution to bacterial killing following inhibition of transcription and translation.

New data added (revised Figure 5 and Figure 5 Supplemental)  

(7) Line 303. Remove "note".

Text revised. We thank the reviewer for identifying this typographical error.  

(8) The introduction and Discussion are very similar, and several lines are repeated.

Text revised with overlapping content removed.

Reviewer #1 (Recommendations for the authors):

It appears that the same datasets for PBS adapted cultures were plotted in A-C and D-F. Either this should be specifically mentioned in the legend or it might be better to integrate the non-adapted plots into A-C which would also allow easier comparison.

Appreciate the reviewer’s suggestion; text modified with added clarification to figure legend.

This manuscript is focused on M. abs and the antibiotics TIG/LZD, so the Mtb data or data using the antibiotics INH/RIF/EMB and serves more as a distraction and can be removed

We appreciate the reviewer’s perspective. However, we wish to include these data to show the similarities (and differences) in starvation-induced tolerance between the three organisms.

Fig 3 -As mentioned for Fig. 1, it appears that the same dataset was used for the control in all the figures A-E. This should be explicitly stated in the Figure legend.

Appreciate the reviewer’s suggestion; text modified with added clarification to figure legend.

The divergent results from the clinical strains are extremely interesting. It would be helpful to determine the oxidative stress levels (similar to the cellROX data shown in 5E), to tease out if the difference in katG role is because of lack of ROS induction in these strains or due to expression of alternate anti-oxidative stress defense mechanisms.

We have performed additional cellROX analysis as suggested by the reviewer and found that the ROS induction is indeed present across all three Mabs strains, but that katG is only required in one of the two strains (Strain #2). These data are now included in the revised Figure 6.

Reviewer #2 (Recommendations for the authors):

GENERAL COMMENTS

This is a nice piece of work that uses the pathogen Mabs as a test subject.

The work has findings that likely apply generally to antibiotics and mycobacteria: 1) phenotypic tolerance is associated with suppression of ROS, 2) lethal protein synthesis inhibitors act via accumulation of ROS, and 3) levofloxacin behaves in an unexpected way. Each is a new observation. However, I believe that each topic requires more work to be firmly established to be suitable for eLife.

Phenotypic tolerance: Association with suppression of ROS is important but expected. I would solidify the conclusion by performing several additional experiments. For example, confirm the lethal effect of ROS by reducing it with an iron chelator and a radical scavenger. There is a large literature on effects of iron uptake, levels, etc. on antibiotic lethality that could be applied to this question. In 2013 Imlay argued against the validity of fluorescent probes. Perhaps getting the same results with another probe would strengthen the conclusion.

We have carried out additional experiments with both an iron chelator and small molecule ROS scavengers to further test this idea but note that these experiments have several inherent limitations: 1) These compounds have highly pleiotropic effects. For example while N-acetyl cysteine (NAC) is an antioxidant it also increases mycobacterial respiration and was shown to paradoxically decrease antibiotic tolerance in M. tuberculosis (PMID: 28396391). 2) It has been shown by the Imlay group that small-molecule antioxidants are often ineffective in quenching ROS in bacteria (PMID: 388893820), making negative results difficult to interpret. Nonetheless, we present new experimental data showing that iron chelation does indeed improve the survival of antibiotic-treated Mabs (revised Figure 5).  However,  small molecule antioxidants such as thiourea do not restore antibiotic tolerance and actually increased bacterial cell death, suggesting that they may be affecting respiration in Mabs in a manner similar to that seen for NAC in Mtb. We also note that our genetic analysis, which identified numerous other genes encoding proteins with antioxidant function (Figure 2) is a strong additional argument in support of the importance of ROS in antibiotic-mediated lethality. 

Regarding the concern raised by Imlay about the validity of oxidation-sensitive dyes - this relates to concern bacterial autofluorescence induced by antibiotics that can confound analyses in some species. We have ruled this out in our analyses by using bacteria unstained by cellROX as controls to confirm that there is negligible autofluorescence in Mabs (<0.1%, Figure 5E, Figure 6A).

Protein synthesis inhibitors: At present, this is simply an observation. More work is needed to suggest a mechanism. For example, with E. coli the aminoglycosides are protein synthesis inhibitors that also cause membrane damage. Membrane damage is known to stimulate ROS-mediated killing. Your observation needs to be extended because chloramphenicol, another protein synthesis inhibitor, blocks ROS production. The lethality may be a property of mycobacteria: does it occur with E. coli (note that rifampicin is bacteriostatic with E. coli but lethal to Mtb)?

We agree with the reviewer that the mechanism underlying ROS accumulation following transcription or translational inhibition in Mabs is of significant interest. It is likely to be a mechanism different from E. coli, because in E. coli tetracyclines and rifamycins are both bacteriostatic, whereas in Mabs they are both bactericidal. Determining the mechanism by which translation inhibitors cause ROS accumulation in Mabs is an ongoing effort in our laboratory using proteomics and metabolomics, but is outside the scope of this manuscript.

Levofloxacin: This is also at the observational stage but is unexpected. In other studies, ROS is involved in quinolone-mediated killing of bacteria. Why is this not the case with Mabs? The observation should be solidified by showing the contrast with moxifloxacin, since this compound has been studied with mycobacteria (Shee 2022 AAC). With E. coli, quinolone structure can affect the relative contribution of ROS to killing (Malik 2007 AAC), as is also seen with Mtb (Malik 2006 AAC). What is happening in the present work with levofloxacin, an important anti-tuberculosis drug? Is there a structure explanation (compare with ofloxacin)?

While these are interesting questions, a detailed exploration of the structure-function relationships between different fluoroquinolone antibiotics and their varying activities on Mtb and Mabs is outside the scope of this manuscript.  

The writing is generally easy to follow. However, the concept of persistence should be changed to phenotypic tolerance with text changes throughout. I base this suggestion on the definitions of tolerance and persistence as stated in the consensus review (Balaban 2019 Nat Micro Rev). Experimentally, tolerance is seen as a gradual decline in survival following antibiotic addition; the decline is slower than seen with wild-type cells. The data presented in this paper fit that definition. In contrast, persistence refers to a rapid drop in survival followed by a distinct plateau (Balaban 2019 Nat Micro Rev; for example, see Wu Lewis AAC 2012 ). Moreover, to claim persistence, it would be necessary to demonstrate subpopulation status, which is not done. The Balaban review is an attempt to bring order to the field with respect to persistence and tolerance, since the two are commonly used without regard for a consistent definition.

We appreciate the reviewer’s suggestion; text modified in multiple places to clarify.

Another issue requiring clarification is the relationship between resistance and tolerance. Killing by antibiotics is a two-step process, as most clearly seen with quinolones. First a reversible bacteriostatic event occurs. Resistance blocks that bacteriostatic damage. Then a lethal metabolic response to that damage occurs. Tolerance selectively blocks the second, killing event, a distinct process that often involves the accumulation of ROS. Direct antibiotic-mediated damage is an additional mode of killing that also stems from the reversible, bacteriostatic damage created by antibiotics. The authors recognize the distinction but could make it clearer. Take a look at Zheng (JJ Collins) 2020, 2022.

Text modified to clarify this point

Many readers would also like to see a bit more background on Mabs. For example, does it grow rapidly? Are there features that make it a good model for studying mycobacteria or bacteria in general? The more general, the better.

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Below I have listed specific comments that I hope are useful in bringing the work to publication and making it highly cited.

SPECIFIC COMMENTS

Line 30 unexpectedly. I would delete this word because the result is expected from the ROS work of Shee et al 2022 with mycobacteria. Moreover, Zeng et al 2022 PNAS showed that ROS participates in antimicrobial tolerance, and persistence is a form of tolerance (Balalban et al, 2019, Nat Micro Rev).

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Line 39 key goal: this is probably untrue in the general sense stated, since bacteriostatic antibiotics are sufficient to clear infection (Wald-Dickler 2019 Clin Infect Dis). However, it is likely to be the goal for Mtb infections.

We agree with the reviewer that bacteriostatic antibiotics are effective in treating most types of infections and do not claim otherwise in the manuscript. However, from a clinical standpoint, eradication of the pathogen causing the infection is indeed the goal of antibiotic therapy in virtually all circumstances (with the exception of specific scenarios such as cystic fibrosis where it is recognized that the infecting organism cannot be fully eliminated). In most cases, the combination of bacteriostatic antibiotics and the host immune response is sufficient to achieve eradication. We have modified the manuscript text to reflect this nuance noted by the reviewer.

Line 62 several: you list three, but hipAB works via ppGpp, so the sentence needs fixing

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Line 70 uncertain: this uncertainty is unreferenced. Since everything is uncertain, this vague phrase does not add to the story.

The reviewer makes an interesting philosophical argument. However, we would submit that some aspects of biology, for example the regulation of glycolysis, are understood in great detail. However, other mechanisms, such as the precise mechanisms of lethality for diverse antibiotics in different bacterial species, are far more uncertain and remain a subject of debate (for example PMID: 39910302). Text not modified.

Line 72 somewhat controversial: I would delete this, because the points in the Science papers by Lewis and Imlay have been clarified and in some cases refuted by prior and subsequent work.

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Line 72 presumed: this suggests that it is wrong and perhaps a different idea has replaced it. Another, and more likely view is that there is an additional mode of killing. I suggest rephrasing to be more in line with the literature.

Text modified for clarity. In this sentence “presume” refers to the historical concept that direct target inhibition was solely responsible for antibiotic lethality. As the reviewer notes, there is now significant literature that ROS (and perhaps other secondary effects) also contribute to bacterial killing.  

Line 73 However and the following might also: this phrasing, plus the presumed, misleads the reader from your intent. I suggest rephrasing.

See above re: line 72

Line 75 citations: these are inappropriate and should be changed to fit the statement. I suggest the initial paper by Collins (Kohanski 2007 Cell) a recent paper by Zhao (Zeng PNAS 2022), and a review Drlica Expert Rev Anti-infect Therapy 2021). The present citations are fine if you want to narrow the statement to mycobacteria, but the history is that the E. coli work came first and was then generalized to mycobacteria. A mycobacterial paper for ROS is Shee 2022 AAC.

We thank the reviewer for noticing that we inadvertently omitted several important E. coli-related references. These have been added.

Line 75 and 76: Conversely ... unresolved. Compelling arguments have been made that show major flaws in the two papers cited, and a large body of evidence has now accumulated showing the validity of the idea promoted by the Collins lab, beginning with Kohanski 2007. In addition to many papers by Collins, see Hong 2019 PNAS and Zeng 2022 PNAS). It is fine if you want to counter the arguments against the Lewis and Imlay papers (summarized in Drlica & Zhao 2021 Expert Rev Anti-infect Therapy), but making a blanket statement suggests that the authors are unfamiliar with the literature.

We agree with the reviewer that the weight of the evidence supports a role for antibiotic-induced ROS as an important mechanism for antibiotic lethality under many (though not all) conditions. We have revised the text to better reflect this nuance.

Line 78. Advantages over what?

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Line 80 exposure: to finish the logic you need to show that E. coli and S. aureus persisters fail to do this.

We thank the reviewer for their suggestion but studying these other organisms is outside the scope of this study. 

Line 82 whereas: this misdirects the reader. It would seem that a simple "and" is better

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Line 89 I think this paragraph is about the need to study Mabs, the subject of the present report. This paragraph could use a more appropriate topic sentence to guide the reader so that no guessing is involved. I suggest rephrasing this paragraph to make the case for studying more compelling.

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Line 96. I suggest citing several references after subinhibitory concentration of antibiotic.

The references are in the following sentence alongside the key observations.

Line 99. Genetic analysis: how does this phrase fit with the idea of persister cells arising stochastically?

There are two issues: 1) We would argue that persister formation is not completely stochastic, but rather a probability that can be modified both genetically and by environment (for example hipA PMID: 6348026). 2) Even if persister formation were totally stochastic, the survival of these cells may depend on specific genes – as we indeed find in our Tn-Seq analysis of Mabs.  

Line 106. In this paragraph you need to define persister. The consensus definition (Balaban 2019 Nat Micro Rev) is a subpopulation of tolerant cells. Tolerance is defined as the slowing or absence of killing while an antibiotic retains its ability to block growth. See Zeng 2022 PNAS for example with rapidly growing cells. Phenotypic tolerance is the absence of killing due to environmental perturbations, most notably nutrient starvation, dormancy, and growth to stationary phase. By extension, phenotypic persistence would be subpopulation status of a phenotypically tolerant cells. If you have a different definition, it is important to state it and emphasize that you disagree with the consensus statement.

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Line 109 unexpectedly. I would delete this word, because the literature leads the reader to expect this result unless you make a clear case for Mabs being fundamentally different from other bacteria with respect to how antibiotics kill bacteria (this is unlikely, see Shee 2022 AAC). Indeed, lines 111-113 state extensions of E. coli work, although suppression of ROS in phenotypic tolerance and genetic persistence have not been demonstrated.

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Line 124 you might add, in parentheses and with references, that a property of persisters is crosspersistence to multiple antibiotic classes. This is also true for tolerance, both genetic and phenotypic. An addition will support your approach.

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Line 128 minimal

Text not modified. We appreciate the reviewer’s preference but both “minimal” and “minimum” are both widely accepted terms. Indeed, the Balaban et al 2019 consensus statement on definitions cited by the author above also uses “minimum” (PMID: 30980069), as do IDSA clinical guidelines (PMID: 39108079).

Line 130 is MIC somehow connected to killing or did you also measure killing? Note that blocking growth and killing cells are mechanistically distinct phenomena, although they are related. By being upstream from killing, blockage of growth will also interfere with killing.

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Line 133 PBS is undefined

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Line 134 increase in persisters ... you need to establish that these are not phenotypically tolerant cells. Do they constitute the entire population (tolerance)? Your data would be more indicative of persisters if you saw a distinct plateau with the PBS samples, as such data are often used to document persistence (retardation of killing is a property of tolerance, Balaban 2019). Fig. 1B is clearly phenotypic tolerance, as the entire population grows. Your data suggest that you are not measuring persistence as defined in the literature (Balaban 2019). Line 139 persister should be tolerance •

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Lines 142, 143, 144. 159, 163, 171, 181, 211, 226, 238, 246, 277, 279,289 persistent should be tolerant

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Line 146 fig 1E Mtb does not show the adaptation phenomenon and it is clearly tolerant, not persistent. This should be pointed out. As stated, you may be misleading the reader.

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*Line 169. Please make it clear whether these genes are affecting antibiotic susceptibility (MIC will affect killing because blocking growth is upstream) or if you are dealing with tolerance (no change in MIC). These measurements are essential and should included as a table. By antibiotic response, do you mean that antibiotics change expression levels?

Regarding MICs, the data for MICs in control and katG mutant are presented in Figure 4C and 4F. Regarding ‘response’ we have clarified the text of this sentence.

Line 174 Interestingly should be as expected

Text not modified; tetracyclines do not induce ROS in E. coli and oxazolidinones have not been studied in this regard.

Line 183 you need to include citations. You can cite the ability of chloramphenicol to block ROS-mediated killing of E. coli. That allows you to use the word unexpected

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Line 199. All of the data in Fig. 3 shows tolerance, not persistence, requiring word changes in this paragraph.

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Line 226. The MIC experiment is important. You can add that this result solidifies the idea that blocking growth and killing cells are distinct phenomena. You can cite Shee 2022 AAC for a mycobacterial paper

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Line 241. The result with levofloxacin is unexpected, because the fluoroquinolones are widely reported to induce ROS, even with mycobacteria (see Shee 2022 AAC). You need to point this out and perhaps redo the experiment to make sure it is correct.

We appreciate the reviewer’s interest in this question. All experiments in this paper were repeated multiple times. This particular experiment was repeated 3 times and in all replicates the katG mutant was sensitized to translation inhibitors but not levofloxacin. Shee et al examined Mtb treated with moxifloxacin and found ROS generation, but did not assess whether a Mtb katG mutant had impaired survival. Thus, in addition to differences in: i) the species studied and ii) the particular fluoroquinolone used, the two sets of experiments were designed to address different questions (ROS accumulation vs protection by katG) . A cell might accumulate ROS without a katG mutant having impaired survival if genetic redundancy exists – a result we indeed see in our clinical Mabs strains under some conditions (new data included in revised Figure 6A).  

Line 269 Additional controls would bolster the conclusion: use of an antioxidant such as thiourea and an iron chelator (dipyridyl) both should reduce ROS effects.

New experiments performed, revised Figure 5.

Line 276 the word no is singular

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Line 284 this suggested ... in fact previous work suggested. This summary paragraph might go better as the first paragraph of the Discussion

Text modified to specify that this is in reference to the work in this manuscript

Lines 294-299 Most of this is redundant and should be deleted.

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Line 299 this species is vague

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Line 310 Do you want to discuss spoT?

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Line 313 paragraph is largely redundant

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Line 314 controversial. As above, I would delete this, especially since it is not referenced and is unlikely to be true. If you believe it, you have the obligation to show why the ROS-lethality idea is untrue. If you are referring to Lewis and Imlay, there were almost a dozen supporting papers before 2013 and many after. This statement does not make the present work more important, so deletion costs you nothing.

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Line 314 direct disruption of targets. This is clearly not a general principle, because the quinolones rapidly kill while inhibition of gyrase by temperature-sensitive mutations does not (Kreuzer 1979 J.Bact; Steck 1985). Indeed, formation of drug-gyrase-DNA complexes is reversible: death is not.

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Line 318 as pointed out above, you have not brought this story up to date. The two papers mainly focused on Kohanski 2007, ignoring other available evidence.’’

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Line 326 you need to cite Shee 2022 AAC

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Line 342 the idea of mutants being protective is not novel, as several have been reported with E. coli studies. Thus, there is a general principle involved.

We agree that this suggests a potential general principle

Line 344. It depends on the inhibitor. For example, aminoglycosides are translation inhibitors and they also cause the accumulation of ROS.

We agree that ROS generation depends on the inhibitor, and indeed upon other variables including drug concentration, growth conditions, and bacterial species as well.  

Line 347. You need to point out the considerable data showing that the absence of catalase increases killing

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Line 363 look at Shee 2022 AAC and Jacobs 2021 AAC

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Line 585 I suggest having a colleague provide critical comments on the manuscript and acknowledge that person.

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One issue: Our onset detection method is based on statistical significance, i.e., the onset is the earliest time point of a significant increase in the cohort (versus unrelated) smooth. One of our reviewers (McMurray) thinks this is not appropriate, because this means that more noisy data and/or data based on smaller samples would lead to later onsets, thus reducing comparability between experiments.

We think of the use of significance as a feature, not a bug: For one, it reduces researcher degrees of freedom because the criterion is automatically determined. Also, this criterion is very broadly applicable (even to other data types, models,, tasks). Finally, we show in our simulation study that sample size and noise play little role in the coverage properties of our method (whereas they affect the bootstrap-based method of Stone et al. much more dramatically).

Nevertheless, ... McMurray is still correct that our method conflates the two things, noise and early/late. In response, I have implemented an option in the package that allows you to specify a "magnitude threshold" for onset detection, which is not based on significance. It's called 'onset_criterion', and by default, it detects an onset when a magnitude of 0.075 logits is reached relative to the baseline (can be changed with 'onset_threshold').

What does this mean for the RR? It seems to me that what is meant by "earlier" in your hypotheses is already connected to the influence of noise? i.e., data from lower-quality webcams can be much more noisy so it'll be harder to detect a significant difference in that condition. In other words, you need a larger effect in terms of proportions for it to be detected and this may only emerge later? If that is true, the default operation of the method (which uses significance) will indeed align well with your hypotheses.

Still, this is something to keep in mind: (1) you might want to make the distinction between noise and early/late more clear in the RR hypothesis. And/or (2) you might want to preregister secondary analysis with a magnitude criterion rather than a significance-based one, in an attempt to separate noise from a magnitude-based increase in proportion of looks.

I also thought about Semiotics of a Kitchen by Martha Rosler so much throughout this essay. Bertillon and Galton's legacy cast a long shadow over us as prospective archivists, and we need to think very carefully about how we operate in the world as archivists, especially in the age of AI.. AI feels like it can reinforce existing social biases and power structures that Galton birthed and this is already happening which scares me- especially because I have to hold myself accountable at making sure I don't let AI control or dominate me as an archivist. The last bit of Ernest Cole resonated with me heavily. As an archivist, we must think about histories and the people whose histories we may be painstakingly collecting that are constantly threatened to become eradicated, erased, and violently displaced. How do we make truth available to people in a way that they are the ones who get to tell their story?

I think this is an interesting example of how technology with limited options benefits those who fit within societal standards and binary categories. However, those who do not fit the norm may be harmed by technologies like these. Because the system only had male or female as the options, this limited the narrator as they would be flagged either way. I think this says a lot about the way our sociocultural beliefs and gender norms are embedded within the very technology we deploy around us.

Author response:

(1) General Statements

Our manuscript studies mechanisms of planar polarity establishment in vivo in the Drosophila pupal wing. Specifically we seek to understand mechanisms of ‘cell-scale signalling’ that is responsible for segregating core pathway planar polarity proteins to opposite cell edges. This is an understudied question, in part because it is difficult to address experimentally.

We use conditional and restrictive expression tools to spatiotemporally manipulate core protein activity, combined with quantitative measurement of core protein distribution, polarity and stability. Our results provide evidence for a robust cell-scale signal, while arguing against mechanisms that depend on depletion of a limited pool of a core protein or polarised transport of core proteins on microtubules. Furthermore, we show that polarity propagation across a tissue is hard, highlighting the strong intrinsic capacity of individual cells to establish and maintain planar polarity.

The original manuscript received three fair and thorough peer-reviews, which raised many important points. In response, we decided to embark on a full revision that attempts to answer all of the points. We have included new data to support our conclusions in Supplemental Figures 1, 2 and 5.

Additionally in response to the reviewers we have revised the manuscript title, which is now ‘Characterisation of cell-scale signalling by the core planar polarity pathway during Drosophila wing development’.

(2) Point-by-point description of the revisions

We thank all of the reviewers for their thorough and thoughtful review of our manuscript. They raise many helpful points which have been extremely useful in assisting us to revise the manuscript.

In response we have carried out a major revision of the manuscript, making numerous changes and additions to the text and also adding new experimental data. Specific changes are listed after our detailed response to each comment.

Reviewer #1:

[…] Major points:

The exact meaning of cell-scale signaling is not defined, but I infer that the authors use this term to describe how what happens on one side of a cell affects another side. The remainder of my critique depends on this understanding of the intended meaning.

As the reviewer points out, it is important that the meaning of the term ‘cell-scale signalling’ is clear to the reader and in response to their comment we have had another go at defining it explicitly in the Introduction to the manuscript.

Specifically, we use the term ‘cell-scale signalling’ to describe possible intracellular mechanisms acting on core protein segregation to opposite cell membranes during core pathway dependent planar polarisation. For example, this could be a signal from distal complexes at one side of the cell leading to segregation of proximal complexes to the opposite cell edge, or vice versa. See also our response to Reviewer #2 regarding the distinction between ‘molecular-scale’ and ‘cell-scale’ signalling. 

Changes to manuscript: Revised definition of ‘cell-scale signalling’ in Introduction.

The authors state that any tissue wide directional information comes from pre-existing polarity and its modification by cell flow, such that the de novo signaling paradigm "bypasses" these events and should therefore not be responsive to any further global cues. It is my understanding that this is not a universally accepted model, and indeed, the authors' data seem to suggest otherwise. For example, the image in Fig 5B shows that de novo induction restores polarity orientation to a predominantly proximal to distal orientation. If no global cue is active, how is this orientation explained?

We assume that the reviewer’s point is that it is not universally accepted that de novo induction after hinge contraction leads to uncoupling from global cues (rather than that it is not accepted that hinge contraction remodels radial polarity to a proximodistal pattern). We are (we believe) the only lab that has used de novo induction as a tool, and we’re not aware of any debate in the literature about whether this bypasses global cues. Nevertheless, we accept that it is hard to prove there is no influence of global cues, when the nature of those cues and the time at which they act remain unclear. Below we summarise the reasons why we believe there are not significance effects of global cues in our experiments that would influence the interpretation of our results.

First, our reading of the literature supports a broad consensus that an early radial core planar polarity pattern is realigned by cell flow produced by hinge contraction beginning at around 16h APF (e.g. Aigouy et al., 2010; Strutt and Strutt, 2015; Aw and Devenport, 2017; Butler and Wallingford, 2017; Tan and Strutt, 2025). Taken at face value, this suggests that there are ‘radial’ cues present prior to hinge contraction, maybe coming from the wing margin – arguably these radial cues could be Ft-Ds or Wnts or both, given they are expressed in patterns consistent with such a role (notwithstanding the published evidence arguing against roles for either of these cues). It then appears that hinge contraction supercedes these cues to convert a radial pattern to a proximodistal pattern – whether the radial cues that affect the core pathway earlier remain active after hinge contraction is unclear, although both Ft-Ds and Wnts appear to maintain their ‘radial’ patterns beyond the beginning of hinge contraction (e.g. Merkel et al., 2014; Ewen-Campen et al., 2020; Yu et al., 2020).

We think that the reviewer is proposing the presence of a proximodistal cue that is active in the proximal region of the wing that we use for our experiments shown e.g. in Fig.5, and that this cue orients core polarity here (but not elsewhere in the wing) in a time window after 18h APF. Ft-Ds and Wnts do not seem to be plausible candidates as they are still in ‘radial’ patterns. This leaves either an unknown proximodistal cue (a gradient of some unknown signalling molecule?), or possibly some ability of hinge contraction to align proximodistal polarity specifically in this wing region but not elsewhere. We cannot definitively rule out either of these possibilities, but neither do we think there is sufficient evidence to justify invoking their existence to explain our observations.

In particular, the reason that we don’t think there is a proximodistal cue in the proximal part of the wing after 18h APF, is that work from our lab shows that induction of Fz or Stbm expression at times around or after the start of hinge contraction (i.e. >16 h APF) results in increasing levels of trichome swirling with polarity not being coordinated with the tissue axis either proximally or distally (Strutt and Strutt, 2002; Strutt and Strutt 2007). Our simplest interpretation for this is that induction at these stages fails to establish the early radial pattern of core pathway polarity and hence hinge contraction cannot reorient radial to proximodistal. If hinge contraction alone could specify proximodistal polarity in the absence of the earlier radial polarity, then we would not expect to see swirling over much of the proximal wing (where the forces from hinge contraction are strongest (Etournay et al., 2015)).

In this manuscript, our earliest de novo experiments begin with Fz induction at 18h APF (de novo 10h), then at 20h APF (de novo 8h) and at 22h APF (de novo 6h). The image in Fig. 5B, referred to by the reviewer, is of a wing where Fz is induced de novo at 22 h APF. In these wings, as expected, the core proteins localise asymmetrically in stereotypical swirling patterns throughout the wing surface (see Fig. 2M and also Strutt and Strutt, 2002; Strutt and Strutt 2007), but – usefully for our experiments – they broadly localise along the proximal-distal axis in the region analysed in Fig. 5B. Given the strong swirling in surrounding regions when inducing at >20h APF, we feel reasonably confident in assuming that the pattern is not due to a proximodistal cue present in the proximal wing.

We appreciate that the original manuscript did not show images including the trichome pattern in adjacent regions, so this point would not have been clear, but we now include these in Supplementary Fig. 5. We have also added a note in the legend to Fig. 5B to clarify that the proximodistal pattern seen is local to this wing region. We apologise for this oversight and the confusion caused and appreciate the feedback.

The 6 hr condition, that has only partial polarity magnitude, is quite disordered. Do the patterns at 8 and 10 hrs become more proximally-distally oriented? It is stated that they all show swirls, but please provide adult wing images, and the corresponding orientation outputs from QuantifyPolarity to help validate the notion that the global cues are indeed bypassed by this paradigm.

In all three ‘normal’ de novo conditions (6h, 8h and 10h), regardless of the time of induction, the polarity orientation patterns of Fz-mKate2 in pupal and adult wings are very similar in the experimentally analysed region (Fig. S5B-E). The strong local hair swirling agrees with the previous published data (Strutt and Strutt, 2002; Strutt and Strutt 2007). Overall, we don’t see any evidence that the 10h de novo induction results in more proximodistally coordinated polarity than the 8h or 6h conditions. This is consistent with our contention that there is no global cue present at these stages, which presumably would have a stronger effect when core pathway activity was induced at earlier stages.

Changes to manuscript: Added additional explanation of the ‘de novo induction’ paradigm and why we believe the resulting polarity patterns are unlikely to be influenced by any global signals in Introduction and Results section ‘Induced core protein relocalisation…’. Added quantification of polarity in the experiment region proximal to the anterior cross-vein in pupal wings (Fig.S5E-E’’’) and zoomed-out images of the surrounding region in adult wings showing that the polarity pattern does not become more proximodistal when induction time is longer, and also that there is not overall proximodistal polarity in proximal regions of the wing (Fig.S5B-D), arguing against an unknown proximodistal polarity cue at these stages of development.

In the de novo paradigm, polarization is initiated immediately or shortly after heat shock induction. However, the results should be differently interpreted if the level of available Fz protein does not rise rapidly and then stabilize before the 6 hr time point, and instead continues to rise throughout the experiment. Western blots of the Fz::mKate2-sfGFP at time points after induction should be performed to demonstrate steady state prior to measurements. Otherwise, polarity magnitude could simply reflect the total available pool of Fz at different times after induction. Interpreting stability is complex, and could depend on the same issue, as well as the amount of recycling that may occur. Prior work from this lab using FRAP suggested that turnover occurs, and could result from recycling as well as replenishment from newly synthesized protein. 

The reviewer raises an important point, which we agree could confound our experimental interpretations. As suggested we have now carried out western blotting and quantitation for Fz::mKate2-sfGFP levels and added these data to Fig.S1 (Fig. S1C,D). Quantified Fz is not significantly different between the three de novo polarity induction timings and not significantly different compared to constitutive Fz::mKate2-sfGFP expression (although there is a trend towards increasing Fz::mKate2-sfGFP protein levels with increasing induction times). These data are consistent with Fz::mKate2-sfGFP being at steady state in our experiments and that levels are sufficient to achieve normal polarity (as constitutive Fz::mKate2-sfGFP does so). Therefore it is unlikely that differing protein levels explain the differing polarity magnitudes at the different induction times. Interestingly, Fz::mKate2-sfGFP levels are lower than endogenous Fz levels, possibly due to lower expression or increased turnover/reduced recycling.

Changes to manuscript: Added western blot analysis of Fz::mKate2-sfGFP expression under 10h, 8h and 6h induction conditions vs endogenous Fz expression and constitutive Fz::mKate2sfGFP expression (Fig.S1C-D) and discussed in Results section ‘Planar polarity establishment is…’.

From the Fig 3 results, the authors claim that limiting pools of core proteins do not explain cellscale signaling, a result expected based on the lack of phenotypes in heterozygotes, but of course they do not test the possibility that Fz is limiting. They do note that some other contributing protein could be. 

Previously published results from our lab (Strutt et al., 2016 Cell Reports; Supplemental Fig. S6E) show that in a heterozygous fz mutant background, Fz protein levels are not affected by halving the gene dosage when compared to wt, suggesting that Fz is most likely produced in excess and is not normally limiting, but that protein that cannot form complexes may be rapidly degraded. We have now added this information to the text.

Changes to manuscript: Added explanation in text that Fz levels had previously been shown to not be dosage sensitive in Results section ‘Planar polarity establishment is…’ and also added a caveat to the Discussion about not directly testing Fz.

In Fig 3, it is unclear why the authors chose to test dsh1/+ rather than dsh[null]/+. In any case, the statistically significant effect of Dsh dose reduction is puzzling, and might indicate that the other interpretation is correct. Ideally, a range including larger and smaller reductions would be tested. As is, I don't think limiting Dsh is ruled out. 

Concerning the choice of dsh allele, we appreciate the query of the reviewer regarding use of dsh[1] instead of a null, as there might be a concern that dsh[1] would give a less strong phenotype. The answer is that over more than two decades we and others have never found any evidence that dsh[1] does not act as a ‘null’ for planar polarity in the pupal wing, and furthermore use of dsh[1] preserves function in Wg signalling – and we would prefer to rule out any phenotypic effects due to any potential cross-talk between the two pathways that might be seen using a complete null. To expand on this point, dsh[1] mutant protein is never seen at cell junctions (Axelrod 2001; Shimada et al., 2001; our own work), and by every criteria we have used, planar polarity is completely disrupted in hemizygous or homozygous mutants e.g. see quantifications of polarity in (Warrington et al., 2017 Curr Biol).

In terms of the broader point, whether we can rule out Dsh being limiting, we were very careful to be clear that we did not see evidence for Dsh (or other core proteins) being limiting in terms of ‘rates of core pathway de novo polarisation’. When the reviewer says ‘the statistically significant effect of Dsh dose reduction is puzzling’ we believe they are referring to the data in Fig. 3J, showing a small but significantly different reduction in stable Fz in de novo 6h conditions (also seen in 8h de novo conditions, Fig. S3I). As Dsh is known to stabilise Fz in complexes (Strutt et al., 2011 Dev Cell; Warrington et al., 2017 Curr Biol), in itself this result is not wholly surprising. Nevertheless, while this shows that halving Dsh levels does modestly reduce Fz stability, it does not alter our conclusion that halving Dsh levels does not affect Fz polarisation rate under either 6h or 8h de novo conditions.

Unfortunately, we do not have available to us a practical way of achieving consistent intermediate reductions in Dsh levels (e.g. a series of verified transgenes expressing at different levels). Levels of all the core proteins could be dialled down using transgenes, to see when the system breaks, and indeed we have previously published that lower levels of polarity are seen if Fmi levels are <<50% or if animals are transheterozygous for pk, stbm, dgo or dsh, pk, stbm, dgo simultaneously (Strutt et al., 2016 Cell Reports). However, it seems to be a trivial result that eventually the ability to polarise is lost if insufficient core proteins are present at the junctions. For this reason we have focused on a simple set of experiments reducing gene dosage singly by 50% under two de novo induction conditions, and have been careful to state our results cautiously. The assays we carried out were a great deal of work even for just the 5 heterozygous conditions tested.

We believe that the experiments shown effectively make the point that there is no strong dosage sensitivity – and it remains our contention that if protein levels were the key to setting up cell-scale polarity, then a 50% reduction would be expected to show an effect on the rate of polarisation. We further note that as Fz::mKate2-sfGFP levels are lower than endogenous Fz levels (see above), the system might be expected to be sensitised to further dosage reductions, and despite this we failed to see an effect on rate of polarisation.

We note that Reviewer #3 made a similar point about whether we can rule out dosage sensitivity on the basis of 50% reductions in protein level. To address the comments of both reviewers we had now added some further narrative and caveats in the text.

In a similar vein, Reviewer #2 requested data on whether dosage reduction altered protein levels by the expected amount. We have now added further explanation/references and western blot data to address this.

Changes to manuscript: Added more explanation of our choice of dsh[1] as an appropriate mutant allele to use in Results section ‘Planar polarity establishment is…’. Added some narrative and caveats regarding whether lowering levels more than 50% would add to our findings in the Discussion. Revised conclusions to be more cautious including altering section title to read ‘Planar polarity establishment is not highly sensitive to variation in protein levels of core complex components’.

Also added westerns and text/references showing that for the tested proteins there is a reduction in protein levels upon removal of one gene dosage in Results section ‘Planar polarity establishment is…’ and Fig.S2.

The data in Fig 5 are somewhat internally inconsistent, and inconsistent with the authors' interpretation. In both repolarization conditions, the authors claim that repolarization extends only to row 1, and row 1 is statistically different from non-repolarized row 1, but so too is row 3. Row 2 is not. This makes no sense, and suggests either that the statistical tests are inappropriate and/or the data is too sparse to be meaningful. 

As we’re sure the reviewer appreciates, this was an extremely complex experiment to perform and analyse. We spent a lot of time trying to find the best way to illustrate the results (finally settling on a 2D vector representation of polarity) and how to show the paired statistical comparisons between different groups. Moreover, in the end we were only able to detect generally quite modest (statistically significant) changes in cell polarity under the experimental conditions.

However, we note that failure to see large and consistent changes in polarity is exactly the expected result if it is hard to repolarise from a boundary – and this is of course the conclusion that we draw. Conversely, if repolarisation were easy, which was our expectation at least under de novo conditions without existing polarity, then we would have expected large and highly statistically significant changes in polarity across multiple cell rows. Hence we stand by our conclusion that ‘it is hard to repolarise from a boundary of Fz overexpression in both control and de novo polarity conditions’.

Overall, we were trying to establish three points:

(1) to demonstrate that repolarisation occurs from a boundary of overexpression i.e. from boundary 0 to row 0

(2) to establish whether a wave of repolarisation occurs across rows 1, 2 and 3

(3) to determine if in repolarisation in de novo condition it is easier to repolarise than in repolarisation in the control (already polarised) condition Taking each in turn:

(1) To detect repolarisation from a boundary relative to the control condition, we have to compare row 0 in repolarisation condition (Fig.5G,K) vs control condition (Fig.5F,J). This comparison shows a significative repolarisation (p=0.0014). From now, row 0 in repolarisation condition is our reference for repolarisation occurring.

(2) To determine if there is a wave of repolarisation in the repolarisation condition we have to compare row 0 vs row 1 to 3 in the repolarisation condition (Fig.5K). Row 1 is not significantly different to row 0, but rows 2 and 3 are different and the vectors show obviously lower polarity than row 0. Hence no wave of repolarisation is detected over rows 1 to 3.

(3) To determine if it is easier to repolarise in the de novo condition, our reference for establishment of a repolarisation pattern is the polarisation condition in rows 0 to 3. So, we compare repolarisation condition vs repolarisation in de novo condition, row 0 vs row 0, row 1 vs row 1, row 2 vs row 2 and row 3 vs row 3 – in each case no significative difference in polarity is detected, supporting our conclusion that it is not easier to repolarise in the de novo condition.

We agree that the variations in row 3 are puzzling, but there is no evidence that this is due to propagation of polarity from row 0, and so in terms of our three questions, it does not alter our conclusions.

Changes to manuscript: We have extensively revised the text describing the results in Fig.5 to hopefully make the reasons for our conclusions clearer and also be more cautious in our conclusions in Results section ‘Induced core protein relocalisation…’. 

For the related boundary intensity data in Fig 6, the authors need to describe exactly how boundaries were chosen or excluded from the analysis. Ideally, all boundaries would be classified as either meido-lateral (meaning anterior-posterior) or proximal-distal depending on angle. 

We thank the reviewer for pointing out that this was not clear.

All boundaries were classified following their orientation compared to the Fz over-expression boundary using hh-GAL4 expressed in the wing posterior compartment. Horizontal junctions were defined as parallel to the Fz over-expression boundary (between 0 and 45 degrees) and mediolateral junctions as junctions linking two horizontal boundaries (between 45 and 90 degrees).

Changes to manuscript: The boundary classification detailed above has been added in the Materials and Methods.

If the authors believe their Fig 5 and 6 analyses, how do they explain that hairs are reoriented well beyond where the core proteins are not? This would be a dramatic finding, because as far as I know, when core proteins are polarized, prehair orientation always follows the core protein distribution. Surprisingly, the authors do not so much as comment about this. The authors should age their wings just a bit more to see whether the prehair pattern looks more like the adult hair pattern or like that predicted by their protein orientation results.

Again the reviewer makes an interesting point, and we agree that this is something that we should have more directly addressed in the manuscript.

There are three reasons why we might expect adult trichomes to show a different effect from the measured core protein polarity pattern seen in our experiments:

(i) we are assaying core protein polarity at 28h APF, but trichomes emerge at >32h APF, so there is still time for polarity to propagate a bit further from the boundary. We now have added data showing that by the point of trichome initiation, the wave of polarisation extends 3-4 cell rows (Fig.S5A).

(ii) it has long been known that a strong localisation of core proteins at a cell edge is not required for polarisation of trichome polarity from a boundary. For instance, in Strutt & Strutt 2007 we show clones of cells overexpressing Fz causing propagation through pk[pk-sple] mutant tissue where there is no detectable core protein polarity. We were following up prior observations of Adler et al., 2000 in the wing and Lawrence et al., 2004 in the abdomen.

(iii) there is evidence to suggest that the polarity of adult trichomes is locally coupled, possibly mechanically. This point is hard to prove without live imaging taking in both initial core protein localisation, the site of actin-rich trichome initiation and then the final orientation of the much larger microtubule filled trichome, and we’re not aware that such data exist. However, Wong & Adler 1993 (JCB) showed that over a number of hours trichomes become much larger and move towards the centre of the cell, presumably becoming decoupled from any core protein cue. The images in Guild … & Tilney, 2005 (MBoC)  are also interesting to look at in this regard. Finally, septate junction proteins have been implicated in local alignment of trichomes, independently of the core pathway (Venema … & Auld, 2004 Dev Biol).

Changes to manuscript: Added new data in Fig.S5A showing where trichomes initiate under 6h de novo induction conditions, for comparison to core protein localisation and adult trichome data in Fig.5. Added some text explaining why adult trichome repolarisation might be stronger than the observed effects on core protein localisation in Discussion. 

Minor points:

As the authors know, there is a model in the literature that suggests microtubule trafficking provides a global cue to orient PCP. The authors' repolarization data in Fig 4 make a reasonably convincing case against a role for no role for microtubules in cell-scale signaling, but do not rule out a role as a global cue. The authors should be careful of language such as "...MTs and core proteins being oriented independently of each other" that would appear to possibly also refer to a role as a global cue. 

Thank you for pointing out that this was not clear. We have now modified the text to hopefully address this.

Changes to manuscript: Text updated in Results section ‘Microtubules do not provide…’.

Significance:

There are two negative conclusions and one positive conclusion made by the authors. Provided the above points are addressed, the negative conclusions, that core proteins are not limiting and that microtubules are not involved in cell-scale signaling are solid. The positive conclusion is more nebulous - the authors say that cell-scale signaling is strong relative to cell-cell signaling - but how strong is strong? Strong relative to their prior expectations? I'm not sure how to interpret such a conclusion. Overall, we learn something from these results, though it fails to reveal anything about mechanism. These results will be of some interest to those studying PCP.

The reviewer raises an interesting point, which is how do you compare the strength of two different processes, even if both processes affect the same outcome (in this case cell polarity). Repolarisation from a boundary has not been carefully studied at the level of core protein localisation in any previous study to our knowledge – this is one of the important novel aspects of this study. Hence there is not a baseline for defining strong repolarisation. Similarly, there has been no investigation of the nature of ‘cell-scale signalling’. This was a considerable challenge for us in writing the manuscript, and we have done our best to find appropriate language that hopefully conveys our message adequately. Minimally our work may provide a baseline for helping to define the ‘strengths’ of these processes in future studies.

One of our main points is that we can generate an artificial boundary of Fz expression, where Fz levels are at least several fold higher than in the neighbouring cell (e.g. compare Fig.4N’ and O’) and only two rows of cells show a significant change in polarity relative to controls. Even when the tissue next to the overexpression domain is still in the process of generating polarity (de novo condition) then the boundary has little effect on polarity in neighbouring cell rows. This was a result that surprised us, and we tried to convey that by using language to suggest cell-scale signalling was stronger than cell-cell signalling i.e. stronger in terms of the ability to define the final direction of polarity.

Changes to manuscript: In the revised manuscript we have reviewed our use of language and now avoid saying ‘strong’ but instead use terms such as ‘effective’ and ‘robust’ in e.g. Results section ‘Induced core protein relocalisation…’, the Discussion and we have also changed the title of the manuscript to avoid claiming a ‘strong’ signal.

Reviewer #2:

[…] Critique

The experiments described in this paper are of high quality with a sophisticated level of design and analysis. However, there needs to be some recalibration of the extent of the conclusions that can be drawn (see below). Moreover, a limitation of this paper is that, despite the quality of their data, they cannot give a molecular hint about the nature of their proposed cell-scale signal. Below are a two key points that the authors may want to clarify.

(1) The first set of repolarisation experiment is performed after the global cell rearrangements that have been shown to act as global signal. However, this approach does not exclude the possible contribution of an unknown diffusible global signal.

A similar point was raised by Reviewer 1. For the convenience of this reviewer, we’ll summarise the arguments against such an unknown cue again below. More broadly, both reviewers asking a similar question indicates that we have failed to lay out the evidence in sufficient detail. In our defence, we have used the same ‘de novo’ paradigm in three previous publications (Strutt and Strutt 2002, 2007; Brittle et al 2022) without attracting (overt) controversy. We have now added text to the Introduction and Results that goes into more detail, as well as more experimental evidence (Fig.S5).

Firstly, it is worth noting that the global cues acting in the wing are poorly understood, with mostly negative evidence against particular cues accruing in recent years. This makes it a hard subject to succinctly discuss. Secondly, we accept that it is hard to prove there is no influence of global cues, when the nature of those cues and the time at which they act remain unclear. Below we summarise the reasons why we believe there are not significance effects of global cues in our experiments that would influence the interpretation of our results.

First, our reading of the literature supports a broad consensus that an early radial core planar polarity pattern is realigned by cell flow produced by hinge contraction beginning at around 16h APF (e.g. Aigouy et al., 2010; Strutt and Strutt, 2015; Aw and Devenport, 2017; Butler and Wallingford, 2017; Tan and Strutt, 2025). Taken at face value, this suggests that there are ‘radial’ cues present prior to hinge contraction, maybe coming from the wing margin – arguably these radial cues could be Ft-Ds or Wnts or both, given they are expressed in patterns consistent with such a role (notwithstanding the published evidence arguing against roles for either of these cues). It then appears that hinge contraction supercedes these cues to convert a radial pattern to a proximodistal pattern – whether the radial cues that affect the core pathway earlier remain active after hinge contraction is unclear, although both Ft-Ds and Wnts appear to maintain their ‘radial’ patterns beyond the beginning of hinge contraction (e.g. Merkel et al., 2014; Ewen-Campen et al.,2020; Yu et al., 2020).

We think that the reviewers are proposing the presence of a proximodistal cue that is active in the proximal region of the wing that we use for our experiments shown e.g. in Fig.5, and that this cue orients core polarity here (but not elsewhere in the wing) in a time window after 18h APF. Ft-Ds and Wnts do not seem to be plausible candidates as they are still in ‘radial’ patterns. This leaves either an unknown proximodistal cue (a gradient of some unknown signalling molecule?), or possibly some ability of hinge contraction to align proximodistal polarity specifically in this wing region but not elsewhere. We cannot definitively rule out either of these possibilities, but neither do we think there is sufficient evidence to justify invoking their existence to explain our observations.

In particular, the reason that we don’t think there is a proximodistal cue in the proximal part of the wing after 18h APF, is that work from our lab shows that induction of Fz or Stbm expression at times around or after the start of hinge contraction (i.e. >16 h APF) results in increasing levels of trichome swirling with polarity not being coordinated with the tissue axis either proximally or distally (Strutt and Strutt, 2002; Strutt and Strutt 2007). Our simplest interpretation of this is that induction at these stages fails to result in the early radial pattern of core pathway polarity being established and hence a failure of hinge contraction to reorient radial to proximodistal. If hinge contraction alone could specify proximodistal polarity in the absence of the earlier radial polarity, then we would not expect to see swirling over much of the proximal wing (where the forces from hinge contraction are strongest, Etournay et al., 2015).

In this manuscript, our earliest de novo experiments begin at 18h APF (de novo 10h), then at 20h APF (de novo 8h) and at 22h APF (de novo 6h). The image in Fig. 5B referred to by Reviewer 1, is of a wing where Fz is induced de novo at 22 h APF. In these wings, as expected, the core proteins localise asymmetrically in stereotypical swirling patterns throughout the wing surface (see Fig. 2M and also Strutt and Strutt, 2002; Strutt and Strutt 2007), but – usefully for our experiments – they broadly localise along the proximal-distal axis in the region analysed in Fig. 5B. Given the strong swirling in surrounding regions when inducing at >20h APF, we feel reasonably confident in assuming that the pattern is not due to a proximodistal cue present in the proximal wing. We appreciate that the original manuscript did not show images including the trichome pattern in adjacent regions, so this point would not have been clear, but we now include these in Supplementary Fig.S5. We have also added a note in the legend to Fig. 5B to clarify that the proximodistal pattern seen is local to this wing region.

Changes to manuscript: Text extended in Introduction and Results to better explain why we believe the de novo conditions that we use most likely result in a polarity pattern that is not significantly influenced by ‘global cues’. Now show zoomed-out images of the surrounding region around the experiment region proximal to the anterior cross-vein region in adult wings, showing that the polarity pattern does not become more proximodistal when induction time is longer, and also that there is not overall proximodistal polarity in proximal regions of the wing, arguing against an unknown proximodistal polarity cue at these stages of development (Fig.S5B-E’’’).

(2) The putative non-local cell scale signal must be more precisely defined (maybe also given a better name). It is not clear to me that one can separate cell-scale from molecular-scale signal.

Local signals can redistribute within a cell (or membrane) so local signals are also cell-scale. Without a clear definition, it is difficult to interpret the results of the gene dosage experiments. The link between gene dosage and cell-scale signal is not rigorously stated. Related to this, the concluding statement of the introduction is too cryptic.

We thank the reviewer for raising this, as again a similar comment was made by Reviewer 1, so we are clearly falling short in defining the term. We have now had another attempt in the Introduction.

To more specifically answer the point made by the reviewer regarding molecular vs cellular, we are essentially being guided here by the prior computational modelling work, as at the biological level the details are still being worked out. A specific class of previous models only allowed ‘signals’ between core proteins to act ‘locally’, meaning within a cell junction, and within the models there was no explicit mechanism by which proteins on other junctions could ‘detect’ the polarity of a neighbouring junction (e.g. Amonlirdviman et al., 2005; Le Garrec et al., 2006; Fischer et al., 2013). Other models implicitly or explicitly encode a mechanism by which cell junctions can be influenced by the polarity of other junctions (e.g. Meinhardt, 2007; Burak and Shraiman, 2009; Abley et al., 2013; Shadkhoo and Mani, 2019), for instance by diffusion of a factor produced by localisation of particular planar polarity proteins.

We agree with the reviewer that a cell-scale signal will depend on ‘molecules’ and thus could be called ‘molecular-scale’, but here by ‘molecular-scale’ we mean signals that at the range of the sizes of molecules i.e. nanometers, rather than cell-scale signals that act at the size of cells i.e. micrometers. A caveat to our definition is that we implicitly include interactions that occur locally on cell junctions (<1 µm range) within ‘molecular-scale’, but this is a shorter range than ‘cellular-scale’ which requires signals acting over the diameter of a cell (3-5 µm). Nevertheless, we think the concept of ‘molecular-scale’ vs ‘cell-scale’ is a helpful one in this context, and have attempted to address the issue through a more careful definition of the terms.

Changes to manuscript: Text revised in Introduction and legend to Fig.1 to more carefully define ‘cell-scale signalling’ and to distinguish it from ‘molecular-scale signalling’. Final sentence of Introduction also altered so we no longer cryptically speculate on the nature of the cell-scale signal but leave this to the Discussion.

Minor comments. 

Some of the (clever) genetic manipulation may need more details in the text. For example:

- Need to specify if the hs-flp approach induces expression throughout the tissue.

We apologise for the lack of clarity. In all the experiments, the hs-FLP transgene is present in all cells, and heat-shock results in ubiquitous expression. 

Changes to manuscript: We have clarified this in the Results and Materials and Methods.

- Need to specify in the text that in the unpolarised condition the tissue is both dsh and fz mutant.

The reviewer is of course correct and we have updated this point in the text. The full genotype for the unpolarised condition is: w dsh¹ hsFLP22/y;; Act>>fz-mKate2sfGFP, fz^P21/fz^P21 (see Table S1). So this line is mutant for dsh and fz with induced expression of Fz-mKate2sfGFP. 

Changes to manuscript: We have clarified this in the relevant part of the Results.

- Need to specify in the text that the experiment illustrated in Fig 5 is with hh-gal4. 

As noted by the reviewer, we continued to use the same hh-GAL4 repolarisation paradigm as in Fig.4 and this info was in the legend to Fig.5 legend. However, we agree it is helpful to be explicit about this in the main text.

Changes to manuscript: We have added this to this section of the Results.

- Need to address a possible shortcoming of the hh experiment, that the AP boundary is a region of high tension.

It is true that the AP boundary is under high tension in the wing disc (e.g. Landsberg et al., 2009). But we are not aware of any evidence that this higher tension persists into the pupal wing. In separate studies we have labelled for Myosin II in pupal wings (Trinidad et al 2025 Curr Biol; Tan & Strutt 2025 Nature Comms), and as far as we have noticed have not seen preferentially higher levels on the AP boundary. We think if tension were higher, the cell boundaries would appear straighter than in surrounding cells (as seen in the wing disc) and this is not evident in our images.

- Need to dispel the possibility that there is no residual polarisation (e.g. of other components) in fz1 mutant (I assume this is the case).

We use the null allele fz[P21] through this work, and we and others have consistently reported a complete loss of polarisation of other core proteins or downstream components in this background. The caveat to this is that core proteins that persist at cell junctions always appear at least slightly punctate in mutant backgrounds for other core proteins, and so any automated detection algorithm will always find evidence of individual cell polarity above a baseline level of uniform distribution. Hence we tend to use lack of local coordination of polarity (variance of cell polarity angle) as an additional measure of loss of polarisation, in addition to direct measures of average cell polarity. (We discuss this in the QuantifyPolarity manuscript Tan et al 2021 e.g. Fig.S6).

Changes to manuscript: We now include in the Materials and Methods section ‘Fly genetics…’ a much more extensive explanation of the evidence for specific mutant alleles being ‘null’ for planar polarity function (including dsh1 as raised by Reviewer 1), specifically that they result in no detectable planar polarisation of either other core proteins or downstream effectors, and added appropriate references.

- Need to provide evidence that 50% gene dosage commensurately affect protein level. 

This is a good suggestion. In the case of Stbm, we have already published a western blot showing that a reduction in gene dosage results in reduced protein levels (Strutt et al 2016, Fig.S6). We have now performed western blots to quantify protein levels upon reduction of fmi, pk and dgo levels (we actually used EGFP-dgo for the latter, as we don’t have antibodies that can detect endogenous Dgo on western blots).

Changes to manuscript: When presenting the dosage reduction experiments, we now refer back to Strutt et al., 2016 explicitly for Stbm, and have added western blot data for Fmi, Pk and EGFPDgo in new Fig.S2.

- I am surprised that the relationship with microtubule polarity was never investigated. Is this true? 

We agree this is a point that needed further clarification, as Reviewer 1 made a related point regarding the two possible roles for microtubules, one being as a mediator of a global cue upstream of the core pathway, and the second (which we investigate in this manuscript) as a mediator of a cell-scale signal downstream of the core pathway.

Both the Uemura and Axelrod groups have published on potential upstream function as a global cue mediator in the Drosophila wing (e.g. Shimada et al., 2006; Harumoto et al., 2010; Matis et al., 2014).

Both groups have also looked out whether core pathway components could affect orientation of microtubules (Harumoto et al., 2010; Olofsson at al., 2014; Sharp and Axelrod 2016). Notably Harumoto et al., 2010 observed that in 24h APF wings, loss of Fz or Stbm did not alter microtubule polarity from a proximodistal orientation consistent with the microtubules aligning along the long cell axis in the absence of other cues. However, this did not rule out an instructive effect of Fz or Stbm on microtubule polarity during core pathway cell-scale signalling. The Axelrod lab manuscripts saw interesting effects of Pk protein isoforms on microtubule polarity, albeit not throughout the entire wing, which hinted at a potential role in cell-scale signalling. Taken together this prior work was the motivation for our directed experiments to specifically test whether the core pathway might generate cell-scale polarity by instructing microtubule polarity.

Changes to manuscript: We have revised the Results section ‘Microtubules do not…’ to make a clearer distinction regarding possible ‘upstream’ and ‘downstream’ roles of microtubules in Drosophila core pathway planar polarity and the motivation for our experiments investigating the latter.

- The authors suggest that polarity does not propagate as a wave. And yet the range measured in adult is longer than in the pupal wing. Explain. 

Again an excellent point, also made by Reviewer 1, which we have now addressed explicitly in the manuscript. For the convenience of this reviewer, we lay out the reasons why we think the propagation of polarity seen in the adult is further than seen for core protein localisation.

There are three reasons why we might expect adult trichomes to show a different effect from the measured core protein polarity pattern seen in our experiments:

(i) we are assaying core protein polarity at 28h APF, but trichomes emerge at >32h APF, so there is still time for polarity to propagate a bit further from the boundary. We now have added data showing that by the point of trichome initiation, the wave of polarisation extends 3-4 cell rows (Fig.S5A).  

(ii) it has long been known that a strong localisation of core proteins at a cell edge is not required for polarisation of trichome polarity from a boundary. For instance, in Strutt & Strutt 2007 we show clones of cells overexpressing Fz causing propagation through pk[pk-sple] mutant tissue where there is no detectable core protein polarity. We were following up prior observations of Adler et al 2000 in the wing and Lawrence et al 2004 in the abdomen.

(iii) there is evidence to suggest that the polarity of adult trichomes is locally coupled, possibly mechanically. This point is hard to prove without live imaging taking in both initial core protein localisation, the site of actin-rich trichome initiation and then the final orientation of the much larger microtubule filled trichome, and we’re not aware that such data exist. However, Wong & Adler 1993 (JCB) showed that over a number of hours trichomes become much larger and move towards the centre of the cell, presumably becoming decoupled from any core protein cue. The images in Guild … & Tilney, 2005 (MBoC)  are also interesting to look at in this regard. Finally, septate junction proteins have been implicated in local alignment of trichomes, independently of the core pathway (Venema … & Auld, 2004 Dev Biol).

Changes to manuscript: Added new data in Fig.S5A showing where trichomes initiate under 6h de novo induction conditions, for comparison to core protein localisation and adult trichome data in Fig.5. Added some text explaining why adult trichome repolarisation might be stronger than the observed effects on core protein localisation in Discussion. 

- The discussion states that the cell-intrinsic system remains to be fully characterised, implying that it has been partially characterised. What do we know about it? 

As the reviewer probably realises, we were attempting to side-step a long speculative discussion about the various hints and ideas in the literature by grouping them under the umbrella of ‘remaining to be fully characterised’. We would argue that this current manuscript is the first to attempt to systematically investigate the nature of ‘cell-scale signalling’. The lack of prior work is probably due to two factors (i) pioneering theoretical work showed that a sufficiently strong global signal coupled with ‘local’ (i.e. confined to one cell junction) protein interactions was sufficient to polarise cells without the need to invoke the existence of a cell-scale signal; (ii) there is no easy way to identify cell-scale signals as their loss results in loss of polarity which will also occur if other (i.e. more locally acting) core pathway functions are compromised.

The main investigation of the potential for cell-scale signalling has been another set of theory studies (Burak and Shraiman 2009; Abley et al., 2013; Shadkhoo and Mani 2019) which have considered the possibility of diffusible signals. In our present work we have further considered the possibility of a ‘depletion’ model, based on the pioneering theory work of Hans Meinhardt, and as discussed above the possibility that microtubules could mediate a cell-scale signal.

Changes to manuscript: We have revised the Discussion to hopefully be clearer about the current state of knowledge.

Reviewer #3:

[…] Major comments

The data are clearly presented and the manuscript is well written. The conclusions are well supported by the data. 

(1) The authors use a system to de novo establish PCP, which has the advantage of excluding global cues orienting PCP and thus to focus on the cell-intrinsic mechanisms. At the same time, the system has the limitation that it is unclear to what extent de novo PCP establishment reflects 'normal' cell scale PCP establishment, in particular because the Gal4/UAS expression system that is used to induce Fz expression will likely result in much higher Fz levels compared with the endogenous levels. The authors should briefly discuss this limitation. 

We apologise if this wasn’t clear. We only used GAL4/UAS overexpression when we were generating an artificial boundary of Fz expression with hh-GAL4 to induce repolarisation. The de novo induction system involves Fz::mKate2-sfGFP being expressed directly under an Act5C promoter without use of GAL4/UAS. In response to a comment from Reviewer 1 we have now carried out western blot analysis which shows that Fz::mKate2-sfGFP levels under Act5C are actually lower than endogenous Fz levels. As we achieve normal levels of polarity, similar to what we measure in wild-type conditions when measured using QuantifyPolarity, we assume that therefore Fz levels are not limiting under these conditions. However, we note that lower than normal levels of Fz might sensitise the system to perturbation, which in fact would be advantageous in our study, as it might for instance have been expected to more readily reveal dosage sensitivity of other components.

Changes to manuscript: We now describe the levels of expression achieved using the de novo induction system (Fig.S1C-D) and discuss possible consequences in the relevant Results sections and Discussion.

(2) Fig. 3. The authors use heterozygous mutant backgrounds to test the robustness of de novo PCP establishment towards (partial) depletion in core PCP proteins. The authors conclude that de novo polarization is 'extremely robust to variation in protein level'. Since the authors (presumably) lowered protein levels by 50%, this conclusion appears to be somewhat overstated. The authors should tune down their conclusion. 

Reviewer 1 makes a similar point about whether we can argue that the lack of sensitivity to a 50% reduction in protein levels actually rules out the depletion model. To address the comments of both reviewers we had now added some further narrative and caveats in the text.

We nevertheless believe that the experiments shown effectively make the point that there is no strong dosage sensitivity – and it remains our contention that if protein levels were the key to setting up cell-scale polarity, then a 50% reduction would be expected to show an effect on the rate of polarisation. We further note that as Fz::mKate2-sfGFP levels are lower than endogenous Fz levels, the system might be expected to be sensitised to further dosage reductions, and despite this we fail to see an effect on rate of polarisation.

In a similar vein, Reviewer 2 requested data on whether dosage reduction altered protein levels by the expected amount. We have now added further explanation/references and western blot data to address this.

Changes to manuscript: Added some narrative and caveats regarding whether lowering levels more than 50% would add to our findings in the Discussion. Revised conclusions to be more cautious including altering section title to read ‘Planar polarity establishment is not highly sensitive to variation in protein levels of core complex components.

Also added westerns and text/references showing that for the tested proteins there is a reduction in protein levels upon removal of one gene dosage in Results section ‘Planar polarity establishment is…’ and Fig.S2.

Minor comments :

(1) Page 3. The authors mention and reference that they used the PCA method to quantify cell polarity magnification and magnitude. It would help the unfamiliar reader, if the authors would briefly describe the principle of this method. 

Changes to manuscript: More details have been added in Materials & Methods.

Significance:

The manuscript contributes to our understanding of how planar cell polarity is established. It extends previous work by the authors (Strutt and Strutt, 2002,2007) that already showed that induction of core PCP pathway activity by itself is sufficient to induce de novo PCP. This manuscript further explores the underlying mechanisms. The authors test whether de novo PCP establishment depends on an 'inhibitory signal', as previously postulated (Meinhardt, 2007), but do not find evidence. They also test whether core PCP proteins help to orient microtubules (which could enhance cell intrinsic polarization of core PCP proteins), but, again, do not find evidence, corroborating previous work (Harumoto et al, 2010). The most significant finding of this manuscript, perhaps, is the observation that local de novo PCP establishment does not propagate far through the tissue. A limitation of the study is that the mechanisms establishing intrinsic cell scale polarity remain unknown. The work will likely be of interest to specialists in the field of PCP.

Author response:

Reviewer #1 (Public review):

Summary:

The study by Yu et al investigated the role of protein N-glycosylation in regulating T-cell activation and functions is an interesting work. By using genome-wide CRISPR/Cas9 screenings, the authors found that B4GALT1 deficiency could activate expression of PD-1 and enhance functions of CD8+ T cells both in vitro and in vivo, suggesting the important roles of protein N-glycosylation in regulating functions of CD8+ T cells, which indicates that B4GALT1 is a potential target for tumor immunotherapy.

Strengths:

The strengths of this study are the findings of novel function of B4GALT1 deficiency in CD8 T cells.

Weaknesses:

However, authors did not directly demonstrate that B4GALT1 deficiency regulates the interaction between TCR and CD8, as well as functional outcomes of this interaction, such as TCR signaling enhancements.

We are very sorry that we did not highlight our results in Fig. 5f-h enough. In those figures, we demonstrated the interaction between TCR and CD8 increased significantly in B4GALT1 deficient T-cells, by FRET assays. To confirm the important role of TCR-CD8 interaction in mediating the functions of B4GALT1 in regulating T-cell functions, such as in vitro killing of target cells, we artificially tethered TCR and CD8 by a CD8β-CD3ε fusion protein and tested its functions in both WT and B4GALT1 knockout CD8⁺ T-cell. Our results demonstrate that such fusion protein could bypass the effect of B4GALT1 knockout in CD8⁺T-cells (Fig. 5g-h). Together with the results that B4GALT1 directly regulates the galactosylation of TCR and CD8, those results strongly support the model that B4GALT1 modulates T-cell functions mainly by galactosylations of TCR and CD8 that interfere their interaction.

Reviewer #2 (Public review):

Summary:

In this study, the authors identify the N-glycosylation factor B4GALT1 as an important regulator of CD8 T-cell function.

Strengths:

(1) The use of complementary ex vivo and in vivo CRISPR screens is commendable and provides a useful dataset for future studies of CD8 T-cell biology.

(2) The authors perform multiple untargeted analyses (RNAseq, glycoproteomics) to hone their model on how B4GALT1 functions in CD8 T-cell activation.

(3) B4GALT1 is shown to be important in both in vitro T-cell killing assays and a mouse model of tumor control, reinforcing the authors' claims.

Weaknesses:

(1) The authors did not verify the efficiency of knockout in their single-gene KO lines.

Thank reviewer for reminding. We verified the efficiency of some gRNAs by FACS and Surveyor assay. We will add those data in supplementary results in revised version later.

(2) As B4GALT1 is a general N-glycosylation factor, the phenotypes the authors observe could formally be attributable to indirect effects on glycosylation of other proteins.

please see response to reviewer #1.

(3) The specific N-glycosylation sites of TCR and CD8 are not identified, and would be helpful for site-specific mutational analysis to further the authors' model.

Thank reviewer for suggestion! Unfortunately, there are multiple-sites of TCR and CD8 involved in N-glycosylation (https://glycosmos.org/glycomeatlas). We worry that mutations of all these sites may not only affect glycosylation of TCR and CD8 but also other essential functions of those proteins.

(4) The study could benefit from further in vivo experiments testing the role of B4GALT1 in other physiological contexts relevant to CD8 T cells, for example, autoimmune disease or infectious disease.

Thank reviewer for this great suggestion to expand the roles of B4GALT1 in autoimmune and infection diseases. However, since in current manuscript we are mainly focusing on tumor immunology, we think we should leave these studies for future works.

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Reply to the reviewers

Response to Reviewer’s Comments

We thank all three reviewers for their thoughtful and detailed comments, which will help us to improve the quality and clarity of our manuscript.

__Reviewer #1 (Evidence, reproducibility and clarity (Required)): __ Summary: In this work, Tripathi et al address the open question of how the Fat/Ds pathway affects organ shape, using the Drosophila wing as a model. The Fat/Ds pathway is a conserved but complex pathway, interacting with Hippo signalling to affect growth and providing planar cell polarity that can influence cellular dynamics during morphogenesis. Here, authors use genetic perturbations combined with quantification of larval, pupal, and adult wing shape and laser ablation to conclude that the Ft/Ds pathway affects wing shape only during larval stages in a way that is at least partially independent of its interaction with Hippo and rather due to an effect on tissue tension and myosin II distribution. Overall the work is clearly written and well presented. I only have a couple major comments on the limitations of the work.

Major comments: 1. Authors conclude from data in Figures 1 and 2 that the Fat/Ds pathway only affects wing shape during larval stages. When looking at the pupal wing shape analysis in Figure 2L, however, it looks there is a difference in wt over time (6h-18h, consistent with literature), but that difference in time goes away in RNAi-ds, indicating that actually there is a role for Ds in changing shape during pupal stages, although the phenotype is clearly less dramatic than that of larval stages. No statistical test was done over time (within the genotype), however, so it's hard to say. I recommend the authors test over time - whether 6h and 18h are different in wild type and in ds mutant. I think this is especially important because there is proximal overgrowth in the Fat/Ds mutants, much of which is contained in the folds during larval stages. That first fold, however, becomes the proximal part of the pupal wing after eversion and contracts during pupal stages to elongate the blade (Aiguoy 2010, Etournay 2015). Also, according to Trinidad Curr Biol 2025, there is a role for Fat/Ds pathway in pupal stages. All of that to say that it seems likely that there would be a phenotype in pupal stages. It's true it doesn't show up in the adult wing in the experiments in Fig 1, but looking at the pupal wing itself is more direct - perhaps the very proximal effect is less prominent later, as there is potential for further development after 18hr before adulthood and the most proximal parts are likely anyway excluded in the analysis.

Response: Our main purpose in examining pupal wing shape was to emphasize that wings lacking ds are visibly abnormal even at early pupal stages. The reviewer makes the point that the change in shape from 6h to 18h APF is greater in control wings than in RNAi-ds wings. We have added quantitation of this to the revised manuscript as suggested. This difference could be interpreted as indicating that Ds-Fat signaling actively contributes to wing shape during pupal morphogenesis. However, given the genetic evidence that Ds-Fat signaling influences wing shape only during larval growth, we favor the interpretation that it reflects consequences of Ds-Fat action during larval stages – eg, overgrowth of the wing, particularly the proximal wing and hinge as occurs in ds and fat mutants, could result in relatively less elongation during the pupal hinge contraction phase. This wouldn’t change our key conclusions, but it is something that we discuss in a revised manuscript.

I think there needs to be a mention and some discussion of the fact that the wing is not really flat. While it starts out very flat at 72h, by 96h and beyond, there is considerable curvature in the pouch that may affect measurements of different axis and cell shape. It is not actually specified in the methods, so I assume the measurements were taken using a 2D projection. Not clear whether the curvature of the pouch was taken into account, either for cell shape measurements presented in Fig 4 or for the wing pouch dimensional analysis shown in Fig 3, 6, and supplements. Do perturbations in Ft/Ds affect this curvature? Are they more or less curved in one or both axes? Such a change could affect the results and conclusions. The extent to which the fat/ds mutants fold properly is another important consideration that is not mentioned. For example, maybe the folds are deeper and contain more material in the ds/fat mutants, and that's why the pouch is a different shape? At the very least, this point about the 3D nature of the wing disc must be raised in discussion of the limitations of the study. For the cell shape analysis, you can do a correction based on the local curvature (calculated from the height map from the projection). For the measurement of A/P, D/V axes of the wing pouch, best would be to measure the geodesic distance in 3D, but this is not reasonable to suggest at this point. One can still try to estimate the pouch height/curvature, however, both in wild type and in fat/ds mutants.

Response: The wing pouch measurements were done on 2D projections of wing discs that were already slightly flattened by coverslips, so there is not much curvature outside of the folds. We will revise the methods to make sure this is clear. While we recognize that the absolute values measured can be affected by this, our conclusions are based on the qualitative differences in proportions between genotypes and time points, and we wouldn’t expect these to differ significantly even if 3D distances were measured. Obtaining accurate 3D measures is technically more challenging - it requires having spacers matching the thickness of the wing disc, which varies at different time points and genotypes, and then measuring distances across curved surfaces. What we propose to address this is to do a limited set of 3D measures on wild-type and dsmutant wing discs at early and late stages and which we expect will confirm our expectation that the conclusions of our analysis are unaffected, while at the same time providing an indication of how much curvature affects the values obtained. We will also make sure the issue of wing disc curvature and folds is discussed in the text.

Minor comments: 1. The analysis of the laser ablation is not really standard - usually one looks at recoil velocity or a more complicated analysis of the equilibrium shape using a model (e.g Shivakumar and Lenne 2016, Piscitello-Gomez 2023, Dye et al 2021). One may be able to extract more information from these experiments - nevertheless, I doubt the conclusions would change, given that that there seems to be a pretty clear difference between wt and ds (OPTIONAL).

Response: We will add measurements of recoil velocities to complement our current analysis of circular cuts.

Figure 7G: I think you also need a statistical test between RNAi-ds and UAS-rokCA+RNAi-ds.

Response: We include this statistical test in the revised manuscript (it shows that they are significantly different).

In the discussion, there is a statement: "However, as mutation or knock down of core PCP components, including pk or sple, does not affect wing shape... 59." Reference 59 is quite old and as far as I can tell shows neither images nor quantifications of the wing shape phenotype (not sure it uses "knockdown" either - unless you mean hypomorph?). A more recent publication Piscitello-Gomez et al Elife 2023 shows a very subtle but significant wing shape phenotype in core PCP mutants. It doesn't change your logic, but I would change the statement to be more accurate by saying "mutation of core PCP components has only subtle changes in adult wing shape"

Response: Thank-you for pointing this out, we have revised the manuscript accordingly.

**Referee cross-commenting**

Reviewer2: Reviewer 2 makes the statement: "The distance along the AP boundary from the pouch border to DV midline is topologically comparable to the PD length of the adult wing. The distance along the DV boundary from A border to P border is topologically comparable to the AP length of the adult wing."

I disagree - the DV boundary wraps around the entire margin of the adult wing (as correctly drawn with the pink line in Fig 2A). It is not the same as the wide axis of the adult wing (perpendicular to the AP boundary). It is not trivial to map the proximal-distal axis of the larval wing to the proximal-distal axis of the adult, due to the changes in shape that occur during eversion. Thus, I find it much easier to look at the exact measurement that the authors make, and it is much more standard in the field, rather than what the reviewer suggests. Alternatively, one could I guess measure in the adult the ratio of the DV margin length (almost the circumference of the blade?) to the AP boundary length. That may be a more direct comparison. Actually the authors leave out the term "boundary" - what they call AP is actually the AP boundary, not the AP axis, and likewise for the DV - what they measure is DV boundary, but I only noticed that in the second read-through now. Just another note, these measurements of the pouch really only correspond to the very distal part of the wing blade, as so much of the proximal blade comes from the folds in the wing disc. Therefore, a measurement of only distal wing shape would be more comparable.

Response: We thank Reviewer 1 for their comments here. In terms of the region measured, we measure to the inner Wg ring in the disc, the location of this ring in the adult is actually more proximal than described above (eg see Fig 1B of Liu, X., Grammont, M. & Irvine, K. D. Roles for scalloped and vestigial in regulating cell affinity and interactions between the wing blade and the wing hinge. Developmental Biology 228, 287–303 (2000)), and this defines roughly the region we have measured in adult wings (with the caveat noted above that the measurements in the disc can be affected by curvature and the hinge/pouch fold, which we will address).

Reviewer 2 states that authors cannot definitively conclude anything about mechanical tension from their reported cutting data because the authors have not looked at initial recoil velocity. I strongly disagree. __The wing disc tissue is elastic on much longer timescales than what's considered after laser ablation (even hours), and the shape of the tissue after it equilibrates from a circular cut (1-2min) can indeed be used to infer tissue stresses (see Dye et al Elife 2021, Piscitello-Gomez et al eLife 2023, Tahaei et al arXiv 2024).__ In the wing disc, the direction of stresses inferred from initial recoil velocity are correlated with the direction of stresses inferred from analysing the equilibrium shape after a circular cut. Rearrangements, a primary mechanism of fluidization in epithelia, does not occur within 1'. Analysing the equilibrium shape after circular ablation may be more accurate for assessing tissue stresses than initial recoil velocity - in Piscitello-Gomez et al 2023, the authors found that a prickle mutation (PCP pathway) affected initial recoil velocity but not tissue stresses in the pupal wing. Such equilibrium circular cuts have also been used to analyze stresses in the avian embryo, where it correlates with directions of stress gathered from force inference methods (Kong et al Scientific Reports 2019). The Tribolium example noted by the reviewer is on the timescale of tens to hundreds of minutes - much longer than the timescale of laser ablation retraction. It is true the analysis of the ablation presented in this paper is not at the same level as those other cited papers and could be improved. But I don't think the analysis would be improved by additional experiments doing timelapse of initial retraction velocity.

Response: Thank-you, we agree with Reviewer 1 here.

Reviewer 2 states "If cell anistropy is caused by polarized myosin activity, that activity is typically polarized along the short edges not long edges" Not true in this case. Myosin II accumulates along long boundaries (Legoff and Lecuit 2013). "Therefore, interpreting what causes the cell anistropy and how DS regulates it is difficult," Agreed - but this is well beyond the scope of this manuscript. The authors clearly show that there is a change of cell shape, at least in these two regions. Better would be to quantify it throughout the pouch and across multiple discs. Similar point for myosin quantifications - yes, polarity would be interesting and possible to look at in these data, and it would be better to do so on multiple discs, but the lack of overall myosin on the junctions shown here is not nothing. Interpreting what Ft/Ds does to influence tension and myosin and eventually tissue shape is a big question that's not answered here. I think the authors do not claim to fully understand this though, and maybe further toning down the language of the conclusions could help.

Response: We agree with Reviewer 1 here and will also add quantitation of myosin across multiple discs and will include higher magnification myosin images and polarity tests.

Reviewer 3: I agree with many of the points raised by Reviewer 3, in particular that relevant for Fig 1. The additional experiments looking at myosin II localization and laser ablation in the other perturbations (Hippo and Rok mutants/RNAi) would certainly strengthen the conclusions.

Response: Reviewer 3 comment on Fig 1 requests Ab stains to assess recovery of expression after downshift, which we will do.

We will add examination of myosin localization in hpo RNAi wing discs, and in the ds/rok combinations. We note that the effects of Rok manipulations on myosin and on recoil velocity have been described previously (eg Rauskolb et al 2014).

Reviewer #1 (Significance (Required)): I think the work provides a clear conceptual advance, arguing that the Ft/Ds pathway can influence mechanical stress independently of its interaction with Hippo and growth. Such a finding, if conserved, could be quite important for those studying morphogenesis and Fat function in this and other organisms. For this point, the genetic approach is a clear strength. Previous work in the Drosophila wing has already shown an adult wing phenotype for Ft/Ds mutations that was attributed to its role in the larval growth phase, as marked clones show aberrant growth in mutants. The novelty of this work is the dissection of the temporal progression of this phenotype and how it relates to Hippo and myosin II activation. It remains unclear exactly how Ft/Ds may affect tissue tension, except that it involves a downregulation of myosin II - the mechanism of that is not addressed here and would involve considerable more work. I think the temporal analysis of the wing pouch shape was quite revealing, providing novel information about how the phenotype evolves in time, in particular that there is already a phenotype quite early in development. As mentioned above, however, the lack of consideration of the wing disc as a 3D object is a potential limitation. While the audience is likely mostly developmental biologists working in basic research, it may also interest those studying the pathway in other contexts, including in vertebrates given its conservation and role in other processes.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __ The manuscript begins with very nice data from a ts sensitive period experiment. Instead of a ts mutation, the authors induced RNAi in a temperature dependent manner. The results are striking and strong. Knockdown of FT or DS during larval stages to late L3 changed shape while knockdown of FT or DS during later pupal stages did not. This indicates they are required during larval, not pupal stages of wing development for this shape effect. They did shift-up or shift-down at "early pupa stage" but precisely what stage that means was not described anywhere in the manuscript. White prepupal? Time? Likewise a shift-down was done at "late L3" but that meaning is also vague. Moreover, I was surprised to see they did not do a shift-up at the late L3 stage, to give completeness to the experiment. Why?

Response: We have added more precise descriptions of the timing, and we will also add the requested late L3 shift-up experiment.

Looking at the "shape" of the larval wing pouch they see a difference in the mutants. The pouch can be approximated as an ellipse, but with differing topology to the adult wing. Here, they muddled the analysis. The adult wing surface is analogous to one hemisphere of the larval wing pouch, ie., either dorsal or ventral compartment. The distance along the AP boundary from the pouch border to DV midline is topologically comparable to the PD length of the adult wing. The distance along the DV boundary from A border to P border is topologically comparable to the AP length of the adult wing. They confusingly call this latter metric the "DV length" and the former metric the "AP length" , and in fact they do not measure the PD length but PD+DP length. Confusing. Please change to make this consistent with earlier analysis of the adult and invert the reported ratio and divide by two.

Then you would find the larval PD/AP ratio is smaller in the FT and DS mutants than wildtype, which resembles the smaller PD/AP ratio seen in the mutant adult wings. Totally consistent and also provides further evidence with the ts experiments that FT and DS exert shape effects in the larval phase of life.

Response: As noted by Reviewer 1 in cross-referencing, some of the statements made by Reviewer 2 here are incorrect, eg “The distance along the DV boundary from A border to P border is topologically comparable to the AP length of the adult wing.” They are correct where they note that the A-P length we measure in the discs is actually equivalent to 2x the adult wing length, since we are measuring along both the dorsal and ventral wing, but this makes no difference to the analysis as the point is to compare shape between time points and genotypes, not to make inferences based on the absolute numbers obtained. The numerical manipulations suggested are entirely feasible but we think they are unnecessary.

The remainder of the manuscript has experimental results that are more problematic, and really the authors do not figure out how the shape effect in larval stages is altered. I outline below the main problems.

1. They compare the FT DS shape phenotypes to those of mutants or knockdowns in Hippo pathway genes (Hippo is known to be downstream of FT and DS). They find these Hippo perturbations do have shape effects trending in same direction as FT and DS effects. Knockdown reduces the PD/AP ratio while overexpressing WARTS increases the PD/AP ratio. The effect magnitudes are not as strong, but then again, they are using hypomorphic alleles and RNAi, which often induces partial or hypomorphic phenotypes. The effect strength is comparable when wing pouches are young but then dissipates over time, while FT and DS effects do not dissipate over time. The complexity of the data do not negate the idea that Hippo signaling is also playing some role and could be downstream of FT and DS in all of this. But the authors really downplay the data to the point of stating "These results imply that Ds-Fat influences wing pouch shape during wing disc growth separately from its effects on Hippo signaling." I think a more expansive perspective is needed given the caveats of the experiments.

Response: Our results emphasize that the effects of Ds-Fat on wing shape cannot be explained solely by effects on Hippo signaling, eg as we stated on page 7 “These observations suggest that Hippo signaling contributes to, but does not fully explain, the influence of ds or fat on adult wing shape.” We also note that impairment of Hippo signaling has similar effects in younger discs, but very different effects in older discs, which clearly indicates that they are having very different effects during disc growth; we will revise the text to make sure our conclusions are clear.

              The reviewer wonders whether some of the differences could be due to the nature of the alleles or gene knockdown. First, the *ex*, *ds*, and *fat* alleles that we use are null alleles (eg see FlyBase), so it is not correct to say that we use only hypomorphic alleles and RNAi. We do use a hypomorphic allele for wts, and RNAi for hpo, for the simple reason that null alleles in these genes are lethal, so adult wings could not be examined. A further issue that is not commented on by the reviewer, but is more relevant here, is that there are multiple inputs into Hippo signaling, so of course even a null allele for ex, ds or fat is not a complete shutdown of Hippo signaling. Nonetheless, one can estimate the relative impairment of Hippo signaling by measuring the increased size of the wings, and from this perspective the knockdown conditions that we use are associated with roughly comparable levels of Hippo pathway impairment, so we stand by our results. We do however, recognize that these issues could be discussed more clearly in the text, and will do so in a revised manuscript.

Puzzlingly, this lack of taking seriously a set of complex results does not transfer to another set of experiments in which they inhibit or activate ROK, the rho kinase. When ROK is perturbed, they also see weak effects on shape when compared to FT or DS perturbation. This weakness is seen in adults, larvae, clones and in epistasis experiments. The epistasis experiment in particular convincingly shows that constitutuve ROK activation is not epistatic to loss of DS; in fact if anything the DS phenotype suppresses the ROK phenotype. These results also show that one cannot simply explain what FT and DS are doing with some single pathway or effector molecule like ROK. It is more complex than that.

What I really think was needed were experiments combining FT and DS knockdown with other mutants or knockdowns in the Hippo and Rho pathways, and even combining Hippo and Rho pathway mutants with FT or DS intact, to see if there are genetic interactions (additive, synergistic, epistatic) that could untangle the phenotypic complexity.

Response: We’re puzzled by these comments. First, we never claimed that what Fat or Ds do could be explained simply by manipulation of Rok (eg, see Discussion). Moreover, examination of wings and wing discs where ds is combined with Rho manipulations is in Fig 7, and Hippo and Rho pathway manipulation combinations are in Fig S5. We don’t think that combining ds or fat mutations with other Hippo pathway mutations would be informative, as it is well established that Ds-Fat are upstream regulators of Hippo signaling.

Laser cutting experiments were done to see if there is anisotropy in tissue tension within the wing pouch. This was to test a favored idea that FT and DS activity generates anisotropy in tissue tension, thereby controlling overall anisotropic shape of the pouch. However there is a fundamental flaw to their laser cutting analysis. Laser cutting is a technique used to measure mechanical tension, with initial recoil velocity directly proportional to the tissue's tension. By cutting a small line and observing how quickly the edges of the cut snap apart, people can quantify the initial recoil velocity and infer the stored mechanical stress in the tissue at the time of ablation. Live imaging with high-speed microscopy is required to capture the immediate response of the tissue to the cut since initial recoil velocity occurs in the first few seconds. A kymograph is created by plotting the movement of the tissue edges over this time scale, perpendicular to the cut. The initial recoil velocity is the slope of the kymograph at time zero, representing how fast the severed edges move apart. A higher recoil velocity indicates higher mechanical tension in the tissue. However, the authors did not measure this initial recoil velocity but instead measured the distance between the severed edges at one time point: 60 seconds after cutting. This is much later than the time point at which the recoil usually begins to dissipate or decay. This decay phase typically lasts a minute or two, during which time the edges continue to separate but at a progressively slower rate. This time-dependent decay of the recoil reveals whether the tissue behaves more like a viscous fluid or an elastic solid. Therefore, the distance metric at 60 seconds is a measurement of both tension and the material properties of the cells. One cannot know then whether a difference in the distance is due to a difference in tension or fluidity of the cells. If the authors made measurements of edge separation at several time points in the first 10 seconds after ablation, they can deconvolute the two. Otherwise their analysis is inconclusive. Anisotropy in recoil could be caused by greater tissue fluidity along one axis. Observing a gradient of cell fluidity in a tissue along one axis of a tissue has been observed in the amnioserosa of Tribolium for example. (Related and important point - was the anisotropy of recoil oriented along the PD or AP axis or not oriented to either axis, this key point was never stated)..

The authors cannot definitiviely conclude anything about mechanical tension from their reported cutting data.

Response: As noted by Reviewer 1 in cross-commenting, there is no fluidity on a time scale of 1 minute in the wing disc, and circular ablations are an established methods to investigate tissue stress. We choose the circular ablation method in part because it interrogates stress over a larger area, whereas cutting individual junctions is subject to more variability, particularly as the orientation of the junction (eg radial vs tangential) impacts the tension detected in the wing disc. Nonetheless, we will add recoil measurements to the revised manuscript to complement our circular ablations, which we expect will provide independent confirmation of our results and address the Reviewer’s concern here.

They measured the eccentricity of wing pouch cells near the pouch border, and found they were highly anisotropic compared to DS mutant cells at comparable locations. Cells were elongated but again what if either axis (PD or AP) they were elongated along was never stated. If cell anistropy is caused by polarized myosin activity, that activity is typically polarized along the short edges not long edges. Thus, recoil velocity after laaser cutting would be stonger along the axis aligned with short cell edges. It looks like the cutting anisotropy they see is greater along the axis aligned with long cell edges. Of course, if the cell anisotropy is caused by a pulling force exerted by the pouch boundary, then it would stretch the cells. This would in fact fit their cutting data. But then again, the observed cell anisotropy could also be caused by variation in the fluid-solid properties of the wing cells as discussed earlier. Compression of the cells then would deform them anisotropically and produce the anisotropic shapes that were observed, Therefore, interpreting what causes the cell anistropy and how DS regulates it is difficult,

Response: As noted by Reviewer 1 in cross-commenting, it is well established that tension and myosin are higher along long edges in the proximal wing. However, we acknowledge that we could do a better job of making the location and orientation of the regions shown in these experiments clear and, we will address this in a revised manuscript.

The imaging and analysis of the myosin RLC by GFP tagging is also flawed. SQH-GFP is a tried and true proxy for myosin activity in Drosophila. Although the authors image the wing pouch of wildtype and DS mutants. they did so under low magnification to image the entire pouch. This gives a "low-res" perspective of overall myosin but what they needed to do was image at high magnification in that proximal region of the pouch and see if Sqh-GFP is polarized in wildtype cells along certain cell edges aligned with an axis. And if such a polarity is observed, is it present or absent in the DS mutant. From the data shown in Figure 5, I cannot see any significant difference between wildtype and knocked down samples at this low resolution. Any difference, if there is any, is not really interpretable.

Response: We agree that examination of myosin localization at high resolution to see if it is polarized is a worthwhile experiment. We did in fact do this, and myosin (Sqh:GFP) appeared unpolarized in ds mutants. However, the levels of myosin were so low that we didn’t feel confident in our assessment, so we didn’t include it. We now recognize that this was a mistake, and we will include high resolution myosin images and assessments of (lack of) polarity in a revised manuscript to address this comment.

In conclusion, the manuscript has multiple problems that make it imposiible for the authors to make the claims they make in the current manuscript. And even if they calibrated their interpretations to fit the data, there is not much of a simple clear picture as to how FT and DS regulate pouch eccentricity in the larval wing.

Response: We think that the legitimate issues raised are addressable, as described above, while some of the criticisms are incorrect (as noted by Reviewer 1).

Reviewer #2 (Significance (Required)): This manuscript describes experiments studying the role that the protocadherins FAT and DACHSOUS play in determining the two dimensional "shape" of the fruit fly wing. By "shape", the manuscript really means how much the wing's outline, when approximated as an ellipse, deviates from a circle. The elliptical approximations of FT and DS mutant wings more closely resemble a circle compared to the more eccentric wildtype wings. This suggests the molecules contribute to anisotropic growth in some way. A great deal of attention has been paid on how FT and DS regulate overall organ growth and planar cell polarity, and the Irvine lab has made extensive contributions to these questions over the years. Somewhat understudied is how FT and DS regulate wing shape, and this manuscript focuses on that. It follows up on an interesting result that the Irvine lab published in 2019, in which mud mutants randomized spindle pole orientation in wing cells but did not change the eccentricity of wings, ruling out biased cell division orientation as a mechanism for the anisotropic growth.

__Reviewer #3 (Evidence, reproducibility and clarity (Required)): __ Summary The authors investigate the mechanisms underlying epithelial morphogenesis using the Drosophila wing as a model system. Specifically, they analyze the contribution of the conserved Fat/Ds pathway to wing shape regulation. The main claim of the manuscript is that Ds/Fat controls wing shape by regulating tissue mechanical stress through MyoII levels, independently of Hippo signaling and tissue growth.

Major Comments To support their main conclusions, the authors should address the following major points and consider additional experiments where indicated. Most of the suggested experiments are feasible within a reasonable timeframe, while a few are more technically demanding but would substantially strengthen the manuscript's central claims.

Figure 1: The authors use temperature-sensitive inactivation of Fat or Ds to determine the developmental window during which these proteins regulate wing shape. To support this claim, it is essential to demonstrate that upon downshift during early pupal stages, Ds or Fat protein levels are restored to normal. For consistency, please include statistical analyses in Figure 1P and ensure that all y-axis values in shape quantifications start at 1.

Response: We will do the requested antibody stains for Fat (Ds antibody is unfortunately no longer available, but the point made by the reviewer can be addressed by Fat as the approach and results are the same for both genes). We have also added the requested statistical analysis to Fig 1P, and adjusted the scales as requested.

Figure 2: The authors propose that wing shape is regulated by Fat/Ds during larval development. However, Figure 2L suggests that wing elongation occurs in control conditions between 6 and 12 h APF, while this elongation is not observed upon Ds RNAi. The authors should therefore perform downshift experiments while monitoring wing shape during the pupal stage to substantiate their main claim. In addition, equivalent data for Fat loss of function should be included to support the assertion that Fat and Ds act similarly.

Response: As noted in our response to point 1 of Reviewer 1, we agree that there does seem to be relatively more elongation in control wings than in ds RNAi wings, but we think this likely reflects effects of ds on growth during larval stages, and we will revise the manuscript to comment on this.

We will also add the suggested examination of fat RNAi pupal wings.

The suggested examination of pupal wing shape in downshift experiments is unfortunately not feasible. Our temperature shift experiments expressing ds or fat RNAi are done using the UAS-Gal4-Gal80tssystem. We also use the UAS-Gal4 system to mark the pupal wing. If we do a downshift experiment, then expression of the fluorescent marker will be shut down in parallel with the shut down of ds or fat RNAi, so the pupal wings would no longer be visible.

Figure 3: The authors state that "These observations indicate that Ds-Fat signaling influences wing shape during the initial formation of the wing pouch, in addition to its effects during wing growth." This conclusion is not fully supported, as the authors only examine wing shape at 72 h AEL. At this stage, fat or ds mutant wings already display altered morphology. The authors could only make this claim if earlier time points were fully analyzed. In fact, the current data rather suggest that Ds function is required before 72 h AEL, as a rescue of wing shape is observed between 72 and 120 h AEL.

Response: First, I think we are largely in agreement with the Reviewer, as the basis for our saying that DS-Fat are likely required during initial formation of the wing pouch is that our data show they must be required before 72 h AEL. Second, 72 h is the earliest that we can look using Wg expression as a marker, as at earlier stages it is in a ventral wedge rather than a ring around the future wing pouch + DV line (eg see Fig 8 of Tripathi, B. K. & Irvine, K. D. The wing imaginal disc. Genetics (2022) doi:10.1093/genetics/iyac020.). We can revise the text to make sure this is clear.

Figure 4: The authors state that "The influence of Ds-Fat on wing shape is not explained by Hippo signaling." However, this conclusion is not supported by their data, which show that partial loss of ex or hippo causes clear defects in wing shape. In addition, the initial wing shape is affected in wts and ex mutants, and hypomorphic alleles were used for these experiments. Therefore, the main conclusion requires revision. It would be useful to include a complete dataset for hippo RNAi, ex, and wts conditions in Figure S1. The purpose and interpretation of the InR^CA experiments are also unclear. While InR^CA expression can increase tissue growth, Hippo signaling has functions beyond growth control. Whether Hippo regulates tissue shape through InR^CA-dependent mechanisms remains to be clarified.

Response: As noted in our response to point 1 of Reviewer 2 - our results emphasize that the effects of Ds-Fat on wing shape cannot be explained solely by effects on Hippo signaling, eg as we stated on page 7 “These observations suggest that Hippo signaling contributes to, but does not fully explain, the influence of ds or fat on adult wing shape.” We also note that impairment of Hippo signaling has similar effects in younger discs, but very different effects in older discs, which clearly indicates that they are having very different effects during disc growth. We will make some revisions to the text to make sure that our conclusions are clear throughout.

While we used a hypomorphic allele for wts, because null alleles are lethal, the ex allele that we used is described in Flybase as an amorph, not a hypomorph, and as noted in our response to Reviewer 2, we will add some discussion about relative strength of effects on Hippo signaling.

In Fig S1, we currently show adult wings for ex[e1] and RNAi-Hpo, and wing discs for wts[P2]/wts[x1], and for ex[e1]. The wts combination does not survive to adult so we can’t include this. We will however, add hpo RNAi wing discs as requested.

              The purpose of including InR^CA experiments is to try to separate effects of Hippo signaling from effects of growth, because InR signaling manipulation provides a distinct mechanism for increasing growth. We will revise the text to try to make sure this is clearer.

Figure 5: This figure presents images of MyoII distribution, but no quantification across multiple samples is provided. Moreover, the relationship between changes in tissue stress and MyoII levels remains unclear. Performing laser ablation and MyoII quantification on the same samples would provide stronger support for the proposed conclusions.

Response: We will revise the quantitation so that it presents analysis of averages across multiple discs, rather than representative examples of single discs.

Both the myosin imaging, and the laser ablation were done on the same genotypes (wildtype and ds) at the same ages (108 h AEL) so we think it is valid to directly compare them. Moreover, the imaging conditions for laser ablation and myo quantification are different, so it’s not feasible to do them at the same time (For ablations we do a single Z plane and a single channel (has to include Ecad, or an equivalent junctional marker) on live discs, so that fast imaging can be done. For Myo imaging we do multiple Z stacks and multiple channels (eg Ecad and Myo), which is not compatible with the fast imaging needed for analysis of laser ablations).

Figure 6: It is unclear when Rok RNAi and Rok^CA misexpression were induced. To substantiate their claims, the authors should measure both MyoII levels and mechanical tension under the different experimental conditions in which wing shape was modified through Rok modulation (i.e. the condition shown in Fig. 7G). For comparison, fat and ds data should be added to Fig 6H. Overall, the effects of Rok modulation appear milder than those of Fat manipulation. Given that Dachs has been shown to regulate tension downstream of Fat/Ds, it would be informative to determine whether tissue tension is altered in dachs mutant wings and to assess the relative contribution of Dachs- versus MyoII-mediated tension to wing shape control. It would also be interesting to test whether Rok activation can rescue dachs loss-of-function phenotypes.

Response: In these Rok experiments there was no separate temporal control of Rok RNAi or Rok^CA expression, they were expressed under nub-Gal4 control throughout development.

We will add examination of myosin in combinations of ds RNAi and rok manipulation as in Fig 7G to a revised manuscript.

Data for fat and ds comparable to that shown in Fig 6H is already presented in Fig 3D, and we don’t think its necessary to reproduce this again in Fig 6H.

We agree that the effects of Rok manipulations are milder than those of Fat manipulations; as we try to discuss, this could be because the pattern or polarity of myosin is also important, not just the absolute level, and we will add assessment of myosin polarity.

The suggestion to also look at dachs mutants is reasonable, and we will add this. In addition, we plan to add an "activated" Dachs (a Zyxin-Dachs fusion protein previously described in Pan et al 2013) that we anticipate will provide further evidence that the effects of Ds-Fat are mediated through Dachs. We will also add the suggested experiment combining Rok activation with dachs loss-of-function.

Figure 7: The authors use genetic interactions to support their claim that Fat controls wing shape independently of Hippo signaling. However, these interactions do not formally exclude a role for Hippo. Moreover, previous work has shown that tissue tension regulates Hippo pathway activity, implying that any manipulation of tension could indirectly affect Hippo and growth. To provide more direct evidence, the authors should further analyze MyoII localization and tissue tension under the various experimental conditions tested (as also suggested above).

Response: As discussed above, our data clearly show that Fat has effects independently of Hippo signaling that are crucial for its effects on wing shape, but we did not mean to imply that the regulation of Hippo signaling by Fat makes no contribution to wing shape control, and we will revise the text to make this clearer. We will also add additional analysis of Myosin localization , as described above.

Reviewer #3 (Significance (Required)): How organ growth and shape are controlled remains a fundamental question in developmental biology, with major implications for our understanding of disease mechanisms. The Drosophila wing has long served as a powerful and informative model to study tissue growth and morphogenesis. Work in this system has been instrumental in delineating the conserved molecular and mechanical processes that coordinate epithelial dynamics during development. The molecular regulators investigated by the authors are highly conserved, suggesting that the findings reported here are likely to be of broad biological relevance.

Previous studies have proposed that anisotropic tissue growth regulates wing shape during larval development and that such anisotropy induces mechanical responses that promote MyoII localization (Legoff et al., 2013, PMID: 24046320; Mao et al., 2013, PMID: 24022370). The Ds/Fat system has also been shown to regulate tissue tension through the Dachs myosin, a known modulator of the Hippo/YAP signaling pathway. As correctly emphasized by the authors, the respective contributions of anisotropic growth and mechanical tension to wing shape control remain only partially understood. The current study aims to clarify this issue by analyzing the role of Fat/Ds in controlling MyoII localization and, consequently, wing shape. This represents a potentially valuable contribution. However, the proposed mechanistic link between Fat/Ds and MyoII localization remains insufficiently explored. Moreover, the role of MyoII is not fully discussed in the broader context of Dachs function and its known interactions with MyoII (Mao et al., 2011, PMID: 21245166; Bosveld et al., 2012, PMID: 22499807; Trinidad et al., 2024, PMID: 39708794). Most importantly, the experimental evidence supporting the authors' conclusions would benefit from further strengthening. It should also be noted that disentangling the relative contributions of anisotropic growth and MyoII polarization to tissue shape and size remains challenging, as MyoII levels are known to increase in response to anisotropic growth (Legoff et al., 2013; Mao et al., 2013), and mechanical tension itself can modulate Hippo/YAP signaling (Rauskolb et al., 2014, PMID: 24995985).

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Reply to the reviewers

Overall Response.

We would like to thank the reviewers for their analysis of the manuscript. From their comments it is clear that our manuscript was not. We completely rewrote the manuscript to focus on the central core question which was how does Adam13 regulates gene expression in general and TFap2a in particular leading to the expression of Calpain8 a protein required for CNC migration.

The following model will be the central line of our story. It will address all of the proteins involved and mechanistical evidences that link Adam13 to one of its proven effector target Calpain8.

• *

*Reviewer #1 (Evidence, reproducibility and clarity (Required)): **

In this manuscript, Pandey et al. show that the ADAM13 protein modulates histone modifications in cranical neural crest and that the Arid3a protein binds the Tfap2a promoter in an Adam13-dependent manner and has promoter-specific effects on transcription. Furthermore, they show that the Adam13 and human ADAM9 proteins associated with histone modifiers as well as proteins involved in RNA splicing. Although the manuscript is mostly clearly written and the figures well assembled, it reads like a couple of separate and unfinished stories.*

I believe that our story line was not clear and that the overarching questions was not well stated. We have made every effort to change this in the revised manuscript. I would like to include a figure that explains the story.

In short:

1 We knew that Adam13 could regulate gene expression in CNC via its cytoplasmic domain.

2 We also knew that this required Adam13 interaction with Arid3a and that a direct target with the transcription factor TFAP2a which in turn regulates functional targets that we had identified including the protocadherin PCNS and the protease Calpain8.

Our goal was to understand the mechanism allowing Adam13 to regulate gene expression.

3 This first part of this manuscript shows how Adam13 modulates Histone modification in vivo in the CNC globally as well as specifically on the Tfap2a promoter. This results I an Open chromatin.

4 Using Chip we show that Adam13 and Arid3a both bind to the Tfap2a promoter and that Arid3a binding to the first ATG depends on Adam13.

5 Using Luciferase reporter we show that both Adam13 and Arid3a can induce expression at the first ATG.

*They show using immunocytochemistry and qPCR that ADAM13 knockouts in CNCs afffects histone modifications. Here ChIP-seq or Cut-n-Run experiments would be more appropriate and would result in a more comprehensive understanding of the changes mediated. *

I agree but we did not have the fund and now I have nobody working in the lab to do this experiment. These are also likely to overlap with the RNAseq data that we have and would simply add more open leads. We selected to go after the only direct target that we know which is TFAP2a and focus on this gene to understand the mechanism.

We believe that the Chip PCR experiment are sufficient for this story.

*The immunohistochemistry assays should at least be verified further using western blotting or other more quantiative methods. *

Immunofluorescence and statistical analysis is a valid quantification method. Western blot of CNC explants is not trivial and requires a large amount of material. Given the small overall change we also would not expect to be able to detect the change over the noise of western blot. The Chip PCR confirms our finding in a completely independent manner.

*The authors then show that ADAM13 interacts with a number of histone modifiers such as KDM3B, KDM4B and KMT2A but strangely they do not follow up this interesting observation to map the interactions further (apart from a co-ip with KMT2A), the domains involved, the functional role of the interactions or how they mediate the changes in chromatin modifications. *

We selected KMT2a because it is expressed in the Hek293T cells. KMT2D has been shown to regulate CNC development in Xenopus and is responsible for the Kabuki syndrome in human. We used aphafold to predict interaction and found that Adam13 interact with the Set domain. In addition we see multiple Set- containing domain protein in our mass spec data. The mass spec is done on Human hek293T cells that express a subset of KMT proteins. We now include evidence that Adam13 interact with the KMT2D SET domain (new figure 5D)

The authors then show that ADAM13 affects expression of the TFAP2a gene in a promoter specific manner - affecting expression from S1 but not S2.

It is the S1 but not S3. Adam13 has no effect on S2.

• They further show that ADAM13 affects the binding of the Arid3 transcription fator to the S1-promoter but not to the S3 promoter. However, ADAM13 was present at both promoters. Absence of ADAM13 resulted in increased H3K9me2/3 and decreased H3K4me3 at the S1 promoter whereas only H3K4me3 was changed at the S2 promoter*

S3 not S2*. Unfortunately, they do not show how this is mediated or through which binding elements this takes place. Why is ADAM13 present at both promoters but only affects Arid3 binding at S1? *

We agree this is a very interesting question that could be the subject of an entire publication. Promoter deletion and mutation to identify which site are bound by and modulated by Adam13/Arid3a is not trivial.

*The authors claim that transfecting Arid3a and Adam13 together further increases expression from a reporter (Fig 4E) but this is not true as no statistical comparison is done between the singly transfected and double transfected cells. *

This is correct, there is a small increase that is not significant with both. The fact that both proteins can induce the promoter suggest but does not prove that they can have additive roles. The loss of function experiment shows that the human Arid3a expressed in Hek293T cells is important for Adam13 increases of S1. It is possible that the dose of the endogenous Arid3a is sufficient to get full activity of Adam13.* Then the authors surprisingly start investigating association of proteins with the two isoforms of TFAP2a which in the mind of this reviewer is a different question entirely. *

We agree and have removed this part of the manuscript.

*They find a number of proteins involved in splicing. And the observation that ADAM13 also interacts with splicing factors is really irrelevant in terms of the story that they are trying to tell. Transcription regulation and splicing are different processes and although both affect the final outcome, mRNA, they need to be investigated separately. The link is at least not very clear from the manuscript. Again, the effects on splicing are not further investigated through functional analysis and as presented the data presented is too open-ended and lacking in clarity. *

We agree that beside the different activities of the TFap2a isoform, the rest of the splicing regulation could be a separate study. We were interested to understand how these two isoforms could activate Calpain8 so differently this is why we looked at LC/MS/MS. We have removed this part of the story from the manuscript.*

Additional points: 1. In the abstract they propose that the ADAMs may act as extracellular sensors. This is not substantiated by the results. *

As an extracellular protein translocating into the nucleus it is a possibility that we propose, but I agree this is not investigated in this manuscript. We will modify the text.* 2. Page 5, line 16: what is referred to by 6 samples 897 proteins? Were 6 samples analyzed for each condition? The number of repeats for the mass spec analysis is not clear from the text nor are the statistical parameters used to analyse the data. This is also true for the mass spec presented in the part on TFAP2aL-S1 and Adam13 regulate splicing. Statistics and repeats are not presented. *

In general we provide biological triplicate and use the statistical function of Scaffold to identify proteins that are significantly enriched or absent in each samples.

When we specify 6 samples it means 6 independent proteins samples were analyzed and used for our statistic. We use Scafold T-test with a p value less than 0.05. Peptides were identified with 95% confidence and proteins with 99% confidence.* 3. Page 6, line 19: set domain should be SET domain. *

Yes* 4. The number of repeats in the RNA sequencing of the CNCs is not clear from the text. *

Three biological replicates (Different batch of embryos from different females).* 5. The explanation of Figure C is a bit lacking. There are two forms of TFAP2a, L and S, but only one is presented in the figure. Do both forms have the extra S1-3 exons? Also, at the top of the figure it is not clear that the boxes are part of a continuous DNA sequence. Also, it is not clear which codon is not coding. *

Xenopus laevis are pseudo tetraploid giving in most cases L and S genes in addition to the 2 alleles from being diploid. The TFAP2a gene structure is conserved between both aloalleles and is similar to the human gene. For promoter analysis and Chip PCR we chose one of the alloallele (L), given that the RNAseq data showed that both genes and variant behave the same in response to Adam13. This only becomes important in loss of function experiment in which both L and S version need to be knock down or Knock out.

* In the sashimi plot there are green and pink shaded areas. What do they denote? What exactly is lacking in the MO13 mutant - seems that a particular exon is missing suggesting skipping?*

MO13 is a morpholino that bocks the translation of Adam13 (Already characterized with >90% of the protein absent) but does not affect Adam13 mRNA expression.* 7. Page 11, line 9: „with either MbC or MbC and MO13" needs to be rephrased. *

Will do *8. Page 11, line 19: „the c-terminus of....and S3) and" should be „the C-terminus of...and S3 and". ** 9. Page 15, line 10: substrateS 10. Page 16, line 23: the sentence „increases H3K9 to the promoter of the most upstream" needs revision. 11. Page 26, line 12: Here the authors say: „for two samples two-tail unpaired". What does this mean? Statistics should not be performed on fewer than three samples. In legnd to Figure 6 it indicates that T-test was performed on two samples. 12. The discussion should be shortened and simplified. 13. Figure 1 legend. How many images were quantitated for each condition? *

At least 3 images per condition. For 3 independent experiments. (9 images per condition).* 14. Figure 2 has a strange order of panels where G is below B. 15. Figure 6 legend, line 12. „proteins that were significantly enriched in either of the 2 samples" is not very clear. What exactly does this mean?

Reviewer #1 (Significance (Required)):

If the authors follow up on either the transcription-part of the story, or the splicing part of the story, they are likely to have important results to present. However, in the present format the paper is lacking in focus as both issues are mixed together without a clear end-result. *

We have entirely changed the paper according to these comments.

*

• *

*Reviewer #2 (Evidence, reproducibility and clarity (Required)): **

Panday et al seeks to determine the function of ADAM13 in regulating histone modifications, gene expression and splicing during cranial neural crest development. Specifically, the authors tested how Adam13, a metalloprotease, could modify chromatin by interaction with Arid3a and Tfap2a and RNA splicing and gene expression. They then utilize knockouts in Xenopus and HEK293T cells followed by immunofluorescence, IPs, BioID, luciferase assays, Mass spec and RNA assays. Although there is some strong data in the BioID and luciferase experiments, the manuscript tells multiple stories, linking together too many things to make a compelling story. The result is a paper that is very difficult to read and understand the take home message. In addition, some of the conclusions are not supported by the data. This unfortunately means it is not ready for publication. However, I have added below some suggestions that would strengthen the manuscript. My comments are below: *

Clarity is clearly an issue here. The new version is entirely re-written.

Here is the take home message:

We knew that Adam13 could regulate gene expression via its cytoplasmic domain. One of the key targets was identified as Calpain8, a protein critical for CNC migration. We subsequently showed that Adam13 and Arid3a regulated Tfap2a expression which in turn regulated Calpain8.

In this manuscript we investigated 1) how Adam13 regulates TFAP2a and 2) how Tfap2a controls Calpain8 expression.

The take home message is that Adam13 bind to Histone methyl transferase and changes the histone methylation code overall in the CNC and in particular at the TFAP2a promoter. This results in more open chromatin. We further find that Adam13 binds to the Tfap2a promoter in vivo and is important for Arid3a binding to the first start. Tfap2a that include this N-terminus sequence regulates Capn8 expression.*

Major comments: 1. I think it would be better to split out the chromatin modification function from the splicing in two separate papers. While there is a connection, having it all together makes the story difficult to follow. *

Agree but I believe that the S1 vs S3 story of Tfap2a is important for the overall story. The new paper does not emphasize splicing.* 2. The immunofluorescence of H3K9me2/3, in Figure 1, 2, 3 following Adam13 knockdown is not convincing. There seems to be a strong edge effect especially in Figure 2 and 3. *

The statistical analysis shows that the results, while modest, are significant (Three independent experiments using 3 different females and 3 explants for each condition were analyzed). The edge effect observed is eliminated by the mask that we use that normalize the expression to either DAPI or Snai2. The edge effect is seen in both control and KD as well. These are further confirmed by the Chip PCR on one direct target.

Similarly the Arid3a expression in Supp Figure 1 if anything seems increased.

We have previously shown that Arid3a expression is not affected by Adam13 KD (Khedgikar et al). Our point here is simply that the difference in Tfap2a cannot be explained by a decrease in Arid3a expression. It is not a critical figure and was eliminated in the new manuscript.

*It would be better to quantify by western blot and not by fluorescent intensity since it is difficult to determine what a small change in fluorescent intensity means in vivo. *

Not all antibodies used here work by western blot and the quantity of material required for western blot is much larger than IF. Given the small overall changes and the variability observed in Western blot it is not a viable alternative.

IF is a quantitative method that has been used widely to assert increase or decrease of protein level or post translational modification. The fact that the same post translational modification that we see in cranial neural crest explants can also be seen by ChipPCR on the Tfap2a promoter confirm this observation.

*Also, it does not say in the text or the figure legend what these are, Xenopus explants of CNC? *

These are CNC explants. It is now clearly stated in the figure legend.* 3. The rationale for isolating KMT2A from the other chromatin modifiers in the dataset is not clear. *

The new manuscript is clarifying that point. Because we are using Hek293T cells in this assay, which are human embryonic kidney derived instead of Xenopus Cranial neural crest cells, we are not interested in a specific protein but rather a family of protein that can modify histones (KMT and KDM). Our rational is if Adam13 can bind to KMT2 via the SET domain, it is likely to interact with KTM2 that are expressed in the CNC. KMT2A and D are expressed in the CNC. This is why we selected KMT2a here (Hek293T). We now include 1 co-IP with the Set domain of Xenopus KMT2D (new figure 5D)

From the RNA-seq in Supp Figure 2 it is not changed as much as likely some of the others.

The new manuscript addresses this point. We did not show or expect that the loss of Adam13 would affect mRNA expression of Kmt2.

*Also, the arrow seems to indicate that it is right above the cutoff. What about other proteins with ATPase activity? That is the top hit in the Dot plot nuclear function. Would be helpful to write out Adam13 cytoplasm/nucleus here. *

We have used another set of proteomics data that does not include the cytoplasmic/nuclear extract to simplify the results. We hope that the changes make it more obvious.

Given that we are looking at Chromatin remodeling enzyme here we did not chose to investigate further in this report the ATPase. This is such a wide category that it could lead us away from the main story here.* 4. The splicing information, while interesting would be better as a different manuscript. The sashimi plot requires more explanation as written. *

We agree and think that a simple representation of the fold change of the different isoform is more obvious. It is now a minor part of figure 1 and the legend has been improved to describe the method here.

How do you tell if the interactions are changed from this?

I do not understand this question. The sashimi plot indicate the read through from the mRNA that goes from one exon to the next quantifying the specific exon usage. It can therefore be quantified and compared between different conditions.

• The authors argue there is a reduction of Tfap2a in Figure 3H but half the explant is not expressing sox9 in the Adam13 knockdown. How is this kind of experiment controlled when measure areas that don't have any fluorescence because of the nature of the explants? *

We have removed this figure as we had already shown previously by western blot that Tfap2a protein decreased in MO13 embryos. As noted on the histogram, the fluorescence is only measured in Sox9 positive cells in each explant. Three independent experiments with 3 explants for each. We also have seen a decrease by Western blot and mRNA expression (Both RNAseq and realtime PCR). In most of our explants, the vast majority of the cells are positive for Snai2 and Sox9, while those that are negative are positive for Sox3 (data not shown here). There is always less signal in the center of the explant possibly due to the penetration of antibody or interference with the signal by the cells pigment or yolk autofluorescence. Our control explants have the same effect so our quantification is valid.* 5. The use of a germ line Xenopus mutant for Adam13 is great but how were these knockouts validated? *

All of the KO were validated by sequencing, RNAseq and protein expression. These are now included in the supplemental figure 1.

*More information is required here. The Chip-qPCR has a lot of variability between the samples, especially in the H3K9me2/3. *

All ChipPCR were performed on Xenopus embryos. The variability is tested by statistical analysis and is either significant or not.

Because these are in cell lines, this should be more consistent.

They are not in cell lines but in Xenopus embryos.

• In addition, it is difficult to understand what this means for cranial neural crest cells when assaying in HEK293T cells with the luciferase assay. *

We use Luciferase assay in Hek293T cells to test if Xenopus protein can induce a specific reporter (Gain of function). We also use luciferase reporter in Xenopus to test if they can perceive the loss of a specific protein (For example Adam13).

Our result show that Adam13 or Arid3a expression in Hek293T cells can induce the TFAP2S1 reporter. * 6. The migration assay shows only an example of what it looks like to have defective migration. But it would be better to show control embryos, embryos with Adam13 knockdown and what the rescues look like so the reader can make their own conclusion.*

We can certainly include this but have published this assay in multiple publication before. The picture is a single example, the histogram shows that statistical validation.

• The argument from the section above suggests the S1 isoform is the primary one but S3 in this assay also rescues, please explain what this result means since it seems to suggest that even though these isoforms have different activity the function is similar in terms of the ability to rescue defective migration. *

The result in Hek293T cells shows that only TFAP2aS1 can induce Calpain8, while both S1 and S3 can partially rescue CNC migration in embryos lacking Adam13. The issue here is the dose of mRNA injected for each variant might be too high. Adam13 proteolytic activity is also critical, so we do not expect a complete rescue. The fact that S1 is significantly better at rescuing than S3 is relevant here. It is possible that if we were to decrease the dose of each mRNA we would find one in which S3 no longer rescues but S1 does.

* The next section again talks about yet another protein Calpain-8. Here the authors use MO13 for luciferase assays instead of HEK293 cells. The authors do not explain why they decided to switch from cells to MO.*

Calpain8 is one of the validate target of Adam13 that can rescue CNC migration (Cousin et al Dev Cell). We use the luciferase reporter corresponding to the Xenopus Capn8 reporter to show 1 in vivo that loss of Adam13 reduce its expression (Similar to the Capn8 gene). We then went in vitro using Hek293T cells for gain of function experiment that shows that only the Tfaps2S1 variant can induce it while S3 does not.

We hope that the graphical summary and the new manuscript make this clear.* 8. The experiment to IP RNA supports only the correlation that Adam9 and Adam13 bind RNA and RNA binding proteins to regulate splicing. This conclusion presented is not supported by the data presented here. While there is a sentence about why Adam9 was chosen here, it would be preferred to focus on Adam13 as the rest of the manuscript is focused on Adam13. The conclusions are generalized to all ADAMs, but ADAM13 and ADAM9 are the only ADAMs investigated in the manuscript *

This figure is no longer included. For each of the protein classes that we identify by Masspec we try to find a validation. RNA-IP is simply a validation that Adam13 and Adam9 can bind to complexes that include RNA in a cytoplasmic domain dependent fashion. The conclusion that Adam13 and possibly ADAM9 might be involved in regulating splicing is 1) that the protein associated with Adam13 are include multiple splicing factors, 2) that the RNAseq analysis shows abnormal splicing in CNC missing Adam13 and 3) that the form of TFAP2a induced by Adam13 (S1) associate significantly more with splicing factor than the S3 isoform.

We agree that the generalization to other ADAM is not demonstrated here but only suggested. We selected ADAM9 and ADAM19 because we have shown that they can each rescue Adam13 function in the CNC. Unfortunately there are no ADAM19 antibody that work by IP on the market. We have tested multiple company and multiple cell lines.

We believe that the ADAM9 experiment is critical to show that the protein associated with Adam13 are not simply the result of overexpressing a different species protein sin ADAM9 is the endogenous protein.*

Minor comments 1. The manuscript using a lot of abbreviations (PCNS, NI, MO, SH3) and lingo that are unclear to a general reader. Please define acronyms when first used, as well as be clear on which model is being used in each experiment. *

We have corrected this* 2. Similarly, the figures are not labeled such that a reader would be able to understand ie MO13 should be Adam13 knockdown etc. *

We have corrected this in the legend

• Please identify the genes on the heatmap and some highlighted genes from volcano plot from the RNA-seq.*

The volcano plot is from MS/MS not RNAseq. We have list of all of the genes and/or proteins corresponding to each figure in tables

We now have a figure from the RNAseq and a subset of genes of interest are show. *4. Why use the flag tag in Figure 5? *

We used Flag-tagged construct to only immunoprecipitated the variants and not the endogenous TFPA2a in these experiments. Also we used RFP-Flag to eliminate any protein that bound to the tag or the antibody.

This figure is no longer in the manuscript.* 5. Is the data in figure 4A-D the same as Supp. Figure 4A-D? *

These are independent biological replicates of the same experiment.* 6. Please italicize gene symbols - e.g. "key transcription factors that exemplify CNC, such as the SOX9, FOXD3, SNAI1, SNAI2, and TFAP2 family". *

We clearly have missed some, we are using italicized for gene, and regular for proteins. It might not be clear in the text when we are referring to genes and proteins. We will correct this in the rewrite. 7. Please review the manuscript for grammatical and typographical errors. * We have used all available software including Word and Grammarly. We will try to improve on the next version. **Cross-commenting**

I think the two reviewers on one the same page on this manuscript.

Reviewer #2 (Significance (Required)):

If more solid, would be a conceptual advance in role of Adam13 in mediating chromatin modification and transcription factors, adds to exiting work from this lab, good for a specialize audience, my expertise is in in neural crest development, non-mammalian modes, epigenetic regulators.*

• *

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors describe a new computational method (SegPore), which segments the raw signal from nanopore direct RNA-Seq data to improve the identification of RNA modifications. In addition to signal segmentation, SegPore includes a Gaussian Mixture Model approach to differentiate modified and unmodified bases. SegPore uses Nanopolish to define a first segmentation, which is then refined into base and transition blocks. SegPore also includes a modification prediction model that is included in the output. The authors evaluate the segmentation in comparison to Nanopolish and Tombo (RNA002) as well as f5c and Uncalled 4 (RNA004), and they evaluate the impact on m6A RNA modification detection using data with known m6A sites. In comparison to existing methods, SegPore appears to improve the ability to detect m6A, suggesting that this approach could be used to improve the analysis of direct RNA-Seq data.

Strengths:

SegPore address an important problem (signal data segmentation). By refining the signal into transition and base blocks, noise appears to be reduced, leading to improved m6A identification at the site level as well as for single read predictions. The authors provide a fully documented implementation, including a GPU version that reduces run time. The authors provide a detailed methods description, and the approach to refine segments appears to be new.

Weaknesses:

The authors show that SegPore reduces noise compared to other methods, however the improvement in accuracy appears to be relatively small for the task of identifying m6A. To run SegPore, the GPU version is essential, which could limit the application of this method in practice.

As discussed in Paragraph 4 of the Discussion, we acknowledge that the improvement of SegPore combined with m6Anet over Nanopolish+m6Anet in bulk in vivo analysis is modest. This outcome is likely influenced by several factors, including alignment inaccuracies caused by pseudogenes or transcript isoforms, the presence of additional RNA modifications that can affect signal baselines, and the fact that m6Anet is specifically trained on Nanopolish-derived events. Additionally, the absence of a modification-free (in vitro transcribed) control sample in the benchmark dataset makes it challenging to establish true k-mer baselines.

Importantly, these challenges do not exist for in vitro data, where the signal is cleaner and better defined. As a result, SegPore achieves a clear and substantial improvement at the single-molecule level, demonstrating the strength of its segmentation approach and its potential to significantly enhance downstream analyses. These results indicate that SegPore is particularly well suited for benchmarking and mechanistic studies of RNA modifications under controlled experimental conditions, and they provide a strong foundation for future developments.

We also recognize that the current requirement for GPU acceleration may limit accessibility in some computational environments. To address this, we plan to further optimize SegPore in future versions to support efficient CPU-only execution, thereby broadening its applicability and impact.

Reviewer #2 (Public review):

Summary:

The work seeks to improve detection of RNA m6A modifications using Nanopore sequencing through improvements in raw data analysis. These improvements are said to be in the segmentation of the raw data, although the work appears to position the alignment of raw data to the reference sequence and some further processing as part of the segmentation, and result statistics are mostly shown on the 'data-assigned-to-kmer' level.

As such, the title, abstract and introduction stating the improvement of just the 'segmentation' does not seem to match the work the manuscript actually presents, as the wording seems a bit too limited for the work involved.

The work itself shows minor improvements in m6Anet when replacing Nanopolish' eventalign with this new approach, but clear improvements in the distributions of data assigned per kmer. However, these assignments were improved well enough to enable m6A calling from them directly, both at site-level and at read-level.

A large part of the improvements shown appear to stem from the addition of extra, non-base/kmer specific, states in the segmentation/assignment of the raw data, removing a significant portion of what can be considered technical noise for further analysis. Previous methods enforced assignment of (almost) all raw data, forcing a technically optimal alignment that may lead to suboptimal results in downstream processing as datapoints could be assigned to neighbouring kmers instead, while random noise that is assigned to the correct kmer may also lead to errors in modification detection.

For an optimal alignment between the raw signal and the reference sequence, this approach may yield improvements for downstream processing using other tools.

Additionally, the GMM used for calling the m6A modifications provides a useful, simple and understandable logic to explain the reason a modification was called, as opposed to the black models that are nowadays often employed for these types of tasks.

Weaknesses:

The manuscript suggests the eventalign results are improved compared to Nanopolish. While this is believably shown to be true (Table 1), the effect on the use case presented, downstream differentiation between modified and unmodified status on a base/kmer, is likely limited for during downstream modification calling the noisy distributions are often 'good enough'. E.g. Nanopolish uses the main segmentation+alignment for a first alignment and follows up with a form of targeted local realignment/HMM test for modification calling (and for training too), decreasing the need for the near-perfect segmentation+alignment this work attempts to provide. Any tool applying a similar strategy probably largely negates the problems this manuscript aims to improve upon. Should a use-case come up where this downstream optimisation is not an option, SegPore might provide the necessary improvements in raw data alignment.

Thank you for this thoughtful comment. We agree that many current state-of-the-art (SOTA) methods perform well on benchmark datasets, but we believe there is still substantial room for improvement. Most existing benchmarks are based on limited datasets, primarily focusing on DRACH motifs in human and mouse transcriptomes. However, m6A modifications can also occur in non-DRACH motifs, where current models tend to underperform. Furthermore, other RNA modifications, such as pseudouridine, inosine, and m5C, remain less studied, and their detection is likely to benefit from more accurate and informative signal modeling.

It is also important to emphasize that raw signal segmentation and RNA modification detection are fundamentally distinct tasks. SegPore focuses on improving the segmentation step by producing a cleaner and more interpretable signal, which provides a stronger foundation for downstream analyses. Even if RNA modification detection algorithms such as m6Anet can partially compensate for noisy segmentation in specific cases, starting from a more accurate signal alignment can still lead to improved accuracy, robustness, and interpretability—particularly in challenging scenarios such as non-canonical motifs or less characterized modifications.

Scientific progress in this field is often incremental, and foundational improvements can have a significant long-term impact. By enhancing raw signal segmentation, SegPore contributes an essential building block that we expect will enable the development of more accurate and generalizable RNA modification detection algorithms as the community integrates it into more advanced workflows.

Appraisal:

The authors have shown their methods ability to identify noise in the raw signal and remove their values from the segmentation and alignment, reducing its influences for further analyses. Figures directly comparing the values per kmer do show a visibly improved assignment of raw data per kmer. As a replacement for Nanopolish' eventalign it seems to have a rather limited, but improved effect, on m6Anet results. At the single read level modification modification calling this work does appear to improve upon CHEUI.

Impact:

With the current developments for Nanopore based modification calling largely focusing on Artificial Intelligence, Neural Networks and the likes, improvements made in interpretable approaches provide an important alternative that enables deeper understanding of the data rather than providing a tool that plainly answers the question of wether a base is modified or not, without further explanation. The work presented is best viewed in context of a workflow where one aims to get an optimal alignment between raw signal data and the reference base sequence for further processing. For example, as presented, as a possible replacement for Nanopolish' eventalign. Here it might enable data exploration and downstream modification calling without the need for local realignments or other approaches that re-consider the distribution of raw data around the target motif, such as a 'local' Hidden Markov Model or Neural Networks. These possibilities are useful for a deeper understanding of the data and further tool development for modification detection works beyond m6A calling.

Reviewer #3 (Public review):

Summary:

Nucleotide modifications are important regulators of biological function, however, until recently, their study has been limited by the availability of appropriate analytical methods. Oxford Nanopore direct RNA sequencing preserves nucleotide modifications, permitting their study, however many different nucleotide modifications lack an available base-caller to accurately identify them. Furthermore, existing tools are computationally intensive, and their results can be difficult to interpret.

Cheng et al. present SegPore, a method designed to improve the segmentation of direct RNA sequencing data and boost the accuracy of modified base detection.

Strengths:

This method is well described and has been benchmarked against a range of publicly available base callers that have been designed to detect modified nucleotides.

Weaknesses:

However, the manuscript has a significant drawback in its current version. The most recent nanopore RNA base callers can distinguish between different ribonucleotide modifications, however, SegPore has not been benchmarked against these models.

The manuscript would be strengthened by benchmarking against the rna004_130bps_hac@v5.1.0 and rna004_130bps_sup@v5.1.0 dorado models, which are reported to detect m5C, m6A_DRACH, inosine_m6A and PseU.

A clear demonstration that SegPore also outperforms the newer RNA base caller models will confirm the utility of this method.

Thank you for highlighting this important limitation. While Dorado, the new ONT basecaller, is publicly available and supports modification-aware basecalling, suitable public datasets for benchmarking m5C, inosine, m6A, and PseU detection on RNA004 are currently lacking. Dorado’s modification-aware models are trained on ONT’s internal data, which is not publicly released. Therefore, it is currently not feasible to directly evaluate or compare SegPore’s performance against Dorado for these RNA modifications.

We would also like to emphasize that SegPore’s primary contribution lies in raw signal segmentation, which is an upstream and foundational step in the RNA modification detection pipeline. As more publicly available datasets for RNA004 modification detection become accessible, we plan to extend our work to benchmark and integrate SegPore with modification detection tasks on RNA004 data in future studies.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Comments based on Author Response

“However, it is valid to compare them on the segmentation task, where SegPore exhibits better performance (Table 1).”

This dodges the point of the actual use case of this approach, as Nanopolish indeed does not support calling modifications for this kind of data, but the general approach it uses might, if adapted for this data, nullify the gains made in the examples presented.

We respectfully disagree with the comment that the advantages demonstrated by SegPore could be “nullified”. Although SegPore’s performance is indeed more modest in in vivo datasets, it shows substantially better performance than CHEUI in in vitro data, clearly demonstrating that improved segmentation directly contributes to more accurate RNA modification estimation.

It is worth noting that CHEUI relies on Nanopolish’s segmentation results for m6A detection. Despite this, SegPore outperforms CHEUI, further supporting the conclusion that segmentation quality has a meaningful impact on downstream modification calling.

In conclusion, based on our current experimental results, SegPore is particularly well suited for RNA modification analysis from in vitro transcribed data, where its improved segmentation provides a clear advantage over existing methods.

Further comments

(2) “(2) Page 3  employ models like Hidden Markov Models (HMM) to segment the signal, but they are prone to noise and inaccuracies”

“That's the alignment/calling part, not the segmentation?”

“Current methods, such as Nanopolish, employ models like Hidden Markov Models (HMM) to segment the signal”

I get the impression the word 'segment' has a different meaning in this work than what I'm used to based on my knowledge around Nanopolish and Tombo, see the deeper code examples further down below.

Additionally, in Nanopolish there is a clear segmentation step (or event detection) without any HMM, then a sort of dynamic timewarping step that aligns the segments and re-combines some segments into a single segment where necessary afterwards. I believe the HMM in Nanopolish is not used at all unless modification calling, but if you can point out otherwise I'm open for proof.

Now I believe it is the meaning of 'segmenting the signal' that confuses me, and now the clarification makes it a bit odd as well:

“Nanopolish and Tombo align the raw signal to the reference sequence to determine which portion of the signal corresponds to each k-mer. We define this process as the segmentation task, referred to as "eventalign" in Nanopolish.”

So now it's clearly stated the raw signal is being 'aligned' and then the process is suddenly defined as the 'segmentation task', and again referred to as "eventalign". Why is it not referred to as the 'alignment task' instead?

I understand the segmentation and alignment parts are closely connected but to me, it seems this work picks the wrong word for the problem being solved.

“Unlike Nanopolish and Tombo, which directly align the raw signal to the reference sequence,…”

Looking at their code, I believe both Nanopolish and Tombo actually do segment the data first (or "event detection"), then they align the segments/events they found, and finally multiple events aligned to the same section are merged. See for yourself:

Nanopolish:

https://github.com/jts/nanopolish/blob/master/src/nanopolish_squiggle_read.cpp<br /> Line 233:

cpp

trim_and_segment_raw(fast5_data.rt, trim_start, trim_end, varseg_chunk, varseg_thresh);

event_table et = detect_events(fast5_data.rt, *ed_params);

Line 270:

cpp

// align events to the basecalled read

std::vector event_alignment = adaptive_banded_simple_event_align(*this, *this->base_model[strand_idx], read_sequence);

Where event detection is further defined at line 268 here:

https://github.com/jts/nanopolish/blob/master/src/thirdparty/scrappie/event_detection.c

Tombo:

https://github.com/nanoporetech/tombo/blob/master/tombo/resquiggle.py

line 1162 and onwards shows a ‘segment_signal’ call and the results are used in a ‘find_adaptive_base_assignment’ call, where ‘segment_signal’ starting at line 1057 tries to find where the signal jumps from a series of similar values to another (start of a base change in the pore), stored in ‘valid_cpts’, and the ‘find_adaptive_base_assignment’ tries to align the resulting segment values to the expected series of values:

python

valid_cpts, norm_signal, new_scale_values = segment_signal(

map_res, num_events, rsqgl_params, outlier_thresh, const_scale)

event_means = ts.compute_base_means(norm_signal, valid_cpts)

dp_res = find_adaptive_base_assignment(

valid_cpts, event_means, rsqgl_params, std_ref, map_res.genome_seq,

start_clip_bases=map_res.start_clip_bases,

seq_samp_type=seq_samp_type, reg_id=map_res.align_info.ID)

These implementations are also why I find the choice of words for what is segmentation and what is alignment a bit confusing in this work, as both Tombo and Nanopolish do a similar, clear segmentation step (or an "event detection" step), followed by the alignment of the segments they determined. The terminology in this work appears to deviate from these.

We thank the reviewer for the detailed comments!

First of all, we sincerely apologize for our earlier misunderstanding regarding how Nanopolish and Tombo operate. Based on a closer examination of their source codes, we now recognize that both tools indeed include a segmentation step based on change-point detection methods, after which the resulting segments are aligned to the reference sequence. We have revised the relevant text in the manuscript accordingly:

- “Current methods, such as Nanopolish, employ change-point detection methods to segment the signal and use dynamic programming methods and HMM to align the derived segments to the reference sequence,”

- “We define this process as the segmentation and alignment task (abbreviated as the segmentation task), which is referred to as “eventalign” in Nanopolish.”

- “In SegPore, we segment the raw signal into small fragments using a Hierarchical Hidden Markov Model (HHMM) and align the mean values of these fragments to the reference, where each fragment corresponds to a sub-state of a k-mer. By contrast, Nanopolish and Tombo use change-point–based methods to segment the signal and employ dynamic programming approaches together with profile HMMs to align the resulting segments to the reference sequence.”

Regarding terminology, we originally borrowed the term “segmentation” from speech processing, where it refers to dividing continuous audio signals into meaningful units. In the context of nanopore signal analysis, segmentation and alignment are often tightly coupled steps. Because of this and because our initial focus was on methodological development rather than terminology, we used the term “segmentation task” to describe the combined process of signal segmentation and alignment.

However, we now recognize that this terminology may cause confusion. Changing every instance of “segmentation” to “segmentation and alignment” or “alignment” would require substantial rewriting of the manuscript. Therefore, in this revision, we have clearly defined “segmentation task” as referring to the combined process of segmentation and alignment. We apologize for any earlier confusion and will adopt the term “alignment” in future work for greater clarity.

(3) I think I do understand the meaning, but I do not understand the relevance of the Aj bit in the last sentence. What is it used for?

Based on the response and another close look at Fig1, it turns out the j refers to extremely small numbers 1 and 2 in step 3. You may want in improve readability for these.

Thank you for the suggestion. We have added subscripts to all nucleotides in the reference sequence in Figure 1A and revised the legend to clarify the notation and improve readability. Specifically, we now include the following explanation:

“For example, A_j denotes the base ‘A’ at the j-th position on the reference sequence. In this example, A₁ and A₂ refer to the first and second occurrences of ‘A’ in the reference sequence, respectively. Accordingly, μ₁ and μ₂ are aligned to A₁, while μ₃ is aligned to A₂”.

(6) “We chose to use the poly(A) tail for normalization because it is sequence-invariant- i.e., all poly(A) tails consist of identical k-mers, unlike transcript sequences which vary in composition. In contrast, using the transcript region for normalization can introduce biases: for instance, reads with more diverse k-mers (having inherently broader signal distributions) would be forced to match the variance of reads with more uniform k-mers, potentially distorting the baseline across k-mers.”

While the next part states there was a benchmark showing SegPore still works without this normalization, I think this answer does not touch upon the underlying issue I'm trying to point out here.

- The biases mentioned here due to a more diverse (or different) subsets of k-mers in a read indeed affects the variance of the signal overall.

- As I pointed out in my earlier remark here, this can be resolved using an approach of 'general normalization', 'mapping to expected signal', 'theil-sen fitting of scale and offset', 're-mapping to expected signal', as Tombo and Nanopolish have implemented.<br /> - Alternatively, one could use the reference sequence (using the read mapping information) and base the expected signal mean and standard deviation on that instead.

- The polyA tail stability as an indicator for the variation in the rest of the signal seems a questionable assumption to me. A 'noisy' pore could introduce a large standard deviation using the polyA tail without increasing the deviations on the signal induced by the variety of k-mers, rather it would be representative for the deviations measured within a single k-mer segment. I thought this possible discrepancy is to be expected from a worn out pore, hence I'd imagine reads sequenced later in a run to provide worse results using this method.

In the current version it is not the statement that is unclear, it is the underlying assumption of how this works that I question.

We thank the reviewer for raising this important point and for the insightful discussion. Our choice of using the poly(A) tail for normalization is based on the working hypothesis that the poly(A) signal reflects overall pore-level variability and provides a stable reference for signal scaling. We find this to be a practical and effective approach in most experimental settings.

We agree that more sophisticated strategies, such as “general normalization” or iterative fitting to the expected signal (as implemented in Tombo and Nanopolish), could in principle generate a "better" normalization. However, these approaches are significantly more challenging to implement in practice. This is because signal normalization and alignment are mutually dependent processes: baseline estimates for k-mers influence alignment accuracy, while alignment accuracy, in turn, affects baseline calculation. This interdependence becomes even more complex in the presence of RNA modifications, which alter signal distributions and further confound model fitting.

It is worth noting that this limitation is already evident in our results. As shown in Figure 4B (first and second k-mers), Nanopolish produces more dispersed baselines than SegPore, even for these unmodified k-mers, suggesting inherent limitations in its normalization strategy. Ideally, baselines for the same k-mer should remain highly consistent across different reads.

In contrast, poly(A)-based normalization offers a simpler and more robust solution that avoids this circular dependency. Because poly(A) sequences are compositionally homogeneous, they enable reliable estimation of scaling parameters without assumptions about k-mer composition or modification state. Regarding the reviewer’s concern about pore instability, we mitigate this issue by including only high-quality, confidently mapped reads in our analysis, which reduces the likelihood of incorporating signals from degraded or “noisy” pores.

We fully agree that exploring more advanced normalization strategies is an important direction for future work, and we plan to investigate such approaches as the field progresses.

(8) “In the remainder of this paper, we refer to these resulting events as the output of eventalign analysis or the segmentation task.”

Picking only one descriptor rather than two alternatives would be easier to follow (and I'd prefer the first).

Thank you for the suggestion. We have revised the sentence to:

“In the remainder of this paper, we refer to these resulting events as the output of eventalign analysis, which also represents the final output of the segmentation and alignment task.”

(9) “Additionally, a complete explanation of how the weighted mean is computed is provided in Section 5.3 of Supplementary Note 1. It is derived from signal points that are assigned to a given 5mer.”

I believe there's no more mention of a weighted mean, and I don't get any hits when searching for 'weight'. Is that intentional?

We apologize for the misplacement of the formulas. We have updated Section 5.3 of Supplementary Note 1 to clarify the definition of the weighted mean. Because multiple current signal segments may be aligned to a single k-mer, we computed the weighted mean for each k-mer across these segments, where the weight corresponds to the number of data points assigned to “curr” state in each event.

(17) Response: We revised the sentence to clarify the selection criteria: "For selected 5mers “that exhibit both a clearly unmodified and a clearly” “modified signal component”, “SegPore reports the modification rate at each site,” “as well as the modification state of that site on individual reads.””

So is this the same set described on page 13 ln 343 or not?

“Due to the differences between human (Supplementary Fig. S2A) and mouse (Supplementary Fig. S2B), only six 5mers were found to have m6A annotations in the test data's ground truth (Supplementary Fig. S2C). For a genomic location to be identified as a true m6A modification site, it had to correspond to one of these six common 5mers and have a read coverage of greater than 20.”

I struggle to interpret the 'For selected 5mers' part, as I'm not sure if this is a selection I'm supposed to already know at this point in the text or if it's a set just introduced here. If the latter, removing the word 'selected' would clear it up for me.

We apologize for the confusion. What we mean is that when pooling signals aligned to the same k-mer across different genomic locations and reads, only a subset of k-mers exhibit a bimodal distribution — one peak corresponding to the unmodified state and another to the modified state. Other k-mers show a unimodal distribution, making it impossible to reliably estimate modification levels. We refer to the subset of k-mers that display a bimodal distribution as the “selected” k-mers.

The “selected k-mers” described on page 13, line 343, must additionally have ground truth labels available in both the training and test datasets. There are 10 k-mers with ground truth annotations in the training data and 11 in the test data, and only 6 of these k-mers are shared between the two datasets, therefore only those 6 overlapping k-mers are retained for evaluation. These 6 k-mers satisfy both criteria: (1) exhibiting a bimodal distribution and (2) having ground truth annotations in both training and test sets.

To improve clarity, we have removed the term “selected” from the sentence.

(21) "Tombo used the "resquiggle" method to segment the raw signals, and we standardized the segments using the “poly(A)” tail to ensure a fair comparison “(See” “preprocessing section in Materials and Methods)."”

In the Materials and Methods:

“The raw signal segment corresponding to the poly(A) tail is used to standardize the raw signal for each read.”

I cannot find more detailed information here on what the standardization does, do you mean to refer to Supplementary Note 1, Section 3 perhaps?

Thank you for pointing this out. Yes, the standardization procedure is described in detail in Supplementary Note 1, Section 3. Tombo itself does not segment and align the raw signal on the absolute pA scale, which can result in very large variance in the derived events if the raw signal is used directly. To ensure a fair comparison, we therefore applied the same preprocessing steps to Tombo’s raw signals as we did for SegPore, using only the event boundary information from Tombo while standardizing the signal in the same way.

We have revised the sentence for clarity as follows:

“Tombo used the "resquiggle" method to segment the raw signals, but the resulting signals are not reported on the absolute pA scale. To ensure a fair comparison with SegPore, we standardized the segments using the poly(A) tail in the same way as SegPore (See preprocessing section in Materials and Methods).”

(22A) The table shown does help showing the benchmark is unlikely to be 'cheated'. However I am suprised to see the Avg std for Nanopolish and Tombo going up instead of down, as I'd expect the transition values to increase the std, and hence, removing them should decrease these values. So why does this table show the opposite?

I believe this table is not in the main text or the supplement, would it not be a good idea to cover this point somewhere in the work?

Thank you for this insightful comment. In response, we carefully re-examined our analysis and identified a bug in the code related to boundary removal for Nanopolish. We have now corrected this issue and included the updated results in Supplementary Table S1 of the revised manuscript. As shown in the updated table, the average standard deviations decrease after removing the boundary regions for both Nanopolish and Tombo.

We have now included this table in Supplementary Table S1 in the revised manuscript and added the following clarification:

“It is worth noting that the data points corresponding to the transition state between two consecutive 5-mers are not included in the calculation of the standard deviation in SegPore’s results in Table 1. However, their exclusion does not affect the overall conclusion, as there are on average only ~6 points per 5-mer in the transition state (see Supplementary Table S1 for more details).”

(22B) As mentioned in 2), I'm happy there's a clear definition of what is meant but I found the chosen word a bit odd.

We apologize for the earlier unclear terminology. We now refer to it as the segmentation and alignment task, abbreviated as the segmentation task.

(23) Reading back I can gather that from the text earlier, but the summation of what is being tested is this:

“including Tombo, MINES (31), Nanom6A (32), m6Anet, Epinano (33), and CHEUI (20). “

next, the identifier "Nanopolish+m6Anet" is, aside from the figure itself, only mentioned in the discussion. Adding a line that explains that "Nanopolish+m6Anet" is the default method of running m6Anet and "SegPore+m6Anet" replaces the Nanopolish part for m6Anet with Segpore, rather than jumping straight to "SegPore+m6Anet", would clarify where this identifier came from.

Thank you for the helpful suggestion. We have added the identifier to the revised manuscript as follows:

“Given their comparable methodologies and input data requirements, we benchmarked SegPore against several baseline tools, including Tombo, MINES (31), Nanom6A (32), m6Anet, Epinano (33), and CHEUI (20). By default, MINES and Nanom6A use eventalign results generated by Tombo, while m6Anet, Epinano, and CHEUI rely on eventalign results produced by Nanopolish. In Fig. 3C, ‘Nanopolish+m6Anet’ refers to the default m6Anet pipeline, whereas ‘SegPore+m6Anet’ denotes a configuration in which Nanopolish’s eventalign results are replaced with those from SegPore.”

(24) For completeness I'd expect tickmarks and values on the y-axis as well.

Thank you for the suggestion. We have updated Figures 3A and 3B in the revised manuscript to include tick marks and values on the y-axis as requested.

(25) Considering this statement and looking back at figure 3a and 3b, wouldn't this be easier to observe if the histograms/KDE's were plotted with overlap in a single figure?

We appreciate the suggestion. However, we believe that overlaying Figures 3A and 3B into a single panel would make the visualization cluttered and more difficult to interpret.

(29) Please change the sentence in the text to make that clear. As it is written now (while it's the same number of motifs, so one might guess it) it does not seem to refer to that particular set of motifs and could be a new selection of 6 motifs.

We appreciate the suggestion and have revised the sentence for clarity as follows:

“We evaluated m6A predictions using two approaches: (1) SegPore’s segmentation results were fed into m6Anet, referred to as SegPore+m6Anet, which works for all DRACH motifs and (2) direct m6A predictions from SegPore’s Gaussian Mixture Model (GMM), which is limited to the six selected 5-mers shown in Supplementary Fig. S2C that exhibit clearly separable modified and unmodified components in the GMM (see Materials and Methods for details). ”

(31) I think we have a different interpretation of the word 'leverage', or perhaps what it applies to. I'd say it leverages the jiggling if there's new information drawn from the jiggling behaviour. It's taking it into account if it filters for it. The HHMM as far as I understand tries to identify the jiggles, and ignore their values for the segmentation etc. So while one might see this as an approach that "leverages the hypothesis", I don't see how this HHMM "leverages the jiggling property" itself.

Thank you for the helpful suggestion. We have replaced the word “leverages” with “models” in the revised manuscript.

New points

pg6ln166: “…we extract the aligned raw signal segment and reference sequence segment from Nanopolish's events [...] we extract the raw signal segment corresponding to the transcript region for each input read based on Nanopolish's poly(A) detection results.”

It is not clear as to why this different approach is applied for these two cases in this part of the text.

Thank you for pointing this out. The two approaches refer to different preprocessing strategies for in vivo and in vitro data.

For in vivo data, a large proportion of reads do not span the full-length transcript and often map only to a portion of the reference sequence. Moreover, because a single gene can generate multiple transcript isoforms, a read may align equally well to several possible transcripts. Therefore, we extract only the raw signal segment that corresponds to the mapped portion of the transcript for each read.

In contrast, for in vitro data, the transcript sequence is known precisely. As a result, we can directly extract all raw signals following the poly(A) tail and align them to the complete reference sequence.

pg10ln259: An important distinction from classical global alignment algorithms is that one or multiple base blocks may align with a single 5mer.”

If there was usually a 1:1 mapping the alignment algorithm would be more or less a direct match, so I think the multiple blocks aligning to a 5mer thing is actually quite common.

Thank you for the comment. The “classical global alignment algorithm” here refers to the Needleman–Wunsch algorithm used for sequence alignment. Our intention was to highlight the conceptual difference between traditional sequence alignment and nanopore signal alignment. In classical sequence alignment, each base typically aligns to a single position in the reference. In contrast, in nanopore signal alignment, one or multiple signal segments — corresponding to varying dwell times of the motor protein — can align to a single 5-mer.

We have revised the sentence as follows:

“An important distinction from classical global alignment algorithms (Needleman–Wunsch algorithm)……”

pg13ln356: "dwell time" is not defined or used before, I guess it's effectively the number of raw samples per segment but this should be clarified.

Thank you for pointing this out. We have now added a clear definition of dwell time in the text as follows:

"such as the normalized mean μ_i, standard deviation σ_i, dwell time l_i (number of data points in the event)."

pg13ln358: “Feature vectors from 80% of the genomic locations were used for training, while the remaining 20% were set aside for validation.”

I assume these are selected randomly but this is not explicitly stated here and should be.

Yes, they are randomly selected. We have revised the sentence as follows:

“Feature vectors from a randomly selected 80% of the genomic locations were used for training, while the remaining 20% were set aside for validation.”

pg18ln488: The manuscript now evaluates RNA004 and compares against f5c and Uncalled4. It mentions the differences between RNA004 and RNA002, namely kmer size and current levels, but does not explain where the starting reference model values for the RNA004 model come from: In pg18ln492 they state "RNA004 provides reference values for 9mers", then later they seem to use a 5mer parameter table (pg19ln508), are they re-using the same table from RNA002 or did they create a 5mer table from the 9mer reference table?

We apologize for the confusion. The reference model table for RNA004 9-mers is obtained from f5c (the array named ‘rna004_130bps_u_to_t_rna_9mer_template_model_builtin_data’in  https://raw.githubusercontent.com/hasindu2008/f5c/refs/heads/master/src/model.h).

Author response image 1.

We have revised the subsection header “5-mer parameter table” in the Method to “5-mer & 9-mer parameter table” to highlight this and added a paragraph about how to obtain the 9-mer parameter table:

“In the RNA004 data analysis (Table 2), we obtained the 9-mer parameter table from the source code of f5c (version 1.5). Specifically, we used the array named ‘rna004_130bps_u_to_t_rna_9mer_template_model_builtin_data’ from the following file: https://raw.githubusercontent.com/hasindu2008/f5c/refs/heads/master/src/model.h (accessed on 17 October 2025).”

Also, in page 18 line 195, we added the following sentence:

“The 9-mer parameter table in pA scale for RNA004 data provided by f5c (see Materials and Methods) was used in the analysis.”

pg19ln520: “Additionally, due to the differences of the k-mer motifs between human and mouse (Supplementary Fig. S2), six shared 5mers were selected to demonstrate SegPore's performance in modification prediction directly.”

"the differences" - in occurrence rates, as I gather from the supplementary figure, but it would be good to explicitly state it in this sentence itself too.

Thank you for the helpful suggestion. We agree that the original sentence was vague. The main reason for selecting only six 5-mers is the difference in the availability of ground truth labels for specific k-mer motifs between human and mouse datasets. We have revised the sentence accordingly:

“Additionally, due to the differences in the availability of ground truth labels for specific k-mer motifs between human and mouse (Supplementary Fig. S2), six shared 5-mers were selected to directly demonstrate SegPore’s performance in modification prediction.”

pg24ln654: “SegPore codes current intensity levels”

"codes" is meant to be "stores" I guess? Perhaps "encodes"?

Thank you for the suggestion. We have now replaced it with “encodes” in the revised manuscript.

Lastly, looking at the feedback from the other reviewers comment:

The 'HMM' mentioned in line 184 looks fine to me, the HHMM is 2 HMM's in a hierarchical setup and the text now refers to one of these HMM layers. If this is to be changed it would need to state the layer (e.g. "the outer HHMM layer") throughout the text instead.

We agree with this assessment and believe that the term “inner HMM” is accurate in this context, as it correctly refers to one of the two HMM layers within the HHMM structure. Therefore, we have decided to retain the current terminology.

Reviewer #3 (Recommendations for the authors):

I recommend the publication of this manuscript, provided that the following comments are addressed.

Page 5, Preprocessing: You comment that the poly(A) tail provides a stable reference that is crucial for the normalisation of all reads. How would this step handle reads that have interrupted poly(A) tails (e.g. in the case of mRNA vaccines that employ a linker sequence)? Or cell types that express TENT4A/B, which can include transcripts with non-A residues in the poly(A) tail: https://www.science.org/doi/full/10.1126/science.aam5794.

It depends on Nanopolish’s ability to reliably detect the poly(A) tail. In general, the poly(A) region produces a long stretch of signals fluctuating around a current level of ~108.9 pA (RNA002) with relatively stable variation, which allows it to be identified and used for normalization.

For in vivo data, if the poly(A) tail is interrupted (e.g., due to non-A residues or linker sequences), two scenarios are possible:

(1) The poly(A) tail may not be reliably detected, in which case the corresponding read will be excluded from our analysis.

(2) Alternatively, Nanopolish may still recognize the initial uninterrupted portion of the poly(A) signal, which is typically sufficient in length and stability to be used for signal normalization.

For in vitro data, the poly(A) tails are uninterrupted, so this issue does not arise.

All analyses presented in this study are based exclusively on reads with reliably detected poly(A) tails.

Page 7, 5mer parameter table: r9.4_180mv_70bps_5mer_RNA is an older kmer model (>2 years). How does your method perform with the newer RNA kmer models that do permit the detection of multiple ribonucleotide modifications? Addressing this comment would be beneficial, however I understand that it would require the generation of new data, as limited RNA004 datasets are available in the public domain.

“r9.4_180mv_70bps_5mer_RNA” is the most widely used k-mer model for RNA002 data. Regarding the newer k-mer models, we believe the reviewer is referring to the “modification basecalling” models available in Dorado, which are specifically designed for RNA004 data. At present, SegPore can perform RNA modification estimation only on RNA002 data, as this is the platform for which suitable training data and ground truth annotations are available. Evaluating SegPore’s performance with the newer RNA004 modification models would require new datasets containing known modification sites generated with RNA004 chemistry. Since such data are currently unavailable, we have not yet been able to assess SegPore under these conditions. This represents an important future direction for extending and validating our method.

The Methods and Results sections contain redundant information -please streamline the information in these sections and reduce the redundancy.

We thank the reviewer for this suggestion and acknowledge that there is some overlap between the Methods and Results sections. However, we feel that removing these parts could compromise the clarity and readability of the manuscript, especially given that Reviewer 2 emphasized the need for clearer explanations. We therefore decided to retain certain methodological descriptions in the Results section to ensure that key steps are understandable without requiring the reader to constantly cross-reference the Methods.

Minor comments

Please be consistent when referring to k-mers and 5-mers (sometimes denoted as 5mers - please change to 5-mers throughout).

We have revised the manuscript to ensure consistency and now use “5-mers” throughout the text.

Introduction

Lines 80 - 112: Please condense this section to roughly half the length (1-2 paragraphs). In general, the results described in the introduction should be very brief, as they are described in full in the results section.

Thank you for the suggestion. We have condensed the original three paragraphs into a single, more concise paragraph as follows:

"SegPore is a novel tool for direct RNA sequencing (DRS) signal segmentation and alignment, designed to overcome key limitations of existing approaches. By explicitly modeling motor protein dynamics during RNA translocation with a Hierarchical Hidden Markov Model (HHMM), SegPore segments the raw signal into small, biologically meaningful fragments, each corresponding to a k-mer sub-state, which substantially reduces noise and improves segmentation accuracy. After segmentation, these fragments are aligned to the reference sequence and concatenated into larger events, analogous to Nanopolish’s “eventalign” output, which serve as the foundation for downstream analyses. Moreover, the “eventalign” results produced by SegPore enhance interpretability in RNA modification estimation. While deep learning–based tools such as m6Anet classify RNA modifications using complex, non-transparent features (see Supplementary Fig. S5), SegPore employs a simple Gaussian Mixture Model (GMM) to distinguish modified from unmodified nucleotides based on baseline current levels. This transparent modeling approach improves confidence in the predictions and makes SegPore particularly well-suited for biological applications where interpretability is essential."

Line 104: Please change "normal adenosine" to "adenosine".

We have revised the manuscript as requested and replaced all instances of “normal adenosine” with “adenosine” throughout the text.

Materials and Methods

Line 176: Please reword "...we standardize the raw current signals across reads, ensuring that the mean and standard deviation of the poly(A) tail are consistent across all reads." To "...we standardize the raw current signals for each read, ensuring that the mean and standard deviation are consistent across the poly(A) tail region."

We have changed sentence as requested.

“Since the poly(A) tail provides a stable reference, we standardize the raw current signals for each read, ensuring that the mean and standard deviation are consistent across the poly(A) tail region.”

Line 182: Please describe the RNA translocation hypothesis, as this is the first mention of it in the text. Also, why is the Hierachical Hidden Markov model perfect for addressing the RNA translocation hypothesis? Explain more about how the HHMM works and why it is a suitable choice.

We have revised the sentence as requested:

“The RNA translocation hypothesis (see details in the first section of Results) naturally leads to the use of a hierarchical Hidden Markov Model (HHMM) to segment the raw current signal.”

The motivation of the HHMM is explained in detail in the the first section “RNA translocation hypothesis” of Results. As illustrated in Figure 2, the sequencing data suggest that RNA molecules may translocate back and forth (often referred to as jiggling) while passing through the nanopore. This behavior results in complex current fluctuations that are challenging to model with a simple HMM. The HHMM provides a natural framework to address this because it can model signal dynamics at two levels. The outer HMM distinguishes between two major states — base states (where the signal corresponds to a stable sub-state of a k-mer) and transition states (representing transitions from one base state to the next). Within each base state, an inner HMM models finer signal variation using three states — “curr”, “prev”, and “next” — corresponding to the current k-mer sub-states and its neighboring k-mer sub-states. This hierarchical structure captures both the stable signal patterns and the stochastic translocation behavior, enabling more accurate and biologically meaningful segmentation of the raw current signal.

Line 184: do you mean HHMM? Please be consistent throughout the text.

As explained in the previous response, the HHMM consists of two layers: an outer HMM and an inner HMM. The term “HMM” in line 184 is meant to be read together with “inner” at the end of line 183, forming the phrase “inner HMM.” It seems the reviewer may have overlooked this when reading the text.

Line 203: please delete: "It is obviously seen that".

We have removed the phrase “It is obviously seen that” from the sentence as requested. The revised sentence now reads:

“The first part of Eq. 2 represents the emission probabilities, and the second part represents the transition probabilities.”

Line 314, GMM for 5mer parameter table re-estimation: "Typically, the process is repeated three to five times until the5mer parameter table stabilizes." How is the stabilisation of the 5mer parameter table quantified? What is a reasonable cut-off that would demonstrate adequate stabilisation of the 5mer parameter table? Please add details of this to the text.

We have revised the sentence to clarify the stabilization criterion as follows:

“Typically, the process is repeated three to five times until the 5-mer parameter table stabilizes (when the average change of mean values of all 5-mers is less than 5e-3).”

Results

Line 377: Please edit to read "Traditional base calling algorithms such as Guppy and Albacore assume that the RNA molecule is translocated unidirectionally through the pore by the motor protein."

We have revised the sentence as:

“In traditional basecalling algorithms such as Guppy and Albacore, we implicitly assume that the RNA molecule is translocated through the pore by the motor protein in a monotonic fashion, i.e., the RNA is pulled through the pore unidirectionally.”

Line 555, m6A identification at the site level: "For six selected m6A motifs, SegPore achieved an ROC AUC of 82.7% and a PR AUC of 38.7%, earning the third best performance compared with deep leaning methods m6Anet and CHEUI (Fig. 3D)." So SegPore performs third best of all deep learning methods. Do you recommend its use in conjunction with m6Anet for m6A detection? Please clarify in the text. This will help to guide users to possible best practice uses of your software.

Thank you for the suggestion. We have added a clarification in the revised manuscript to guide users.

“For practical applications, we recommend taking the intersection of m6A sites predicted by SegPore and m6Anet to obtain high-confidence modification sites, while still benefiting from the interpretability provided by SegPore’s predictions.”

Figures.

Figure 1A please refer to poly(A) tail, rather than polyA tail.

We have updated it to poly(A) tail in the revised manuscript.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

The study by Pinho et al. presents a novel behavioral paradigm for investigating higher-order conditioning in mice. The authors developed a task that creates associations between light and tone sensory cues, driving mediated learning. They observed sex differences in task acquisition, with females demonstrating faster-mediated learning compared to males. Using fiber photometry and chemogenetic tools, the study reveals that the dorsal hippocampus (dHPC) plays a central role in encoding mediated learning. These findings are crucial for understanding how environmental cues, which are not directly linked to positive/negative outcomes, contribute to associative learning. Overall, the study is well-designed, with robust results, and the experimental approach aligns with the study's objectives. 

Strengths: 

(1) The authors develop a robust behavioral paradigm to examine higher-order associative learning in mice. 

(2) They discover a sex-specific component influencing mediated learning, with females exhibiting enhanced learning abilities. 

(3) Using fiber photometry and chemogenetic techniques, the authors identify the dorsal hippocampus but not the ventral hippocampus, which plays a crucial for encoding mediated learning.

We appreciate the strengths highlighted by the Reviewer and the valuable and complete summary of our work.

Weaknesses: 

(1) The study would be strengthened by further elaboration on the rationale for investigating specific cell types within the hippocampus.  

We thank the Reviewer for highlighting this important point. In the revised manuscript, we have added new information (Page 11, Lines 27-34) to specifically explain the rational of studying the possible cell-type specific involvement in sensory preconditioning.

(2) The analysis of photometry data could be improved by distinguishing between early and late responses, as well as enhancing the overall presentation of the data.  

According to the Reviewer comment, we have included new panels in Figure 3E and the whole Supplementary Figure 4, which separates the photometry data across different preconditioning and conditioning sessions, respectively. Overall, this data suggests that there are no major changes on cell activity in both hippocampal regions during the different sessions as similar light-tone-induced enhancement of activity is observed. These findings have been incorporated in the Results Section (Page 12, Lines 13-15, 19-20 and 35-36).

(3) The manuscript would benefit from revisions to improve clarity and readability.

Based on the fair comment, we have gone through the text to increase clarity and readability.

Reviewer #2 (Public review): 

Summary: 

Pinho et al. developed a new auditory-visual sensory preconditioning procedure in mice and examined the contribution of the dorsal and ventral hippocampus to learning in this task. Using photometry they observed activation of the dorsal and ventral hippocampus during sensory preconditioning and conditioning. Finally, the authors combined their sensory preconditioning task with DREADDs to examine the effect of inhibiting specific cell populations (CaMKII and PV) in the DH on the formation and retrieval/expression of mediated learning. 

Strengths: 

The authors provide one of the first demonstrations of auditory-visual sensory preconditioning in male mice. Research on the neurobiology of sensory preconditioning has primarily used rats as subjects. The development of a robust protocol in mice will be beneficial to the field, allowing researchers to take advantage of the many transgenic mouse lines. Indeed, in this study, the authors take advantage of a PV-Cre mouse line to examine the role of hippocampal PV cells in sensory preconditioning. 

We acknowledge the Reviewer´s effort and for highlighting the strengths of our work.

Weaknesses: 

(1) The authors report that sensory preconditioning was observed in both male and female mice. However, their data only supports sensory preconditioning in male mice. In female mice, both paired and unpaired presentations of the light and tone in stage 1 led to increased freezing to the tone at test. In this case, fear to the tone could be attributed to factors other than sensory preconditioning, for example, generalization of fear between the auditory and visual stimulus.

We thank the comment raised by the Reviewer. At first, we were hypothesizing that female mice were somehow able to associate light and tone although they were presented separately during the preconditioning sessions. Thus, we designed new experiments (shown in Supplementary Figure 2D) to test if we would observe data congruent with our initial hypothesis or with fear generalization as proposed by the reviewer. We have performed a new experiment comparing a Paired group with two additional control groups that are (i) an Unpaired group where we increased the time between the light and tone presentations and (ii) an experimental group where the light was absent during the conditioning. Clearly, the new results indicate the presence of fear generalization in female mice aswe found a significant cue-induced increase on freezing responses in all the experimental groups tested. In accordance with the Reviewer’s suggestion, we can conclude that mediated learning is not correctly observed in female mice using the protocol described (i.e. with 2 conditioning sessions). All these new results forced us to reorganize the structure and the figures of the manuscript to focus more in male mice in the Main Figures whereas showing the data with female mice in Supplementary Figures. Overall, our data clearly revealed the necessity to have adapted behavioral protocols for each sex demonstrating sex differences in sensory preconditioning, which was added in the Discussion Section (Page 15, lines 12-37).

(2) In the photometry experiment, the authors report an increase in neural activity in the hippocampus during both phase 1 (sensory preconditioning) and phase 2 (conditioning). In the subsequent experiment, they inhibit neural activity in the DH during phase 1 (sensory preconditioning) and the probe test, but do not include inhibition during phase 2 (conditioning). It was not clear why they didn't carry forward investigating the role of the hippocampus during phase 2 conditioning. Sensory preconditioning could occur due to the integration of the tone and shock during phase two, or retrieval and chaining of the tonelight-shock memories at test. These two possibilities cannot be differentiated based on the data. Given that we do not know at which stage the mediate learning is occurring, it would have been beneficial to additionally include inhibition of the DH during phase 2. 

Following the Reviewer’s valuable comment, we have conducted a new experiment where we have chemogenetically inhibited the CaMKII-positive neurons of the dHPC during the conditioning to explore their involvement in mediated learning formation. Notably, the inhibition of principal neurons of the dHPC during conditioning does not impair the formation ofthe mediated learning in our hands. These new results are now shown in Supplementary Figure 7G and added in the Results section (Page 13, Lines 19-23).

(3) In the final experiment, the authors report that inhibition of the dorsal hippocampus during the sensory preconditioning phase blocked mediated learning. While this may be the case, the failure to observe sensory preconditioning at test appears to be due more to an increase in baseline freezing (during the stimulus off period), rather than a decrease in freezing to the conditioned stimulus. Given the small effect, this study would benefit from an experiment validating that administration of J60 inhibited DH cells. Further, given that the authors did not observe any effect of DREADD inhibition in PV cells, it would also be important to validate successful cellular silencing in this protocol.  

According to the Reviewer comments, we have performed new experiments to validate the use of J60 to inhibit hippocampal cells that are shown in Supplementary Figure 7 E-F for CaMKII-positive neurons, in which J60 administration tends to decrease the frequency of calcium events both in the dHPC and vHPC. Furthermore, in Supplementary Figure 8 B-C we show that J60 is also able to modify calcium events in PV-positive interneurons. Although,the best method to validate the use of DREADD (i.e. to inhibit hippocampal cell activity) could be electrophysiology recordings, we lack this technique in our laboratory. Thus, in order to adress the reviewer comment, we decided to combine the DREADD modulation through J60 administration with photometry recordings, where several tendencies are confirmed. In addition, a similar approach has been used in another preprint of the lab (https://doi.org/10.1101/2025.08.29.673009), where there is an increase of phospho-PDH, a marker of neuronal inhibition upon J60 administration in the dHPC, as well as in other experiments conducted from a collaborator lab where they were able to observe a modulation of SOM-positive interneurons activity upon J60 administration (PhD defense of Miguel Sabariego, University Pompeu Fabra, Barcelona). 

Reviewer #3 (Public review): 

Summary: 

Pinho et al. investigated the role of the dorsal vs ventral hippocampus and the gender differences in mediated learning. While previous studies already established the engagement of the hippocampus in sensory preconditioning, the authors here took advantage of freely-moving fiber photometry recording and chemogenetics to observe and manipulate sub-regions of the hippocampus (dorsal vs. ventral) in a cell-specific manner. The authors first found sex differences in the preconditioning phase of a sensory preconditioning procedure, where males required more preconditioning training than females for mediating learning to manifest, and where females displayed evidence of mediated learning even when neutral stimuli were never presented together within the session. 

After validation of a sensory preconditioning procedure in mice using light and tone neutral stimuli and a mild foot shock as the unconditioned stimulus, the authors used fiber photometry to record from all neurons vs. parvalbumin_positive_only neurons in the dorsal hippocampus or ventral hippocampus of male mice during both preconditioning and conditioning phases. They found increased activity of all neurons, as well as PV+_only neurons in both sub-regions of the hippocampus during both preconditioning and conditioning phases. Finally, the authors found that chemogenetic inhibition of CaMKII+ neurons in the dorsal, but not ventral, hippocampus specifically prevented the formation of an association between the two neutral stimuli (i.e., light and tone cues), but not the direct association between the light cue and the mild foot shock. This set of data: (1) validates the mediated learning in mice using a sensory preconditioning protocol, and stresses the importance of taking sex effect into account; (2) validates the recruitment of dorsal and ventral hippocampi during preconditioning and conditioning phases; and (3) further establishes the specific role of CaMKII+ neurons in the dorsal but not ventral hippocampus in the formation of an association between two neutral stimuli, but not between a neutralstimulus and a mild foot shock. 

Strengths: 

The authors developed a sensory preconditioning procedure in mice to investigate mediated learning using light and tone cues as neutral stimuli, and a mild foot shock as the unconditioned stimulus. They provide evidence of a sex effect in the formation of light-cue association. The authors took advantage of fiber-photometry and chemogenetics to target sub-regions of the hippocampus, in a cell-specific manner and investigate their role during different phases of a sensory conditioning procedure. 

We thank the Reviewer for the extensive summary of our work and for giving interesting value to some of our findings.

Weaknesses: 

The authors went further than previous studies by investigating the role of sub-regions of the hippocampus in mediated learning, however, there are several weaknesses that should be noted: 

(1) This work first validates mediated learning in a sensory preconditioning procedure using light and tone cues as neutral stimuli and a mild foot shock as the unconditioned stimulus, in both males and females. They found interesting sex differences at the behavioral level, but then only focused on male mice when recording and manipulating the hippocampus. The authors do not address sex differences at the neural level. 

We appreciate the comment of the Reviewer. Indeed, thanks to other Reviewer comments during this revision process (see Point 1 of Reviewer #2), we performed an additional experiment that reveals that using the described protocol in female mice we observed fear generalization rather than mediated learning responding. This data pointed to the need of sex-specific changes in the behavioral protocols to measure sensory preconditioning. The revised version of the manuscript, although highlighting these sex differences in behavioral performance (see Supplementary Figure 2), is more focused in male mice and, accordingly, all photometry or chemogenetic experiments are performed using male mice. In future studies, once we are certain to have a sensory preconditioning paradigm working in female mice, it will be very interesting to study if the same hippocampal mechanisms mediating this behavior in male mice are also observed in female mice.  

(2) As expected in fear conditioning, the range of inter-individual differences is quite high. Mice that didn't develop a strong light-->shock association, as evidenced by a lower percentage of freezing during the Probe Test Light phase, should manifest a low percentage of freezing during the Probe Test Tone phase. It would interesting to test for a correlation between the level of freezing during mediated vs test phases. 

Thanks to the comment raised by the reviewer, we generated a new set of data correlating mediated and direct fear responses. As it can be observed in Supplementary Figure 3, there is a significant correlation between mediated and direct learning in male mice (i.e. the individuals that freeze more in the direct learning test, correlate with the individuals that express more fear response in the mediated learning test). In contrast, this correlation is absent in female mice, further confirming what we have explained above. We have highlighted this new analysis in the Results section (Page 11, Lines 20-24).

(3) The use of a synapsin promoter to transfect neurons in a non-specific manner does not bring much information. The authors applied a more specific approach to target PV+ neurons only, and it would have been more informative to keep with this cell-specific approach, for example by looking also at somatostatin+ inter-neurons. 

The idea behind using a pan neuronal promoter was to assess in general terms how neuronal activity in the hippocampus is engaged during different phases of the lighttone sensory preconditioning. However, the comment of the Reviewer is very pertinent and, as suggested, we have generated some new data targeting CaMKII-positive neurons (see Point 4 below). Finally, although it could be extremely interesting, we believe that targeting different interneuron subtypes is out of the scope of the present work. However, we have added this in the Discussion Section as a future perspective/limitation of our study (Page 17, Lines 9-24).   

(4) The authors observed event-related Ca2+ transients on hippocampal pan-neurons and PV+ inter-neurons using fiber photometry. They then used chemogenetics to inhibit CaMKII+ hippocampal neurons, which does not logically follow. It does not undermine the main finding of CaMKII+ neurons of the dorsal, but not ventral, hippocampus being involved in the preconditioning, but not conditioning, phase. However, observing CaMKII+ neurons (using fiber photometry) in mice running the same task would be more informative, as it would indicate when these neurons are recruited during different phases of sensory preconditioning. Applying then optogenetics to cancel the observed event-related transients (e.g., during the presentation of light and tone cues, or during the foot shock presentation) would be more appropriate.  

We have generated new photometry data to analyze the activity of CaMKII-positive neurons during the preconditioning phase to confirm their engagement during the light-tone pairings. Thus, we infused a CaMKII-GCAMP calcium sensor into the dHPC and vHPC of mice and we recorded its activity during the 6 preconditioning sessions. The new results can be found in Figure 3 and explained in the Results section (Page 12, Lines 26-36). The results clearly show an engagement of CaMKII-positive neurons during the light-tone pairing observed both in the dHPC and vHPC. Finally, although the suggestion of performing optogenetic manipulations would be very elegant, we expect to have convinced the reviewer that our chemogenetic results clearly show and are enough to demonstrate the involvement of dHPC in the formation of mediated learning in the Light-Tone sensory preconditioning paradigm. However, we have added this in the Discussion Section as a future perspective/limitation of our study (Page 17, Lines 9-24).  

(5) Probe tests always start with the "Probe Test Tone", followed by the "Probe Test Light". "Probe Test Tone" consists of an extinction session, which could affect the freezing response during "Probe Test Light" (e.g., Polack et al. (http://dx.doi.org/10.3758/s13420-013-0119-5)). Preferably, adding a group of mice with a Probe Test Light with no Probe Test Tone could help clarify this potential issue. The authors should at least discuss the possibility that the tone extinction session prior to the "Probe Test Light" could have affected the freezing response to the light cue. 

We appreciate the comment raised by the reviewer. However, we think that our direct learning responses are quite robust in all of our experiments and, thus, the impact of a possible extinction based on the tone presentation should not affect our direct learning. However, as it is an important point, we have discussed it in the Discussion Section (Page 17, Lines 12-14).  

Reviewer #4 (Public review): 

Summary 

Pinho et al use in vivo calcium imaging and chemogenetic approaches to examine the involvement of hippocampal sub-regions across the different stages of a sensory preconditioning task in mice. They find clear evidence for sensory preconditioning in male but not female mice. They also find that, in the male mice, CaMKII-positive neurons in the dorsal hippocampus: (1) encode the audio-visual association that forms in stage 1 of the task, and (2) retrieve/express sensory preconditioned fear to the auditory stimulus at test. These findings are supported by evidence that ranges from incomplete to convincing. They will be valuable to researchers in the field of learning and memory. 

We appreciate the summary of our work and all the constructive comments raised by the Reviewer, which have greatly improved the clarity and quality of our manuscript.  

Abstract 

Please note that sensory preconditioning doesn't require the stage 1 stimuli to be presented repeatedly or simultaneously. 

The reviewer is right, and we have corrected and changed that information in the revised abstract.  

"Finally, we combined our sensory preconditioning task with chemogenetic approaches to assess the role of these two hippocampal subregions in mediated learning."  This implies some form of inhibition of hippocampal neurons in stage 2 of the protocol, as this is the only stage of the protocol that permits one to make statements about mediated learning. However, it is clear from what follows that the authors interrogate the involvement of hippocampal sub-regions in stages 1 and 3 of the protocol - not stage 2. As such, most statements about mediated learning throughout the paper are potentially misleading (see below for a further elaboration of this point). If the authors persist in using the term mediated learning to describe the response to a sensory preconditioned stimulus, they should clarify what they mean by mediated learning at some point in the introduction. Alternatively, they might consider using a different phrase such as "sensory preconditioned responding". 

Considering the arguments of the Reviewer, we have modified our text in the Abstract and through the main text. Moreover, based on a comment of Reviewer #2 (Point 2) we have generated new data demonstrating that dHPC does not seem to be involved in mediated learning formation during Stage 2, as its inhibition does not impair sensory preconditioning responding. This new data can be seen in Supplementary Figure 7G.  

Introduction 

"Low-salience" is used to describe stimuli such as tone, light, or odour that do not typically elicit responses that are of interest to experimenters. However, a tone, light, or odour can be very salient even though they don't elicit these particular responses. As such, it would be worth redescribing the "low-salience" stimuli in some other terms. 

Through the revised version of the manuscript, we have replaced the term “lowsalience” by “innocuous stimuli” or avoiding any adjective as we think is not necessary.  

"These higher-order conditioning processes, also known as mediated learning, can be captured in laboratory settings through sensory preconditioning procedures2,6-11."  Higher-order conditioning and mediated learning are not interchangeable terms: e.g., some forms of second-order conditioning are not due to mediated learning. More generally, the use of mediated learning is not necessary for the story that the authors develop in the paper and could be replaced for accuracy and clarity. E.g., "These higher-order conditioning processes can be studied in the laboratory using sensory preconditioning procedures2,6-11." 

According to the Reviewer proposal, we have modified the text. 

In reference to Experiment 2, it is stated that: "However, when light and tone were separated on time (Unpaired group), male mice were not able to exhibit mediated learning response (Figure 2B) whereas their response to the light (direct learning) was not affected (Figure 2D). On the other hand, female mice still present a lower but significant mediated learning response (Figure 2C) and normal direct learning (Figure 2E). Finally, in the No-Shock group, both male (Figure 2B and 2D) and female mice (Figure 2C and 2E) did not present either mediated or direct learning, which also confirmed that the exposure to the tone or light during Probe Tests do not elicit any behavioral change by themselves as the presence of the electric footshock is required to obtain a reliable mediated and direct learning responses."  The absence of a difference between the paired and unpaired female mice should not be described as "significant mediated learning" in the latter. It should be taken to indicate that performance in the females is due to generalization between the tone and light. That is, there is no sensory preconditioning in the female mice. The description of performance in the No-shock group really shouldn't be in terms of mediated or direct learning: that is, this group is another control for assessing the presence of sensory preconditioning in the group of interest. As a control, there is no potential for them to exhibit sensory preconditioning, so their performance should not be described in a way that suggests this potential. 

All these comments are very pertinent and also raised by Reviewer #2 (Point 1, see above). In the revised version of the manuscript, we have carefully changed, when necessary, our interpretation of the results (e.g. in the case of the No-Shock group). In addition, we have generated new data that confirm that using similar conditions (i.e. 2 conditioning sessions in our SPC) in female mice we observe fear generalization and not a confident sensory preconditioning responding. In our opinion, this is not discarding the presence of mediated learning in female mice but suggesting that adapted protocols must be used in each sex. These results forced us to change the organization of the Figures but we hope the reviewer would agree with all the changes proposed. In addition, we have re-wrote a paragraph in the Discussion Section to explain these sex differences (see Page 15, lines 12-37). 

Methods - Behavior 

I appreciate the reasons for testing the animals in a new context. This does, however, raise other issues that complicate the interpretation of any hippocampal engagement: e.g., exposure to a novel context may engage the hippocampus for exploration/encoding of its features - hence, it is engaged for retrieving/expressing sensory preconditioned fear to the tone. This should be noted somewhere in the paper given that one of its aims is to shed light on the broader functioning of the hippocampus in associative processes. 

This general issue - that the conditions of testing were such as to force engagement of the hippocampus - is amplified by two further features of testing with the tone. The first is the presence of background noise in the training context and its absence in the test context. The second is the fact that the tone was presented for 30 s in stage 1 and then continuously for 180s at test. Both changes could have contributed to the engagement of the hippocampus as they introduce the potential for discrimination between the tone that was trained and tested. 

We have now added these pertinent comments in a “Study limitations” paragraph found in the Discussion Section (Page 17, Lines 9-24). Indeed, the different changes of context (including the presence of background noise) have been implemented by the fact that during the setting up of the paradigm we had problems of fear generalization (also in male mice). Similarly, differences in cue exposure between the preconditioning phase and the test phase were also decided based on important differences between previous protocols used in rats compared to how mice are responding. Certainly, mice were not able to adapt their behavioral responses when shorter time windows exposing the cue were used as it clearly happens with rats [1].

Results - Behavior 

The suggestion of sex differences based on differences in the parameters needed to generate sensory preconditioning is interesting. Perhaps it could be supported through some set of formal analyses. That is, the data in supplementary materials may well show that the parameters needed to generate sensory preconditioning in males and females are not the same. However, there needs to be some form of statistical comparison to support this point. As part of this comparison, it would be neat if the authors included body weight as a covariate to determine whether any interactions with sex are moderated by body weight.  

Regarding the comparison between male and female mice, although the comments of the Reviewer are pertinent and interesting, we think that with the new data generated is not appropriate to compare both sexes as we still have to optimize the SPC protocol for female mice. 

What is the value of the data shown in Figure 1 given that there are no controls for unpaired presentations of the sound and light? In the absence of these controls, the experiment cannot have shown that "Female and male mice show mediated learning using an auditory-visual sensory preconditioning task" as implied by its title. Minimally, this experiment should be relabelled. 

Based on the new data generated with female mice, we have decided to remove Figure 1 and re-organize the structure of the manuscript. We hope that the Reviewer would agree that this has improved the clarity of the manuscript.  

"Altogether, this data confirmed that we successfully set up an LTSPC protocol in mice and that this behavioral paradigm can be used to further study the brain circuits involved in higherorder     conditioning."  Please insert the qualifier that LTSPC was successfully established in male mice. There is no evidence of LTSPC in female mice. 

We fully agree with the Reviewer and our new findings further confirm this issue. Thus, we have changed the statement in the revised version of the manuscript.  

Results - Brain 

"Notably, the inhibition of CaMKII-positive neurons in the dHPC (i.e. J60 administration in DREADD-Gi mice) during preconditioning (Figure 4B), but not before the Probe Test 1 (Figure 4B), fully blocked mediated, but not direct learning (Figure  4D)." The right panel of Figure 4B indicates no difference between the controls and Group DPC in the percent change in freezing from OFF to ON periods of the tone. How does this fit with the claim that CaMKII-positive neurons in the dorsal hippocampus regulate associative formation during the session of tone-light exposures in stage 1 of sensory preconditioning? 

To improve the quality of the figures and to avoid possible redundancies between panels, in the new version of the manuscript, we have decided to remove all the panels regarding the percentage of change. However, in our opinion regarding the issue raised by the Reviewer, the inhibition of the dHPC clearly induced an impairment of mediated learning as animals do not change their behavior (i.e. there is no significant increase of freezing between OFF and ON periods) when the tone appears in comparison with the other two groups. The graphs indicating the percentage of change (old version of the manuscript) was a different manner to show the presence of tone- or light-induced responses in each experimental group. Thus, a significant effect (shown by # symbol) meant that in that specific experimental group there was a significant change in behavior (freezing) when the cue (tone or light) appeared compared when there was no cue (OFF period). Thus, in the old panel 4B commented by the Reviewer, in our opinion, the absence of significance in the group where the dHPC has been inhibited during thepreconditioning, compared to the other groups, where a clear significant effect can be observed, indicate an impairment of mediated learning formation. However, to avoid any confusion, we have slightly modified the text to strictly mention what is being analyzed and/or shown in the graphs and, as mentioned, the graphs of percentage of change have been removed.  

Discussion 

"When low salience stimuli were presented separated on time or when the electric footshock was absent, mediated and direct learning were abolished in male mice. In female mice, although light and tone were presented separately during the preconditioning phase, mediated learning was reduced but still present, which implies that female mice are still able to associate the two low-salience stimuli." 

This doesn't quite follow from the results. The failure of the female unpaired mice to withhold their freezing to the tone should not be taken to indicate the formation of a light-tone association across the very long interval that was interpolated between these stimulus presentations. It could and should be taken to indicate that, in female mice, freezing conditioned to the light simply generalized to the tone (i.e., these mice could not discriminate well between the tone and light). 

As discussed above, we fully agree with the Reviewer and all the manuscript has been modified as described above. 

"Indeed, our data suggests that when hippocampal activity is modulated by the specific manipulation of hippocampal subregions, this brain region is not involved during retrieval."  Does this relate to the results that are shown in the right panel of Figure 4B, where there is no significant difference between the different groups? If so, how does it fit with the results shown in the left panel of this figure, where differences between the groups are observed? 

"In line with this, the inhibition of CaMKII-positive neurons from the dorsal hippocampus, which has been shown to project to the restrosplenial cortex56, blocked the formation of mediated learning." 

Is this a reference to the findings shown in Figure 4B and, if so, which of the panels exactly? That is, one panel appears to support the claim made here while the other doesn't. In general, what should the reader make of data showing the percent change in freezing from stimulus OFF to stimulus ON periods? 

In our opinion, as pointed above, the graphs indicating the percentage of change were a different manner to show the presence of tone- or light-induced behavioral responses in each experimental group. Thus, a significant effect (shown by # symbol) meant that in this specific experimental group there was a significant change in behavior (freezing) when the cue (tone or light appear) compared when there was no cue (OFF period). Thus, in the old panel 4B commented by the Reviewer, in our opinion, the absence of significance in the group where the dHPC has been inhibited during the preconditioning, compared to the other groups where a clear significant effect can be observed, indicates an impairment of mediated learning formation. In the revised version of the manuscript, we have rephrased these sentences to stick to what the graphs are showing and, as explained, the graphs of percentage of change have been removed.

Reviewer #1 (Recommendations for the authors): 

The authors may address the following questions: 

(1) The study identifies major sex differences in the conditioning phase, with females showing faster learning. Since hormonal fluctuations can influence learning and behavior, it would be helpful for the authors to comment on whether they tracked the estrous cycle of the females and whether any potential effects of the cycle on mediated learning were considered. 

This is a relevant and important point raised by the Reviewer. In our study we did not track the estrous cycle to investigate whether it exists any effect of the cycle on mediated learning, which could be an interesting project by itself. Although in the revised version of the manuscript we provide new information regarding the mediated learning performance in male and female mice, we agree with the reviewer that sex hormones may account for the observed sex differences. However, the aim of the present work was to explore potential sex differences in mediated learning responding rather than to investigate the specific mechanisms behind these potential sex differences. 

For this reason and to avoid adding further complexity to our present study, we did not check the estrous cycle in the female mice, the testosterone levels in male mice or analyze the amount of sex hormones during different phases of the sensory preconditioning task. Indeed, we think that checking the estrous cycle in female mice would still not be enough to ascertain the role of sex hormones because checking the androgen levels in male mice would also be required. In line with this, meta-analysis of neuroscience literature using the mouse model as research subjects [2-4]  has revealed that data collected from female mice (regardless of the estrous cycle) did not vary more than the data from males. In conclusion, we think that using randomized and mixed cohorts of male and female mice (as in the present study) would provide the same degree of variability in both sexes. Nevertheless, we have added a sentence to point to this possibility in the Discussion Section (Page 15, lines 32-37). 

(2) The rationale for including parvalbumin (PV) cells in the study could be clarified. Is there prior evidence suggesting that this specific cell type is involved in mediated learning? This could apply to sensory stimuli not used in the current study.

In the revised version of the manuscript, we have better clarified why we targeted PV interneurons, specifically mentioning previous studies [5] (see Page 11, Lines 27-34). 

(3) The photometry recordings from the dHPC during the preconditioning phase, shown in Figure 3, are presented as average responses. It would be beneficial to separate the early vs. late trials to examine whether there is an increase in hippocampal activity as the associative learning progresses, rather than reporting the averaged data. Additionally, to clarify the dynamics of the dHPC in associative learning, the authors could compare the magnitude of photometry responses when light and tone stimuli are presented individually in separate sessions versus when they are presented closely in time to facilitate associative learning.

As commented above, according to the Reviewer’s comment, we have now included a new Supplementary Figure 4, which splits the photometry data by the different preconditioning and conditioning sessions. Overall, this data suggests that there are no major changes on cell activity in both hippocampal regions during the different sessions as similar light-tone-induced enhancement of activity is observed. There is only an interesting trend in the activity of Pan-Neurons over the onset of light during conditioning sessions. All this is included now in the Results Section (Page 12, Line 13-15).

(4) The authors note that PV cell responses recorded with GCaMP were similar to general hippocampal neurons, yet chemogenetic manipulations of PV cells did not impact behavior. A more detailed discussion of this discrepancy would be helpful. 

As suggested by the Reviewer, we have included additional Discussion to explain the potential discrepancy between the activity of PV interneurons assessed by photometry and its modulation by chemogenetics (see Page 16, Lines 27-33).   

(5) All fiber photometry recordings were conducted in male mice. Given the sex differences observed in associative learning, the authors could expand the study to include dHPC responses in females during both preconditioning and conditioning sessions. 

We appreciate the comment of the Reviewer. Indeed, thanks to other comments made by other Reviewers in this revision (see Point 1 of Reviewer #2), we are not still sure that we have an optimal protocol to study mediated learning in female mice due to sexspecific changes related to fear generalization. Thus, the revised version of the manuscript, although highlighting these sex differences in behavioral performance (see Supplementary Figure 2), is more focused in male mice and, accordingly, all photometry or chemogenetic experiments are performed exclusively using male mice. In future studies, once we would be sure to have a sensory preconditioning paradigm working in female mice, it will be very interesting to study if the same hippocampal mechanisms mediating this behavior in male mice are also observed in female mice. 

Minor Comments: 

(1) In the right panel of Figure 2A, females received only one conditioning session, so the "x2" should be corrected to "x1" conditioning to accurately reflect the data. 

We thank the Reviewer for the comment that has been addressed in the revised version of the manuscript.  

(2) The overall presentation of Figure 3 could be improved. For example, the y-axis in Panel B could be cut to a maximum of 3 rather than 6, which would better highlight the response data. Alternatively, including heatmap representations of the z-score responses could enhance clarity and visual impact.  

We thank the Reviewer for the comment that has been addressed providing a new format for Figures 2 and 3 in the revised version of the manuscript.   

(3) There are several grammatical errors throughout the manuscript. It is recommended that the authors use a grammar correction tool to improve the overall writing quality and readability.  

We have tried to correct the grammar through all the manuscript.  

Reviewer #2 (Recommendations for the authors):  

(1) In the abstract the authors write that sensory preconditioning requires the "repeated and simultaneous presentation of two low-salience stimuli such as a light and a tone". Previous research has shown that sensory preconditioning can still occur if the two stimuli are presented serially, rather than simultaneously. Further, the tone and the light are not necessarily "low-salience", for example, they can be loud or bright. It would be better to refer to them as innocuous. 

In the revised version of the abstract, we have included the modifications suggested by the Reviewer.   

(2) The authors develop a novel automated tool for assessing freezing behaviour in mice that correlates highly with both manual freezing and existing, open-source freeze estimation software (ezTrack). The authors should explain how the new program differs from ezTrack, or if it provides any added benefit over this existing software. 

We have added new information in the Results Section (Page 10, Lines 13-20 to better explain how the new tool to quantify freezing could improve existing software.  

(3) In Experiment 1, the authors report a sex difference in levels of freezing between male and female mice when they are only given one session of sensory preconditioning. This should be supported by a statistical comparison of levels of freezing between male and female mice. 

Based on the new results obtained with female mice, we have decided to remove the original Figure 1 of the manuscript as it is not meaningful to compare male and female mediated learning response if we do not have an optimal protocol in female mice.  

(4) Why did the authors choose to vary the duration of the stimuli across preconditioning, conditioning, and testing? During preconditioning, the light-tone compound was 30s, in conditioning the light was 10s, and at test both stimuli were presented continuously for 3 min. Did the level of freezing vary across the three-minute probe session? There is some evidence that rodents can learn the timing of stimuli and it may be the case that freezing was highest at the start of the test stimulus, when it most closely resembled the conditioned stimulus. 

Differences in cue exposure between the preconditioning phase and the test phase were decided based on important differences between previous protocols used in rats compared to how mice are responding. Indeed, mice were not able to adapt their behavioral responses when shorter time windows exposing the cue were used as it clearly happens with rats1. In addition, we have added a new graph to show the time course of the behavioral responses (see Figure 1 and 4 and Supplementary Figure 2) that correlate with the quantification of freezing responses shown by the percentage of freezing during ON and OFF periods.   

(5) The title of Experiment 1 "Female and male mice show mediated learning using an auditory-visual sensory preconditioning task" - this experiment does not demonstrate mediated learning; it merely shows that animals will freeze more in the presence of a stimulus as compared with no stimulus. This experiment lacks the necessary controls to claim mediated learning (which are presented in Experiment 2) and should therefore be retitled something more appropriate.

As stated above, based on the new results obtained with female mice, we have decided to remove the original Figure 1 of the manuscript as it is not meaningful to compare male and female mediated learning response if we do not have an optimal protocol in female mice.   

(6) In Figure 2, why does the unpaired group show less freezing to the tone than the paired group given that the tone was directly paired with the shock in both groups? 

We believe the Reviewer may have referred to the tone in error (i.e. there are no differences in the freezing observed to the tone) and (s)he might be talking about the freezing induced by the Light in the direct learning test. In this case, it is true that the direct learning (e.g. percentage of freezing) seems to be slightly lower in the unpaired group compared to the paired one, which could be due to a latent inhibition process caused by the different exposure of cues between paired and unpaired experimental groups. However, the direct learning in both groups is clear and significant and there are no significant differences between them, which makes difficult to extract any further conclusion. 

(7) The stimuli in the design schematics are quite small and hard to see, they should be enlarged for clarity. The box plots also looked stretched and the colour difference between the on and off periods is difficult to discern. 

We have included some important modification to the Figures in order to address the comments made by the Reviewer and improve its quality.   

(8) The authors do not include labels for the experimental groups (paired, unpaired, no shock) in Figures 2B, 2D, 2C, and 2E. This made it very difficult to interpret the figure.  

According to this suggestion, Figure 2 has been changed accordingly. 

(9) The levels of freezing during conditioning should be presented for all experiments.  

We have generated a new Supplementary Figure 9 to show the freezing levels during conditioning sessions. 

(10) In the final experiment, the authors wrote that mice were injected with J60 or saline, but I could not find the data for the saline animals.  

In the Results and Methods section, we have included a sentence to better explain this issue. In addition, we have added a new Supplementary Figure 7 to show the performance of all control groups.  

(11) Please list the total number of animals (per group, per sex) for each experiment.  

In the revised version of the manuscript, we have added this information in each Figure Legend.  

Reviewer #3 (Recommendations for the authors): 

I found this study very interesting, despite a few weaknesses. I have several minor comments to add, hoping that it would improve the manuscript: 

(1) The terminology used is not always appropriate/consistent. I would use "freely moving fiber photometry" or simply "fiber photometry" as calcium imaging conventionally refers to endoscopic or 2-photon calcium imaging. 

We thank the Reviewer for this comment that has been addressed and corrected in the revised version of the manuscript. 

(2) "Dorsal hippocampus mediates light-tone sensory preconditioning task in mice" suggests that a brain region mediates a task. I would rather suggest, e.g. "Dorsal hippocampus mediates light-tone association in mice" 

We thank the Reviewer for this comment that has been addressed and corrected in the revised version of the manuscript.

(3) As you are using low-salience stimuli, it would be better to also inform the readership with the light intensity used for the light cue, for replicability purposes. 

In the Methods section (Page 5, Line 30), we have added new information regarding the visual stimuli used. 

(4) If the authors didn't use a background noise during the probe tests, the tone cue could have been perceived as being louder/clearer by mice. Couldn't it have inflated the freezing response for the tone cue?  

This is an interesting comment made by the Reviewer although we do not have any data to directly answer his/her suggestion. However, the presence of the Background noise resulted necessary to set up the protocol and to change different aspects of the context through all the paradigm, which was necessary to avoid fear generalization in mice. In addition, as demonstrated before [6] , the presence of background noise is important to avoid that other auditory cue (i.e. tone) could induce fear responses by itself as the transition of noise to silence is a signal to danger for animals. 

(5) "salience" is usually used for the intensity of a stimulus, not for an association or pairing. Rather, we usually refer to the strength of an association. 

We thank the Reviewer for this comment that has been addressed and corrected in the revised version of the manuscript.

(6) Figure 3, panel A. "RCaMP Neurons", maybe "Pan-Neurons" would be more appropriate, as PV+ inter-neurons are also neurons. 

We thank the Reviewer for this comment that has been corrected accordingly.

(7) Figure 4, panel A, please add the AAV injected, and the neurons labelled in your example slice. 

We thank the Reviewer for this comment that has been corrected accordingly.

References

(1) Wong, F. S., Westbrook, R. F. & Holmes, N. M. 'Online' integration of sensory and fear memories in the rat medial temporal lobe. Elife 8 (2019). https://doi.org:10.7554/eLife.47085

(2) Prendergast, B. J., Onishi, K. G. & Zucker, I. Female mice liberated for inclusion in neuroscience and biomedical research. Neurosci Biobehav Rev 40, 1-5 (2014). https://doi.org:10.1016/j.neubiorev.2014.01.001

(3) Becker, J. B., Prendergast, B. J. & Liang, J. W. Female rats are not more variable than male rats: a meta-analysis of neuroscience studies. Biol Sex Differ 7, 34 (2016). https://doi.org:10.1186/s13293-016-0087-5

(4) Shansky, R. M. Are hormones a "female problem" for animal research? Science 364,  825-826 (2019). https://doi.org:10.1126/science.aaw7570

(5) Busquets-Garcia, A. et al. Hippocampal CB1 Receptors Control Incidental Associations. Neuron 99, 1247-1259 e1247 (2018). https://doi.org:10.1016/j.neuron.2018.08.014

(6) Pereira, A. G., Cruz, A., Lima, S. Q. & Moita, M. A. Silence resulting from the cessation of movement signals danger. Curr Biol 22, R627-628 (2012). https://doi.org:10.1016/j.cub.2012.06.015

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public Review): 

Summary: 

This paper by Schommartz and colleagues investigates the neural basis of memory reinstatement as a function of both how recently the memory was formed (recent, remote) and its development (children, young adults). The core question is whether memory consolidation processes as well as the specificity of memory reinstatement differ with development. A number of brain regions showed a greater activation difference for recent vs. remote memories at the long versus shorter delay specifically in adults (cerebellum, PHG, LOC). A different set showed decreases in the same comparison, but only in children (precuneus, RSC). The authors also used neural pattern similarity analysis to characterize reinstatement, though still in this revised paper I have substantive concerns about how the analyses were performed. While scene-specific reinstatement decreased for remote memories in both children and adults, claims about its presence cannot be made given the analyses. Gist-level reinstatement was observed in children but not adults, but I also have concerns about this analysis. Broadly, the behavioral and univariate findings are consistent with the idea memory consolidation differs between children and adults in important ways, and takes a step towards characterizing how.

Strengths: 

The topic and goals of this paper are very interesting. As the authors note, there is little work on memory consolidation over development, and as such this will be an important data point in helping us begin to understand these important differences. The sample size is great, particularly given this is an onerous, multi-day experiment; the authors are to be commended for that. The task design is also generally well controlled, for example as the authors include new recently learned pairs during each session.  

Weaknesses: 

As noted above and in my review of the original submission, the pattern similarity analysis for both item and category-level reinstatement were performed in a way that is not interpretable given concerns about temporal autocorrelation within scanning run.Unfortunately these issues remain of concern in this revision because they were not rectified. Most of my review focuses on this analytic issue, though I also outline additional concerns. 

(1) The pattern similarity analyses are largely uninterpretable due to how they were performed. 

(a) First, the scene-specific reinstatement index: The authors have correlated a neural pattern during a fixation cross (delay period) with a neural pattern associated with viewing a scene as their measure of reinstatement. The main issue with this is that these events always occurred back-to-back in time. As such, the two patterns will be similar due simply to the temporal autocorrelation in the BOLD signal. Because of the issues with temporal autocorrelation within scanning run, it is always recommended to perform such correlations only across different runs. In this case, the authors always correlated patterns extracted from the same run, and which moreover have temporal lags that are perfectly confounded with their comparison of interest (i.e., from Fig 4A, the "scene-specific" comparisons will always be back-to-back, having a very short temporal lag; "set-based" comparisons will be dispersed across the run, and therefore have a much higher lag). The authors' within-run correlation approach also yields correlation values that are extremely high - much higher than would be expected if this analysis was done appropriately. The way to fix this would be to restrict the analysis to only cross-run comparisons, which is not possible given the design. 

To remedy this, in the revision the authors have said they will refrain from making conclusions about the presence of scene-specific reinstatement (i.e., reinstatement above baseline). While this itself is an improvement from the original manuscript, I still have several concerns. First, this was not done thoroughly and at times conclusions/interpretations still seem to imply or assume the presence of scene reinstatement (e.g., line 979-985, "our research supports the presence of scene-specific reinstatement in 5-to-7-year-old children"; line 1138). 

We thank the reviewers for pointing out that there are inconsistencies in our writing. We agree that we cannot make any claims about the baseline level of scene-specific reinstatement. To reiterate, our focus is on the changes in reinstatement over time (30 minutes, 24 hours, and two weeks after learning), which showed a robust decrease. Importantly, scenespecific reinstatement indices for recent items — tested on different days — did not significantly differ, as indicated by non-significant main effects of Session (all p > .323) and Session x ROI interactions (all p > .817) in either age group. This supports our claim that temporal autocorrelation is stable and consistent across conditions and that the observed decline in scene-specific reinstatement reflects a time-dependent change in remote retrieval. We have revised the highlighted passages, accordingly, emphasizing the delay-related decrease in scene-specific reinstatement rather than its absolute magnitude. 

Second, the authors' logic for the neural-behavioural correlations in the PLSC analysis involved restricting to regions that showed significant reinstatement for the gist analysis, which cannot be done for the analogous scene-specific reinstatement analysis. This makes it challenging to directly compare these two analyses since one was restricted to a small subset of regions and only children (gist), while scene reinstatement included both groups and all ROIs. 

We thank the reviewer for pointing this out and want to clarify that it was not our intention to directly compare these analyses. For the neural-behavioral correlations, we included only those regions identified based on gist-like representations baseline, whereas for scene-specific reinstatement, we included all regions due to the absence of such a baseline. The primary aim of the PLSC analysis was to identify a set of regions that, after a stringent permutation and bootstrapping procedure, form a latent variable that explains a significant proportion of variance in behavioral performance across all participants. 

Third, it is also unclear whether children and adults' values should be directly comparable given pattern similarity can be influenced by many factors like motion, among other things. 

We thank the reviewer for raising this important point. In our multivariate analysis, we included confounding regressors specifically addressing motion-related artefacts. Following recent best practices for mitigating motion-related confounding factors in both adult and pediatric fMRI data (Ciric et al., 2017; Esteban et al., 2020; Jones et al., 2021; Satterthwaite et al., 2013), we implemented the most effective motion correction strategies. 

Importantly, our group × session interaction analysis focuses on relative changes in reinstatement over time rather than comparing absolute levels of pattern similarity between children and adults. This approach controls for potential baseline differences and instead examines whether the magnitude of delay-related changes differs across groups. We believe this warrants the comparison and ensures that our conclusions are not driven by group-level differences in baseline similarity or motion artifacts.

My fourth concern with this analysis relates to the lack of regional specificity of the effects. All ROIs tested showed a virtually identical pattern: "Scene-specific reinstatement" decreased across delays, and was greater in children than adults. I believe control analyses are needed to ensure artifacts are not driving these effects. This would greatly strengthen the authors' ability to draw conclusions from the "clean" comparison of day 1 vs. day 14. (A) The authors should present results from a control ROI that should absolutely not show memory reinstatement effects (e.g., white matter?). Results from the control ROI should look very different - should not differ between children and adults, and should not show decreases over time. 

(C) If the same analysis was performed comparing the object cue and immediately following fixation (rather than the fixation and the immediately following scene), the results should look very different. I would argue that this should not be an index of reinstatement at all since it involves something presented visually rather than something reinstated (i.e., the scene picture is not included in this comparison). If this control analysis were to show the same effects as the primary analysis, this would be further evidence that this analysis is uninterpretable and hopelessly confounded. 

We appreciate the reviewer’s suggestion to strengthen the interpretation of our findings by including appropriate control analyses to rule out non-memory-related artifacts. In response, we conducted several control analyses, detailed below, which collectively support the specificity of the observed reinstatement effects. The report of the results is included in the manuscript (line 593-619).

We checked that item reinstatement for incorrectly remembered trial did not show any session-related decline for any ROI. This indicates that the reinstatement for correctly remembered items is memory-related (see Fig. S5 for details). 

We conducted additional analyses on three subregions of the corpus callosum (the body, genu, and splenium). The results of the linear mixed-effects models revealed no significant group effect (all p > .426), indicating no differences between children and adults. In contrast, all three ROIs showed a significant main effect of Session (all p < .001). However, post hoc analyses indicated that this effect was driven by differences between the recent and the Day 14 remote condition. The main contrasts of interest – recent vs. Day 1 remote and Day 1 remote vs. Day 14 remote – were not significant (all p > .080; see Table S10.4), suggesting that, unlike in other ROIs, there was no delay-related decrease in scene-specific reinstatement in these white matter regions.

Then we repeated our analysis using the same procedure but replaced the “scene” time window with the “object” time window. The rationale for this control is that comparing the object cue to the immediately following fixation period should not reflect scene reinstatement, as the object and the reinstated scene rely on distinct neural representations. Accordingly, we did not expect a delay-related decrease in the reinstatement index. Consistent with this expectation, the analysis using the object – fixation similarity index – though also influenced by temporal autocorrelation – did not reveal any significant effect of session or delay in any ROI (all p > .059; see Table S9, S9.1).

Together, these control analyses provide converging evidence that our findings are not driven by global or non-specific signal changes. We believe that these control analyses strengthen our interpretation about delay-related decrease in scene-specific reinstatement index. 

(B) Do the recent items from day 1 vs. day 14 differ? If so, this could suggest something is different about the later scans (and if not, it would be reassuring). 

The recent items tested on day 1 and day14 do not differ (all p. > .323). This effect remains stable across all ROIs.

(b) For the category-based neural reinstatement: (1) This suffers from the same issue of correlations being performed within run. Again, to correct this the authors would need to restrict comparisons to only across runs (i.e., patterns from run 1 correlated with patterns for run 2 and so on). The authors in their response letter have indicated that because the patterns being correlated are not derived from events in close temporal proximity, they should not suffer from the issue of temporal autocorrelation. This is simply not true. For example, see the paper by Prince et al. (eLife 2022; on GLMsingle). This is not the main point of Prince et al.'s paper, but it includes a nice figure that shows that, using standard modelling approaches, the correlation between (same-run) patterns can be artificially elevated for lags as long as ~120 seconds (and can even be artificially reduced after that; Figure 5 from that paper) between events. This would affect many of the comparisons in the present paper. The cleanest way to proceed is to simply drop the within-run comparisons, which I believe the authors can do and yet they have not. Relatedly, in the response letter the authors say they are focusing mainly on the change over time for reinstatement at both levels including the gist-type reinstatement; however, this is not how it is discussed in the paper. They in fact are mainly relying on differences from zero, as children show some "above baseline" reinstatement while adults do not, but I believe there were no significant differences over time (i.e., the findings the authors said they would lean on primarily, as they are arguably the most comparable).  

We thank the reviewer for this important comment regarding the potential inflation of similarity values due to within-run comparisons.

To address the reviewer’s concern, we conducted an additional cross-run analysis for all correctly retrieved trials. The approach restricted comparisons to non-overlapping runs (run1run2, run2-run3, run1-run3). This analysis revealed robust gist-like reinstatement in children for remote Day 14 memories in the mPFC (p = .035) and vlPFC (p = .0007), in adults’ vlPFC remote Day 1 memories (p = .029), as well as in children and adults remote Day 1 memories in LOC (p < .02). A significant Session effect in both regions (mPFC: p = .026; vlPFC: p = .002) indicated increased reinstatement for long delay (Day 14) compared to short-delay and recent session (all p < .05). Given that the cross-run results largely replicate and reinforce the effects found previously with within-run, we believe that combining both sources of information is methodologically justified and statistically beneficial. Specifically, both approaches independently identified significant gist-like reinstatement in children’s mPFC and vlPFC (although within-run vlPFC effect (short delay: p = .038; long delay p = .047) did not survive multiple comparisons), particularly for remote memories. Including both withinrun and between-run comparisons increases the number of unique, non-repeated trial pairs, improving statistical power without introducing redundancy. While we acknowledge that same-run comparisons may be influenced by residual autocorrelation (as shown by Prince et al. 2022, eLife), we believe that our design mitigates this risk through consistency between within-run and cross-run results, long inter-trial intervals, and trial-wise estimation of activation. We have adjusted the manuscript, accordingly, reporting the combined analysis. We also report cross-run and within-run analysis separately in supplementary materials (Tables S12.1, S12.2, showing that they converge with the cross-run results and thus strengthen rather than dilute the findings. 

As suggested, we now explicitly highlight the change over time as the central finding. We observe a clear increase in gist-like reinstatement from recent to remote memories in children, particularly in mPFC and vlPFC. These effects based on combined within- and cross-run comparisons, are now clearly stated in the main results and interpreted in the discussion accordingly. 

(2) This analysis uses a different approach of comparing fixations to one another, rather than fixations to scenes. In their response letter and the revised paper, the authors do provide a bit of reasoning as to why this is the most sensible. However, it is still not clear to me whether this is really "reinstatement" which (in my mind) entails the re-evoking of a neural pattern initially engaged during perception. Rather, could this be a shared neural state that is category specific? 

We thank the reviewer for raising this important conceptual point about whether our findings reflect reinstatement in the classical sense — namely, the reactivation of perceptual neural patterns — or a shared, category-specific state.

While traditional definitions of reinstatement emphasize item-specific reactivation (e.g., Ritchey et al., 2013; Xiao et al., 2017) it is increasingly recognized that memory retrieval can also involve the reactivation of abstracted, generalized, or gist-like representations, especially as memories consolidate. Our analysis follows this view, aimed to capture how memory representations evolve over time, particularly in development.

Several studies support this broader notion of gist-like reinstatement. For instance, Chen et al. (2017) showed that while event-specific patterns were reinstated across the default mode network and medial temporal lobe, inter-subject recall similarity exceeded encodingretrieval similarity, suggesting transformation and abstraction beyond perceptual reinstatement. Zhuang et al. (2021) further showed that loss of neural distinctiveness in the

MTL over time predicted false memories, linking neural similarity to representational instability. This aligns with our finding that greater gist-like reinstatement is associated with lower memory accuracy.

Ye et al. (2020) discuss how memory representations are reshaped post-encoding — becoming more differentiated, integrated, or weakened depending on task goals and neural resources. While their work focuses on adults, our previous findings (Schommartz et al., 2023) suggest that children’s neural systems (the same sample) are structurally immature, making them more likely to rely on gist-based consolidation (see Fandakova et al., 2019). Adults, by contrast, may retain more item-specific traces.

Relatedly, St-Laurent & Buchsbaum (2019) show that with repeated encoding, neural memory representations become increasingly distinct from perception, suggesting that reinstatement need not mimic perception. We agree that reinstatement does not always reflect reactivation of low-level sensory patterns, particularly over long delays or in developing brains.

Finally, while we did not correlate retrieval patterns directly with perceptual encoding patterns, we assessed neural similarity among retrieved items within vs. between categories, based on non-repeated, independently sampled trials. This approach is intended to capture the structure and delay-related transformation of mnemonic representations, especially in terms of how they become more schematic or gist-like over time. Our findings align conceptually with the results of Kuhl et al. (2012), who used MVPA to show that older and newer visual memories can be simultaneously reactivated during retrieval, with greater reactivation of older memories interfering with retrieval accuracy for newer memories. Their work highlights how overlapping category-level representations in ventral temporal cortex can reflect competition among similar memories, even in the absence of item-specific cues. In our developmental context, we interpret the increased neural similarity among category members in children as possibly reflecting such representational overlap or competition, where generalized traces dominate over item-specific ones. This pattern may reflect a shift toward efficient but less precise retrieval, consistent with developmental constraints on memory specificity and consolidation.

In this context, we view our findings as evidence of memory trace reorganization — from differentiated, item-level representations toward more schematic, gist-like neural patterns (Sekeres et al., 2018), particularly in children. Our cross-run analyses further confirm that this is not an artifact of same-run correlations or low-level confounds. We have clarified this distinction and interpretation throughout the revised manuscript (see lines 144-158; 1163-1170).

In any case, I think additional information should be added to the text to clarify that this definition differs from others in the literature. The authors might also consider using some term other than reinstatement. Again (as I noted in my prior review), the finding of no category-level reinstatement in adults is surprising and confusing given prior work and likely has to do with the operationalization of "reinstatement" here. I was not quite sure about the explanation provided in the response letter, as category-level reinstatement is quite widespread in the brain for adults and is robust to differences in analytic procedures etc. 

We agree that our operationalization of "reinstatement" differs from more conventional uses of the term, which typically involve direct comparisons between encoding and retrieval phases, often with item-level specificity. As our analysis is based on similarity among retrieval-phase trials (fixation-based activation patterns) and focuses on within- versus between-category neural similarity, we agree that the term reinstatement may suggest a stronger encoding–retrieval mapping than we are claiming.

To avoid confusion and overstatement, we have revised the terminology throughout the manuscript: we now refer to our measure as “gist-like representations” rather than “gist-like reinstatement.” This change better reflects the nature of our analysis — namely, that we are capturing shared neural patterns among category-consistent memories that may reflect reorganized or abstracted traces, especially after delay and in development.

As the reviewer rightly points out, category-level reinstatement is well documented in adults (e.g., Kuhl & Chun, 2014; Tompary et al., 2020; Tompary & Davachi, 2017). The absence of such effects in our adult group may indeed reflect differences in study design, particularly our use of non-repeated, cross-trial comparisons based on fixation events. It may also reflect different consolidation strategies, with adults preserving more differentiated or item-specific representations, while children form more schematic or generalizable representations — a pattern consistent with our interpretation and supported by prior work (Fandakova et al., 2019; Sekeres et al., 2018) 

We have updated the relevant sections of the manuscript (Results, Discussion (particularly lines 1163- 1184), and Figure captions) to clarify this terminology shift and explicitly contrast our approach with more standard definitions of reinstatement. We hope this revision provides the needed conceptual clarity while preserving the integrity of our developmental findings.

(3) Also from a theoretical standpoint-I'm still a bit confused as to why gist-based reinstatement would involve reinstatement of the scene gist, rather than the object's location (on the screen) gist. Were the locations on the screen similar across scene backgrounds from the same category? It seems like a different way to define memory retrieval here would be to compare the neural patterns when cued to retrieve the same vs. similar (at the "gist" level) vs. different locations across object-scene pairs. This is somewhat related to a point from my review of the initial version of this manuscript, about how scene reinstatement is not necessary. The authors state that participants were instructed to reinstate the scene, but that does not mean they were actually doing it. The point that what is being measured via the reinstatement analyses is actually not necessary to perform the task should be discussed in more detail in the paper. 

We appreciate the reviewer’s thoughtful theoretical question regarding whether our measure of “gist-like representations” might reflect reinstatement of spatial (object-location) gist, rather than scene-level gist. We would like to clarify several key points about our task design and interpretation:

(1) Object locations were deliberately varied and context dependent.

In our stimulus set, each object was embedded in a rich scene context, and the locations were distributed across six distinct possible areas within each scene, with three possible object placements per location. These placements were manually selected to ensure realistic and context-sensitive positioning of objects within the scenes. Importantly, locations were not fixed across scenes within a given category. For example, objects placed in “forest” scenes could appear in different screen locations across different scene exemplars (e.g., one in the bottom-left side, another floating above). Therefore, the task did not introduce a consistent spatial schema across exemplars from the same scene category that could give rise to a “location gist.”

(2) Scene categories provided consistent high-level contextual information.

By contrast, the scene categories (e.g., farming, forest, indoor, etc.) provided semantically coherent and visually rich contextual backgrounds that participants could draw upon during retrieval. This was emphasized in the instruction phase, where participants were explicitly encouraged to recall the whole scene based on the stories they created during learning (not just the object or its position). While we acknowledge that we cannot directly verify the reinstated content, this instruction aligns with prior studies showing that scene and context reinstatement can occur even without direct task relevance (e.g., Kuhl & Chun, 2014; Ritchey et al., 2013).

(3) Our results are unlikely to reflect location-based reinstatement.

If participants had relied on a “location gist” strategy, we would have expected greater neural similarity across scenes with similar spatial layouts, regardless of category. However, our design avoids this confound by deliberately varying locations across exemplars within categories. Additionally, our categorical neural similarity measure contrasted within-category vs. between-category comparisons — making it sensitive to shared contextual or semantic structure, not simply shared screen positions.

Considering this, we believe that the neural similarity observed in the mPFC and vlPFC in children at long delay reflects the emergence of scene-level, gist-like representations, rather than low-level spatial regularities. Nevertheless, we now clarify this point in the manuscript and explicitly discuss the limitation that reinstatement of scene context was encouraged but not required for successful task performance.

Future studies could dissociate spatial and contextual components of reinstatement more directly by using controlled spatial overlap or explicit location recall conditions. However, given the current task structure, location-based generalization is unlikely to account for the category-level similarity patterns we observe.

(2) Inspired by another reviewer's comment, it is unclear to me the extent to which age group differences can be attributed to differences in age/development versus memory strength. I liked the other reviewer's suggestions about how to identify and control for differences in memory strength, which I don't think the authors actually did in the revision. They instead showed evidence that memory strength does seem to be lower in children, which indicates this is an interpretive confound. For example, I liked the reviewer's suggestion of performing analyses on subsets of participants who were actually matched in initial learning/memory performance would have been very informative. As it is, the authors didn't really control for memory strength adequately in my opinion, and as such their conclusions about children vs. adults could have been reframed as people with weak vs. strong memories. This is obviously a big drawback given what the authors want to conclude. Relatedly, I'm not sure the DDM was incorporated as the reviewer was suggesting; at minimum I think the authors need to do more work in the paper to explain what this means and why it is relevant. (I understand putting it in the supplement rather

than the main paper, but I still wanted to know more about what it added from an interpretive perspective.) 

We appreciate the reviewer’s thoughtful concerns regarding potential confounding effects of memory strength on the observed age group differences. This is indeed a critical issue when interpreting developmental findings.

While we agree that memory strength differs between children and adults — and our own DDM-based analysis confirms this, mirroring differences observed in accuracy — we would like to emphasize that these differences are not incidental but rather reflect developmental changes in the underlying memory system. Given the known maturation of both structural and functional memory-related brain regions, particularly the hippocampus and prefrontal cortex, we believe it would be theoretically inappropriate to control for memory strength entirely, as doing so would remove variance that is central to the age-related neural effects we aim to understand.

To address the reviewer's concern empirically, we conducted an additional control analysis in which we subsampled children to include only those who reached learning criterion after two cycles (N = 28 out of 49 children, see Table S1.1, S1.2, Figure S1, Table S9.1), thereby selecting a high-performing subgroup. Importantly, this subsample replicated behavioral and neural results to the full group. This further suggests that the observed age group differences are not merely driven by differences in memory strength.

As abovementioned, the results of the DDM support our behavioral findings, showing that children have lower drift rates for evidence accumulation, consistent with weaker or less accessible memory representations. While these results are reported in the Supplementary Materials (section S2.1, Figure S2, Table S2), we agree that their interpretive relevance should be more clearly explained in the main text. We have therefore updated the Discussion section to explicitly state how the DDM results provide converging evidence for our interpretation that developmental differences in memory quality — not merely strategy or task performance — underlie the observed neural differences (see lines 904-926).

In sum, we view memory strength not as a confound to be removed, but as a meaningful and theoretically relevant factor in understanding the emergence of gist-like representations in children. We have clarified this interpretive stance in the revised manuscript and now discuss the role of memory strength more explicitly in the Discussion.

(3) Some of the univariate results reporting is a bit strange, as they are relying upon differences between retrieval of 1- vs. 14-day memories in terms of the recent vs. remote difference, and yet don't report whether the regions are differently active for recent and remote retrieval. For example in Figure 3A, neither anterior nor posterior hippocampus seem to be differentially active for recent vs. remote memories for either age group (i.e., all data is around 0). Precuneus also interestingly seems to show numerically recent>remote (values mostly negative), whereas most other regions show the opposite. This difference from zero (in either direction) or lack thereof seems important to the message. In response to this comment on the original manuscript, the authors seem to have confirmed that hippocampal activity was greater during retrieval than implicit baseline. But this was not really my question - I was asking whether hippocampus is (and other ROIs in this same figure are) differently engaged for recent vs. remote memories.

We thank the reviewer for bringing up this important point. Our previous analysis showed that both anterior and posterior regions of the hippocampus, anterior parahippocampal gyrus and precuneus exhibited significant activation from zero in children and adults for correctly remembered items (see Fig. S2, Table S7 in Supplementary Materials). Based on your suggestion, our additional analysis showed: 

(i) The linear mixed-effects model for correctly remembered items showed no significant interaction effects (group x session x memory age (recent, remote)) for the anterior hippocampus (all p > .146; see Table S7.1).

(ii) For the posterior hippocampus, we observed a significant main effect of group (F(1,85),   = 5.62, p = .038), showing significantly lower activation in children compared to adults (b = .03, t = -2.34, p = .021). No other main or interaction effects were significant (all p > .08; see Table S7.1).

(iii) For the anterior PHG, that also showed no significant remote > recent difference, the model showed that there was indeed no difference between remote and recent items across age groups and delays (all p > .194; Table S7.1). 

Moreover, when comparing recent and remote hippocampal activation directly, there were no significant differences in either group (all FDR-adjusted p > .116; Table S7.2), supporting the conclusion that hippocampal involvement was stable across delays for successfully retrieved items. 

In contrast, analysis of unsuccessfully remembered items showed that hippocampal activation was not significantly different from zero in either group (all FDR-adjusted p > .052; Fig. S2.1, Table S7.1), indicating that hippocampal engagement was specific to successful memory retrieval.

To formally test whether hippocampal activation differs between remembered and forgotten items, we ran a linear mixed-effects model with Group, Memory Success (remembered vs. forgotten), and ROI (anterior vs. posterior hippocampus) as fixed effects. This model revealed a robust main effect of memory success (F(1,1198) = 128.27, p < .001), showing that hippocampal activity was significantly higher for remembered compared to forgotten items (b = .06, t(1207) = 11.29, p < .001; Table S7.3). 

As the reviewer noted, precuneus activation was numerically higher for recent vs. remote items, and this was confirmed in our analysis. While both recent and remote retrieval elicited significantly above-zero activation in the precuneus (Table S7.2), activation for recent items was significantly higher than for remote items, consistent across both age groups.

Taken together, these analyses support the conclusion that hippocampal involvement in successful retrieval is sustained across delays, while other ROIs such as the precuneus may show greater engagement for more recent memories. We have now updated the manuscript text ( lines 370-390) and supplementary materials to reflect these findings more clearly, as well as to clarify the distinction between activation relative to baseline and memory-agerelated modulation.

(4) Related to point 3, the claims about hippocampus with respect to multiple trace theory feel very unsupported by the data. I believe the authors want to conclude that children's memory retrieval shows reliance on hippocampus irrespective of delay, presumably because this is a detailed memory task. However the authors have not really shown this; all they have shown is that hippocampal involvement (whatever it is) does not vary by delay. But we do not have compelling evidence that the hippocampus is involved in this task at all. That hippocampus is more active during retrieval than implicit baseline is a very low bar and does not necessarily indicate a role in memory retrieval. If the authors want to make this claim, more data are needed (e.g., showing that hippocampal activity during retrieval is higher when the upcoming memory retrieval is successful vs. unsuccessful). In the absence of this, I think all the claims about multiple trace theory supporting retrieval similarly across delays and that this is operational in children are inappropriate and should be removed. 

We thank the reviewer for pointing this out. We agree that additional analysis of hippocampal activity during successful and unsuccessful memory retrieval is warranted. This will provide stronger support for our claim that strong, detailed memories during retrieval rely on the hippocampus in both children and adults. Our previously presented results on the remote > recent univariate signal difference in the hippocampus (p. 14-18; lines 433-376, Fig. 3A) show that this difference does not vary between children and adults, or between Day 1 and Day 14. Our further analysis showed that both anterior and posterior regions of the hippocampus exhibited significant activation from zero in children and adults for correctly remembered items (see Fig. S2, Table S7 in Supplementary Materials). Based on your suggestion, our recent additional analysis showed:

(i) For forgotten items, we did not observe any activation significantly higher than zero in either the anterior or posterior hippocampus for recent and remote memory on Day 1 and Day 14 in either age group (all p > .052 FDR corrected; see Table S7.1, Fig. S2.1).

(ii) After establishing no difference between recent and remote activation across and between sessions (Day 1, Day 14), we conducted another linear mixed-effects model with group x memory success (remembered, forgotten) x region (anterior hippocampus, posterior hippocampus), with subject as a random effect. The model showed no significant effects for the memory success x region interaction (F = 1.12(1,1198), p = .289) and no significant group x memory success x region interaction (F = .017(1,1198), p = .895). However, we observed a significant main effect of memory success (F = 128.27(1,1198), p < .001), indicating significantly higher hippocampal activation for remembered compared to forgotten items (b = .06, t = 11.29, p <.001; see Table S7.3).

(iii) Considering the comparatively low number of incorrect trials for recent items in the adult group, we reran this analysis only for remote items. Similarly, the model showed no significant effects for the memory success x region interaction (F = .72(1,555), p = .398) and no significant group x memory success x region interaction (F = .14(1,555), p = .705). However, we observed a significant main effect of memory success (F = 68.03(1,555), p < .001), indicating significantly higher hippocampal activation for remote remembered compared to forgotten items (b = .07, t = 8.20, p <.001; see Table S7.3).

Taken together, our results indicate that significant hippocampal activation was observed only for correctly remembered items in both children and adults, regardless of memory age and session. For forgotten items, we did not observe any significant hippocampal activation in either group or delay. Moreover, hippocampal activation was significantly higher for remembered compared to forgotten memories. This evidence supports our conclusions regarding the Multiple Trace and Trace Transformation Theories, suggesting that the hippocampus supports retrieval similarly across delays, and provides novel evidence that this process is operational in both children and adults. This aligns also with Contextual Bindings Theory, as well as empirical evidence by Sekeres, Winokur, & Moscovitch (2018), among others. We have added this information to the manuscript.

(5) There are still not enough methodological details in the main paper to make sense of the results. Some of these problems were addressed in the revision but others remain. For example, a couple of things that were unclear: that initially learned locations were split, where half were tested again at day 1 and the other half at day 14; what specific criterion was used to determine to pick the 'well-learned' associations that were used for comparisons at different delay periods (object-scene pairs that participants remembered accurately in the last repetition of learning? Or across all of learning?). 

We thank the reviewer for pointing this out. The initially learned object-scene associations on Day 0 were split in two halves based on  their categories before the testing. Specifically, half of the pairs from the first set and half of the pairs from the second set of 30 object-scene associations were used to create the set 30 remote pair for Day 1 testing. A similar procedure was repeated for the remaining pairs to create a set of remote object-scene associations for Day 14 retrieval. We tried to equally distribute the categories of pairs between the testing sets. We added this information to the methods section of the manuscript (see p. 47, lines 12371243). In addition, the sets of association for delay test on Day 1 and Day 14 were not based on their learning accuracy. Of note, the analysis of variance revealed that there was no difference in learning accuracy between the two sets created for delay tests in either age group (children: p = .23; adults  p = .06). These results indicate that the sets were comprised of items learned with comparable accuracy in both age groups. 

(6) In still find the revised Introduction a bit unclear. I appreciated the added descriptions of different theories of consolidation, though the order of presented points is still a bit hard to follow. Some of the predictions I also find a bit confusing as laid out in the introduction. (1) As noted in the paper multiple trace theory predicts that hippocampal involvement will remain high provided memories retained are sufficiently high detail. The authors however also predict that children will rely more on gist (than detailed) memories than adults, which would seem to imply (combined with the MTT idea) that they should show reduced hippocampal involvement over time (while in adults, it should remain high). However, the authors' actual prediction is that hippocampus will show stable involvement over time in both kids and adults. I'm having a hard time reconciling these points. (2) With respect to the extraction of gist in children, I was confused by the link to Fuzzy Trace Theory given the children in the present study are a bit young to be showing the kind of gist extraction shown in the Brainerd & Reyna data. Would 5-7 year olds not be more likely to show reliance on verbatim traces under that framework? Also from a phrasing perspective, I was confused about whether gist-like information was something different from just gist in this sentence: "children may be more inclined to extract gist information at the expense of detailed or gist-like information." (p. 8) - is this a typo? 

We thank the reviewer for this thoughtful observation. 

Our hypothesis of stable hippocampal engagement over time was primarily based on Contextual Binding Theory (Yonelinas et al., 2019), and the MTT, supported by the evidence provided by Sekeres et al., 2018, which posits that the hippocampus continues to support retrieval when contextual information is preserved, even for older, consolidated memories. Given that our object-location associations were repeatedly encoded and tied to specific scene contexts, we believe that retrieval success for both recent and remote memories likely involved contextual reinstatement, leading to sustained hippocampal activity. Also in accordance with the MTT and related TTT, different memory representations may coexist, including detailed and gist-like memories. Therefore, we suggest that children may not rely on highly detailed item-specific memory, but rather on sufficiently contextualized schematic traces, which still engage the hippocampus. This distinction is now made clearer in the Introduction (see lines 223-236).

We appreciate the reviewer’s point regarding Fuzzy Trace Theory (Brainerd & Reyna, 2002). Indeed, in classic FTT, young children are thought to rely more on verbatim traces due to immature gist extraction mechanisms (primarily from verbal material). However, we use the term “gist-like representations” to refer to schematic or category-level retrieval that emerges through structured, repeated learning (as in our task). This form of abstraction may not require full semantic gist extraction in the FTT sense but may instead reflect consolidation-driven convergence onto shared category-level representations — especially when strategic resources are limited. We now clarify this distinction and revise the ambiguous sentence with typo (“at the expense of detailed or gist-like information”) to better reflect our intended meaning (see p.8).

(7) For the PLSC, if I understand this correctly, the profiles were defined for showing associations with behaviour across age groups. (1) As such, is it not "double dipping" to then show that there is an association between brain profile and behaviour-must this not be true by definition? If I am mistaken, it might be helpful to clarify this in the paper. (2) In addition, I believe for the univariate and scene-specific reinstatement analyses these profiles were defined across both age groups. I assume this doesn't allow for separate definition of profiles across the two group (i.e., a kind of "interaction"). If this is the case, it makes sense that there would not be big age differences... the profiles were defined for showing an association across all subjects. If the authors wanted to identify distinct profiles in children and adults they may need to run another analysis. 

We thank the reviewer for this thoughtful comment. 

(1) We agree that showing the correlation between the latent variable and behavior may be redundant, as the relationship is already embedded in the PLSC solution and quantified by the explained variance. Our intention was merely to visualize the strength of this relationship. In hindsight, we agree that this could be misinterpreted, and we have removed the additional correlation figure from the manuscript.

We also see the reviewer’s point that, given the shared latent profile across groups, it is expected that the strength of the brain-behavior relationship does not differ between age groups. Instead, to investigate group differences more appropriately, we examined whether children and adults differed in their expression of the shared latent variable (i.e., brain scores). This analysis revealed that children showed significantly lower brain scores than adults both in short delay, t(83) = -4.227, p = .0001, and long delay, t(74) = -5.653, p < .001, suggesting that while the brain-behavior profile is shared, its expression varies by group. We have added this clarification to the Results section (p. 19-20) of the revised manuscript. 

(2) Regarding the second point, we agree with the reviewer that defining the PLS profiles across both age groups inherently limits the ability to detect group-specific association, as the resulting latent variables represent shared pattern across the full sample. To address this, we conducted additional PLS analyses separately within each age group to examine whether distinct neural upregulation profiles (remote > recent) emerge for short and long delay conditions.

These within-group analyses, however, were based on smaller subsamples, which reduced statistical power, especially when using bootstrapping to assess the stability of the profiles. For the short delay, although some regions reached significance, the overall latent variables did not reach conventional thresholds for stability (all p > .069), indicating that the profiles were not robust. This suggests that within-group PLS analyses may be underpowered to detect subtle effects, particularly when modelling neural upregulation (remote > recent), which may be inherently small.

Nonetheless, when we exploratively applied PLSC separately within each group using recent and remote activity levels against the implicit baseline (rather than the contrast remote > recent) and its relation to memory performance, we observed significant and stable latent variables in both children and adults. This implies that such contrasts (vs. baseline) may be more sensitive and better suited to detect meaningful brain–behavior relationships within age groups. We have added this clarification to the Results sections of the manuscript to highlight the limitations of within-group contrasts for neural upregulation. 

Author response image 1.

(3) Also, as for differences between short delay brain profile and long delay brain profile for the scene-specific reinstatement - there are 2 regions that become significant at long delay that were not significant at a short delay (PC, and CE). However, given there are ceiling effects in behaviour at the short but not long delay, it's unclear if this is a meaningful difference or just a difference in sensitivity. Is there a way to test whether the profiles are statistically different from one another?

We thank the reviewer for this comment. To better illustrate differential profiles also for high memory accuracy after immediate delay (30 minutes delay), we added the immediate (30 minutes delay) condition as a third reference point, given the availability of scene-specific reinstatement data at this time point. Interestingly, the immediate reinstatement profile revealed a different set of significant regions, with distinct expression patterns compared to both the short and long delay conditions. This supports the view that scene-specific reinstatement is not static but dynamically reorganized over time.

Regarding the ceiling effect at short delay, we acknowledge this as a potential limitation. However, we note that our primary analyses were conducted across both age groups combined, and not solely within high-performing individuals. As such, the grouping may mitigate concerns that ceiling-level performance in a subset of participants unduly influenced the overall reinstatement profile. Moreover, we observed variation in neural reinstatement despite ceiling-level behavior, suggesting that the neural signal retains sensitivity to consolidation-related processes even when behavioral accuracy is near-perfect.

While we agree that formal statistical comparisons of reinstatement profiles across delays (e.g., using representational profile similarity or interaction tests) could be an informative direction, we feel that this goes beyond the scope of the current manuscript. 

(4) As I mentioned above, it also was not ideal in my opinion that all regions were included for the scene-specific reinstatement due to the authors' inability to have an appropriate baseline and therefore define above-chance reinstatement. It makes these findings really challenging to compare with the gist reinstatement ones. 

We appreciate the reviewer’s comment and agree that the lack of a clearly defined baseline for scene-specific reinstatement limits our ability to determine whether these values reflect above-chance reinstatement. However, we would like to clarify that we do not directly compare the magnitude of scene-specific reinstatement to that of gist-like reinstatement in our analyses or interpretations. These two analyses serve complementary purposes: the scenespecific analysis captures trial-unique similarity (within-item reinstatement), while the gistlike analysis captures category-level representational structure (across items). Because they differ not only in baseline assumptions but also in analytical scope and theoretical interpretation, our goal was not to compare them directly, but rather to explore distinct but co-existing representational formats that may evolve differently across development and delay.

(8) I would encourage the authors to be specific about whether they are measuring/talking about memory representations versus reinstatement, unless they think these are the same thing (in which case some explanation as to why would be helpful). For example, especially under the Fuzzy Trace framework, couldn't someone maintain both verbatim and gist traces of a memory yet rely more on one when making a memory decision? 

We thank the reviewer for pointing out the importance of conceptual clarity when referring to memory representations versus reinstatement. We agree that these are distinct but related concepts: in our framework, memory representations refer to the neural content stored as a result of encoding and consolidation, whereas reinstatement refers to the reactivation of those representations during retrieval. Thus, reinstatement serves as a proxy for the underlying memory representation — it is how we measure or infer the nature (e.g., specificity, abstraction) of the stored content.

Under Fuzzy Trace Theory, it is indeed possible for both verbatim and gist representations to coexist. Our interpretation is not that children lack verbatim traces, but rather that they are more likely to rely on schematic or gist-like representations during retrieval, especially after a delay. Our use of neural pattern similarity (reinstatement) reflects which type of representation is being accessed, not necessarily which traces exist in parallel.

To avoid ambiguity, we have revised the manuscript to more explicitly distinguish between reinstatement (neural reactivation) and the representational format (verbatim vs. gist-like), especially in the framing of our hypotheses and interpretation of age group differences.

(9) With respect to the learning criteria - it is misleading to say that "children needed between two to four learning-retrieval cycles to reach the criterion of 83% correct responses" (p. 9). Four was the maximum, and looking at the Figure 1C data it appears as though there were at least a few children who did not meet the 83% minimum. I believe they were included in the analysis anyway? Please clarify. Was there any minimum imposed for inclusion?

We thank the reviewer for pointing this out. As stated in Methods Section (p. 50, lines 13261338) “These cycles ranged from a minimum of two to a maximum of four.<…> The cycles ended when participants provided correct responses to 83% of the trials or after the fourth cycle was reached.” We have corrected the corresponding wording in the Results section (line 286-289) to reflect this more accurately. Indeed, five children did not reach the 83% criterion but achieved final performance between 70 and 80% after the fourth learning cycle. These participants were included in this analysis for two main reasons:

(1) The 83% threshold was established during piloting as a guideline for how many learningretrieval cycles to allow, not a strict learning criterion. It served to standardize task continuation, rather than to exclude participants post hoc.

(2) The performance of these five children was still well above chance level (33%), indicating meaningful learning. Excluding them would have biased the sample toward higherperforming children and reduced the ecological validity of our findings. Including them ensures a more representative view of children’s performance under extended learning conditions.

(10) For the gist-like reinstatement PLSC analysis, results are really similar a short and long delays and yet some of the text seems to implying specificity to the long delay. One is a trend and one is significant (p. 31), but surely these two associations would not be statistically different from one another?  

We agree with the reviewer that the associations at short and long delays appeared similar. While a formal comparison (e.g., using a Z-test for dependent correlations) would typically be warranted, in the reanalyzed dataset only the long delay profile remains statistically significant, which limits the interpretability of such a comparison. 

(11) As a general comment, I had a hard time tying all of the (many) results together. For example adults show more mature neocortical consolidation-related engagement, which the authors say is going to create more durable detailed memories, but under multiple trace theory we would generally think of neocortical representations as providing more schematic information. If the authors could try to make more connections across the different neural analyses, as well as tie the neural findings in more closely with the behaviour & back to the theoretical frameworks, that would be really helpful.  

We thank the reviewer for this valuable suggestion. We have revised the discussion section to more clearly link the behavioral and neural findings and to interpret them in light of existing consolidation theories for better clarity. 

Reviewer #2 (Public Review): 

Schommartz et al. present a manuscript characterizing neural signatures of reinstatement during cued retrieval of middle-aged children compared to adults. The authors utilize a paradigm where participants learn the spatial location of semantically related item-scene memoranda which they retrieve after short or long delays. The paradigm is especially strong as the authors include novel memoranda at each delayed time point to make comparisons across new and old learning. In brief, the authors find that children show more forgetting than adults, and adults show greater engagement of cortical networks after longer delays as well as stronger item-specific reinstatement. Interestingly, children show more category-based reinstatement, however, evidence supports that this marker may be maladaptive for retrieving episodic details. The question is extremely timely both given the boom in neurocognitive research on the neural development of memory, and the dearth of research on consolidation in this age group. Also, the results provide novel insights into why consolidation processes may be disrupted in children. 

We thank the reviewer for the positive evaluation.

Comments on the revised version: 

I carefully reviewed not only the responses to my own reviews as well as those raised by the other reviewers. While they addressed some of the concerns raised in the process, I think many substantive concerns remain. 

Regarding Reviewer 1: 

The authors point that the retrieval procedure is the same over time and similarly influenced by temporal autocorrelations, which makes their analysis okay. However, there is a fundamental problem as to whether they are actually measuring reinstatement or they are only measuring differences in temporal autocorrelation (or some non-linear combination of both). The authors further argue that the stimuli are being processed more memory wise rather than perception wise, however, I think there is no evidence for that and that perception-memory processes should be considered on a continuum rather than as discrete processes. Thus, I agree with reviewer 1 that these analyses should be removed. 

We thank the reviewer for raising this important question. We would like to clarify a few key points regarding temporal autocorrelation and reinstatement.

During the fixation window, participants were instructed to reinstate the scene and location associated with the cued object from memory. This task was familiar to them, as they had been trained in retrieving locations within scenes. Our analysis aims to compare the neural representations during this retrieval phase with those when participants view the scene, in order to assess how these representations change in similarity over time, as memories become less precise.

We acknowledge that temporal proximity can lead to temporal autocorrelation. However, evidence suggests that temporal autocorrelation is consistent and stable across conditions (Gautama & Van Hulle, 2004; Woolrich et al., 2004). Shinn & Lagalwar (2021)further demonstrated that temporal autocorrelation is highly reliable at both the subject and regional levels. Given that we analyze regions of interest (ROIs) separately, potential spatial variability in temporal autocorrelation is not a major concern.

No difference between item-specific reinstatement for recent items on day 1 and day 14 (which were merged) for further delay-related comparison also suggests that the reinstatement measure was stable for recent items even sampled at two different testing days. 

Importantly, we interpret the relative change in the reinstatement index rather than its absolute value.

In addition, when we conducted the same analysis for incorrectly retrieved memories, we did not observe any delay-related decline in reinstatement (see p. 25, lines 623-627). This suggests that the delay-related changes in reinstatement are specific to correctly retrieved memories. 

Finally, our control analysis examining reinstatement between object and fixation time points (as suggested by Reviewer 1) revealed no delay-related effects in any ROI (see p.24, lines 605-612), further highlighting the specificity of the observed delay-related change in item reinstatement.

We emphasize that temporal autocorrelation should be similar across all retrieval delays due to the identical task design and structure. Therefore, any observed decrease in reinstatement with increasing delay likely reflects a genuine change in the reinstatement index, rather than differences in temporal autocorrelation. Since our analysis includes only correctly retrieved items, and there is no perceptual input during the fixation window, this process is inherently memory-based, relying on mnemonic retrieval rather than sensory processing.

We respectfully disagree with the reviewer's assertion that retrieval during the fixation period cannot be considered more memory-driven than perception-driven. At this time point, participants had no access to actual images of the scene, making it necessary for them to rely on mnemonic retrieval. The object cue likely triggered pattern completion for the learned object-scene association, forming a unique memory if remembered correctly(Horner & Burgess, 2013). This process is inherently mnemonic, as it is based on reconstructing the original neural representation of the scene (Kuhl et al., 2012; Staresina et al., 2013).

While perception and memory processes can indeed be viewed as a continuum, some cognitive processes are predominantly memory-based, involving reconstruction rather than reproduction of previous experiences (Bartlett, 1932; Ranganath & Ritchey, 2012). In our task, although the retrieved material is based on previously encoded visual information, the process of recalling this information during the fixation period is fundamentally mnemonic, as it does not involve visual input. Our findings indicate that the similarity between memorybased representations and those observed during actual perception decreases over time, suggesting a relative change in the quality of the representations. However, this does not imply that detailed representations disappear; they may still be robust enough to support correct memory recall. Previous studies examining encoding-retrieval similarity have shown similar findings(Pacheco Estefan et al., 2019; Ritchey et al., 2013).

We do not claim that perception and memory processes are entirely discrete, nor do we suggest that only perception is involved when participants see the scene. Viewing the scene indeed involves recognition processes, updating retrieved representations from the fixation period, and potentially completing missing or unclear information. This integrative process demonstrates the interrelation of perception and memory, especially in complex tasks like the one we employed.

In conclusion, our task design and analysis support the interpretation that the fixation period is primarily characterized by mnemonic retrieval, facilitated by cue-triggered pattern completion, rather than perceptual processing. We believe this approach aligns with the current understanding of memory retrieval processes as supported by the existing literature.

The authors seem to have a design that would allow for across run comparisons, however, they did not include these additional analyses. 

Thank you for pointing this out. We ran as additional cross-run comparison. This results and further proceeding are reported in the comment for reviewer 1. 

To address the reviewer’s concern, we conducted an additional cross-run analysis for all correctly retrieved trials. The approach restricted comparisons to non-overlapping runs (run1run2, run2-run3, run1-run3). This analysis revealed robust gist-like reinstatement in children for remote Day 14 memories in the mPFC (p = .035) and vlPFC (p = .0007), in adults’ vlPFC remote Day 1 memories (p = .029), as well as in children and adults remote Day 1 memories in LOC (p < .02). A significant Session effect in both regions (mPFC: p = .026; vlPFC: p = .002) indicated increased reinstatement for long delay (Day 14) compared to short-delay and recent session (all p < .05). Given that the cross-run results largely replicate and reinforce the effects found previously with within-run, we believe that combining both sources of information is methodologically justified and statistically beneficial. Specifically, both approaches independently identified significant gist-like reinstatement in children’s mPFC and vlPFC (although within-run vlPFC effect (short delay: p = .038; long delay p = .047) did not survive multiple comparisons), particularly for remote memories. Including both withinrun and between-run comparisons increases the number of unique, non-repeated trial pairs, improving statistical power without introducing redundancy. While we acknowledge that same-run comparisons may be influenced by residual autocorrelation(Prince et al., 2022), we believe that our design mitigates this risk through consistency between within-run and crossrun results, long inter-trial intervals, and trial-wise estimation of activation. We have adjusted the manuscript, accordingly, reporting the combined analysis. We also report cross-run and within-run analysis separately in supplementary materials (Tables S12.1, S12.2, showing that they converge with the cross-run results and thus strengthen rather than dilute the findings. 

As suggested, we now explicitly highlight the change over time as the central finding. We observe a clear increase in gist-like reinstatement from recent to remote memories in children, particularly in mPFC and vlPFC. These effects based on combined within- and cross-run comparisons, are now clearly stated in the main results and interpreted in the discussion accordingly. 

(1) The authors did not satisfy my concerns about different amounts of re-exposures to stimuli as a function of age, which introduces a serious confound in the interpretation of the neural data. 

(2) Regarding Reviewer 1's point about different number of trials being entered into analysis, I think a more formal test of sub-sampling the adult trials is warranted. 

(1) We thank the reviewer for pointing this out. Overall, children needed 2 to 4 learning cycles to improve their performance and reach the learning criteria, compared to 2 learning cycles in adults. To address the different amounts of re-exposure to stimuli between the age groups, we subsampled the child group to only those children who reached the learning criteria after 2 learning cycles. For this purpose, we excluded 21 children from the analysis who needed 3 or 4 learning cycles. This resulted in 39 young adults and 28 children being included in the subsequent analysis. 

(i) We reran the behavioral analysis with the subsampled dataset (see Supplementary Materials,  Table S1.1, Fig. S1, Table S1.2). This analysis replicated the previous findings of less robust memory consolidation in children across all time delays. 

(ii) We reran the univariate analysis (see in Supplementary Materials, Table S9.1). This analysis also replicated fully the previous findings. This indicates that the inclusion of child participants with greater material exposure during learning in the analysis of neural retrieval patterns did not affect the group differences in univariate neural results. 

These subsampled results demonstrated that the amount of re-exposure to stimuli during encoding does not affect consolidation-related changes in memory retrieval at the behavioral and neural levels in children and adults across all time delays. We have added this information to the manuscript (line 343-348, 420-425). 

(2) We appreciate Reviewer 1's suggestion to perform a formal test by sub-sampling the adult trials to match the number of trials in the child group. However, we believe that this approach may not be optimal for the following reasons:

(i) Loss of Statistical Power: Sub-sampling the adult trials would result in a reduced sample size, potentially leading to a significant loss of statistical power and the ability to detect meaningful effects, particularly in a context where the adult group is intended to serve as a robust control or comparison group.

(ii) Introducing sub-sampling could introduce variability that complicates the interpretation of results, particularly if the trial sub-sampling process does not fully capture the variability inherent in the original adult data.

(iii) Robustness of Existing Findings: We have already addressed potential concerns about unequal trial numbers by conducting analyses that control for the number of learning cycles, as detailed in our supplementary materials. These analyses have shown that the observed effects are consistent, suggesting that the differences in trial numbers do not critically influence our findings.

Given these considerations, we hope the reviewer understands our rationale and agrees that the current analysis is robust and appropriate for addressing the research questions.

I also still fundamentally disagree with the use of global signals when comparing children to adults, and think this could very much skew the results. 

We thank the reviewer for raising this important issue. To address this concern comprehensively, we have taken the following steps:

(1) Overview of the literature support for global signal regression (GSR). A growing body of methodological and empirical research supports the inclusion of global signal repression as part of best practice denoising pipelines, particularly when analyzing pediatric fMRI data. Studies such as (Ciric et al., 2017; Parkes et al., 2018; J. D. Power et al., 2012, 2014; Power et al., 2012), and (Thompson et al., 2016) show that  GSR improves motion-related artifact removal. Critically, pediatric-specific studies (Disselhoff et al., 2025; Graff et al., 2022) conclude that pipelines including GSR are most effective for signal recovery and artifact removal in younger children. Graff et al. (2021) demonstrated that among various pipelines, GSR yielded the best noise reduction in 4–8-year-olds. Additionally, (Li et al., 2019; Qing et al., 2015) emphasized that GSR reduces artifactual variance without distorting the spatial structure of neural signals. (Ofoghi et al., 2021)demonstrated that global signal regression helps mitigate non-neuronal noise sources, including respiration, cardiac activity, motion, vasodilation, and scanner-related artifacts. Based on this and other recent findings, we consider GSR particularly beneficial for denoising paediatric  fMRI data in our study.

(2) Empirical comparison of pipelines with and without GSR. We re-run the entire first-level univariate analysis using the pipeline that excluded the global signal regression. The resulting activation maps (see Supplementary Figure S3.2, S4.2, S5.2, S9.2) differed notably from the original pipeline. Specifically, group differences in cortical regions such as mPFC, cerebellum, and posterior PHG no longer reached significance, and the overall pattern of results appeared noisier. 

(3) Evaluation of the pipeline differences. To further evaluate the impact of GSR, we conducted the following analyses:

(a) Global signal is stable across groups and sessions. A linear mixed-effects model showed no significant main effects or interactions involving group or session on the global signal (F-values < 2.62, p > .11), suggesting that the global signal was not group- or session-dependent in our sample. 

(b) Noise Reduction Assessment via Contrast Variability. We compared the variability (standard deviation and IQR) of contrast estimates across pipelines. Both SD (b = .070, p < .001) and IQR (b = .087, p < .001) were significantly reduced in the GSR pipeline, especially in children (p < .001) compared to adults (p = .048). This suggests that GSR reduces inter-subject variability in children, likely reflecting improved signal quality.

(c) Residual Variability After Regressing Global Signal. We regressed out global signal post hoc from both pipelines and compared the residual variance. Residual standard deviation was significantly lower for the GSR pipeline (F = 199, p < .001), with no interaction with session or group, further indicating that GSR stabilizes the signal and attenuates non-neuronal variability.

Conclusion

In summary, while we understand the reviewer’s concern, we believe the empirical and theoretical support for GSR, especially in pediatric samples, justifies its use in our study. Nonetheless, to ensure full transparency, we provide full results from both pipelines in the Supplementary Materials and have clarified our reasoning in the revised manuscript.

Reviewer #1 (Recommendations For The Authors): 

(1) Some figures are still missing descriptions of what everything on the graph means; please clarify in captions. 

We thank the reviewer for pointing this out. We undertook the necessary adjustments in the graph annotations. 

(2) The authors conclude they showed evidence of neural reorganization of memory representations in children (p. 41). But the gist is not greater in children than adults, and also does not differ over time-so, I was confused about what this claim was based on? 

We thank the reviewer for raising this question. Our results on gist-like reinstatements suggest that gist-like reinstatement was significantly higher in children compared to adults in the mPFC in addition to the child gist-like reinstatement indices being significantly higher than zero (see p.27-28). These results support our claim on neural reorganization of memory represenations in children. We hope this clarifies the issue. 

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https://doi.org/10.1038/s41562-021-01188-4

Author response:

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

Reviewer #1 (Public review):

Summary:

The Major Histocompatibility Complex (MHC) region is a collection of numerous genes involved in both innate and adaptive immunity. MHC genes are famed for their role in rapid evolution and extensive polymorphism in a variety of vertebrates. This paper presents a summary of gene-level gain and loss of orthologs and paralogs within MHC across the diversity of primates, using publicly available data.

Strengths:

This paper provides a strong case that MHC genes are rapidly gained (by paralog duplication) and lost over millions of years of macroevolution. The authors are able to identify MHC loci by homology across species, and from this infer gene duplications and losses using phylogenetic analyses. There is a remarkable amount of genic turnover, summarized in Figure 6 and Figure 7, either of which might be a future textbook figure of immune gene family evolution. The authors draw on state-of-the-art phylogenetic methods, and their inferences are robust insofar as the data might be complete enough to draw such conclusions.

Weaknesses:

One concern about the present work is that it relies on public databases to draw inferences about gene loss, which is potentially risky if the publicly available sequence data are incomplete. To say, for example, that a particular MHC gene copy is absent in a taxon (e.g., Class I locus F absent in Guenons according to Figure 1), we need to trust that its absence from the available databases is an accurate reflection of its absence in the genome of the actual organisms. This may be a safe assumption, but it rests on the completeness of genome assembly (and gene annotations?) or people uploading relevant data. This reviewer would have been far more comfortable had the authors engaged in some active spot-checking, doing the lab work to try to confirm absences at least for some loci and some species. Without this, a reader is left to wonder whether gene loss is simply reflecting imperfect databases, which then undercuts confidence in estimates of rates of gene loss.

Indeed, just because a locus has not been confirmed in a species does not necessarily mean that it is absent. As we explain in the Figure 1 caption, only a few species have had their genomes extensively studied (gray background), and only for these species does the absence of a point in this figure mean that a locus is absent. The white background rows represent species that are not extensively studied, and we point out that the absence of a point does not mean that a locus is absent from the species, rather undiscovered. We have also added a parenthetical to the text to explain this (line 156): “Only species with rows highlighted in gray have had their MHC regions extensively studied (and thus only for these rows is the absence of a gene symbol meaningful).”

While we agree that spot-checking may be a helpful next step, one of the goals of this manuscript is to collect and synthesize the enormous volume of MHC evolution research in the primates, which will serve as a jumping-off point for other researchers to perform important wet lab work.

Some context is useful for comparing rates of gene turnover in MHC, to other loci. Changing gene copy numbers, duplications, and loss of duplicates, are common it seems across many loci and many organisms; is MHC exceptional in this regard, or merely behaving like any moderately large gene family? I would very much have liked to see comparable analyses done for other gene families (immune, like TLRs, or non-immune), and quantitative comparisons of evolutionary rates between MHC versus other genes. Does MHC gene composition evolve any faster than a random gene family? At present readers may be tempted to infer this, but evidence is not provided.

Our companion paper (Fortier and Pritchard, 2025) demonstrates that the MHC is a unique locus in many regards, such as its evidence for deep balancing selection and its excess of disease associations. Thus, we expect that it is evolving faster than any random gene family. It would be interesting to repeat this analysis for other gene families, but that is outside of the scope of this project. Additionally, allele databases for other gene families are not nearly as developed, but as more alleles become available for other polymorphic families, a comparable analysis could become possible.

We have added a paragraph to the discussion (lines 530-546) to clarify that we do not know for certain whether the MHC gene family is evolving rapidly compared to other gene families.

While on the topic of making comparisons, the authors make a few statements about relative rates. For instance, lines 447-8 compare gene topology of classical versus non-classical genes; and line 450 states that classical genes experience more turnover. But there are no quantitative values given to these rates to provide numerical comparisons, nor confidence intervals provided (these are needed, given that they are estimates), nor formal statistical comparisons to confirm our confidence that rates differ between types of genes.

More broadly, the paper uses sophisticated phylogenetic methods, but without taking advantage of macroevolutionary comparative methods that allow model-based estimation of macroevolutionary rates. I found the lack of quantitative measurements of rates of gene gain/loss to be a weakness of the present version of the paper, and something that should be readily remedied. When claiming that MHC Class I genes "turn over rapidly" (line 476) - what does rapidly mean? How rapidly? How does that compare to rates of genetic turnover at other families? Quantitative statements should be supported by quantitative estimates (and their confidence intervals).

These statements refer to qualitative observations, so we cannot provide numerical values. We simply conclude that certain gene groups evolve faster or slower based on the species and genes present in each clade. It is difficult to provide estimates because of the incomplete sampling of genes that survived to the present day. In addition, the presence or absence of various orthologs in different species still needs to be confirmed, at which point it might be useful to be more quantitative. We have also added a paragraph to the discussion to address this concern and advocate for similar analyses of other gene families in the future when more data is available (lines 530-546).

The authors refer to 'shared function of the MHC across species' (e.g. line 22); while this is likely true, they are not here presenting any functional data to confirm this, nor can they rule out neofunctionalization or subfunctionalization of gene duplicates. There is evidence in other vertebrates (e.g., cod) of MHC evolving appreciably altered functions, so one may not safely assume the function of a locus is static over long macroevolutionary periods, although that would be a plausible assumption at first glance.

Indeed, we cannot assume that the function of a locus is static across time, especially for the MHC region. In our research, we read hundreds of papers that each focused on a small number of species or genes and gathered some information about them, sometimes based on functional experiments and sometimes on measures such as dN/dS. These provide some indication of a gene’s broad classification in a species or clade, even if the evidence is preliminary. Where possible, we used this preliminary evidence to give genes descriptors “classical,” “non-classical,” “dual characteristics,” “pseudogene,” “fixed”, or “unfixed.” Sometimes multiple individuals and haplotypes were analyzed, so we could even assign a minimum number of gene copies present in a species. We have aggregated all of these references into Supplementary Table 1 (for Class I/Figure 1) and Supplementary Table 2 (for Class II/Figure 2) along with specific details about which data points in these figures that each reference supports. We realize that many of these classifications are based on a small number of individuals or indirect measures, so they may change in the future as more functional data is generated.

Reviewer #2 (Public review):

Summary:

The authors aim to provide a comprehensive understanding of the evolutionary history of the Major Histocompatibility Complex (MHC) gene family across primate species. Specifically, they sought to:

(1) Analyze the evolutionary patterns of MHC genes and pseudogenes across the entire primate order, spanning 60 million years of evolution.

(2) Build gene and allele trees to compare the evolutionary rates of MHC Class I and Class II genes, with a focus on identifying which genes have evolved rapidly and which have remained stable.

(3) Investigate the role of often-overlooked pseudogenes in reconstructing evolutionary events, especially within the Class I region.

(4) Highlight how different primate species use varied MHC genes, haplotypes, and genetic variation to mount successful immune responses, despite the shared function of the MHC across species.

(5) Fill gaps in the current understanding of MHC evolution by taking a broader, multi-species perspective using (a) phylogenomic analytical computing methods such as Beast2, Geneconv, BLAST, and the much larger computing capacities that have been developed and made available to researchers over the past few decades, (b) literature review for gene content and arrangement, and genomic rearrangements via haplotype comparisons.

(6) The authors overall conclusions based on their analyses and results are that 'different species employ different genes, haplotypes, and patterns of variation to achieve a successful immune response'.

Strengths:

Essentially, much of the information presented in this paper is already well-known in the MHC field of genomic and genetic research, with few new conclusions and with insufficient respect to past studies. Nevertheless, while MHC evolution is a well-studied area, this paper potentially adds some originality through its comprehensive, cross-species evolutionary analysis of primates, focus on pseudogenes and the modern, large-scale methods employed. Its originality lies in its broad evolutionary scope of the primate order among mammals with solid methodological and phylogenetic analyses.

The main strengths of this study are the use of large publicly available databases for primate MHC sequences, the intensive computing involved, the phylogenetic tool Beast2 to create multigene Bayesian phylogenetic trees using sequences from all genes and species, separated into Class I and Class II groups to provide a backbone of broad relationships to investigate subtrees, and the presentation of various subtrees as species and gene trees in an attempt to elucidate the unique gene duplications within the different species. The study provides some additional insights with summaries of MHC reference genomes and haplotypes in the context of a literature review to identify the gene content and haplotypes known to be present in different primate species. The phylogenetic overlays or ideograms (Figures 6 and 7) in part show the complexity of the evolution and organisation of the primate MHC genes via the orthologous and paralogous gene and species pathways progressively from the poorly-studied NWM, across a few moderately studied ape species, to the better-studied human MHC genes and haplotypes.

Weaknesses:

The title 'The Primate Major Histocompatibility Complex: An Illustrative Example of GeneFamily Evolution' suggests that the paper will explore how the Major Histocompatibility Complex (MHC) in primates serves as a model for understanding gene family evolution. The term 'Illustrative Example' in the title would be appropriate if the paper aimed to use the primate Major Histocompatibility Complex (MHC) as a clear and representative case to demonstrate broader principles of gene family evolution. That is, the MHC gene family is not just one instance of gene family evolution but serves as a well-studied, insightful example that can highlight key mechanisms and concepts applicable to other gene families. However, this is not the case, this paper only covers specific details of primate MHC evolution without drawing broader lessons to any other gene families. So, the term 'Illustrative Example' is too broad or generalizing. In this case, a term like 'Case Study' or simply 'Example' would be more suitable. Perhaps, 'An Example of Gene Family Diversity' would be more precise. Also, an explanation or 'reminder' is suggested that this study is not about the origins of the MHC genes from the earliest jawed vertebrates per se (~600 mya), but it is an extension within a subspecies set that has emerged relatively late (~60 mya) in the evolutionary divergent pathways of the MHC genes, systems, and various vertebrate species.

Thank you for your input on the title; we have changed it to “A case study of gene family evolution” instead.

Thank you also for pointing out the potential confusion about the time span of our study. We have added “Having originated in the jawed vertebrates,” to a sentence in the introduction (lines 38-39). We have also added the sentence “Here, we focus on the primates, spanning approximately 60 million years within the over 500-million-year evolution of the family \citep{Flajnik2010}.“ to be more explicit about the context for our work (lines 59-61).

Phylogenomics. Particular weaknesses in this study are the limitations and problems associated with providing phylogenetic gene and species trees to try and solve the complex issue of the molecular mechanisms involved with imperfect gene duplications, losses, and rearrangements in a complex genomic region such as the MHC that is involved in various effects on the response and regulation of the immune system. A particular deficiency is drawing conclusions based on a single exon of the genes. Different exons present different trees. Which are the more reliable? Why were introns not included in the analyses? The authors attempt to overcome these limitations by including genomic haplotype analysis, duplication models, and the supporting or contradictory information available in previous publications. They succeed in part with this multidiscipline approach, but much is missed because of biased literature selection. The authors should include a paragraph about the benefits and limitations of the software that they have chosen for their analysis, and perhaps suggest some alternative tools that they might have tried comparatively. How were problems with Bayesian phylogeny such as computational intensity, choosing probabilities, choosing particular exons for analysis, assumptions of evolutionary models, rates of evolution, systemic bias, and absence of structural and functional information addressed and controlled for in this study?

We agree that different exons have different trees, which is exactly why we repeated our analysis for each exon in order to compare and contrast them. In particular, the exons encoding the binding site of the resulting protein (exons 2 and 3 for Class I and exon 2 for Class II) show evidence for trans-species polymorphism and gene conversion. These phenomena lead to trees that do not follow the species tree and are fascinating in and of themselves, which we explore in detail in our companion paper (Fortier and Pritchard, 2025). Meanwhile, the non-peptide-binding extracellular-domain-encoding exon (exon 4 for Class I and exon 3 for Class II) is comparably sized to the binding-site-encoding exons and provides an interesting functional contrast. As this exon is likely less affected by trans-species polymorphism, gene conversion, and convergent evolution, we present results from it most often in the main text, though we occasionally touch on differences between the exons. See lines 191-196, 223-226, and 407-414 for some examples of how we discuss the exons in the text. Additionally, all trees from all of these exons can be found in the supplement. 

We agree that introns would valuable to study in this context. Even though the non--binding-site-encoding exons are probably *less* affected by trans-species polymorphism, gene conversion, and convergent evolution, they are still functional. The introns, however, experience much more relaxed selection, if any, and comparing their trees to those for the exons would be valuable and illuminating. We did not generate intron trees for two reasons. Most importantly, there is a dearth of data available for the introns; in the databases we used, there was often intron data available only for human, chimpanzee, and sometimes macaque, and only for a small subset of the genes. This limitation is at odds with the comprehensive, many-gene-many-species approach which we feel is the main novelty of this work. Secondly, the introns that *are* available are difficult to align. Even aligning the exons across such a highly-diverged set of genes and pseudogenes was difficult and required manual effort. The introns proved even more difficult to try to align across genes. In the future, when more intron data is available and sufficient effort is put into aligning them, it will be possible and desirable to do a comparable analysis. We also added a sentence to the “Data” section to briefly explain why we did not include introns (lines 134-135).

We explain our Bayesian phylogenetics approach in detail in the Methods (lines 650-725), including our assumptions and our solutions to challenges specific to this application. For further explanation of the method itself, we suggest reading the original BEAST and BEAST2 papers (Drummond & Rambaut (2007), Drummond et al. (2012), Bouckaert et al. (2014), and Bouckaert et al. (2019)). Known structural and functional information helped us validate the alignments we used in this study, but the fact that such information is not fully known for every gene and species should not affect the method itself.

Gene families as haplotypes. In the Introduction, the MHC is referred to as a 'gene family', and in paragraph 2, it is described as being united by the 'MHC fold', despite exhibiting 'very diverse functions'. However, the MHC region is more accurately described as a multigene region containing diverse, haplotype-specific Conserved Polymorphic Sequences, many of which are likely to be regulatory rather than protein-coding. These regulatory elements are essential for controlling the expression of multiple MHC-related products, such as TNF and complement proteins, a relationship demonstrated over 30 years ago. Non-MHC fold loci such as TNF, complement, POU5F1, lncRNA, TRIM genes, LTA, LTB, NFkBIL1, etc, are present across all MHC haplotypes and play significant roles in regulation. Evolutionary selection must act on genotypes, considering both paternal and maternal haplotypes, rather than on individual genes alone. While it is valuable to compile databases for public use, their utility is diminished if they perpetuate outdated theories like the 'birth-and-death model'. The inclusion of prior information or assumptions used in a statistical or computational model, typically in Bayesian analysis, is commendable, but they should be based on genotypic data rather than older models. A more robust approach would consider the imperfect duplication of segments, the history of their conservation, and the functional differences in inheritance patterns. Additionally, the MHC should be examined as a genomic region, with ancestral haplotypes and sequence changes or rearrangements serving as key indicators of human evolution after the 'Out of Africa' migration, and with disease susceptibility providing a measurable outcome. There are more than 7000 different HLA-B and -C alleles at each locus, which suggests that there are many thousands of human HLA haplotypes to study. In this regard, the studies by Dawkins et al (1999 Immunol Rev 167,275), Shiina et al. (2006 Genetics 173,1555) on human MHC gene diversity and disease hitchhiking (haplotypes), and Sznarkowska et al. (2020 Cancers 12,1155) on the complex regulatory networks governing MHC expression, both in terms of immune transcription factor binding sites and regulatory non-coding RNAs, should be examined in greater detail, particularly in the context of MHC gene allelic diversity and locus organization in humans and other primates.

Thank you for these comments. To clarify that the MHC “region” is different from (and contains) the MHC “gene family” as we describe it, we changed a sentence in the abstract (lines 8-10) from “One large gene family that has experienced rapid evolution is the Major Histocompatibility Complex (MHC), whose proteins serve critical roles in innate and adaptive immunity.” to “One large gene family that has experienced rapid evolution lies within the Major Histocompatibility Complex (MHC), whose proteins serve critical roles in innate and adaptive immunity.” We know that the region is complex and contains many other genes and regulatory sequences; Figure 1 of our companion paper (Fortier and Pritchard, 2025) depicts these in order to show the reader that the MHC genes we focus on are just one part of the entire region.

We love the suggestion to look at the many thousands of alleles present at each of the classical loci. This is the focus of our complimentary paper (Fortier and Pritchard, 2025) which explores variation at the allele level. In the current paper, we look mainly at the differences between genes and the use of different genes in different species.

Diversifying and/or concerted evolution. Both this and past studies highlight diversifying selection or balancing selection model is the dominant force in MHC evolution. This is primarily because the extreme polymorphism observed in MHC genes is advantageous for populations in terms of pathogen defence. Diversification increases the range of peptides that can be presented to T cells, enhancing the immune response. The peptide-binding regions of MHC genes are highly variable, and this variability is maintained through selection for immune function, especially in the face of rapidly evolving pathogens. In contrast, concerted evolution, which typically involves the homogenization of gene duplicates through processes like gene conversion or unequal crossing-over, seems to play a minimal role in MHC evolution. Although gene duplication events have occurred in the MHC region leading to the expansion of gene families, the resulting paralogs often undergo divergent evolution rather than being kept similar or homozygous by concerted evolution. Therefore, unlike gene families such as ribosomal RNA genes or histone genes, where concerted evolution leads to highly similar copies, MHC genes display much higher levels of allelic and functional diversification. Each MHC gene copy tends to evolve independently after duplication, acquiring unique polymorphisms that enhance the repertoire of antigen presentation, rather than undergoing homogenization through gene conversion. Also, in some populations with high polymorphism or genetic drift, allele frequencies may become similar over time without the influence of gene conversion. This similarity can be mistaken for gene conversion when it is simply due to neutral evolution or drift, particularly in small populations or bottlenecked species. Moreover, gene conversion might contribute to greater diversity by creating hybrids or mosaics between different MHC genes. In this regard, can the authors indicate what percentage of the gene numbers in their study have been homogenised by gene conversion compared to those that have been diversified by gene conversion?

We appreciate the summary, and we feel we have appropriately discussed both gene conversion and diversifying selection in the context of the MHC genes. Because we cannot know for sure when and where gene conversion has occurred, we cannot quantify percentages of genes that have been homogenized or diversified.  

Duplication models. The phylogenetic overlays or ideograms (Figures 6 and 7) show considerable imperfect multigene duplications, losses, and rearrangements, but the paper's Discussion provides no in-depth consideration of the various multigenic models or mechanisms that can be used to explain the occurrence of such events. How do their duplication models compare to those proposed by others? For example, their text simply says on line 292, 'the proposed series of events is not always consistent with phylogenetic data'. How, why, when? Duplication models for the generation and extension of the human MHC class I genes as duplicons (extended gene or segmental genomic structures) by parsimonious imperfect tandem duplications with deletions and rearrangements in the alpha, beta, and kappa blocks were already formulated in the late 1990s and extended to the rhesus macaque in 2004 based on genomic haplotypic sequences. These studies were based on genomic sequences (genes, pseudogenes, retroelements), dot plot matrix comparisons, and phylogenetic analyses of gene and retroelement sequences using computer programs. It already was noted or proposed in these earlier 1999 studies that (1) the ancestor of HLA-P(90)/-T(16)/W(80) represented an old lineage separate from the other HLA class I genes in the alpha block, (2) HLA-U(21) is a duplicated fragment of HLA-A, (3) HLA-F and HLA-V(75) are among the earliest (progenitor) genes or outgroups within the alpha block, (4) distinct Alu and L1 retroelement sequences adjoining HLA-L(30), and HLA-N genomic segments (duplicons) in the kappa block are closely related to those in the HLA-B and HLA-C in the beta block; suggesting an inverted duplication and transposition of the HLA genes and retroelements between the beta and kappa regions. None of these prior human studies were referenced by Fortier and Pritchard in their paper. How does their human MHC class I gene duplication model (Fig. 6) such as gene duplication numbers and turnovers differ from those previously proposed and described by Kulski et al (1997 JME 45,599), (1999 JME 49,84), (2000 JME 50,510), Dawkins et al (1999 Immunol Rev 167,275), and Gaudieri et al (1999 GR 9,541)? Is this a case of reinventing the wheel?

Figures 6 and 7 are intended to synthesize and reconcile past findings and our own trees, so they do not strictly adhere to the findings of any particular study and cannot fully match all studies. In the supplement, Figure 6 - figure supplement 1 and Figure 7 - figure supplement 1 duly credit all of the past work that went into making these trees. Most previous papers focus on just one aspect of these trees, such as haplotypes within a species, a specific gene or allelic lineage relationship, or the branching pattern of particular gene groups. We believe it was necessary to bring all of these pieces of evidence together. Even among papers with the same focus (to understand the block duplications that generated the current physical layout of the MHC), results differ. For example, Geraghty (1992), Hughes (1995), Kulski (2004)/Kulski (2005),  and Shiina (1999) all disagree on the exact branching order of the genes MHC-W, -P, and -T, and of MHC-G, -J, and -K. While the Kulski studies you pointed out were very thorough for their era, they still only relied on data from three species and one haplotype per species. Our work is not intended to replace or discredit these past works, simply build upon them with a larger set of species and sequences. We hope the hypotheses we propose in Figures 6 and 7 can help unify existing research and provide a more easily accessible jumping-off-point for future work.

Results. The results are presented as new findings, whereas most if not all of the results' significance and importance already have been discussed in various other publications. Therefore, the authors might do better to combine the results and discussion into a single section with appropriate citations to previously published findings presented among their results for comparison. Do the trees and subsets differ from previous publications, albeit that they might have fewer comparative examples and samples than the present preprint? Alternatively, the results and discussion could be combined and presented as a review of the field, which would make more sense and be more honest than the current format of essentially rehashing old data.

In starting this project, we found that a large barrier to entry to this field of study is the immense amount of published literature over 30+ years. It is both time-consuming and confusing to read up on the many nuances of the MHC genes, their changing names, and their evolution, making it difficult to start new, innovative projects. We acknowledge that while our results are not entirely novel, the main advantage of our work is that it provides a thorough, comprehensive starting point for others to learn about the MHC quickly and dive into new research. We feel that we have appropriately cited past literature in both the main text, appendices, and supplement, so that readers may dive into a particular area with ease.

Minor corrections:

(1) Abstract, line 19: 'modern methods'. Too general. What modern methods?

To keep the abstract brief, the methods are introduced in the main text when each becomes relevant as well as in the methods section.

(2) Abstract, line 25: 'look into [primate] MHC evolution.' The analysis is on the primate MHC genes, not on the entire vertebrate MHC evolution with a gene collection from sharks to humans. The non-primate MHC genes are often differently organised and structurally evolved in comparison to primate MHC.

Thank you! We have added the word “primate” to the abstract (line 25).

(3) Introduction, line 113. 'In a companion paper (Fortier and Pritchard, 2024)' This paper appears to be unpublished. If it's unpublished, it should not be referenced.

This paper is undergoing the eLife editorial process at the same time; it will have a proper citation in the final version.

(4) Figures 1 and 2. Use the term 'gene symbols' (circle, square, triangle, inverted triangle, diamond) or 'gene markers' instead of 'points'. 'Asterisks "within symbols" indicate new information.

Thank you, the word “symbol” is much clearer! We have changed “points” to “symbols” in the captions for Figure 1, Figure 1 - figure supplement 1, Figure 2, and Figure 2 - figure supplement 1. We also changed this in the text (lines 157-158 and 170).

(5) Figures. A variety of colours have been applied for visualisation. However, some coloured texts are so light in colour that they are difficult to read against a white background. Could darker colours or black be used for all or most texts?

With such a large number of genes and species to handle in this work, it was nearly impossible to choose a set of colors that were distinct enough from each other. We decided to prioritize consistency (across this paper, its supplement, and our companion paper) as well as at-a-glance grouping of similar sequences. Unfortunately, this means we had to sacrifice readability on a white background, but readers may turn to the supplement if they need to access specific sequence names.

(6) Results, line 135. '(Fortier and Pritchard, 2024)' This paper appears to be unpublished. If it's unpublished, it should not be referenced.

Repeat of (3). This paper is undergoing the eLife editorial process at the same time; it will have a proper citation in the final version.

(7) Results, lines 152 to 153, 164, 165, etc. 'Points with an asterisk'. Use the term 'gene symbols' (circle, square, triangle, inverted triangle, diamond) or 'gene markers' instead of 'points'. A point is a small dot such as those used in data points for plotting graphs .... The figures are so small that the asterisks in the circles, squares, triangles, etc, look like points (dots) and the points/asterisks terminology that is used is very confusing visually.

Repeat of (4). Thank you, the word “symbol” is much clearer! We have changed “points” to “symbols” in the captions for Figure 1, Figure 1 - figure supplement 1, Figure 2, and Figure 2 - figure supplement 1. We also changed this in the text (lines 157-158 and 170).

(8) Line 178 (BEA, 2024) is not listed alphabetically in the References.

Thank you for catching this! This reference maps to the first bibliography entry, “SUMMARIZING POSTERIOR TREES.” We are unsure how to cite a webpage that has no explicit author within the eLife Overleaf template, so we will consult with the editor.

(9) Lines 188-190. 'NWM MHC-G does not group with ape/OWM MHC-G, instead falling outside of the clade containing ape/OWM MHC-A, -G, -J and -K.' This is not surprising given that MHC-A, -G, -J, and -K are paralogs of each other and that some of them, especially in NWM have diverged over time from the paralogs and/or orthologs and might be closer to one paralog than another and not be an actual ortholog of OWM, apes or humans.

We included this sentence to clarify the relationships between genes and to help describe what is happening in Figure 6. Figure 6 - figure supplement 1 includes all of the references that go into such a statement and Appendix 3 details our reasoning for this and other statements.

(10) Line 249. Gene conversion: This is recombination between two different genes where a portion of the genes are exchanged with one another so that different portions of the gene can group within one or other of the two gene clades. Alternatively, the gene has been annotated incorrectly if the gene does not group within either of the two alternative clades. Another possibility is that one or two nucleotide mutations have occurred without a recombination resulting in a mistaken interpretation or conclusion of a recombination event. What measures are taken to avoid false-positive conclusions? How many MHC gene conversion (recombination) events have occurred according to the authors' estimates? What measures are taken to avoid false-positive conclusions?

All of these possibilities are certainly valid. We used the program GENECONV to infer gene conversion events, but there is considerable uncertainty owing to the ages of the genes and the inevitable point mutations that have occurred post-event. Gene conversion was not the focus of our paper, so we did our best to acknowledge it (and the resulting differences between trees from different exons) without spending too much time diving into it. A list of inferred gene conversion events can be found in Figure 3 - source data 1 and Figure 4 - source data 1.

(11) Lines 284-286. 'The Class I MHC region is further divided into three polymorphic blocks-alpha, beta, and kappa blocks-that each contains MHC genes but are separated by well-conserved non-MHC genes.' The MHC class I region was first designated into conserved polymorphic duplication blocks, alpha and beta by Dawkins et al (1999 Immunol Rev 167,275), and kappa by Kulski et al (2002 Immunol Rev 190,95), and should be acknowledged (cited) accordingly.

Thank you for catching this! We have added these citations (lines 302-303)!

(12) Lines 285-286. 'The majority of the Class I genes are located in the alpha-block, which in humans includes 12 MHC genes and pseudogenes.' This is not strictly correct for many other species, because the majority of class I genes might be in the beta block of new and old-world monkeys, and the authors haven't provided respective counts of duplication numbers to show otherwise. The alpha block in some non-primate mammalian species such as pigs, rats, and mice has no MHC class I genes or only a few. Most MHC class I genes in non-primate mammalian species are found in other regions. For example, see Ando et al (2005 Immunogenetics 57,864) for the pig alpha, beta, and kappa regions in the MHC class I region. There are no pig MHC genes in the alpha block.

Yes, which is exactly why we use the phrase “in humans” in that particular sentence. The arrangement of the MHC in several other primate reference genomes is shown in Figure 1 - figure supplement 2.

(13) Line 297 to 299. 'The alpha-block also contains a large number of repetitive elements and gene fragments belonging to other gene families, and their specific repeating pattern in humans led to the conclusion that the region was formed by successive block duplications (Shiina et al., 1999).' There are different models for successive block duplications in the alpha block and some are more parsimonious based on imperfect multigenic segmental duplications (Kulski et al 1999, 2000) than others (Shiina et al., 1999). In this regard, Kulski et al (1999, 2000) also used duplicated repetitive elements neighbouring MHC genes to support their phylogenetic analyses and multigenic segmental duplication models. For comparison, can the authors indicate how many duplications and deletions they have in their models for each species?

We have added citations to this sentence to show that there are different published models to describe the successive block duplications (line 307). Our models in Figure 6 and Figure 7 are meant to aggregate past work and integrate our own, and thus they were not built strictly by parsimony. References can be found in Figure 6 - figure supplement 1 and Figure 7 - figure supplement 1.

(14) Lines 315-315. 'Ours is the first work to show that MHC-U is actually an MHC-A-related gene fragment.' This sentence should be deleted. Other researchers had already inferred that MHC-U is actually an MHC-A-related gene fragment more than 25 years ago (Kulski et al 1999, 2000) when the MHC-U was originally named MHC-21.

While these works certainly describe MHC-U/MHC-21 as a fragment in the 𝛼-block, any relation to MHC-A was by association only and very few species/haplotypes were examined. So although the idea is not wholly novel, we provide convincing evidence that not only is MHC-U related to MHC-A by sequence, but also that it is a very recent partial duplicate of MHC-A. We show this with Bayesian phylogenetic trees as well as an analysis of haplotypes across many more species than were included in those papers.  

(15) Lines 361-362. 'Notably, our work has revealed that MHC-V is an old fragment.' This is not a new finding or hypothesis. Previous phylogenetic analysis and gene duplication modelling had already inferred HLA-V (formerly HLA-75) to be an old fragment (Kulski et al 1999, 2000).

By “old,” we mean older than previous hypotheses suggest. Previous work has proposed that MHC-V and -P were duplicated together, with MHC-V deriving from an MHC-A/H/V ancestral gene and MHC-P deriving from an MHC-W/T/P ancestral gene (Kulski (2005), Shiina (1999)). However, our analysis (Figure 5A) shows that MHC-V sequences form a monophyletic clade outside of the MHC-W/P/T group of genes as well as outside of the MHC-A/B/C/E/F/G/J/K/L group of genes, which is not consistent with MHC-A and -V being closely related. Thus, we conclude that MHC-V split off earlier than the differentiation of these other gene groups and is thus older than previously thought. We explain this in the text as well (lines 317-327) and in Appendix 3.  

(16) Line 431-433. 'the Class II genes have been largely stable across the mammals, although we do see some lineage-specific expansions and contractions (Figure 2 and Figure 2-gure Supplement 2).' Please provide one or two references to support this statement. Is 'gure' a typo?

We corrected this typo, thank you! This conclusion is simply drawn from the data presented in Figure 2 and Figure 2 - figure supplement 2. The data itself comes from a variety of sources, which are already included in the supplement as Figure 2 - source data 1.

(17) Line 437. 'We discovered far more "specific" events in Class I, while "broad-scale" events were predominant in Class II.' Please define the difference between 'specific' and 'broad-scale'.

These terms are defined in the previous sentence (lines 466-469).

450-451. 'This shows that classical genes experience more turnover and are more often affected by long-term balancing selection or convergent evolution.' Is balancing selection a form of divergent evolution that is different from convergent evolution? Please explain in more detail how and why balancing selection or convergent evolution affects classical and nonclassical genes differently.

Balancing selection acts to keep alleles at moderate frequencies, preventing any from fixing in the population. In contrast, convergent evolution describes sequences or traits becoming similar over time even though they are not similar by descent. While we cannot know exactly what selective forces have occurred in the past, we observe different patterns in the trees for each type of gene. In Figures 1 and 2, viewers can see at first glance that the nonclassical genes (which are named throughout the text and thoroughly described in Appendix 3) appear to be longer-lived than the classical genes. In addition, lines 204-222 and 475-488 describe topological differences in the BEAST2 trees of these two types of genes. However, we acknowledge that it could be helpful to have additional, complimentary information about the classical vs. non-classical genes. Thus, we have added a sentence and reference to our companion paper (Fortier and Pritchard, 2025), which focuses on long-term balancing selection and draws further contrast between classical and non-classical genes. In lines 481-484, we added  “We further explore the differences between classical and non-classical genes in our companion paper, finding ancient trans-species polymorphism at the classical genes but not at the non-classical genes \citep{Fortier2025b}.”

References

Some references in the supplementary materials such as Alvarez (1997), Daza-Vamenta (2004), Rojo (2005), Aarnink (2014), Kulski (2022), and others are missing from the Reference list. Please check that all the references in the text and the supplementary materials are listed correctly and alphabetically.

We will make sure that these all show up properly in the proof.

Reviewer #3 (Public review):

Summary:

The article provides the most comprehensive overview of primate MHC class I and class II genes to date, combining published data with an exploration of the available genome assemblies in a coherent phylogenetic framework and formulating new hypotheses about the evolution of the primate MHC genomic region.

Strengths:

I think this is a solid piece of work that will be the reference for years to come, at least until population-scale haplotype-resolved whole-genome resequencing of any mammalian species becomes standard. The work is timely because there is an obvious need to move beyond short amplicon-based polymorphism surveys and classical comparative genomic studies. The paper is data-rich and the approach taken by the authors, i.e. an integrative phylogeny of all MHC genes within a given class across species and the inclusion of often ignored pseudogenes, makes a lot of sense. The focus on primates is a good idea because of the wealth of genomic and, in some cases, functional data, and the relatively densely populated phylogenetic tree facilitates the reconstruction of rapid evolutionary events, providing insights into the mechanisms of MHC evolution. Appendices 1-2 may seem unusual at first glance, but I found them helpful in distilling the information that the authors consider essential, thus reducing the need for the reader to wade through a vast amount of literature. Appendix 3 is an extremely valuable companion in navigating the maze of primate MHC genes and associated terminology.

Weaknesses:

I have not identified major weaknesses and my comments are mostly requests for clarification and justification of some methodological choices.

Thank you so much for your kind and supportive review!

Reviewer #1 (Recommendations for the authors):

(1) Line 151: How is 'extensively studied' defined?

Extensively studied is not a strict definition, but a few organisms clearly stand apart from the rest in terms of how thoroughly their MHC regions have been studied. For example, the macaque is a model organism, and individuals from many different species and populations have had their MHC regions fully sequenced. This is in contrast to the gibbon, for example, in which there is some experimental evidence for the presence of certain genes, but no MHC region has been fully sequenced from these animals.

(2) Can you clarify how 'classical' and 'non-classical' MHC genes are being determined in your analysis?

Classical genes are those whose protein products perform antigen presentation to T cells and are directly involved in adaptive immunity, while non-classical genes are those whose protein products do not do this. For example, these non-classical genes might code for proteins that interact with receptors on Natural Killer cells and influence innate immunity. The roles of these proteins are not necessarily conserved between closely related species, and experimental evidence is needed to evaluate this. However, in the absence of such evidence, wherever possible we have provided our best guess as to the roles of the orthologous genes in other species, presented in Figure 1 - source data 1 and Figure 2 - source data 1. This is based on whatever evidence is available at the moment, sometimes experimental but typically based on dN/dS ratios and other indirect measures.

(3) I find the overall tone of the paper to be very descriptive, and at times meandering and repetitive, with a lot of similar kinds of statements being repeated about gene gain/loss. This is perhaps inevitable because a single question is being asked of each of many subsets of MHC gene types, and even exons within gene types, so there is a lot of repetition in content with a slightly different focus each time. This does not help the reader stay focused or keep track. I found myself wishing for a clearly defined question or hypothesis, or some rate parameter in need of estimation. I would encourage the authors to tighten up their phrasing, or consider streamlining the results with some better signposting to organize ideas within the results.

We totally understand your critique, as we talk about a wide range of specific genes and gene groups in this paper. To improve readability, we have added many more signposting phrases and sentences:

“Aside from MHC-DRB, …” (line 173)

“Now that we had a better picture of the landscape of MHC genes present in different primates, we wanted to understand the genes’ relationships. Treating Class I, Class IIA, and Class IIB separately, ...” (line 179-180)

“We focus first on the Class I genes.” (line 191)

“... for visualization purposes…” (line195)

“We find that sequences do not always assort by locus, as would be expected for a typical gene.” (lines 196-197)

“... rather than being directly orthologous to the ape/OWM MHC-G genes.” (lines 201-202)

“Appendix 3 explains each of these genes in detail, including previous work and findings from this study.“ (lines 202-203)

“... (but not with NWM) …” (line 208)

“While genes such as MHC-F have trees which closely match the overall species tree, other genes show markedly different patterns, …” (lines 212-213)

“Thus, while some MHC-G duplications appear to have occurred prior to speciation events within the NWM, others are species-specific.” (lines 218-219)

“... indicating rapid evolution of many of the Class I genes” (lines 220-221)

“Now turning to the Class II genes, …“ (line 223)

“(see Appendix 2 for details on allele nomenclature) “ (line 238)

“(e.g. MHC-DRB1 or -DRB2)” (line 254)

“...  meaning their names reflect previously-observed functional similarity more than evolutionary relatedness.” (lines 257-258)

“(see Appendix 3 for more detail)” (line 311)

“(a 5'-end fragment)” (line 324)

“Therefore, we support past work that has deemed MHC-V an old fragment.” (lines 326-327)

“We next focus on MHC-U, a previously-uncharacterized fragment pseudogene containing only exon 3.” (line 328-329)

“However, it is present on both chimpanzee haplotypes and nearly all human haplotypes, and we know that these haplotypes diverged earlier---in the ancestor of human and gorilla. Therefore, ...” (lines 331-333)

“Ours is the first work to show that MHC-U is actually an MHC-A-related gene fragment and that it likely originated in the human-gorilla ancestor.” (lines 334-336)  

“These pieces of evidence suggest that MHC-K and -KL duplicated in the ancestor of the apes.” (lines 341-342)

“Another large group of related pseudogenes in the Class I $\alpha$-block includes MHC-W, -P, and -T (see Appendix 3 for more detail).” (lines 349-350)

“...to form the current physical arrangement” (lines 354)

“Thus, we next focus on the behavior of this subgroup in the trees.” (line 358)

“(see Appendix 3 for further explanation).” (line 369)

“Thus, for the first time we show that there must have been three distinct MHC-W-like genes in the ape/OWM ancestor.” (lines 369-371)

“... and thus not included in the previous analysis. ” (lines 376-377)

“MHC-Y has also been identified in gorillas (Gogo-Y) (Hans et al., 2017), so we anticipate that Gogo-OLI will soon be confirmed. This evidence suggests that the MHC-Y and -OLI-containing haplotype is at least as old as the human-gorilla split. Our study is the first to place MHC-OLI in the overall story of MHC haplotype evolution“ (lines 381-384)

“Appendix 3 explains the pieces of evidence leading to all of these conclusions (and more!) in more detail.” (lines 395-396)

“However, looking at this exon alone does not give us a complete picture.” (lines 410-411)

“...instead of with other ape/OWM sequences, …” (lines 413-414)

“Figure 7 shows plausible steps that might have generated the current haplotypes and patterns of variation that we see in present-day primates. However, some species are poorly represented in the data, so the relationships between their genes and haplotypes are somewhat unclear.” (lines 427-429)

“(and more-diverged)” (line 473)

“(of both classes)” (line 476)

“..., although the classes differ in their rate of evolution.”  (line 487-488)

“Including these pseudogenes in our trees helped us construct a new model of $\alpha$-block haplotype evolution. “ (lines 517-518)

(4) Line 480-82: "Notably...." why is this notable? Don't merely state that something is notable, explain what makes it especially worth drawing the reader's attention to: in what way is it particularly significant or surprising?

We have changed the text from “Notably” to “In particular” (line 390) so that readers are expecting us to list some specific findings. Similarly, we changed “Notably” to “Specifically” (line 515).

(5) The end of the discussion is weak: "provide context" is too vague and not a strong statement of something that we learned that we didn't know before, or its importance. This is followed by "This work will provide a jumping-off point for further exploration..." such as? What questions does this paper raise that merit further work?

We have made this paragraph more specific and added some possible future research directions. It now reads “By treating the MHC genes as a gene family and including more data than ever before, this work enhances our understanding of the evolutionary history of this remarkable region. Our extensive set of trees incorporating classical genes, non-classical genes, pseudogenes, gene fragments, and alleles of medical interest across a wide range of species will provide context for future evolutionary, genomic, disease, and immunologic studies. For example, this work provides a jumping-off-point for further exploration of the evolutionary processes affecting different subsets of the gene family and the nuances of immune system function in different species. This study also provides a necessary framework for understanding the evolution of particular allelic lineages within specific MHC genes, which we explore further in our companion paper \citep{Fortier2025b}. Both studies shed light on MHC gene family evolutionary dynamics and bring us closer to understanding the evolutionary tradeoffs involved in MHC disease associations.” (lines 576-586)

Reviewer #3 (Recommendations for the authors):

(1) Figure 1 et seq. Classifying genes as having 'classical', 'non-classical' and 'dual' properties is notoriously difficult in non-model organisms due to the lack of relevant information. As you have characterised a number of genes for the first time in this paper and could not rely entirely on published classifications, please indicate the criteria you used for classification.

The roles of these proteins are not necessarily conserved between closely related species, and experimental evidence is needed to evaluate this. However, in the absence of such evidence, wherever possible we have provided our best guess as to the roles of the orthologous genes in other species, presented in Figure 1 - source data 1 and Figure 2 - source data 1. This is based on whatever evidence is available at the moment, sometimes experimental but typically based on dN/dS ratios and other indirect measures.

(2) Line 61 It's important to mention that classical MHC molecules present antigenic peptides to T cells with variable alphabeta T cell receptors, as non-classical MHC molecules may interact with other T cell subsets/types.

Thank you for pointing this out; we have updated the text to make this clearer (lines 63-65). We changed “‘Classical’ MHC molecules perform antigen presentation to T cells---a key part of adaptive immunity---while ‘non-classical’ molecules have niche immune roles.” to “‘Classical’ MHC molecules perform antigen presentation to T cells with variable alphabeta TCRs---a key part of adaptive immunity---while ‘non-classical’ molecules have niche immune roles.”

(3) Perhaps it's worth mentioning in the introduction that you are deliberately excluding highly divergent non-classical MHC molecules such as CD1.

Thank you, it’s worth clarifying exactly what molecules we are discussing. We have added a sentence to the introduction (lines 38-43): “Having originated in the jawed vertebrates, this group of genes is now involved in diverse functions including lipid metabolism, iron uptake regulation, and immune system function (proteins such as zinc-𝛼2-glycoprotein (ZAG), human hemochromatosis protein (HFE), MHC class I chain–related proteins (MICA, MICB), and the CD1 family) \citep{Hansen2007,Kupfermann1999,Kaufman2022,Adams2013}. However, here we focus on…”

(4) Line 94-105 This material presents results, it could be moved to the results section as it now somewhat disrupts the flow.

We feel it is important to include a “teaser” of the results in the introduction, which can be slightly more detailed than that in the abstract.

(5) Line 118-131 This opening section of the results sets the stage for the whole presentation and contains important information that I feel needs to be expanded to include an overview and justification of your methodological choices. As the M&M section is at the end of the MS (and contains limited justification), some information on two aspects is needed here for the benefit of the reader. First, as far as I understand, all phylogenetic inferences were based entirely on DNA sequences of individual (in some cases concatenated) exons. It would be useful for the reader to explain why you've chosen to rely on DNA rather than protein sequences, even though some of the genes you include in the phylogenetic analysis are highly divergent. Second, a reader might wonder how the "maximum clade credibility tree" from the Bayesian analysis compares to commonly seen trees with bootstrap support or posterior probability values assigned to particular clades. Personally, I think that the authors' approach to identifying and presenting representative trees is reasonable (although one might wonder why "Maximum clade credibility tree" and not "Maximum credibility tree" https://www.beast2.org/summarizing-posterior-trees/), since they are working with a large number of short, sometimes divergent and sometimes rather similar sequences - in such cases, a requirement for strict clade support could result in trees composed largely of polytomies. However, I feel it's necessary to be explicit about this and to acknowledge that the relationships represented by fully resolved bifurcating representative trees and interpreted in the study may not actually be highly supported in the sense that many readers might expect. In other words, the reader should be aware from the outset of what the phylogenies that are so central to the paper represent.

We chose to rely on DNA rather than protein sequences because convergent evolution is likely to happen in regions that code for extremely important functions such as adaptive and innate immunity. Convergent evolution acts upon proteins while trans-species polymorphism retains ancient nucleotide variation, so studying the DNA sequence can help tease apart convergent evolution from trans-species polymorphism.

As for the “maximum clade credibility tree”, this is a matter of confusing nomenclature. In the online reference guide (https://www.beast2.org/summarizing-posterior-trees/), the tree with the maximum product of the posterior clade probabilities is called the “maximum credibility tree” while the tree that has the maximum sum of posterior clade probabilities is called the “Maximum credibility tree”. The “Maximum credibility tree” (referring to the sum) appears to have only been named in this way in the first version of TreeAnnotator. However, the version of TreeAnnotator that I used lists the options “maximum clade credibility tree” and “maximum sum of clade probabilities”. So the context suggests that the “maximum clade credibility tree” option is actually maximizing the product. This “maximum clade credibility tree” is the setting I used for this project (in TreeAnnotator version 2.6.3).

We agree that readers may not fully grasp what the collapsed trees represent upon first read. We have added a sentence to the beginning of the results (line 188-190) to make this more explicit.

(6) Line 224, you're referring to the DPB1*09 lineage, not the DRB1*09 lineage.

Indeed! We have changed these typos.

(7) Line 409, why "Differences between MHC subfamilies" and not "Differences between MHC classes"?

We chose the word “subfamilies” because we discuss the difference between classical and non-classical genes in addition to differences between Class I and Class II genes.

(8) Line 529-544 This might work better as a table.

We agree! This information is now presented as Table 1.

(9) Line 547 MHC-DRB9 appears out of the blue here - please say why you are singling it out.

Great point! We added a paragraph (lines 614-623) to explain why this was necessary.

(10) Line 550-551 Even though you've screened the hits manually, it would be helpful to outline your criteria for this search.

Thank you! We’ve added a couple of sentences to explain how we did this (lines 607-610).

(11) Line 556-580 please provide nucleotide alignments as supplementary data so that the reader can get an idea of the actual divergence of the sequences that have been aligned together.

Thank you! We’ve added nucleotide alignments as supplementary files.

(12) Line 651-652 Why "Maximum clade credibility tree" and not "Maximum credibility tree"? 

Repeat of (5). This is a matter of confusing nomenclature. In the online reference guide (https://www.beast2.org/summarizing-posterior-trees/), the tree with the maximum product of the posterior clade probabilities is called the “maximum credibility tree” while the tree that has the maximum sum of posterior clade probabilities is called the “Maximum credibility tree”. The “Maximum credibility tree” (referring to the sum) appears to have only been named in this way in the first version of TreeAnnotator. However, the version of TreeAnnotator that I used lists the options “maximum clade credibility tree” and “maximum sum of clade probabilities”. So the context suggests that the “maximum clade credibility tree” option is actually maximizing the product. This “maximum clade credibility tree” is the setting I used for this project (in TreeAnnotator version 2.6.3).

(13) In the appendices, links to references do not work as expected.

We will make sure these work properly when we receive the proofs.

Author response:

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

Reviewer #1 (Public Review):

but see Franzius, Sprekeler, Wiskott, PLoS Computational Biology, 2007

We have discussed the differences with this work in the response to Editor recommendations above.

While the findings reported here are interesting, it is unclear whether they are the consequence of the specific model setting, and how well they would generalize.

We have considered deep vision models across different architectures in our paper, which include traditional feedforward convolutional neural networks (VGG-16), convolutional neural networks with skip connections (ResNet-50) and the Vision Transformer (VIT) which employs self-attention instead of convolution as its core information processing unit.

In particular, examining the pictures shown in Fig. 1A, it seems that local walls of the ’box’ contain strong oriented features that are distinct across different views. Perhaps the response of oriented visual filters can leverage these features to uniquely determine the spatial variable. This is concerning because this is a very specific setting that is unlikely to generalize.

The experimental set up is based on experimental studies of spatial cognition in rodents. They are typically foraging in square or circular environments. Indeed, square environments will have more borders and corners that will provide information about the spatial environment, which is true in both empirical studies and our simulations. In any navigation task, and especially more realistic environments, visual information such as borders or landmarks likely play a major role in spatial information available to the agent. In fact, studies that do not consider sensory information to contribute to spatial information are likely missing a major part of how animals navigate.

The prediction would be that place cells/head direction cells should go away in darkness. This implies that key aspects of functional cell types in the spatial cognition are missing in the current modeling framework.

We addressed this comment in our response to the editor’s highlight. To briefly recap, we do not intend to propose a comprehensive model of the brain that captures all spatial phenomena, as we would not expect this from an object recognition network. Instead, we show that such a simple and nonspatial model can reproduce key signatures of spatial cells, raising important questions about how we interpret spatial cell types that dominate current research.

Reviewer #2 (Public Review):

The network used in the paper is still guided by a spatial error signal [...] one could say that the authors are in some way hacking this architecture and turning it into a spatial navigation one through learning.

To be clear, the base networks we use do not undergo spatial error training. They have either been pre-trained on image classification tasks or are untrained. We used a standard neuroscience approach: training linear decoders on representations to assess the spatial information present in the network layers. The higher decoding errors in early layer representations (Fig. 2A) indicate that spatial information differs across layers—an effect that cannot be attributed to the linear decoder alone.

My question is whether the paper is fighting an already won battle.

Intuitive cell type discovery are still being celebrated. Concentrating on this kind of cell type discovery has broader implications that could be deleterious to the future of science. One point to note is that this issue depends on the area or subfield of neuroscience. In some subfields, papers that claim to find cell types with a strong claim of specific functions are relatively rare, and population coding is common (e.g., cognitive control in primate prefrontal cortex, neural dynamics of motor control). Although rodent neuroscience as a field is increasingly adopting population approaches, influential researchers and labs are still publishing “cell types” and in top journals (here are a few from 2017-2024: Goal cells (Sarel et al., 2017), Object-vector cells (Høydal et al., 2019), 3D place cells (Grieves et al., 2020), Lap cells (Sun et al., 2020), Goal-vector cells (Ormond and O’Keefe, 2022), Predictive grid cells (Ouchi and Fujisawa, 2024).

In some cases, identification of cell types is only considered a part of the story, and there are analyses on behavior, neural populations, and inactivationbased studies. However, our view (and suggest this is shared amongst most researchers) is that a major reason these papers are reviewed and accepted to top journals is because they have a simple, intuitive “cell type” discovery headline, even if it is not the key finding or analysis that supports the insightful aspects of the work. This is unnecessary and misleading to students of neuroscience, related fields, and the public, it affects private and public funding priorities and in turn the future of science. Worse, it could lead the field down the wrong path, or at the least distribute attention and resources to methods and papers that could be providing deeper insights. Consistent with the central message of our work, we believe the field should prioritize theoretical and functional insights over the discovery of new “cell types”.

Reviewer #3 (Public Review):

The ability to linearly decode position from a large number of units is not a strong test of spatial information, nor is it a measure of spatial cognition

Using a linear decoder to test what information is contained in a population of neurons available for downstream areas is a common technique in neuroscience (Tong and Pratte, 2012; DiCarlo et al., 2012) including spatial cells (e.g., Diehl et al. 2017; Horrocks et al. 2024). A linear decoder is used because it is a direct mapping from neurons to potential output behavior. In other words, it only needs to learn some mapping to link one set of neurons to another set which can “read out” the information. As such, it is a measure of the information contained in the population, and it is a lower bound of the information contained - as both biological and artificial neurons can do more complex nonlinear operations (as the activation function is nonlinear).

We understand the reviewer may understand this concept but we explain it here to justify our position and for completeness of this public review.

For example, consider the head direction cells in Figure 3C. In addition to increased activity in some directions, these cells also have a high degree of spatial nonuniformity, suggesting they are responding to specific visual features of the environment. In contrast, the majority of HD cells in the brain are only very weakly spatially selective, if at all, once an animal’s spatial occupancy is accounted for (Taube et al 1990, JNeurosci). While the preferred orientation of these cells are anchored to prominent visual cues, when they rotate with changing visual cues the entire head direction system rotates together (cells’ relative orientation relationships are maintained, including those that encode directions facing AWAY from the moved cue), and thus these responses cannot be simply independent sensory-tuned cells responding to the sensory change) (Taube et al 1990 JNeurosci, Zugaro et al 2003 JNeurosci, Ajbi et al 2023).

As we have noted in our response to the editor, one of the main issues is how the criteria to assess what they are interested in is created in a subjective, and biased way, in a circular fashion (seeing spatial-like responses, developing criteria to determine a spatial response, select a threshold).

All the examples the reviewer provides concentrate on strict criteria developed after finding such cells. What is the purpose of these cells for function, for behavior? Just finding a cell that looks like it is tuned to something does not explain its function. Neuroscience began with tuning curves in part due to methodological constraints, which was a promising start, but we propose that this is not the way forward.

The metrics used by the authors to quantify place cell tuning are not clearly defined in the methods, but do not seem to be as stringent as those commonly used in real data. (e.g. spatial information, Skaggs et al 1992 NeurIPS).

We identified place cells following the definition from Tanni et al. (2022), by one of the leading labs in the field. Since neurons in DNNs lack spikes, we adapted their criteria by focusing on the number of spatial bins in the ratemap rather than spike-based measures. However, our central argument is that the very act of defining spatial cells is problematic. Researchers set out to find place cells to study spatial representations, find spatially selective cells with subjective, qualitative criteria (sometimes combined with prior quantitative criteria, also subjectively defined), then try to fine-tune the criteria to more “stringent” criteria, depending on the experimental data at hand. It is not uncommon to see methodological sections that use qualitative judgments, such as: “To avoid bias ... we applied a loose criteria for place cells” Tanaka et al. (2018) , which reflects the lack of clarity for and subjectivity of place cell selection criteria.

A simple literature survey reveals inconsistent criteria across studies. For place field selection, Dombeck et al. (2010) required mean firing rates exceeding 25% of peak rate, while Tanaka et al. (2018) used a 20% threshold. Speed thresholds also vary dramatically: Dombeck et al. (2010) calculated firing rates only when mice moved faster than 8.3 cm/s, whereas Tanaka et al. (2018) used 2 cm/s. Additional criteria differ further: Tanaka et al. (2018) required firing rates between 1-10 Hz and excluded cells with place fields larger than 1/3 of the area, while Dombeck et al. (2010) selected fields above 1.5 Hz, and Tanni et al. (2022) used a 10 spatial bins to 1/2 area threshold. As Dombeck et al. (2010) noted, differences in recording methods and place field definitions lead to varying numbers of identified place cells. Moreover, Grijseels et al. (2021) demonstrated that different detection methods produce vastly different place cell counts with minimal overlap between identified populations.

This reflects a deeper issue. Unlike structurally and genetically defined cell types (e.g., pyramidal neurons, interneurons, dopamingeric neurons, cFos expressing neurons), spatial cells lack such clarity in terms of structural or functional specialization and it is unclear whether such “cell types” should be considered cell types in the same way. While scientific progress requires standardized definitions, the question remains whether defining spatial cells through myriad different criteria advances our understanding of spatial cognition. Are researchers finding the same cells? Could they be targeting different populations? Are they missing cells crucial for spatial cognition that they exclude due to the criteria used? We think this is likely. The inconsistency matters because different criteria may capture genuinely different neural populations or computational processes.

Variability in definitions and criteria is an issue in any field. However, as we have stated, the deeper issue is whether we should be defining and selecting these cells at all before commencing analysis. By defining and restricting to spatial “cell types”, we risk comparing fundamentally different phenomena across studies, and worse, missing the fundamental unit of spatial cognition (e.g., the population).

We have added a paragraph in Discussion (lines 357-366) noting the inconsistency in place cell selection criteria in the literature and the consequences of using varying criteria.

We have also added a sentence (lines 354-356) raising the comparison of functionally defined spatial cell types with structurally and genetically defined cell types in the Discussion.

Thus, the question is not whether spatially tuned cells are influenced by sensory information, but whether feed-forward sensory processing alone is sufficient to account for their observed turning properties and responses to sensory manipulations.

These issues indicate a more significant underlying issue of scientific methodology relating to the interpretation of their result and its impact on neuroscientific research. Specifically, in order to make strong claims about experimental data, it is not enough to show that a control (i.e. a null hypothesis) exists, one needs to demonstrate that experimental observations are quantitatively no better than that control.

Where the authors state that ”In summary, complex networks that are not spatial systems, coupled with environmental input, appear sufficient to decode spatial information.” what they have really shown is that it is possible to decode *some degree* of spatial information. This is a null hypothesis (that observations of spatial tuning do not reflect a ”spatial system”), and the comparison must be made to experimental data to test if the so-called ”spatial” networks in the brain have more cells with more reliable spatial info than a complex-visual control.

We agree that good null hypotheses with quantitative comparisons are important. However, it is not clear that researchers in the field have not been using a null hypothesis, rather they make the assumption that these cell types exist and are functional in the way they assume. We provide one null hypothesis. The field can and should develop more and stronger null hypotheses.

In our work, we are mainly focusing on criteria of finding spatial cells, and making the argument that simply doing this is misleading. Researcher develop criteria and find such cells, but often do not go further to assess whether they are real cell “types”, especially if they exclude other cells which can be misleading if other cells also play a role in the function of interest.

But from many other experiments including causal manipulations (e.g. Robinson et al 2020 Cell, DeLauilleon et al 2015 Nat Neuro), which the authors conveniently ignore. Thus, I do not find their argument, as strongly stated as it is, to be well-supported.

We acknowledge that there are several studies that have performed inactivation studies that suggest a strong role for place cells in spatial behavior. Most studies do not conduct comprehensive analyses to confirm that their place cells are in fact crucial for the behavior at hand.

One question is how the criteria were determined. Did the researchers make their criteria based on what “worked”, so they did not exclude cells relevant to the behavior? What if their criteria were different, then the argument could have been that non-place cells also contribute to behavior.

Another question is whether these cells are the same kinds of cells across studies and animals, given the varied criteria across studies? As most studies do not follow the same procedures, it is unclear whether we can generalize these results across cells and indeed, across task and spatial environments.

Finally, does the fact that the place cells – the strongly selective cells with a place field – have a strong role in navigation provide any insight into the mechanism? Identifying cells by itself does not contribute to our understanding of how they work. Consistent with our main message, we argue that performing analyses and building computational models that uncover how the function of interest works is more valuable than simply naming cells.

Finally, I find a major weakness of the paper to be the framing of the results in opposition to, as opposed to contributing to, the study of spatially tuned cells. For example, the authors state that ”If a perception system devoid of a spatial component demonstrates classically spatially-tuned unit representations, such as place, head-direction, and border cells, can ”spatial cells” truly be regarded as ’spatial’?” Setting aside the issue of whether the perception system in question does indeed demonstrate spatiallytuned unit representations comparable to those in the brain, I ask ”Why not?” This seems to be a semantic game of reading more into a name then is necessarily there. The names (place cells, grid cells, border cells, etc) describe an observation (that cells are observed to fire in certain areas of an animal’s environment). They need not be a mechanistic claim... This is evidenced by the fact that even within e.g. the place cell community, there is debate about these cells’ mechanisms and function (eg memory, navigation, etc), or if they can even be said to serve only a single function. However, they are still referred to as place cells, not as a statement of their function but as a history-dependent label that refers to their observed correlates with experimental variables. Thus, the observation that spatially tuned cells are ”inevitable derivatives of any complex system” is itself an interesting finding which *contributes to*, rather than contradicts, the study of these cells. It seems that the authors have a specific definition in mind when they say that a cell is ”truly” ”spatial” or that a biological or artificial neural network is a ”spatial system”, but this definition is not stated, and it is not clear that the terminology used in the field presupposes their definition.

We have to agree to disagree with the reviewer on this point. Although researchers may reflect on their work and discuss what the mechanistic role of these cells are, it is widely perceived that cell type discovery is perceived as important to journals and funders due to its intuitive appeal and easy-tounderstand impact – even if there is no finding of interest to be reported. As noted in the comment above, papers claiming cell type discovery continue to be published in top journals and is continued to be funded.

Our argument is that maybe “cell type” discovery research should not celebrated in the way it is, and in fact they shouldn’t be discovered when they are not genuine cell types like structural or genetic cell types. By using this term it make it appear like they are something they are not, which is misleading. They may be important cells, but providing a name like a “place” cell also suggests other cells are not encoding space - which is very unlikely to be true.

In sum, our view is that finding and naming cells through a flawed theoretical lens that may not actually function as their names suggests can lead us down the wrong path and be detrimental to science.

Reviewer #1 (Recommendations For The Authors):

The novelty of the current study relative to the work by Franzius, Sprekeler, Wiskott (PLoS Computational Biology, 2007) needs to be carefully addressed. That study also modeled the spatial correlates based on visual inputs.

Our work differs from Franzius et al. (2007) on both theoretical and experimental fronts. While both studies challenge the mechanisms underlying spatial cell formation, our theoretical contributions diverge. Franzius et al. (2007) assume spatial cells are inherently important for spatial cognition and propose a sensory-driven computational mechanism as an alternative to mainstream path integration frameworks for how spatial cells arise and support spatial cognition. In contrast, we challenge the notion that spatial cells are special at all. Using a model with no spatial grounding, we demonstrate that 1) spatial cells as naturally emerge from complex non-linear processing and 2) are not particularly useful for spatial decoding tasks, suggesting they are not crucial for spatial cognition.

Our approach employs null models with fixed weights—either pretrained on classification tasks or entirely random—that process visual information non-sequentially. These models serve as general-purpose information processors without spatial grounding. In contrast, Franzius et al. (2007)’s model learns directly from environmental visual information, and the emergence of spatial cells (place or head-direction cells) in their framework depends on input statistics, such as rotation and translation speeds. Notably, their model does not simultaneously generate both place and head-direction cells; the outcome varies with the relative speed of rotation versus translation. Their sensory-driven model indirectly incorporates motion information through learning, exhibiting a time-dependence influenced by slow-feature analysis.

Conversely, our model simultaneously produces units with place and headdirection cell profiles by processing visual inputs sampled randomly across locations and angles, independent of temporal or motion-related factors. This positions our model as a more general and fundamental null hypothesis, ideal for challenging prevailing theories on spatial cells due to its complete lack of spatial or motion grounding.

Finally, unlike Franzius et al. (2007), who do not evaluate the functional utility of their spatial representations, we test whether the emergent spatial cells are useful for spatial decoding. We find that not only do spatial cells emerge in our non-spatial model, but they also fail to significantly aid in location or head-direction decoding. This is the central contribution of our work: spatial cells can arise without spatial or sensory grounding, and their functional relevance is limited. We have updated the manuscript to clarify the novelty of the current contribution to previous work (lines 324-335).

In Fig. 2, it may be useful to plot the error in absolute units, rather than the normalized error. The direction decoding can be quantified in terms of degree Also, it would be helpful to compare the accuracy of spatial localization to that of the actual place cells in rodents.

We argue it makes more sense and put comparison in perspective when we normalize the error by dividing the maximal error possible under each task. For transparency, we plot the errors in absolute physical units used by the Unity game engine in the updated Appendix (Fig. 1).

Reviewer #2 (Recommendations For The Authors):

Regarding the involvement of ’classified cells’ in decoding, I think a useful way to present the results would be to show the relationship between ’placeness’, ’directioness’ and ’borderness’ and the strength of the decoder weights. Either as a correlation or as a full scatter plot.

We appreciate your suggestion to visualize the relationship between units’ spatial properties and their corresponding decoder weights. We believe it would be an important addition to our existing results. Based on the exclusion analyses, we anticipated the correlation to be low, and the additional results support this expectation.

As an example, we present unit plots below for VGG-16 (pre-trained and untrained, at its penultimate layer with sampling rate equals 0.3; Author response image 1 and 2). Additional plots for various layers and across models are included in the supplementary materials (Fig. S12-S28). Consistently across conditions, we observed no significant correlations between units’ spatial properties (e.g., placeness) and their decoding weight strengths. These results further corroborate the conclusions drawn from our exclusion analyses.

Reviewer #3 (Recommendations For The Authors):

My main suggestions are that the authors: -perform manipulations to the sensory environment similar to those done in experimental work, and report if their tuned cells respond in similar ways -quantitatively compare the degree of spatial tuning in their networks to that seen in publicly available data -re-frame the discussion of their results to critically engage with and contribute to the field and its past work on sensory influences to these cells

As we noted in our opening section, our model is not intended as a model of the brain. It is a non-spatial null model, and we present the surprising finding that even such a model contains spatial cell-like units if identified using criteria typically used in the field. This raises the question whether simply finding cells that show spatial properties is sufficient to grant the special status of “cell type” that is involved in the brain function of interest.

Author response image 1.

VGG-16 (pre-trained), penultimate layer units, show no apparent relationship between spatial properties and their decoder weight strengths.

Author response image 2.

VGG-16 (untrained), penultimate layer units, show no apparent relationship between spatial properties and their decoder weight strengths.

Furthermore, our main simulations were designed to be compared to experimental work where rodents foraged around square environments in the lab. We did not do an extensive set of simulations as the purpose of our study is not to show that we capture exactly every single experimental finding, but rather raise the issues with the functional cell type definition and identification approach for progressing neuroscientific knowledge.

Finally, as we note in more detail below, different labs use different criteria for identifying spatial cells, which depend both on the lab and the experimental design. Our point is that we can identify such cells using criteria set by neuroscientists, and that such cell types may not reflect any special status in spatial processing. Additional simulations that show less alignment with certain datasets will not provide support for or against our general message.

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Reply to the reviewers

Reviewer 1, point 1: In general, the statistical analysis is not transparent. The size of the sample, i.e. the number of observations or data points, is never specified. This information is essential for further evaluation of the statistical details.

The size of each sample quantified, given as number of ommatidia/number of retinas, is indicated in the figure legends. This must have escaped the attention of reviewer 1, so we have added a sentence in the legend of Fig. 2 to state it more clearly. We think that the figure legends are the best place to put this information for ease of comparison to the figures.

*Reviewer 1, point 2: To gain a better understanding of chitin deposition, it would be beneficial to have data on Kkv overexpression in cone cells versus outer pigment cells. Does it cause reb/exp-like effects on chitin deposition and corneal lens formation? Furthermore, can the authors rule out the involvement of chitin synthase 2 in chitin matrix formation and the retention of the matrix in kkv knockdowns? *

We will generate clones of cells that over-express Kkv in either central cells (cone and primary pigment cells) or lattice cells (secondary and tertiary pigment cells), using the same drivers that we used to over-express Reb, and will examine chitin secretion at 54 h after puparium formation (APF) and in adults.

As there are no available mutations in Chitin synthase 2 (Chs2), we will knock it down with RNAi in all retinal cells using lGMR-GAL4 and look for corneal lens defects. However, we think that Chs2 is unlikely to contribute chitin to the corneal lens, because its expression is restricted to the digestive system, and because kkv knockdown essentially eliminates chitin from the corneal lens.

*Reviewer 1, point 3: Recent results published by the authors regarding ZP domain proteins, such as dusky-like (dyl), have not been adequately discussed in the context of chitin secretion and Kkv expression, a matter that must be addressed. It has been demonstrated that dyl mutants do not affect Kkv expression, but chitin levels are reduced. Does Dyl exhibit Kkv-like phenotypes? Furthermore, what is the expression of Dyl or Dmupy in Kkv knockdowns? Is there any interaction between the ZP domain protein matrix and the chitin matrix required for lens formation? *

In dyl mutants, chitin deposition is delayed, but it does accumulate later in development, so the phenotype is different from kkv mutants. We have clarified this in the manuscript (p. 6). To address the other points, we will examine the expression of Dyl and of Dumpy-YFP in mid-pupal and late pupal retinas in which kkv is knocked down in all cells with lGMR-GAL4. The ZP protein matrix is originally deposited before chitin secretion begins, so we will examine whether loss of chitin affects its later maintenance.

*Reviewer 1, point 4: What is retained in the chitin matrix if chitin is missing in kkv knockdown? Is it the ZP domain matrix (see the above question) or are the chitin matrix proteins also involved, such as Obst-A, Obst-C (Gasp), Knk and others? Obst proteins are particularly essential for the regular packaging of chitin and thus for the formation of the chitin layer, which is shown in Fig. 1. Beyond this story, it would also be interesting to see how the aforementioned chitin matrix proteins (Obst-A, Obst-C (Gasp), Knk and others) impact lens formation. *

Adult corneal lenses derived from kkv knockdown retinas do not contain chitin, but there is remaining corneal lens material. We do not think that this is the ZP domain matrix, as this is normally lost in late pupal development, but we will check whether Dpy-YFP is retained in kkv knockdown adults. We will try to detect Obst-A and Gasp proteins using available antibodies. However, this may not be successful, as we have found that antibodies do not penetrate the corneal lens well. Our transcriptomic studies have identified numerous secreted proteins that are expressed at high levels in the mid-pupal retina and could be components of the corneal lens. We may be able to detect some of these using fluorescently tagged forms, but it is possible that the currently available tools will not be sufficient to answer this question.

We have begun to work on how some of these proteins affect corneal lens structure, but this will take a significant amount of time and we think it would work better as a separate manuscript. We see our current manuscript as a short and focused story about the importance of the source of chitin in determining corneal lens shape.

*Reviewer 1, minor comment 1: Figure 1 is not easily comprehensible for those who are not already familiar with the subject of eye development. Fig -1A' please label the cone cells and pigment cells. *

We have labeled these cells in Fig. 1A’’.

*Reviewer 1, minor comment 2: Fig. 1H - The meaning of the abbreviations and numbers is not given in the legend. It would also be beneficial to include a meaningful cartoon illustrating the corneal lens situation before and after chitin secretion, as shown in Figure 3. *

We have defined the abbreviations in the figure legend. Fig. 1H did show the corneal lens situation before, during and after chitin secretion, but we have added the cone and pigment cells to the 72 h APF and adult diagrams to make them more meaningful (now Fig. 1I).

*Reviewer 1, minor comment 3: Fig.1 F when does the authors recognize a first chitin assembly as initial corneal lens at the eye and how does it look like? Chitin expression is high already at 54h APF, which means 20 hours earlier. *

We think that the reviewer is asking when the chitin first starts to form a dome shape. We have added an orthogonal view of chitin in a 54 h APF retina viewed with LIGHTNING microscopy, showing that the external curvature is already present at this stage (new Fig. 1F).

*Reviewer 1, minor comment 4: Page 6 / Fig 2E: cells autonomously synthesize chitin and no lateral diffusion. Please label which lens contains chitin and which not *

Fig. 2E shows part of a retina in which kkv has been knocked down in all cells, so none of the corneal lenses contain chitin. We have clarified this in the legend to Fig. 2.

*Reviewer 1, minor comment 5: Page 7: The authors state that reb/exp knockdown affects external and internal curvature. However, Fig. S1 statistics does not support this statement. *

We were referring to the double knockdown, which Fig. 2L, M show is significant, and not to the single knockdowns quantified in Fig. S1. We have clarified this in the text.

*Reviewer 1, minor comment 6: Fig.2 and Fig. S1: what is Chp (Chaoptin)? *

We have stated in the legend to Fig. 2 that Chaoptin is a component of photoreceptor rhabdomeres.

*Reviewer 1, minor comment 7: Fig. S1E,I: which part of the eye is marked by the chitin staining outside the cone and pigment cells? *

Chitin is still present in the mechanosensory bristles in Fig.S1I, as these do not express lGMR-GAL4. We have stated this in the figure legend.

*Reviewer 1, minor comment 8: Fig. 2 L,M, Why do exp/reb show different statistical results at outer angle in exp and reb knockdown when compared with the IGMR driver line, although chitin reduction is eliminated in exp knockdown already from 54h APF onwards? *

The double knockdown of exp and reb has a more significant effect on the adult corneal lens outer angle than the single exp knockdown, even though the exp knockdown lacks chitin at 54 h APF. We believe that this is because Reb is sufficient for some chitin synthesis at later stages of development. This was mentioned in the text (p. 6) and we have added further clarification in the legend to Fig. S1.

*Reviewer 1, minor comment 9: Fig 3 G-H: please clarify where the chitin reduction can be observed at the edge of adult corneal lens and provide comparable wt staining's. Fig. S2 D. What was the normalization and the sample number? *

We have added a high magnification image of a mosaic ommatidium with one wild-type and one kkv knockdown edge, showing the region at the edge of the corneal lens in which chitin fluorescence was quantified and the central region used for the normalization (Fig. 3I). The sample numbers are given in the legend to Fig. S2D.

Reviewer 1, minor comment 10: Page 6, last paragraph: I fully agree that ZP domain proteins may retain other corneal lens components. But deeper discussion is missing. It should be noted that the authors hypothesis fits well to the proposed function of the ZP matrix in providing chitin matrix adhesion to the underlying cell surface. A loss of the ZP domain protein Piopio causes loss of the chitin matrix as show recently in trachea and at epidermal tendon cells (Göpfert et al., 2025; https://www.sciencedirect.com/science/article/pii/S1742706125003733). Furthermore, a recent publication identifies ZPD proteins as modular units that establish the mechanical environment essential for nanoscale morphogenesis (Itakura et al., https://www.biorxiv.org/content/10.1101/2024.08.20.608778v1.full.pdf*). This should be cited and discussed accordingly.

It could be that outer and inner part of the chitin is different in ultrastructure due to expression pattern. In dragonfly the surface morphology analysis by scanning electron microscopy revealed that the outer part of corneal lenses consisted of long chitin fibrils with regular arrays of papillary structures while the smoother inner part had concentric lamellated chitin formation with shorter chitin nanofibrils (Kaya et al., 2016; https://www.sciencedirect.com/science/article/pii/S0141813016303646?via%3Dihub#fig0020) . Thus, a ultrastructure analyses would be very beneficial, or at least a detailed discussion. *

We have added a discussion of these points and papers to the text (p. 6 and 9). Although we are not specifically addressing differences between the inner and outer parts of the corneal lens in this manuscript, we have now included a high-resolution LIGHTNING image showing how the layered structure of the corneal lens is affected when chitin production by central cells is increased (Fig. 4F).

*Reviewer 2, point 1: Adult corneal lenses lacking chitin still form a thin structure in kkv RNAi. The authors suggest that this may be due to the presence of the ZP domain proteins Dyl, Dpy and Pio. Immunostaining for these ZP domain proteins could provide supporting evidence. *

To clarify, we meant to say that the earlier presence of the ZP domain matrix could retain components other than chitin in the corneal lens. The ZP domain proteins are no longer present in the adult. We have made this clearer in the text. As described under reviewer 1, points 3 and 4, we will examine Dyl and Dpy-YFP expression in kkv knockdown retinas at mid-pupal and adult stages, and we will also look at the expression of another ZP domain protein, Piopio.

*Reviewer 2, minor comment 1: At 50 h APF, Kkv (Fig. 2B, B') and Reb (Fig. S1A, A') appear to be expressed at higher levels in lattice cells than in central cells, even though chitin is mainly present in the central cells at this time (Fig. 1B-B'). Discuss possible explanation for their expression pattern and their roles at this stage. *

We agree that this is a surprising result. We have added a discussion of possible explanations, such as the lack of another component necessary for chitin secretion in lattice cells at this stage, or the presence of high levels of chitinases (p. 7).

*Reviewer 2, minor comment 2: Fig. 1F and G: Indicate that the cryosection images represent single ommatidia, and label "external" and "internal" to help orient readers. *

We have made these changes to the figure panels (now G and H), and indicated in the legend that they are single ommatidia.

*Reviewer 2, minor comment 3: Figure 2. The cartoon diagram showing the angle measurement (currently Fig S1K) should be moved to the main figure to help readers understand the quantifications. *

We have moved this diagram to Figure 2L.

*Reviewer 2, minor comment 4: Figure 3H. It would be helpful to clearly mark the edge of the corneal lens in the chitin intensity image. *

As described under reviewer 1, minor comment 9, we have added a high magnification picture showing the edge region used for chitin quantification (Fig. 3I), which should also address reviewer 2’s concern.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Wang et al. studied an old, still unresolved problem: Why are reaching movements often biased? Using data from a set of new experiments and from earlier studies, they identified how the bias in reach direction varies with movement direction, and how this depends on factors such as the hand used, the presence of visual feedback, the size and location of the workspace, the visibility of the start position and implicit sensorimotor adaptation. They then examined whether a visual bias, a proprioceptive bias, a bias in the transformation from visual to proprioceptive coordinates and/or biomechanical factors could explain the observed patterns of biases. The authors conclude that biases are best explained by a combination of transformation and visual biases.

A strength of this study is that it used a wide range of experimental conditions with also a high resolution of movement directions and large numbers of participants, which produced a much more complete picture of the factors determining movement biases than previous studies did. The study used an original, powerful, and elegant method to distinguish between the various possible origins of motor bias, based on the number of peaks in the motor bias plotted as a function of movement direction. The biomechanical explanation of motor biases could not be tested in this way, but this explanation was excluded in a different way using data on implicit sensorimotor adaptation. This was also an elegant method as it allowed the authors to test biomechanical explanations without the need to commit to a certain biomechanical cost function.

We thank the reviewer for their enthusiastic comments.

(1) The main weakness of the study is that it rests on the assumption that the number of peaks in the bias function is indicative of the origin of the bias. Specifically, it is assumed that a proprioceptive bias leads to a single peak, a transformation bias to two peaks, and a visual bias to four peaks, but these assumptions are not well substantiated. Especially the assumption that a transformation bias leads to two peaks is questionable. It is motivated by the fact that biases found when participants matched the position of their unseen hand with a visual target are consistent with this pattern. However, it is unclear why that task would measure only the effect of transformation biases, and not also the effects of visual and proprioceptive biases in the sensed target and hand locations. Moreover, it is not explained why a transformation bias would lead to this specific bias pattern in the first place.

We would like to clarify two things.

Frist, the measurements of the transformation bias are not entirely independent of proprioceptive and visual biases. Specifically, we define transformation bias as the misalignment between the internal representation of a visual target and the corresponding hand position. By this definition, the transformation error entails both visual and proprioceptive biases (see Author response image 1). Transformation biases have been empirically quantified in numerous studies using matching tasks, where participants either aligned their unseen hand to a visual target (Wang et al., 2021) or aligned a visual target to their unseen hand (Wilson et al., 2010). Indeed, those tasks are always considered as measuring proprioceptive biases assuming visual bias is small given the minimal visual uncertainty.

Author response image 1.

Second, the critical difference between models is in how these biases influence motor planning rather than how those biases are measured. In the Proprioceptive bias model, a movement is planned in visual space. The system perceives the starting hand position in proprioceptive space and transforms this into visual space (Vindras & Viviani, 1998; Vindras et al., 2005). As such, bias only affects the perceived starting position; there is no influence on the perceived target location (no visual bias).

In contrast, the Transformation bias model proposes that while both the starting and target positions are perceived in visual space, movement is planned in proprioceptive space. Consequently, both positions must be transformed from visual space to proprioceptive coordinates before movement planning (i.e., where is my sensed hand and where do I want it to be). Under this framework, biases can emerge from both the start and target positions. This is how the transformation model leads to different predictions compared to the perceptual models, even if the bias is based on the same measurements.

We now highlight the differences between the Transformation bias model and the Proprioceptive bias model explicitly in the Results section (Lines 192-200):

“Note that the Proprioceptive Bias model and the Transformation Bias model tap into the same visuo-proprioceptive error map. The key difference between the two models arises in how this error influences motor planning. For the Proprioceptive Bias model, planning is assumed to occur in visual space. As such, the perceived position of the hand (based on proprioception) is transformed into the visual space. This will introduce a bias in the representation of the start position. In contrast, the Transformation Bias model assumes that the visually-based representations of the start and target positions need to be transformed into proprioceptive space for motor planning. As such, both positions are biased in the transformation process. In addition to differing in terms of their representation of the target, the error introduced at the start position is in opposite directions due to the direction of the transformation (see fig 1g-h).”

In terms of the motor bias function across the workspace, the peaks are quantitatively derived from the model simulations. The number of peaks depends on how we formalize each model. Importantly, this is a stable feature of each model, regardless of how the model is parameterized. Thus, the number of peaks provides a useful criterion to evaluate different models.

Figure 1 g-h illustrates the intuition of how the models generate distinct peak patterns. We edited the figure caption and reference this figure when we introduce the bias function for each model.

(2) Also, the assumption that a visual bias leads to four peaks is not well substantiated as one of the papers on which the assumption was based (Yousif et al., 2023) found a similar pattern in a purely proprioceptive task.

What we referred to in the original submission as “visual bias” is not an eye-centric bias, nor is it restricted to the visual system. Rather, it may reflect a domain-general distortion in the representation of position within polar space. We called it a visual bias as it was associated with the perceived location of the visual target in the current task. To avoid confusion, we have opted to move to a more general term and now refer to this as “target bias.”

We clarify the nature of this bias when introducing the model in the Results section (Lines 164-169):

“Since the task permits free viewing without enforced fixation, we assume that participants shift their gaze to the visual target; as such, an eye-centric bias is unlikely. Nonetheless, prior studies have shown a general spatial distortion that biases perceived target locations toward the diagonal axes(Huttenlocher et al., 2004; Kosovicheva & Whitney, 2017). Interestingly, this bias appears to be domain-general, emerging not only for visual targets but also for proprioceptive ones(Yousif et al., 2023). We incorporated this diagonal-axis spatial distortion into a Target Bias model. This model predicts a four-peaked motor bias pattern (Fig 1f).”

We also added a paragraph in the Discussion to further elaborate on this model (Lines 502-511):

“What might be the source of the visual bias in the perceived location of the target? In the perception literature, a prominent theory has focused on the role of visual working memory account based on the observation that in delayed response tasks, participants exhibit a bias towards the diagonals when recalling the location of visual stimuli(Huttenlocher et al., 2004; Sheehan & Serences, 2023). Underscoring that the effect is not motoric, this bias is manifest regardless of whether the response is made by an eye movement, pointing movement, or keypress(Kosovicheva & Whitney, 2017). However, this bias is unlikely to be dependent on a visual input as similar diagonal bias is observed when the target is specified proprioceptively via the passive displacement of an unseen hand(Yousif et al., 2023). Moreover, as shown in the present study, a diagonal bias is observed even when the target is continuously visible. Thus, we hypothesize that the bias to perceive the target towards the diagonals reflects a more general distortion in spatial representation rather than being a product of visual working memory.”

(3) Another weakness is that the study looked at biases in movement direction only, not at biases in movement extent. The models also predict biases in movement extent, so it is a missed opportunity to take these into account to distinguish between the models.

We thank the reviewer for this suggestion. We have now conducted a new experiment to assess angular and extent biases simultaneously (Figure 4a; Exp. 4; N = 30). Using our KINARM system, participants were instructed to make center-out movements that would terminate (rather than shoot past) at the visual target. No visual feedback was provided throughout the experiment.

The Transformation Bias model predicts a two-peaked error function in both the angular and extent dimensions (Figure 4c). Strikingly, when we fit the data from the new experiment to both dimensions simultaneously, this model captures the results qualitatively and quantitatively (Figure 4e). In terms of model comparison, it outperformed alternative models (Figure 4g) particularly when augmented with a visual bias component. Together, these results provide strong evidence that a mismatch between visual and proprioceptive space is a key source of motor bias.

This experiment is now reported within the revised manuscript (Lines 280-301).

Overall, the authors have done a good job mapping out reaching biases in a wide range of conditions, revealing new patterns in one of the most basic tasks, but unambiguously determining the origin of these biases remains difficult, and the evidence for the proposed origins is incomplete. Nevertheless, the study will likely have a substantial impact on the field, as the approach taken is easily applicable to other experimental conditions. As such, the study can spark future research on the origin of reaching biases.

We thank the reviewer for these summary comments. We believe that the new experiments and analyses do a better job of identifying the origins of motor biases.

Reviewer #2 (Public Review):

Summary:

This work examines an important question in the planning and control of reaching movements - where do biases in our reaching movements arise and what might this tell us about the planning process? They compare several different computational models to explain the results from a range of experiments including those within the literature. Overall, they highlight that motor biases are primarily caused by errors in the transformation between eye and hand reference frames. One strength of the paper is the large number of participants studied across many experiments. However, one weakness is that most of the experiments follow a very similar planar reaching design - with slicing movements through targets rather than stopping within a target. Moreover, there are concerns with the models and the model fitting. This work provides valuable insight into the biases that govern reaching movements, but the current support is incomplete.

Strengths:

The work uses a large number of participants both with studies in the laboratory which can be controlled well and a huge number of participants via online studies. In addition, they use a large number of reaching directions allowing careful comparison across models. Together these allow a clear comparison between models which is much stronger than would usually be performed.

We thank the reviewer for their encouraging comments.

Weaknesses:

Although the topic of the paper is very interesting and potentially important, there are several key issues that currently limit the support for the conclusions. In particular I highlight:

(1) Almost all studies within the paper use the same basic design: slicing movements through a target with the hand moving on a flat planar surface. First, this means that the authors cannot compare the second component of a bias - the error in the direction of a reach which is often much larger than the error in reaching direction.

Reviewer 1 made a similar point, noting that we had missed an opportunity to provide a more thorough assessment of reaching biases. As described above, we conducted a new experiment in which participants made pointing movements, instructed to terminate the movements at the target. These data allow us to analyze errors in both angular and extent dimensions. The transformation bias model successfully predicts angular and extent biases, outperformed the other models at both group and individual levels. We have now included this result as Exp 4 in the manuscript. Please see response to Reviewer 1 Comment 3 for details.

Second, there are several studies that have examined biases in three-dimensional reaching movements showing important differences to two-dimensional reaching movements (e.g. Soechting and Flanders 1989). It is unclear how well the authors' computational models could explain the biases that are present in these much more common-reaching movements.

This is an interesting issue to consider. We expect the mechanisms identified in our 2D work will generalize to 3D.

Soechting and Flanders (1989) quantified 3D biases by measuring errors across multiple 2D planes at varying heights (see Author response image 2 for an example from their paper). When projecting their 3-D bias data to a horizontal 2D space, the direction of the bias across the 2D plane looks relatively consistent across different heights even though the absolute value of the bias varies (Author response image 2). For example, the matched hand position is generally to the leftwards and downward of the target. Therefore, the models we have developed and tested in a specific 2D plane are likely to generalize to other 2D plane of different heights.

Author response image 2.

However, we think the biases reported by Soechting and Flanders likely reflect transformation biases rather than motor biases. First, the movements in their study were performed very slowly (3–5 seconds), more similar to our proprioceptive matching tasks and much slower than natural reaching movements (<500ms). Given the slow speed, we suspect that motor planning in Soechting and Flanders was likely done in a stepwise, incremental manner (closed loop to some degree). Second, the bias pattern reported in Soechting and Flanders —when projected into 2D space— closely mirrors the leftward transformation errors observed in previous visuo-proprioceptive matching task (e.g., Wang et al., 2021).

In terms of the current manuscript, we think that our new experiment (Exp 4, where we measure angular and radial error) provides strong evidence that the transformation bias model generalizes to more naturalistic pointing movements. As such, we expect these principles will generalize were we to examine movements in three dimensions, an extension we plan to test in future work.

(2) The model fitting section is under-explained and under-detailed currently. This makes it difficult to accurately assess the current model fitting and its strength to support the conclusions. If my understanding of the methods is correct, then I have several concerns. For example, the manuscript states that the transformation bias model is based on studies mapping out the errors that might arise across the whole workspace in 2D. In contrast, the visual bias model appears to be based on a study that presented targets within a circle (but not tested across the whole workspace). If the visual bias had been measured across the workspace (similar to the transformation bias model), would the model and therefore the conclusions be different?

We have substantially expanded the Methods section to clarify the modeling procedures (detailed below in section “Recommendations for the Authors”). We also provide annotated code to enable others to easily simulate the models.

Here we address three points relevant to the reviewer’s concern about whether the models were tested on equal footing, and in particular, concern that the transformation bias model was more informed by prior literature than the visual bias model.

First, our center-out reaching task used target locations that have been employed in both visual and proprioceptive bias studies, offering reasonable comprehensive coverage of the workspace. For example, for a target to the left of the body’s midline, visual biases tend to be directed diagonally (Kosovicheva & Whitney, 2017), while transformation biases are typically leftward and downward (Wang et al, 2021). In this sense, the models were similarly constrained by prior findings.

Second, while the qualitative shape of each model was guided by prior empirical findings, no previous data were directly used to quantitatively constrain the models. As such, we believe the models were evaluated on equal footing. No model had more information or, best we can tell, an inherent advantage over the others.

Third, reassuringly, the fitted transformation bias closely matches empirically observed bias maps reported in prior studies (Fig 2h). The strong correspondence provides convergent validity and supports the putative causality between transformation biases to motor biases.

(3) There should be other visual bias models theoretically possible that might fit the experimental data better than this one possible model. Such possibilities also exist for the other models.

Our initial hypothesis, grounded in prior literature, was that motor biases arise from a combination of proprioceptive and visual biases. This led us to thoroughly explore a range of visual models. We now describe these alternatives below, noting that in the paper, we chose to focus on models that seemed the most viable candidates. (Please also see our response to Reviewer 3, Point 2, on another possible source of visual bias, the oblique effect.)

Quite a few models have described visual biases in perceiving motion direction or object orientation (e.g., Wei & Stocker, 2015; Patten, Mannion & Clifford, 2017). Orientation perception would be biased towards the Cartesian axis, generating a four-peak function. However, these models failed to account for the motor biases observed in our experiments. This is not surprising given that these models were not designed to capture biases related to a static location.

We also considered a class of eye-centric models where biases for peripheral locations are measured under fixation. A prominent finding here is that the bias is along the radial axis in which participants overshoot targets when they fixate on the start position during the movement (Beurze et al., 2006; Van Pelt & Medendorp, 2008). Again, this is not consistent with the observed motor biases. For example, participants undershoot rightward targets when we measured the distance bias in Exp 4. Importantly, since most our tasks involved free viewing in natural settings with no fixation requirements, we considered it unlikely that biases arising from peripheral viewing play a major role.

We note, though, that in our new experiment (Exp 4), participants observed the visual stimuli from a fixed angle in the KinArm setup (see Figure 4a). This setup has been shown to induce depth-related visual biases (Figure 4b, e.g., Volcic et al., 2013; Hibbard & Bradshaw, 2003). For this reason, we implemented a model incorporating this depth bias as part of our analyses of these data. While this model performed significantly worse than the transformation bias model alone, a mixed model that combined the depth bias and transformation bias provided the best overall fit. We now include this result in the main text (Lines 286-294).

We also note that the “visual bias” we referred to in the original submission is not restricted to the visual system. A similar bias pattern has been observed when the target is presented visually or proprioceptively (Kosovicheva & Whitney, 2017; Yousif, Forrence, & McDougle, 2023). As such, it may reflect a domaingeneral distortion in the representation of position within polar space. Accordingly, in the revision, we now refer to this in a more general way, using the term “target bias.” We justify this nomenclature when introducing the model in the Results section (Lines 164-169). Please also see Reviewer 1 comment 2.

We recognize that future work may uncover a better visual model or provide a more fine-grained account of visual biases (or biases from other sources). With our open-source simulation code, such biases can be readily incorporated—either to test them against existing models or to combine them with our current framework to assess their contribution to motor biases. Given our explorations, we expect our core finding will hold: Namely, that a combination of transformation and target biases offers the most parsimonious account, with the bias associated with the transformation process explaining the majority of the observed motor bias in visually guided movements.

Given the comments from the reviewer, we expanded the discussion session to address the issue of alternative models of visual bias (lines 522-529):

“Other forms of visual bias may influence movement. Depth perception biases could contribute to biases in movement extent(Beurze et al., 2006; Van Pelt & Medendorp, 2008). Visual biases towards the principal axes have been reported when participants are asked to report the direction of moving targets or the orientation of an object(Patten et al., 2017; Wei & Stocker, 2015). However, the predicted patterns of reach biases do not match the observed biases in the current experiments. We also considered a class of eye-centric models in which participants overestimate the radial distance to a target while maintaining central fixation(Beurze et al., 2006; Van Pelt & Medendorp, 2008). At odds with this hypothesis, participants undershot rightward targets when we measured the radial bias in Exp 4. The absence of these other distortions of visual space may be accounted for by the fact that we allowed free viewing during the task.”

(4) Although the authors do mention that the evidence against biomechanical contributions to the bias is fairly weak in the current manuscript, this needs to be further supported. Importantly both proprioceptive models of the bias are purely kinematic and appear to ignore the dynamics completely. One imagines that there is a perceived vector error in Cartesian space whereas the other imagines an error in joint coordinates. These simply result in identical movements which are offset either with a vector or an angle. However, we know that the motor plan is converted into muscle activation patterns which are sent to the muscles, that is, the motor plan is converted into an approximation of joint torques. Joint torques sent to the muscles from a different starting location would not produce an offset in the trajectory as detailed in Figure S1, instead, the movements would curve in complex patterns away from the original plan due to the non-linearity of the musculoskeletal system. In theory, this could also bias some of the other predictions as well. The authors should consider how the biomechanical plant would influence the measured biases.

We thank the reviewer for encouraging us on this topic and to formalize a biomechanical model. In response, we have implemented a state-of-the-art biomechanical framework, MotorNet

(https://elifesciences.org/articles/88591), which simulates a six-muscle, two-skeleton planar arm model using recurrent neural networks (RNNs) to generate control policies (See Figure 6a). This model captures key predictions about movement curvature arising from biomechanical constraints. We view it as a strong candidate for illustrating how motor bias patterns could be shaped by the mechanical properties of the upper limb.

Interestingly, the biomechanical model did not qualitatively or quantitatively reproduce the pattern of motor biases observed in our data. Specifically, we trained 50 independent agents (RNNs) to perform random point-to-point reaching movements across the workspace used in our task. We used a loss function that minimized the distance between the fingertip and the target over the entire trajectory. When tested on a center-out reaching task, the model produced a four-peaked motor bias pattern (Figure 6b), in contrast to the two-peaked function observed empirically. These results suggest that upper limb biomechanical constraints are unlikely to be a primary driver of motor biases in reaching. This holds true even though the reported bias is read out at 60% of the reaching distance, where biomechanical influences on the curvature of movement are maximal. We have added this analysis to the results (lines 367-373).

It may seem counterintuitive that biomechanics plays a limited role in motor planning. This could be due to several factors. First, First, task demands (such as the need to grasp objects) may lead the biomechanical system to be inherently organized to minimize endpoint errors (Hu et al., 2012; Trumbower et al., 2009). Second, through development and experience, the nervous system may have adapted to these biomechanical influences—detecting and compensating for them over time (Chiel et al., 2009).

That said, biomechanical constraints may make a larger contribution in other contexts; for example, when movements involve more extreme angles or span larger distances, or in individuals with certain musculoskeletal impairments (e.g., osteoarthritis) where physical limitations are more likely to come into play. We address this issue in the revised discussion.

“Nonetheless, the current study does not rule out the possibility that biomechanical factors may influence motor biases in other contexts. Biomechanical constraints may have had limited influence in our experiments due to the relatively modest movement amplitudes used and minimal interaction torques involved. Moreover, while we have focused on biases that manifest at the movement endpoint, biomechanical constraints might introduce biases that are manifest in the movement trajectories.(Alexander, 1997; Nishii & Taniai, 2009) Future studies are needed to examine the influence of context on reaching biases.”

Reviewer #3 (Public review):

The authors make use of a large dataset of reaches from several studies run in their lab to try to identify the source of direction-dependent radial reaching errors. While this has been investigated by numerous labs in the past, this is the first study where the sample is large enough to reliably characterize isometries associated with these radial reaches to identify possible sources of errors.

(1) The sample size is impressive, but the authors should Include confidence intervals and ideally, the distribution of responses across individuals along with average performance across targets. It is unclear whether the observed “averaged function” is consistently found across individuals, or if it is mainly driven by a subset of participants exhibiting large deviations for diagonal movements. Providing individual-level data or response distributions would be valuable for assessing the ubiquity of the observed bias patterns and ruling out the possibility that different subgroups are driving the peaks and troughs. It is possible that the Transformation or some other model (see below) could explain the bias function for a substantial portion of participants, while other participants may have different patterns of biases that can be attributable to alternative sources of error.

We thank the reviewer for encouraging a closer examination of the individual-level data. We did include standard error when we reported the motor bias function. Given that the error distribution is relatively Gaussian, we opted to not show confidence intervals since they would not provide additional information.

To examine individual differences, we now report a best-fit model frequency analysis. For Exp 1, we fit each model at the individual level and counted the number of participants that are best predicted by each model. Among the four single source models (Figure 3a), the vast majority of participants are best explained by the transformation bias model (48/56). When incorporating mixture models, the combined transformation + target bias model emerged as the best fit for almost all participants across experiments (50/56). The same pattern holds for Exp 3b, the frequency analysis is more distributed, likely due to the added noise that comes with online studies.

We report this new analysis in the Results. (see Fig 3. Fig S2). Note that we opted to show some representative individual fits, selecting individuals whose data were best predicted by different models (Fig S2). Given that the number of peaks characterizes each model (independent of the specific parameter values), the two-peaked function exhibited for most participants indicates that the Transformation bias model holds at the individual level and not just at the group level.

(2) The different datasets across different experimental settings/target sets consistently show that people show fewer deviations when making cardinal-directed movements compared to movements made along the diagonal when the start position is visible. This reminds me of a phenomenon referred to as the oblique effect: people show greater accuracy for vertical and horizontal stimuli compared to diagonal ones. While the oblique effect has been shown in visual and haptic perceptual tasks (both in the horizontal and vertical planes), there is some evidence that it applies to movement direction. These systematic reach deviations in the current study thus may reflect this epiphenomenon that applies across modalities. That is, estimating the direction of a visual target from a visual start position may be less accurate, and may be more biased toward the horizontal axis, than for targets that are strictly above, below, left, or right of the visual start position. Other movement biases may stem from poorer estimation of diagonal directions and thus reflect more of a perceptual error than a motor one. This would explain why the bias function appears in both the in-lab and on-line studies although the visual targets are very different locations (different planes, different distances) since the oblique effects arise independent of plane, distance, or size of the stimuli. When the start position is not visible like in the Vindras study, it is possible that this oblique effect is less pronounced; masked by other sources of error that dominate when looking at 2D reach endpoint made from two separate start positions, rather than only directional errors from a single start position. Or perhaps the participants in the Vindras study are too variable and too few (only 10) to detect this rather small direction-dependent bias.

The potential link between the oblique effect and the observed motor bias is an intriguing idea, one that we had not considered. However, after giving this some thought, we see several arguments against the idea that the oblique effect accounts for the pattern of motor biases.

First, by the oblique effect, perceptual variability is greater along the diagonal axes compared to the cardinal axes. These differences in perceptual variability have been used to explain biases in visual perception through a Bayesian model under the assumption that the visual system has an expectation that stimuli are more likely to be oriented along the cardinal axes (Wei & Stocker, 2015). Importantly, the model predicts low biases at targets with peak perceptual variability. As such, even though those studies observed that participants showed large variability for stimuli at diagonal orientations, the bias for these stimuli was close to zero. Given we observed a large bias for targets at locations along the diagonal axes, we do not think this visual effect can explain the motor bias function.

Second, the reviewer suggested that the observed motor bias might be largely explained by visual biases (or what we now refer to as target biases). If this hypothesis is correct, we would anticipate observing a similar bias pattern in tasks that use a similar layout for visual stimuli but do not involve movement. However, this prediction is not supported. For example, Kosovicheva & Whitney (2017) used a position reproduction/judgment task with keypress responses (no reaching). The stimuli were presented in a similar workspace as in our task. Their results showed four-peaked bias function while our results showed a two-peaked function.

In summary, we don’t think oblique biases make a significant contribution to our results.

A bias in estimating visual direction or visual movement vector Is a more realistic and relevant source of error than the proposed visual bias model. The Visual Bias model is based on data from a study by Huttenlocher et al where participants “point” to indicate the remembered location of a small target presented on a large circle. The resulting patterns of errors could therefore be due to localizing a remembered visual target, or due to relative or allocentric cues from the clear contour of the display within which the target was presented, or even movements used to indicate the target. This may explain the observed 4-peak bias function or zig-zag pattern of “averaged” errors, although this pattern may not even exist at the individual level, especially given the small sample size. The visual bias source argument does not seem well-supported, as the data used to derive this pattern likely reflects a combination of other sources of errors or factors that may not be applicable to the current study, where the target is continuously visible and relatively large. Also, any visual bias should be explained by a coordinates centre on the eye and should vary as a function of the location of visual targets relative to the eyes. Where the visual targets are located relative to the eyes (or at least the head) is not reported.

Thank you for this question. A few key points to note:

The visual bias model has also been discussed in studies using a similar setup to our study. Kosovicheva & Whitney (2017) observed a four-peaked function in experiments in which participants report a remembered target position on a circle by either making saccades or using key presses to adjust the position of a dot. However, we agree that this bias may be attenuated in our experiment given that the target is continuously visible. Indeed, the model fitting results suggest the peak of this bias is smaller in our task (~3°) compared to previous work (~10°, Kosovicheva & Whitney, 2017; Yousif, Forrence, & McDougle, 2023).

We also agree with the reviewer that this “visual bias” is not an eye-centric bias, nor is it restricted to the visual system. A similar bias pattern is observed even if the target is presented proprioceptively (Yousif, Forrence, & McDougle, 2023). As such, this bias may reflect a domain-general distortion in the representation of position within polar space. Accordingly, in the revision, we now refer to this in a more general way, using the term “target bias”, rather than visual bias. We justify this nomenclature when introducing the model in the Results section (Lines 164-169). Please also see Reviewer 1 comment 2 for details.

Motivated by Reviewer 2, we also examined multiple alternative visual bias models (please refer to our response to Reviewer 2, Point 3.

The Proprioceptive Bias Model is supposed to reflect errors in the perceived start position. However, in the current study, there is only a single, visible start position, which is not the best design for trying to study the contribution. In fact, my paradigms also use a single, visual start position to minimize the contribution of proprioceptive biases, or at least remove one source of systematic biases. The Vindras study aimed to quantify the effect of start position by using two sets of radial targets from two different, unseen start positions on either side of the body midline. When fitting the 2D reach errors at both the group and individual levels (which showed substantial variability across individuals), the start position predicted most of the 2D errors at the individual level – and substantially more than the target direction. While the authors re-plotted the data to only illustrate angular deviations, they only showed averaged data without confidence intervals across participants. Given the huge variability across their 10 individuals and between the two target sets, it would be more appropriate to plot the performance separately for two target sets and show confidential intervals (or individual data). Likewise, even the VT model predictions should differ across the two targets set since the visual-proprioceptive matching errors from the Wang et al study that the model is based on, are larger for targets on the left side of the body.

To be clear, in the Transformation bias model, the vector bias at the start position is also an important source of error. The critical difference between the proprioceptive and transformation models is how bias influences motor planning. In the Proprioceptive bias model, movement is planned in visual space. The system perceives the starting hand position in proprioceptive space and transforms this into visual space (Vindras & Viviani, 1998; Vindras et al., 2005). As such, the bias is only relevant in terms of the perceived start position; it does not influence the perceived target location. In contrast, the transformation bias model proposes that while both the starting and target positions are perceived in visual space, movements are planned in proprioceptive space. Consequently, when the start and target positions are visible, both positions must be transformed from visual space to proprioceptive coordinates before movement planning. Thus, bias will influence both the start and target positions. We also note that to set the transformation bias for the start/target position, we referred to studies in which bias is usually referred to as proprioception error measurement. As such, changing the start position has a similar impact on the Transformation and the Proprioceptive Bias models in principle, and would not provide a stronger test to separate them.

We now highlight the differences between the models in the Results section, making clear that the bias at the start position influences both the Proprioceptive bias and Transformation bias models (Lines 192200).

“Note that the Proprioceptive Bias model and the Transformation Bias model tap into the same visuo-proprioceptive error map. The key difference between the two models arises in how this error influences motor planning. For the Proprioceptive Bias model, planning is assumed to occur in visual space. As such, the perceived position of the hand (based on proprioception) is transformed into visual space. This will introduce a bias in the representation of the start position. In contrast, the Transformation Bias model assumes that the visually-based representations of the start and target positions need to be transformed into proprioceptive space for motor planning. As such, both positions are biased in the transformation process. In addition to differing in terms of their representation of the target, the error introduced at the start position is in opposite directions due to the direction of the transformation (see fig 1g-h).”

In terms of fitting individual data, we have conducted a new experiment, reported as Exp 4 in the revised manuscript (details in our response to Reviewer 1, comment 3). The experiment has a larger sample size (n=30) and importantly, examined error for both movement angle and movement distance. We chose to examine the individual differences in 2-D biases using this sample rather than Vindras’ data as our experiment has greater spatial resolution and more participants. At both the group and individual level, the Transformation bias model is the best single source model, and the Transformation + Target Bias model is the best combined model. These results strongly support the idea that the transformation bias is the main source of the motor bias.

As for the different initial positions in Vindras et al (2005), the two target sets have very similar patterns of motor biases. As such, we opted to average them to decrease noise. Notably, the transformation model also predicts that altering the start location should have limited impact on motor bias patterns: What matters for the model is the relative difference between the transformation biases at the start and target positions rather than the absolute bias.

Author response image 3.

I am also having trouble fully understanding the V-T model and its associated equations, and whether visual-proprioception matching data is a suitable proxy for estimating the visuomotor transformation. I would be interested to first see the individual distributions of errors and a response to my concerns about the Proprioceptive Bias and Visual Bias models.

We apologize for the lack of clarity on this model. To generate the T+V (Now Transformation + Target bias, or TR+TG) model, we assume the system misperceives the target position (Target bias, see Fig S5a) and then transforms the start and misperceived target positions into proprioceptive space (Fig S5b). The system then generates a motor plan in proprioceptive space; this plan will result in the observed motor bias (Fig. S5c). We now include this figure as Fig S5 and hope that it makes the model features salient.

Regarding whether the visuo-proprioceptive matching task is a valid proxy for transformation bias, we refer the reviewer to the comments made by Public Reviewer 1, comment 1. We define the transformation bias as the discrepancy between corresponding positions in visual and proprioceptive space. This can be measured using matching tasks in which participants either aligned their unseen hand to a visual target (Wang et al., 2021) or aligned a visual target to their unseen hand (Wilson et al., 2010).

Nonetheless, when fitting the model to the motor bias data, we did not directly impose the visual-proprioceptive matching data. Instead, we used the shape of the transformation biases as a constraint, while allowing the exact magnitude and direction to be free parameters (e.g., a leftward and downward bias scaled by distance from the right shoulder). Reassuringly, the fitted transformation biases closely matched the magnitudes reported in prior studies (Fig. 2h, 1e), providing strong quantitative support for the hypothesized causal link between transformation and motor biases.

Recommendations for the authors:

Overall, the reviewers agreed this is an interesting study with an original and strong approach. Nonetheless, there were three main weaknesses identified. First, is the focus on bias in reach direction and not reach extent. Second, the models were fit to average data and not individual data. Lastly, and most importantly, the model development and assumptions are not well substantiated. Addressing these points would help improve the eLife assessment.

Reviewer #1 (Recommendations for the authors):

It is mentioned that the main difference between Experiments 1 and 3 is that in Experiment 3, the workspace was smaller and closer to the shoulder. Was the location of the laptop relative to the participant in Experiment 3 known by the authors? If so, variations in this location across participants can be used to test whether the Transformation bias was indeed larger for participants who had the laptop further from the shoulder.

Another difference between Experiments 1 and 3 is that in Experiment 1, the display was oriented horizontally, whereas it was vertical in Experiment 3. To what extent can that have led to the different results in these experiments?

This is an interesting point that we had not considered. Unfortunately, for the online work we do not record the participants’ posture.

Regarding the influence of display orientation (horizontal vs. vertical), Author response image 4 presents three relevant data points: (1) Vandevoorde and Orban de Xivry (2019), who measured motor biases in-person across nine target positions using a tablet and vertical screen; (2) Our Experiment 1b, conducted online with a vertical setup; (3) Our in-person Experiment 3b, using a horizontal monitor. For consistency, we focus on the baseline conditions with feedback, the only condition reported in Vandevoorde. Motor biases from the two in-person studies were similar despite differing monitor orientations: Both exhibited two-peaked functions with comparable peak locations. We note that the bias attenuation in Vandevoorde may be due to their inclusion of reward-based error signals in addition to cursor feedback. In contrast, compared to the in-person studies, the online study showed reduced bias magnitude with what appears to be a four peaked function. While more data are needed, these results suggest that the difference in the workspace (more restricted in our online study) may be more relevant than monitor orientation.

Author response image 4.

For the joint-based proprioceptive model, the equations used are for an arm moving in a horizontal plane at shoulder height, but the figures suggest the upper arm was more vertical than horizontal. How does that affect the predictions for this model?

Please also see our response to your public comment 1. When the upper limb (or the lower limb) is not horizontal, it will influence the projection of the upper limb to the 2-D space. Effectively in the joint-based proprioceptive model, this influences the ratio between L1 and L2 (see  Author response image 5b below). However, adding a parameter to vary L1/L2 ratio would not change the set of the motor bias function that can be produced by the model. Importantly, it will still generate a one-peak function. We simulated 50 motor bias function across the possible parameter space. As shown by  Author response image 5c-d, the peak and the magnitude of the motor bias functions are very similar with and without the L1/L2 term. We characterize the bias function with the peak position and the peak-to-valley distance. Based on those two factors, the distribution of the motor bias function is very similar ( Author response image 5e-f). Moreover, the L1/L2 ratio parameter is not recoverable by model fitting ( Author response image 5c), suggesting that it is redundant with other parameters. As such we only include the basic version of the joint-based proprioceptive model in our model comparisons.

Author response image 5.

It was unclear how the models were fit and how the BIC was computed. It is mentioned that the models were fit to average data across participants, but the BIC values were based on all trials for all participants, which does not seem consistent. And the models are deterministic, so how can a log-likelihood be determined? Since there were inter-individual differences, fitting to average data is not desirable. Take for instance the hypothetical case that some participants have a single peak at 90 deg, and others have a single peak at 270 deg. Averaging their data will then lead to a pattern with two peaks, which would be consistent with an entirely different model.

We thank the reviewer for raising these issues.

Given the reviewers’ comments, we now report fits at both the group and individual level (see response to reviewer 3 public comment 1). The group-level fitting is for illustration purposes. Model comparison is now based on the individual-level analyses which show that the results are best explained by the transformation model when comparing single source models and best explained by the T+V (now TG+TR) model when consider all models. These new results strongly support the transformation model.

Log-likelihoods were computed assuming normally distributed motor noise around the motor biases predicted by each model.

We updated the Methods section as follows (lines 841-853):

“We used the fminsearchbnd function in MATLAB to minimize the sum of loglikelihood (LL) across all trials for each participant. LL were computed assuming normally distributed noise around each participant’s motor biases:

[11] LL = normpdf(x, b, c)

where x is the empirical reaching angle, b is the predicted motor bias by the model, c is motor noise, calculated as the standard deviation of (x − b). For model comparison, we calculated the BIC as follow:

[12] BIC = -2LL+k∗ln(n)

where k is the number of parameters of the models. Smaller BIC values correspond to better fits. We report the sum of ΔBIC by subtracting the BIC value of the TR+TG model from all other models.

For illustrative purposes, we fit each model at the group level, pooling data across all participants to predict the group-averaged bias function.”

What was the delay of the visual feedback in Experiment 1?

The visual delay in our setup was ~30 ms, with the procedure used to estimate this described in detail in Wang et al (2024, Curr. Bio.). We note that in calculating motor biases, we primarily relied on the data from the no-feedback block.

Minor corrections

In several places it is mentioned that movements were performed with proximal and distal effectors, but it's unclear where that refers to because all movements were performed with a hand (distal effector).

By 'proximal and distal effectors,' we were referring to the fact that in the online setup, “reaching movements” are primarily made by finger and/or wrist movements across a trackpad, whereas in the inperson setup, the participants had to use their whole arm to reach about the workspace. To avoid confusion, we now refer to these simply as 'finger' versus 'hand' movements.

In many figures, Bias is misspelled as Bais.

Fixed.

In Figure 3, what is meant by deltaBIC (*1000) etc? Literally, it would mean that the bars show 1,000 times the deltaBIC value, suggesting tiny deltaBIC values, but that's probably not what's meant.

×1000' in the original figure indicates the unit scaling, with ΔBIC values ranging from approximately 1000 to 4000. However, given that we now fit the models at the individual level, we have replaced this figure with a new one (Figure 3e) showing the distribution of individual BIC values.

Reviewer #2 (Recommendations for the authors):

I have concerns that the authors only examine slicing movements through the target and not movements that stop in the target. Biases create two major errors - errors in direction and errors in magnitude and here the authors have only looked at one of these. Previous work has shown that both can be used to understand the planning processes underlying movement. I assume that all models should also make predictions about the magnitude biases which would also help support or rule out specific models.

Please see our response to Reviewer 1 public review 3.

As discussed above, three-dimensional reaching movements also have biases and are not studied in the current manuscript. In such studies, biomechanical factors may play a much larger role.

Please see our response to your public review.

It may be that I am unclear on what exactly is done, as the methods and model fitting barely explain the details, but on my reading on the methods I have several major concerns.

First, it feels that the visual bias model is not as well mapped across space if it only results from one study which is then extrapolated across the workspace. In contrast, the transformation model is actually measured throughout the space to develop the model. I have some concerns about whether this is a fair comparison. There are potentially many other visual bias models that might fit the current experimental results better than the chosen visual bias model.

Please refers to our response to your public review.

It is completely unclear to me why a joint-based proprioceptive model would predict curved planned movements and not straight movements (Figure S1). Changes in the shoulder and elbow joint angles could still be controlled to produce a straight movement. On the other hand, as mentioned above, the actual movement is likely much more complex if the physical starting position is offset from the perceived hand.

Natural movements are often curved, reflecting a drive to minimize energy expenditure or biomechanical constraints (e.g., joint and muscle configuration). This is especially the case when the task emphasizes endpoint precision (Codol et al., 2024) like ours. Trajectory curvature was also observed in a recent simulation study in which a neural network was trained to control a biomechanical model (2-limb, 6muscles) with the cost function specified to minimize trajectory error (reach to a target with as straight a movement as possible). Even under these constraints, the movements showed some curvature. To examined whether the endpoint reaching bias somehow reflects the curvature (or bias during reaching), we included the prediction of this new biomechanical model in the paper to show it does not explain the motor bias we observed.

To be clear, while we implemented several models (Joint-based proprioceptive model and the new biomechanical model) to examine whether motor biases can be explained by movement curvature, our goal in this paper was to identify the source of the endpoint bias. Our modeling results reveal a previously underappreciated source of motor bias—a transformation error that arises between visual and proprioceptive space—plays a dominant role in shaping motor bias patterns across a wide range of experiments, including naturalistic reaching contexts where vision and hand are aligned at the start position. While the movement curvature might be influenced by selectively manipulating factors that introduce a mismatch between the visual starting position and the actual hand position (such as Sober and Sabes, 2003), we think it will be an avenue for future work to investigate this question.

The model fitting section is barely described. It is unclear how the data is fit or almost any other aspects of the process. How do the authors ensure that they have found the minimum? How many times was the process repeated for each model fit? How were starting parameters randomized? The main output of the model fitting is BIC comparisons across all subjects. However, there are many other ways to compare the models which should be considered in parallel. For example, how well do the models fit individual subjects using BIC comparisons? Or how often are specific models chosen for individual participants? While across all subjects one model may fit best, it might be that individual subjects show much more variability in which model fits their data. Many details are missing from the methods section. Further support beyond the mean BIC should be provided.

We fit each model 150 times and for each iteration, the initial value of each parameter was randomly selected from a uniform distribution. The range for each parameter was hand tuned for each model, with an eye on making sure the values covered a reasonable range. Please see our response to your first minor comment below for the range of all parameters and how we decide the iteration number for each model.

Given the reviewers’ comments in the individual difference, we now fit the models at individual level and report a frequency analysis, describing the best fitting model for each participant. In brief, the data for a vast majority of the participants was best explained by the transformation model when comparing single source models and by the T+V (TR+TG) model when consider all models. Please see response to reviewer 3 public comment 1 for the updated result.

We updated the method session, and it reads as follows (lines 841-853):

_“_We used the fminsearchbnd function in MATLAB to minimize the sum of loglikelihood (LL) across all trials for each participant. LL were computed assuming normally distributed noise around each participant’s motor biases:

[11]       𝐿𝐿 = 𝑛𝑜𝑟𝑚𝑝𝑑𝑓(𝑥, 𝑏, 𝑐)

where x is the empirical reaching angle, b is the predicted motor bias by the model, c is motor noise, calculated as the standard deviation of x-b.

For model comparison, we calculated the BIC as follows:

[12] BIC = -2LL+k∗ln(n)

where k is the number of parameters of the models. Smaller BIC values correspond to better fits. We report the sum of ΔBIC by subtracting the BIC value of the TR+TG model from all other models.”

Line 305-307. The authors state that biomechanical issues would not predict qualitative changes in the motor bias function in response to visual manipulation of the start position. However, I question this statement. If the start position is offset visually then any integration of the proprioceptive and visual information to determine the start position would contain a difference from the real hand position. A calculation of the required joint torques from such a position sent through the mechanics of the limb would produce biases. These would occur purely because of the combination of the visual bias and the inherent biomechanical dynamics of the limb.

We thank the reviewer for this comment. We have removed the statement regarding inferences about the biomechanical model based on visual manipulations of the start position. Additionally, we have incorporated a recently proposed biomechanical model into our model comparisons to expand our exploration of sources of bias. Please refer to our response to your public review for details.

Measurements are made while the participants hold a stylus in their hand. How can the authors be certain that the biases are due to the movement and not due to small changes in the hand posture holding the stylus during movements in the workspace. It would be better if the stylus was fixed in the hand without being held.

Below, we have included an image of the device used in Exp 1 for reference. The digital pen was fixed in a vertical orientation. At the start of the experiment, the experimenter ensured that the participant had the proper grip alignment and held the pen at the red-marked region. With these constraints, we see minimal change in posture during the task.

Author response image 6.

Minor Comments

Best fit model parameters are not presented. Estimates of the accuracy of these measures would also be useful.

In the original submission, we included a Table S1 that presented the best-fit parameters for the TR+TG (Previously T+V) model. Table S1 now shows the parameters for the other models (Exp 1b and 3b, only). We note the parameter values from these non-optimal models are hard to interpret given that core predictions are inconsistent with the data (e.g., number of peaks).

We assume that by "accuracy of these measures," the reviewers are referring to the reliability of the model fits. To assess this, we conducted a parameter recovery analysis in which we simulated a range of model parameters for each model and then attempted to recover them through fitting. Each model was simulated 50 times, with the parameters randomly sampled from distributions used to define the initial fitting parameters. Here, we only present the results for the combined models (TR+TG, PropV+V, and PropJ+V), as the nested models would be even easier to fit.

As shown in Fig. S4, all parameters were recovered with high accuracy, indicating strong reliability in parameter estimation. Additionally, we examined the log-likelihood as a function of fitting iterations (Fig. S4d). Based on this curve, we determined that 150 iterations were sufficient given that the log-likelihood values were asymptotic at this point. Moreover, in most cases, the model fitting can recover the simulated model, with minimal confusion across the three models (Fig. S4e).

What are the (*1000) and (*100) in the Change in BIC y-labels? I assume they indicate that the values should be multiplied by these numbers. If these indicate that the BIC is in the hundreds or thousands it would be better the label the axes clearly, as the interpretation is very different (e.g. a BIC difference of 3 is not significant).

×1000' in the original figure indicates the unit scaling, with ΔBIC values ranging from approximately 1000 to 4000. However, given that we now fit the models at the individual level, we have replaced this figure with a new one showing the distribution of individual BIC values.

Lines 249, 312, and 315, and maybe elsewhere - the degree symbol does not display properly.

Corrected.

Line 326. The authors mention that participants are unaware of their change in hand angle in response to clamped feedback. However, there may be a difference between sensing for perception and sensing for action. If the participants are unaware in terms of reporting but aware in terms of acting would this cause problems with the interpretation?

This is an interesting distinction, one that has been widely discussed in the literature. However, it is not clear how to address this in the present context. We have looked at awareness in different ways in prior work with clamped feedback. In general, even when the hand direction might have deviated by >20d, participants report their perceived hand position after the movement as near the target (Tsay et al, 2020). We also have used post-experiment questionnaires to probe whether they thought their movement direction had changed over the course of the experiment (volitionally or otherwise). Again, participants generally insist they moved straight to the target throughout the experiment. So it seems that they unaware of any change in action or perception.

Reaction time data provide additional support that participants are unaware of any change in behavior. The RT function remains flat after the introduction of the clamp, unlike the increases typically observed when participants engage in explicit strategy use (Tsay et al, 2024).

Figure 1h: The caption suggests this is from the Wang 2021 paper. However, in the text 180-182 it suggests this might be the map from the current results. Can the authors clarify?

Fig 1e is the data from Wang et al, 2021. We formalized an abstract map based on the spatial constrains observed in Fig 1e, and simulated the error at the start and target position based on this abstraction (Fig 1h). We have revised the text to now read (Lines 182-190):

“Motor biases may thus arise from a transformation error between these coordinate systems. Studies in which participants match a visual stimulus to their unseen hand or vice-versa provide one way to estimate this error(Jones et al., 2009; Rincon-Gonzalez et al., 2011; van Beers et al., 1998; Wang et al., 12/2020). Two key features stand out in these data: First, the direction of the visuo-proprioceptive mismatch is similar across the workspace: For right-handers using their dominant limb, the hand is positioned leftward and downward from each target. Second, the magnitude increases with distance from the body (Fig 1d). Using these two empirical constraints, we simulated a visual-proprioceptive error map (Fig. 1h) by applying a leftward and downward error vector whose magnitude scaled with the distance from each location to a reference point.”

Reviewer #3 (Recommendations for the authors):

The central idea behind the research seems quite promising, and I applaud the efforts put forth. However, I'm not fully convinced that the current model formulations are plausible explanations. While the dataset is impressively large, it does not appear to be optimally designed to address the complex questions the authors aim to tackle. Moreover, the datasets used to formulate the 3 different model predictions are SMALL and exhibit substantial variability across individuals, and based on average (and thus "smoothed") data.

We hope to have addressed these concerns with the two major changes to revised manuscript: 1) The new experiment in which we examine biases in both angle and extent and 2) the inclusion in the analyses of fits based on individual data sets.

Author response:

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

Reviewer #1 (Public Review):

(1) Discrepancies with previous findings need clarification, especially regarding the absence of similar behavioral effects in F1. Lack of discussion on the decision to modify paradigms instead of using the same model. Presentation of behavioral data in supplementary materials, with a recommendation to include behavioral quantification in main figures. Absence of quantification for freezing behavior, a crucial measure in fear conditioning.

We agree, thank you. One of the major revisions we have made to this version of the manuscript is the addition of much more thorough analysis of our F1 behavior. While not captured by the (relatively gross) measure of the approach-avoid index, further analysis has highlighted interesting differences between the F1s of unpaired and paired offspring, and in an odor-specific manner. As these analyses have given rise to many new results and conclusions, we have attempted to adjust the manuscript to reflect the major change that we do, in fact, find effects in F1, if subtle. 

Classical odor-shock pairing was used in both Dias & Ressler’s and our study to directly expand upon the findings of increase in cell number. This enabled our discovery of biasing of newborn OSNs. For our behavioral readouts, we chose to focus on the ethological behavior of avoidance. From our extensive behavioral analysis (Figures 5 & 6), we successfully identified several behavioral differences in the F1 offspring that had not previously been described.

Reviewer #2 (Public Review):

(1) The main weakness is the disconnect between the morphological changes reported and the lack of change in aversion to the odorant in F1 progeny. The authors also do not address the mechanisms underlying the inheritance of the phenotype, which may lie outside of the scope of the present study.

Thank you for your comments. Our revised manuscript includes both new experiments and new analyses that probe the relationship between a change in cell number and a change in avoidance behavior, and we have revised the manuscript text to address this point directly. In short, we find both in the F0 generation (at extended time points) and in the F1, that an increase in cell number does not always correlate with avoidance behavior. However, we do find nuanced behavioral differences between the offspring of unpaired and paired fathers. Whether the increase in cell number in offspring is necessary to observe the behavioral changes is outside the scope of the current study, but certainly a question we are interested in answering in future work. 

Reviewer #3 (Public Review):

(1) In the abstract / summary, the authors raise expectations that are not supported by the data. For example, it is claimed that "increases in F0 were due to biased stem cell receptor choice." While an active field of study that has seen remarkable progress in the past decade, olfactory receptor gene choice and its relevant timing in particular is still unresolved. Here, Liff et al., do not pinpoint at what stage during differentiation the "biased choice" is made. 

EdU is only taken into stem cells in the S phase, and differences in EdU-labeled M71 or MOR23 OSNs across fear conditioning groups indicates a biasing in subtype identity. We do not make claims regarding the exact stage of OSN maturation at which biasing may occur; rather, we demonstrate that the stem cells that were dividing during EdU administration are more likely to mature into an M71 OSN if a mouse receives paired acetophenone conditioning compared to unpaired or no conditioning (and similarly with MOR23 and lyral). This phenomenon must involve receptor choice, as that is the mechanism by which OSN subtypes form. 

(2) Similarly, the concluding statement that the study provides "insight into the heritability of acquired phenotypes" is somewhat misleading. The experiments do not address the mechanisms underlying heritability. 

We do not claim to provide direct insight into the mechanisms underlying heritability. Our experiments do provide insight into the heritability of acquired phenotypes, as we corroborate previous studies that this olfactory fear conditioning paradigm induces heritable changes in the nose and in behavior. We also demonstrate odor-specific behavioral differences in the offspring conditioned fathers, suggesting that the mechanisms underlying the specific behavioral phenotypes may be unique to the conditioning odorant, and not one universal mechanism. These results provide basic knowledge that will accelerate our ability to uncover the mechanisms driving heritable changes. 

(3) The statement that "the percentage of newborn M71 cells is 4-5 times that of MOR23 may simply reflect differences in the birth rates of the two cell populations" should, if true, result in similar differences in the occurrence of mature OSNs with either receptor identity. According to Fig. 1H & J, however, this is not the case. 

We have removed that statement from the manuscript, as subtype-specific differences in proliferation rates are not the focus of this study and we do not wish to make claims about it based on our EdU experiments. We do not compare our iDISCO cell density counts to EdU co-labeling counts nor ratio counts, as differences between M71 and MOR23 quantification in cleared tissue versus EdU uptake may simply reflect the inherent differences between methodologies. Our claims are solely within M71 cohorts and MOR23 cohorts. 

(4) An important result is that Liff et al., in contrast to results from other studies, "do not observe the inheritance of odor-evoked aversion to the conditioned odor in the F1 generation." This discrepancy needs to be discussed. 

This is discussed in the manuscript, and we report behavioral differences revealed by additional analyses. 

(5) The authors speculate that "the increase in neurons responsive to the conditioned odor could enhance the sensitivity to, or the discrimination of, the paired odor in F0 and F1. This would enable the F1 population to learn that odor predicts shock with fewer training cycles or less odorant when trained with the conditioned odor." This is a fascinating idea that, in fact, could have been readily tested by Liff and coworkers. If this hypothesis were found true, this would substantially enhance the impact of the study for the field.

We agree that additional F1 behavioral paradigms are a major next step to understand the functional behavioral differences that may emerge from an increase in specific OSN subtype. Due to the nontrivial amount of time and effort it requires to generate F1 offspring (on the order of many months), and because we do not test individual offspring in multiple behavioral assays (such that they are naïve to their father’s conditioning odor), these experiments are outside the scope of this current study. 

Reviewer #1 (Recommendations For The Authors):

(1) Considering that the authors are expanding upon the previous findings of Dias and Ressler (2014), it is crucial to clarify the discrepancies in the results between both works in the discussion. While I acknowledge the use of a different experimental design by the authors, if the premise assumes there is a universal mechanism for transgenerational acquired modification it prompts the question: Why don't we observe similar behavioral effects in F1 in the present model? This issue needs extensive discussion in the manuscript to advance the field's understanding of this topic. Additionally, I am also curious about the author's decision to modify the paradigms instead of using exactly the same model to further extend their findings on stem cells, for example. Could you please provide comments on this choice and elaborate on this aspect in the discussion? 

We agree, thank you. One of the major revisions we have made to this version of the manuscript is the addition of much more thorough analysis of our F1 behavior. While not captured by the (relatively gross) measure of the approach-avoid index, further analysis has highlighted interesting differences between the F1s of unpaired and paired offspring, and in an odor-specific manner. As these analyses have given rise to many new results and conclusions, we have attempted to adjust the manuscript to reflect the major change that we do, in fact, find effects in F1, if subtle. 

Classical odor-shock pairing was used in both Dias & Ressler’s and our study to directly expand upon the findings of increase in cell number. This enabled our discovery of biasing of newborn OSNs. For our behavioral readouts, we chose to focus on the ethological behavior of avoidance. From our extensive behavioral analysis (Figures 5 & 6), we successfully identified several behavioral differences in the F1 offspring that had not previously been described. We have revised the discussion section to elaborate on these decisions.

We incorporated the behavioral data into the main figures and included a freezing metric to Figure 5 (F, J, & N). We did do an analysis of time spent freezing in the control vs. conditioned chamber, but since the F0 paired mice spend so little time in the conditioned odor chamber, they also spend most of their time freezing in the control odor chamber. Thus, we felt it was better to show the overall time spent freezing during the trial.

(2) It is unclear why the authors chose to present all behavioral data to supplementary materials. I strongly recommend not only incorporating the behavioral data into the main figures but also expanding the behavioral quantification. It appears that the author dismissed the potential effects on F1 without a thorough exploration of animals' behaviors. The task contains valuable information that could be further investigated, potentially altering the findings or even the conclusions of the study. Notably, the absence of quantification for freezing behavior is incomprehensive. Freezing is a crucial measure in fear conditioning, and it's surprising that the authors did not mention it throughout the manuscript. I encourage the author to include freezing data in the analysis and other behavioral quantification as follows: a) freezing during odor presentation and ITI for conditioning days. b) freezing during odor preference test in all compartments. c) it is not very clear the design of the Odor preference behavioral testing. Is the odor presented in a discrete manner or the order is constantly presented in the compartment? Could the authors quantify the latency to avoid after the visit in the compartment? d) in the video it is very clear the animals are doing a lot of risk assessment, this could be also analyzed and included as a fear measure.  

Thanks for the suggestion. We incorporated the behavioral data into the main figures and included a freezing metric to Figure 5 (F, J, & N). We did do an analysis of time spent freezing in the control vs. conditioned chamber, but since the F0 paired mice spend so little time in the conditioned odor chamber, they also spend most of their time freezing in the control odor chamber. Thus, we felt it was better to show the overall time spent freezing during the trial. In the methods section we describe that the odor is continuously bubbled into the chamber throughout the trial, but we have clarified this in the main text as well. As for further behavioral metrics like latencies and risk assessment, initial analyses have not shown anything in the F1 data that we wished to report here. Future work from the lab will investigate this further.

(3) In the Dias and Ressler paper, a crucial difference exists between the models that could elucidate the absence of transgenerational effects on F1. In their study, the presence of the unconditioned stimulus (US) is consistent across all generations in the startle task. I am curious whether, in the present study, the authors considered pairing the F1 with a US-paired task in a protocol that does not induce fear conditioning (e.g., lower shock intensity or fewer pairings). Could this potentially lead to an increased response in the parental-paired offspring? Did the author consider this approach? I understand how extensive this experiment can be, therefore I'm not directly requesting, although it would be a fantastic achievement if the results are positive. Please consider discussing this fundamental difference in the manuscript. 

To clarify, the F1 generation is presented with the unconditioned stimulus, just never conditioned with it. In these experiments, we were primarily interested in the F1’s naïve reaction to their father’s conditioning odorant, and whether the presentation of that odor in the absence of a stressor would lead to any fear-like behavioral responses.

We have considered the experiments you have suggested and have ongoing projects in the lab further investigating F1 effects and whether their father’s experiences affect their ability to learn in conditioning tasks. Because of the amount of time and effort it requires to generate F1 offspring, and because we do not wish to test individual offspring in multiple assays, we do not present any of these experiments in the current manuscript. Ongoing work is looking into whether 1-day (vs. 3-day) conditioning is sufficient in the offspring of paired mice, and we appreciate the suggestion of subthreshold shock intensity. We will also clarify in the discussion that future work will try to answer these questions. 

(4) If the videos were combined it would be better to appreciate the behavioral differences of paired vs unpaired. 

Thank you for the suggestion, fixed. Video S1 is now a combination of unpaired and paired example videos. 

(5) Figure 3E, is there an outlier in the paired group that is driving the difference? Please run an outlier test on the data if this has not been done. If already done, please express the stats. 

We ran an outlier test using the ROUT method (Q=1%) and did not find any outliers to be removed. We also ran the same test on all other data and removed one mouse from the Acetophenone F1 Paired group in Figure 5 (also described in the Methods section). 

(6) I understand that using the term "olfactory" twice in the title may seem redundant. However, the authors specifically demonstrate the effects of olfactory fear conditioning. I suggest including "odor-induced" before "fear conditioning" in the title for greater specificity and accuracy. This modification would better reflect the study's focus on olfactory fear conditioning, especially given the authors did not explore fear conditioning broadly (e.g., contextual, and auditory aspects were not examined). 

Thank you for your feedback. We found “olfactory” twice as cumbersome. We have changed the title to “Fear conditioning biases olfactory sensory neuron expression across generations”, to more accurately highlight the importance of the olfactory sensory neuron expression, intergenerationally. 

(7) The last page of the manuscript has a list of videos (8 videos), but only two were presented.

We have made sure to include all 7 videos (videos 1 and 2 were combined) in this version.  

Reviewer #2 (Recommendations For The Authors):

(1) The analyses mentioned on lines 210-220 should be presented. 

Thank you for the suggestion. We have removed this part of the manuscript as we do not have a large enough n to draw conclusions about cell longevity in this paper. Future studies in the lab will incorporate this analysis.

Reviewer #3 (Recommendations For The Authors):

(1) The manuscript contains several supplementary figures and movies that are not referred to in the main text. 

All supplementary figures and movies are now referred to in the manuscript text.

(2) In the abstract, the authors state that they "investigated changes in the morphology of the olfactory epithelium." I think that is (technically) not what they did. In fact, the authors do not show any morphometry of the epithelium (e.g., thickness, layers, etc.), but count the density of OSNs that share a specific receptor identity. Along the same lines, the authors state in the abstract that recent work has shown that conditioning is "resulting in increases in olfactory receptor frequencies." However, recent studies did not show increased "receptor frequencies", but changes in cell count. Whether (or not) receptor expression per OSN is also changed remains unknown (would be interesting though). 

Yes, agreed. We changed “morphology” to “cellular composition.” We also changed any references to “receptor frequencies” to “olfactory sensory neuron frequencies.”

(3) Reference 20 needs to be updated. 

Thank you, updated.

(4) l.52: the distribution of OSNs into (four) zones is a somewhat outdated concept as zonal boundaries are rather blurry. Generally, of course, dorsoventral differences are real. 

Yes, we agree and changed the verbiage to “region” as opposed to “zone.” We mainly bring this up because it later becomes relevant that both M71 and MOR23 are expressed in the same (antero-dorsal) region and thus can be quantified with the same methodology.

(5) Fig. 3B & C: the EdU background staining is quite peculiar. Any reason why the epithelium is mostly (with the sustentacular nuclei being a noticeable exception) devoid of background? 

We use the ThermoFisher Click-iT Plus EdU kit (Invitrogen, C10638) and it has consistently produced very good signal to noise ratio.

Responses to Editor’s note

We thank the editor for their constructive suggestions. 

(1) Should you choose to revise your manuscript, 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. 

Thank you for the suggestion. We created two supplementary tables with statistical reporting: Table S1 for the main figure statistics, and Table S2 for the supplementary figure statistics.

Author response:

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

Reviewer #1 (Public review):

The study mainly replicates the authors' previously reported results about generalized and trajectory-specific coding of task structure by prefrontal neurons, and stable and changing representations over learning (Muysers et al., 2024, PMID: 38459033; Muysers et al., 2025, PMID: 40057953), although there are useful results about changes in goal-selective and taskphase selective cells over learning. There are basic shortcomings in the scientific premise of two new points in this manuscript, that of the contribution of pre-existing spatial representations, and the role of replay sequences in the prefrontal cortex, both of which cannot be adequately tested in this experimental design.

We agree with the reviewer that we have not made sufficiently clear which aspects of our paper add to previous publications. We have now better explained methodological differences.

Also, we agree that our very general statements on pre-existing spatial representations in the introduction and abstract in the previous manuscript were not properly followed up in the Results section. In the revision, the respective statements are clarified, and we also added analysis of a further control condition (see response to A), which shows that particularly a subset of task cells maintains there firing fields from an early habituation period, arguing that, while the population representation of the task largely develops during learning, there exists a scaffold of small but significant amount of cells that could be interpreted as a schema.

We also further clarified our view on replay sequences in the prefrontal cortex (see response to B). Particularly, we are grateful to the reviewer for the suggestion to also include other reactivation analysis which led to new results presented in new Figure 3.

[A] The study denotes neurons that show precise spatial firing equivalently irrespective of goal, as generalized task representations, and uses this as a means to testing whether pre-existing spatial representations can contribute to task coding and learning. …. [I]n order to establish generalization for abstract task rules or cognitive flexibility, as motivated in the manuscript, there is a need to show that these neurons "generalize" not just to firing in the same position during learning of a given task… For an adequate test of pre-existing spatial structure, either a comparison task, as in the examples above, is needed, or at least a control task in which animals can run similar trajectories without the task contingencies. An unambiguous conclusion about pre-existing spatial structure is not possible without these controls.

We thank the reviewer for this suggestion. We may, however, note that the previous manuscript did not make strong claims about pre-existing structures in the Results or Discussion. Also Schemas were only taken up as a discussion point. We nevertheless agree with the reviewer that assessment of the spatial prestructure requests further analysis. To address their point, we analyzed neuronal activity during the habituation phase before the start of task training, when the animals freely explored the same maze without any task contingency (animals explored mostly in the arms of the maze). We compared the place fields of neurons during this habituation period with their task-related activity. Consistent with the small overlap of firing rate maps between learning and learned phase, also this analysis revealed a small number of cells with significant correlations (up to 20% for task cells; a significant fraction according to a  binomial test). The results are shown as a new Figure supplement to Figure 2.

[B] The scientific premise for the test of replay sequences is motivated using hippocampal activity in internally guided spatial working memory rule tasks [...] and applied here to prefrontal activity in a sensory-cue guided spatial memory task [...]. There are several issues with the conclusion in the manuscript that prefrontal replay sequences are involved in evaluating behavioral outcomes rather than planning future outcomes.

We agree with the reviewer that preplay in Hippocampus and mPFC are distinct. We further emphasized this distinctiveness in the respective paragraph in the discussion (see response to B1).

[B. 1] First, odor sampling in odor-guided memory tasks is an active sensory processing state that leads to beta and other oscillations in olfactory regions, hippocampus, prefrontal cortex, and many other downstream networks [...]. This is an active sensory state, not conducive to internal replay sequences, unlike references used in this manuscript to motivate this analysis, which are hippocampal spatial memory studies with internally guided rather than sensory-cue guided decisions, where internal replay is seen during immobility at reward wells. These two states cannot be compared with the expectation of finding similar replay sequences, so it is trivially expected that internal replay sequences will not be seen during odor sampling.

We agree with the reviewer that the sampling phase cannot be compared with the “preplay” state in the hippocampus. We have rewritten the manuscript in the results and discussion sections to clarify. We, however, disagree, that the absence of replay sequences in the mPFC 1P calcium data is trivial, since we actually do see many sequences during sampling (Fig 4E, Fig 4 suppl 2 A). These sequences are just not related to task activity and may e.g. reflect activity related to sensing, but do not contain information about goal arm.

[B. 2] Second, sequence replay is not the only signature of reactivation. Many studies have quantified prefrontal replay using template matching and reactivation strength metrics that do not involve sequences [...].  Third, previous studies have explicitly shown that prefrontal activity can be decoded during odor sampling to predict future spatial choices - this uses sensory-driven ensemble activity in prefrontal cortex and not replay, as odor sampling leads to sensory driven processing and recall rather than a reactivation state [..].

We thank the reviewer for the suggestion to also perform reactivation analysis (Peyrache et al., 2009, 2010). The results are summarized in the new Figure 3. And show that indeed reactivation is stronger during the sampling phase and it is goal arm specific, arguing that sequence analysis extracts information (partly) complementary to rate covariance based analysis.

We hope to have convinced the reviewer that, together, the complementary results of reactivation an sequence analysis, as well as the ability to follow these measures over an extended period of time, gives unique insights far beyond the previous publications of these data sets. A consistent analysis of population representation, however, required some reanalyses of previous findings, since we only could focus on a limited number of animals and cells, for which tracking was possible over such a long period of time.

Reviewer #2 (Public review):

Further controls are needed to validate the results.

We thank the reviewer for their generally supportive statements. The revised manuscript contains a number of controls in several new figure supplements.

Reviewer #3 (Public review):

[They] conclude that the frequency of TSs and GSs is limited (I believe because most sequence clusters were non-SI - the authors can verify this and write it in the text?). In the discussion, they say, "In addition to GSs and TSs, we found that most of the recurring sequences are not related to behavior".

The reviewer is correct most clusters were not SI (Fig 5 A). We have added this information in the MS.

[...] They conclude "Together with our finding of strong changes in sequence expression after learning (Figure 3E) these findings suggest that a representation of task develops during learning, however, it does not reflect previous network structure." I am not sure what is meant here by the second part of this sentence (after "however ..."). Is it the idea that the replay represents network structure, and the lack of Reward replay in the learning condition means that the network structure must have been changed to get to the learned condition? Please clarify.

The reviewer is correct in their assertion. We rewrote the sentence to clarify: “Together with our finding of strong changes in sequence expression after learning (now Fig 4E) these findings suggest that a representation of task develops during learning, however, it does not reflect sequence structure during learning and habituation”.

(1) There are some statements that are not clear, such as at the end of the introduction, where the authors write, "Both findings suggest that the mPFC task code is locally established during learning." What is the reasoning behind the "locally established" statement? Couldn't the learning be happening in other areas and be inherited by the mPFC? Or are the authors assuming that newly appearing sequences within a 500-ms burst period must be due to local plasticity?

We agree that the wording “local” can be misleading, we rephrased the corresponding sentences.

(2) The threshold for extracting burst events (0.5 standard deviations, presumably above the mean, but the authors should verify this) seems lower than what one usually sees as a threshold for population burst detection. What fraction of all data is covered by 500 ms periods around each such burst? However, it is potentially a strength of this work that their results are found by using this more permissive threshold.

Since we work with a slow calcium signal, we cannot use as strict thresholds as usually employed using electrophysiology. In addition, our sequence detection approach adds a further level of strictness such that we only consider bursts with recurring sequence structure. In response to this reviewer’s question, we have added quantification of the fraction of all data covered by 500 ms periods in Figure Supplement 1, panels D and E. Indeed we include a large fraction (20 to 40%) (except sleep and habituation), which is consistent with our interpretation that during the outward phase sequences mainly reflect task field firing.

Reviewer #1(Recommendations for the  Authors):

It is possible that 1-photon recordings do not have the temporal resolution and information about oscillatory activity to enable these kinds of analyses. Therefore, an unambiguous conclusion about the existence and role of prefrontal reactivation is not possible in this experimental and analytical design.

We indeed cannot extract information encoded in LFP oscillations from the calcium signal, we now mention the relation between LFP oscillations and olfaction-guided behaviors in the discussion (including the suggested references). However, our finding that sequence and covariance-based analysis yield partly complementary results argues that it indeed allows conclusion about the existence and role of prefrontal reactivation.

Reviewer #2 (Recommendations for the authors):

The results of the Muysers et al. (2025) paper need to be discussed in detail and explain why the cell categorization is different, three groups of spatial cells vs two groups here. Also, explain in what aspect the major findings in this work go beyond what was shown in Figure 4 in that paper.

The main goal of this paper was to explore sequence/replay like activity, which is not at all captured in the Muysers et al. 2025 paper. Because of this focus on sequences, we excluded the inward runs (from reward to sampling point) for better interpretability and thus ended up with only two types of cells. Muysers et al. included backward runs and could thereby also assess whether the place field remains in the outward and inward runs. We added this clarification in the Results section.

Regarding the reviewer’s question regarding figure 4: Our task cells would largely overlap with the “path-equivalent cells” from Muysers et al. 2025 (albeit not taking into account inward runs). In this sense their finding that the share of path-equivalent cells increases with learning  is consistent with our report of increasing fraction of task cells in Figure 2 C. Our Figure 2 adds that some task cells develop from previous goal cells with fields at the same location (generalizing). Moreover, we use spatial information as a criterion to identify TC and GCs, showing that a large fraction of cells actually is and remains spatially unselective. In Muysers et al. 2025 a statistical criterion was not applied on spatial selectivity but peak height, with fewer neurons failing this test. Moreover, we were analyzing only those cells trackable over the whole period. Despite all these methodological differences, the result of increasing the number of task/path-equivalent cells over learning was consistent. The main reason for recategorization of the cells in the present manuscript was to be able to meaningfully link them to sequence activity (Fig. 5E, F).

It is not clear from the description how the cell type transitions were quantified. Was the last learning day compared to the first learned day? Given that, particularly during learning, there are changes across days in the spatial representations according to Figure 2 of Muysers et al. (2025), this is the meaningful way to make the comparisons. Nevertheless, it is also not clear whether the daily variations within learning and learned conditions differ from the transition day, so without comparing these three conditions, it is hard to make a firm conclusion from examining only changes in the transition days.

The analysis of cell type transitions was performed by pooling all learning sessions and comparing them with all learned sessions, without taking into account the chronological order of sessions within each category. This approach allowed us to identify broad changes associated with learning state. Figure supplement 1.C shows the session intervals per animal. We argue that the large interval between learning and learned session justifies this analysis approach.

Identifying sequences by a clustering method in which sequence patterns of individual events are compared is an interesting idea. Nevertheless, there is a danger, as with any clustering method, that data without clustering tendency could be artificially subdivided into clusters.

In Figure 4.C, we show three example sequence cluster templates (colored) obtained via hierarchical clustering, along with representative member sequences (black) sorted by cluster membership. In response to this reviewer’s comment, we now included a complete clustering result for one animal, including all sequence clusters and their member sequences. It is provided in Figure 4 supplement 1. This comprehensive visualization serves as an additional control, demonstrating that the clustering approach identifies consistent sequence patterns across the dataset.

Furthermore, it is possible that some cells at the edge of the cluster boundary may show a more similar sequence tendency to events detected at the overlapping border region of another cluster. Was this controlled for? It would be essential to show that events clustered together all show higher similarity to each other than to events in any other clusters.

By default, the clusters are rejected if in the adjacency matrix of the graph constructed by significant motif similarity,  the number of within cluster edges is smaller than the number of without cluster edges. In subsequent cluster merges the separation is increased since only those clusters are merged that show significant similarity. As a visual control, we monitor plots as shown in Figure 4 supplement 1. Sequence templates (color dot clouds) are supposed to show no serial correlation when ordered according to any one template other than its own. We have added more clarification to the Methods including a new Figure 6 illustrating the Method.

From the description, it was not clear how the sequence similarity was established between pairs of individual events. The only way I can see it is that the sequence (orders at which cells fire) is established with one event, and the rank order correlation is calculated with this order for the other event. However, in this case, distance A-B is not the same as distance B-A. Not sure how this is handled with the clustering procedure. Secondly, how the number of clusters is established in the hierarchical clustering procedure needs to be explained. Furthermore, from the method description, it is not clear how GS and TS sequences are identified. Can an event be classified as both a TS and GS event at the same time?

The reviewer is correct in their assertion that we compute all pairwise rank order correlations (that are then subject to a statistical test detailed in the original method publication Chenani et al., 2019). By nature of the rankorder correlation the coefficients A-B and B-A are symmetric. This is now more carefully explained in the Methods.

Several control analyses are needed to show that the sequences detected reflect not random patterns but those that repeat at a higher than random chance. This requires, at the first step, to establish to what degree sequences are consistent within a cluster and to what degree individual events show a sequential firing tendency. And at the next stage, these need to be compared with randomised events in which spike timing of cells is jittered or spike identity is randomised, and show that these events result in poorer sequence tendency and less consistent clusters.

The controls requested by the reviewer are already implemented in our Method (see original publication of the Method in Chenani et al., 2019). This is now made clearer in the Methods section.

Firing rate and place-related firing of cells alone could generate sequences even if cells otherwise fire independently from each other. In a similar manner, it was shown before that reactivation of waking cell assemblies could be seen in sleep, in which case firing rate differences across cells belonging to the same assembly could also generate sequential patterns without temporal coordination. Appropriate shuffling procedures need to be performed to exclude such scenarios.

We are aware that the sequential firing in our data (particularly during the outward phase when the animal is performing the task), is most likely resulting from the correlations between rate maps and the animals trajectory. During the reward, this is less likely. An intrinsic control is that during sampling we do not see these sequences. Given the nature of the calcium signal, a direct connection to firing rate is not possible. However, we argue that using our center of mass-approach of the calcium trace effectively normalizes for firing rate effects. Shuffling dF/F amplitudes (as a proxy for firing rates) would thus have no effect on the center of mass sequences. We, however, consider this to be an important methodological difference between sequence analysis with spikes and Calcium signals and have added a related comment to the Methods part.

The past literature describing mPFC reactivation, replay, and sequences needs to be described, and findings of this work need to be appropriately acknowledged, and those findings compared with this work (starting with this work from 2007 PMID: 18006749). In the current reading, a novice reader of this field might conclude that this is the first work that identified relay and sequences in the mPFC.

We would like to apologize that the manuscript evokes this impression. This was not our intention, in fact we have given strong emphasis on the Kaefer et al. paper in the Discussion. We have now added early references on PFC replay based on electro-physiological recordings in the Discussion section.

The analysis of Figure 4H is not sufficient to show that only forward sequences occur. If 50% are forward and 50% are reverse, the median is zero. Some of the presented histograms look like Gaussian distributions with SD=1, which would show that those events were not real sequences. It should be tested whether the distributions are significantly different from the expected Gaussian.

We agree with the reviewer that we did not explicitly test for significance of individual replays, but only tested for the rightward shift of the median. We have now added these significance tests/p values in Figure 5) and indeed could show that none of the significant backward replays exceed the fraction expected by chance, whereas forward replay significantly exceeds chance levels only in the cases where the median had a significant right ward shift (except for non-SI clusters). We would like to thank the reviewer for this suggestion, which we think makes the analysis stronger.

Overall, the clarity of the text could be improved, and further examples of reactivated sequences should be shown, and the methods should be illustrated in the figures. At the current version, I fear that even readers in this field would give up on reading the current text given an insufficient level of clarity.

We have included more examples of reactivated sequence (Suppl2 to Figure 5) and made extensive additions to the methods part. Particularly, we followed the reviewer’s request for method illustration (new Figure 6).

Reviewer #3 (Recommendations for the authors):

My main comment here is for the authors to increase the clarity of the manuscript.[...] For instance, it was difficult to follow what was being done to determine TSs and GSs.

We have made extensive additions to the Methods section including a new Figure 6 depicting the workflow of the sequence analysis in a schematic manner.

Author response:

The following is the authors’ response to the original reviews

Reviewer 1:

Strengths:

The innovation on the task alone is likely to be impactful for the field, extending recent continuous report (CPR) tasks to examine other aspects of perceptual decision-making and allowing more naturalistic readouts. One interesting and novel finding is the observation of dyadic convergence of confidence estimates even when the partner is incidental to the task performance, and that dyads tend to be more risk-seeking (indicating greater confidence) than when playing solo. The paper is well-written and clear.”

We thank reviewer 1 for this encouraging evaluation. Below we address the identified weaknesses and recommendations.

(1) Do we measure metacognitive confidence?

One concern with the novel task is whether confidence is disambiguated from a tracking of stimulus strength or coherence. […] But in the context of an RDK task, one simple strategy here is to map eccentricity directly to (subjective) motion coherence - such that the joystick position at any moment in time is a vector with motion direction and strength. This would still be an interesting task - but could be solved without invoking metacognition or the need to estimate confidence in one's motion direction decision. […] what the subjects might be doing is tracking two features of the world - motion strength and direction. This possibility needs to be ruled out if the authors want to claim a mapping between eccentricity and decision confidence […].”

We thank reviewer 1 for pointing out that the joystick tilt responses of our subjects could potentially be driven by stimulus coherence instead of metacognitive decision confidence. Below, we present four arguments to address this point of concern:

(1.1) Similar physical coherence between high and low confidence states

Nominal motion coherence is a discrete value, but the random noisiness in the stimulus causes the actual frame-by-frame coherence to be distributed around this nominal value. Because of this, subjects might scale their joystick tilt report according to the coherence fluctuations around the nominal value. To check if this was the case, we use a median split to separate stimulus states into states with large versus small joystick tilt, individually for each nominal coherence. For each stimulus state, we extracted the actual instantaneous (frame-to-frame) motion coherence, which is based on the individual movements of dots in the stimulus patch between two frames, recorded in our data files.

First, we compared the motion coherence between stimulus states with large versus small joystick tilt. For each stimulus state, we calculated average instantaneous motion coherence, and analyzed the difference of the medians for the large versus small tilt distributions for each subject and each coherence level. The resulting histograms show the distribution of differences across all 38 subjects for each nominal coherence, and are, except for the coherence of 22%, not significantly different from zero across subjects (Author response image 1). For the 22% coherence condition, the difference amounts to 0.19% – a very small, non-perceptible difference. Thus, we do no find systematic differences between the average motion coherence in states with high versus low joystick tilt.

Author response image 1.

Histograms of within-subject difference between medians of average coherence distributions with large and small joystick tilt for all subjects. Coherence is color-coded (cyan – 0%, magenta – 98%). On top, the title of each panel illustrates the number of significant differences (Ranksum test in each subject) without correction for multiple comparisons (see Author response table 1 below). In the second row of the title, we show the result of the population t-test against zero. Only 22% coherence shows a significant bias. Positive values indicate higher average coherence for large joystick tilt.  

Author response table 1.

List of all individual significantly different coherence distributions between high and low tilt states, without correction for multiple comparisons. Median differences do not show a consistent bias (i.e. positive values) that would indicate higher average coherence for the large tilts.

(1.2) Short-term stimulus fluctuations have no effect

[…] But to fully characterise the task behaviour it also seems important to ask how and whether fluctuations in motion energy (assuming that the RDK frames were recorded) during a steady state phase are affecting continuous reporting of direction and eccentricity, prior to asking how social information is incorporated into subjects' behaviour.

In addition to the analysis of stimulus coherence and tilt averaged across each stimulus state (1.1), we analyzed moment-to-moment relationship between instantaneous coherence and ongoing reports of accuracy and tilt. Below, we provide evidence that short-term fluctuations in the instantaneous coherence (i.e. the motion energy of the stimulus) do not result in correlated changes in joystick responses, neither for tilt nor accuracy. For each continuous stimulus state, we calculated cross-correlation functions between the instantaneous coherence, tilt and accuracy, and then averaged the cross-correlation across all states of the same nominal coherence, and then across subjects. The resulting average cross-correlation functions are essentially flat. This further supports our interpretation that the joystick reports do not reflect short-term fluctuations of motion energy.

Author response image 2.

Cross-correlation between the length of the resultant vector with joystick accuracy (left) and tilt (right). Coherence is color-coded. Shaded background illustrates 95% confidence intervals.

(1.3) Joystick tilt changes over time despite stable average stimulus coherence

If perceptual confidence is derived from evidence integration, we should see changes over time even when the stimulus is stable. Here, we have analyzed the average slope of the joystick tilt as a function of time within each stimulus state for each subject and each coherence, to verify if our participants tilted their joystick more with additional evidence. This is illustrated with a violin plot below (Author response image 3). The linear slopes of the joystick tilt progression over the course of stimulus states are different between coherence levels. High coherence causes more tilt over time, resulting in positive slopes for most subjects. In contrast, low/no coherence results mostly in flat or negative slopes. This tilt progression over time indicates that low coherence results in lower confidence, as subjects do not wager more with weak evidence. In contrast, high coherence causes subjects to exhibit more confidence, indicated by positive slope of the joystick tilt.

Author response image 3.

Violin plots showing the fitted slopes of the joystick tilt time course in the last 200 samples (1667 ms) leading up to a next stimulus direction (cf. Figure 2D). Positive values signify an increase in joystick tilt over time. Each dot shows the average slope for one subject. Coherence is color-coded. The dashed line at zero indicates unchanged joystick tilt over the analyzed time window.

(1.4) Cross-correlation between response accuracy and joystick tilt

Similar to 1.2 above, we have cross-correlated the frame-by-frame changes of joystick accuracy and tilt for each individual stimulus state and each subject. Across subjects, changes in tilt occur later than changes in accuracy, indicating that changes in the quality of the report are followed by changes in the size of the wager. Given that this process is not driven by short-term changes in the motion energy of the stimulus (see 1.2 above), we interpret this as additional evidence for a metacognitive assessment of the quality of the behavioral report (i.e. accuracy) reflected in the size of the wager (our measure for confidence). (See Figure 2E).

(2) Peri-decision wagering is different to post-decision wagering

[…] One route to doing this would be to ask whether the eccentricity reports show statistical signatures of confidence that have been established for more classical punctate tasks. Here a key move has been to identify qualitative patterns in the frame of reference of choice accuracy - with confidence scaling positively with stimulus strength for correct decisions, and negatively with stimulus strength for incorrect decisions (the so-called X-pattern, for instance Sanders et al. 2016 Neuron […].

We thank reviewer 1 for the constructive feedback. Our behavioral data do not show similar signatures to the previously reported post-decision confidence expression (Desender et al., 2021; Sanders et al., 2016). The previously described patterns show, first of all, that confidence for the incorrect type1 decisions diverges from the correct type1 decisions, declining with stimulus strength (e.g. coherence), as compared to increase for correct decisions. In our task, there is a graded accuracy and (putative) confidence expression, but there are no correct or incorrect decisions – instead, there are hits and misses of the reward targets presented at nominal directions. Instead of a decline for misses, we observe an equally positive scaling with coherence for the confidence, both for hits and misses (Author response image 4A). This is because in our peri-decision wagering task, the expression of confidence causally determines the binary hit or miss outcome. The outcome in our task is a function of the two-dimensional joystick response: higher tilt (confidence) requires a more accurate response to successfully hit a target. Thus, a subject can display a high (but not high enough) level of accuracy and confidence but still remain unsuccessful. If we instead median-split the confidence reports by high and low accuracy (Author response image 4C), we observe a slight separation, especially for higher coherences, but still no clear different in slopes.

We do observe the other two dynamic signatures of confidence (Desender et al., 2021): signature 2 – monotonically increasing accuracy as a function of confidence (Author response image 4), and signature 3 – steeper type 1 psychometric performance (accuracy) for high versus low confidence (Author response image 4D).

Author response image 4.

Confidence (i.e., joystick tilt, left column) and accuracy reports (right column) for different stimulus coherence, sorted by discrete outcome (hit versus miss, upper row) and the complementary joystick dimension (lower row, based on median split).

Author response image 5.

Accuracy reports correlate positively with confidence reports. For each stimulus state, we averaged the joystick response in the time window between 500 ms (60 samples) after a direction change until the first reward target appearance. If there was no target, we took all samples until the next RDP direction change into account. This corresponds to data snippets averaged in Figure 2D. Thus, for each stimulus state, we extracted a single value for joystick accuracy and for tilt (confidence). Subsequently, we fitted a linear regression to the accuracy-confidence scatter within each subject and within each coherence level. The plot above shows the average linear regression between accuracy and confidence across all subjects (i.e., the slopes and intercepts were averaged across n=38 subjects). Coherence is color-coded.

(3)  Additional analyses regarding the continuous nature of our data

I was surprised not to see more analysis of the continuous report data as a function of (lagged) task variables. […]

Reviewer 1 requested more analyses regarding the continuous nature of our data. We agree that this is a useful addition to our paper, and thank reviewer 1 for this suggestion. To address this point, we revised main Figure 2 and provided additional panels. Panel D illustrates the continuous ramp-up of both accuracy and tilt (confidence) for high coherence levels, suggesting ongoing evidence integration and meta-cognitive assessment. Panel E shows the cross-correlation between frame-by-frame changes in accuracy and tilt (see 1.4 above). Here, we demonstrate that changes in the accuracy precede changes in joystick tilt, characterizing the continuous nature of the perceptual decision-making process.

(4) Explicit motivation regarding continuous social experiments

This paper is innovating on a lot of fronts at once - developing a new CPR task for metacognition, and asking exploratory questions about how a social setting influences performance on this novel task. However, the rationale for this combination was not made explicit. Is the social manipulation there to help validate the new task as a measure of confidence as dissociated from other perceptual variables? (see query 1 below). Or is the claim that the social influence can only be properly measured in the naturalistic CPR task, and not in a more established metacognition task?

Our rationale for the combination of real-time decision making and social settings was twofold:

i. Primates, including humans, are social species. Naturally, most behavior is centered around a social context and continuously unfolds in real-time. We wanted to showcase a paradigm in which distinct aspects of continuous perceptual decision-making could be assessed over time in individual and social environments.

ii. Human behavior is susceptible to what others think and do. We wanted to demonstrate that the sheer presence of a co-acting social partner affects continuous decision-making, and quantify the extent and direction of social modulation.

We agree that the motivation for combining the new task and this specific type of social co-action should be more clear. We have clarified this aspect in the Introduction, line 92-109. In brief, the continuous, free-flowing nature of the CPR task and real-time availability of social information made this design a very suitable paradigm for assessing unconstrained social influences. We see this study as the first step into disentangling the neural basis of social modulation in primates. See also the response to reviewer 2, point 2, below.

(5) Response to minor points

(5.1)  Clarification on behavioral modulation patterns

Lines 295-298, isn't it guaranteed to observe these three behavioral patterns (both participants improving, both getting worse, only one improving while the other gets worse) even in random data?

The reviewer is correct. We now simply illustrate these possibilities in Figure 4B and how these patterns could lead to divergence or convergence between the participants (see also line 282). Unlike random data, our results predominantly demonstrate convergence.

(5.2) Clarification on AUC distributions

Lines 703-707, it wasn't clear what the AUC values referred to here (also in Figure 3) - what are the distributions that are being compared? I think part of the confusion here comes from AUC being mentioned earlier in the paper as a measure of metacognitive sensitivity (correct vs. incorrect trial distributions), whereas my impression here is that here AUC is being used to investigate differences in variables (e.g., confidence) between experimental conditions.

We apologize for the confusion. Indeed, the AUC analysis was used for the two purposes:

(i) To assess the metacognitive sensitivity (line 175, Supplementary Figure 2).

(ii) To assess the social modulation of accuracy and confidence (starting at line 232, Figures 3-6). 

We now introduce the second AUC approach for assessing social modulation, and the underlying distributions of accuracy and confidence derived from each stimulus state, separately in each subject, in line 232.

(5.3) Clarification of potential ceiling effects

Could the findings of the worse solo player benefitting more than the better solo player (Figure 4c) be partly due to a compressive ceiling effect - e.g., there is less room to move up the psychometric function for the higher-scoring player?

We thank the reviewer for this insight. First, even better performing participants were not at ceiling most of the times, even at the highest coherence (cf. Figure 2 and Supplementary Figure 3C). To test for the potential ceiling effect in the better solo players, we correlated their social modulation (expressed as AUC as in Figure 4) to the solo performance. There was no significant negative correlation for the accuracy (p > 0.063), but there was a negative correlation for the confidence (r = - 0.39, p = 0.0058), indicating that indeed low performing “better players in a dyad” showed more positive social modulation. We note however that this correlation was driven mainly by few such initially low performing “better” players, who mostly belonged to the dyads where both participants improved in confidence (green dots, Figure 4B), and that even the highest solo average confidence was at ceiling (<0.95). To conclude, the asymmetric social modulation effect we observe is mainly due to the better players declining (orange and red dots, Figure 4B), rather than due to both players improving but the better player improving less (green dots, Figure 4B).

Reviewer 2:

Strengths:

There are many things to like about this paper. The visual psychophysics has been undertaken with much expertise and care to detail. The reporting is meticulous and the coverage of the recent previous literature is reasonable. The research question is novel.

We thank reviewer 2 for this positive evaluation. Below we address the identified weaknesses and recommendations.

(1) Streamlining the text to make the paper easier to read

The paper is difficult to read. It is very densely written, with little to distinguish between what is a key message and what is an auxiliary side note. The Figures are often packed with sometimes over 10 panels and very long captions that stick to the descriptive details but avoid clarity. There is much that could be shifted to supplementary material for the reader to get to the main points.

We thank reviewer 2 for the honest assessment that our article was difficult to read and understand, and for providing specific examples of confusion. We substantially improved the clarity:

We added a Glossary that defines key terms, including Accuracy and Hit rate. 

We replaced the confusing term “eccentricity” with joystick “tilt”.

We simplified Figures 3 and 5, moving some panels into supplementary figures.

We substantially redesigned and simplified our main Figure 4, displaying the data in a more straightforward, less convoluted way, and removing several panels. This change was accompanied by corresponding changes in the text (section starting at line 277).

More generally, we shortened the Introduction, substantially revised the Results and the figure legends, and streamlined the Discussion.

(2) Dyadic co-action vs joint dyadic decision making

A third and very important one is what the word "dyadic" refers to in the paper. The subjects do not make any joint decisions. However, the authors calculate some "dyadic score" to measure if the group has been able to do better than individuals. So the word dyadic sometimes refers to some "nominal" group. In other places, dyadic refers to the social experimental condition. For example, we see in Figure 3c that AUC is compared for solo vs dyadic conditions. This is confusing.

[…] my key criticism is that the paper makes strong points about collective decision-making and compares its own findings with many papers in that field when, in fact, the experiments do not involve any collective decision-making. The subjects are not incentivized to do better as a group either. […]

The reviewer is correct to highlight these important aspects. We did, in fact, not investigate a situation where two players had to reach a joint decision with interdependent payoff and there was no incentive to collaborate or even incorporate the information provided by the other player. To make the meaning of “dyadic” in our context more explicit, we have clarified the nature of the co-action and independent payoff (e.g. lines 107, 211, 482, 755 - Glossary), and used the term “nominal combined score” (line 224) and “nominal “average accuracy” within a dyad” (line 439).

Concerning the key point about embedding our findings into the literature on collective decision-making, we would like to clarify our motivation. Outside of the recent study by Pescetelli and Yeung, 2022, we are not aware of any perceptual decision-making studies that investigated co-action without any explicit joint task. So naturally, we were stimulated by the literature on collective decisions, and felt it is appropriate to compare our findings to the principles derived from this exciting field.  Besides developing continuous – in time and in “space” (direction) – peri-decision wagering CPR game, the social co-action context is the main novel contribution of our work. Although it is possible to formulate cooperative or competitive contexts for the CPR, we leveraged the free-flowing continuous nature of the task that makes it most readily amendable to study spontaneously emerging social information integration.

We now more explicitly emphasize that most prior work has been done using the joint decision tasks, in contrast to the co-action we study here, in Introduction and Discussion.

(3) Addition of relevant literature to Discussion

[…] To see why this matters, look at Lorenz et al PNAS (https://www.pnas.org/doi/10.1073/pnas.1008636108) and the subsequent commentary that followed it from Farrell (https://www.pnas.org/doi/full/10.1073/pnas.1109947108). The original paper argued that social influence caused herding which impaired the wisdom of crowds. Farrell's reanalysis of the paper's own data showed that social influence and herding benefited the individuals at the expense of the crowd demonstrating a form of tradeoff between individual and joint payoff. It is naive to think that by exposing the subjects to social information, we should, naturally, expect them to strive to achieve better performance as a group.

Another paper that is relevant to the relationship between the better and worse performing members of the dyad is Mahmoodi et al PNAS 2015 (https://www.pnas.org/doi/10.1073/pnas.1421692112). Here too the authors demonstrate that two people interacting with one another do not "bother" figuring out each others' competence and operate under "equality assumption". Thus, the lesser competent member turns out to be overconfident, and the more competent one is underconfident. The relevance of this paper is that it manages to explain patterns very similar to Schneider et al by making a much simpler "equality bias" assumption.

We thank reviewer 2 for pointing out these highly relevant references, which we have now integrated in the Discussion (lines 430 and 467). Regarding the debate of Lorenz et al and Farell, although it is about very different type of tasks – single-shot factual knowledge estimation, it is very illuminating for understanding the differing perspectives on individual vs group benefit. We fully agree that it is naïve to assume that during independent co-action in our highly demanding task participants would strive to achieve better performance as a group – if anything, we expected less normative and more informational, reliability-driven effects as a way to cope with task demands.

Mahmoodi et al. is a particularly pertinent and elegant study, and the equality bias they demonstrate may indeed underlie the effects we see. We admit that we did not know this paper at the time of our initial writing, but it is encouraging to see the convergence [pun intended] despite task and analysis differences. As highlighted above (2), our novel contributions remain that we observe mutual alignment, or convergence, in real-time without explicitly formulated collective decision task and associated social pressure, and that we separate asymmetric social effects on accuracy and confidence.

Other reviewer-independent changes:

Additional information: Angular error in Figure 2

In panel A of the main Figure 2, we have added the angular error of the solo reports (blue dashed line) to give readers an impression about the average deviation of subjects’ joystick direction from the nominal stimulus direction. We have pointed out that angular error is the basis for accuracy calculation.

Data alignment

In the previous version of the manuscript, we have presented data with different alignments: Accuracy values were aligned to the appearance of the first target in a stimulus state (target-alignment) to avoid the predictive influence of target location within the remaining stimulus state, while the joystick tilt was extracted at the end of each stimulus state (state-alignment) to allow subjects more time to make a deliberate, confidence-guided report (Methods). We realized that this is confusing as it compares the social modulation of the two response dimensions at different points in time. In the revision, we use state-aligned data in most figures and analyses and clearly indicate which alignment type has been used. We kept the target-alignment for the illustration of the angular error in the solo-behavior (Figure 2). Specifically, this has only changed the reporting on accuracy statistics. None of the results have changed fundamentally, but the social modulation on accuracy became even stronger in state-aligned data.

In summary, we hope that these revisions have resulted in an easier-to-understand and convincing article, with clear terminology and concise and important takeaway messages.

We thank both reviewers and the editors again for their time and effort, and look forward to the reevaluation of our work.

References

Desender K, Donner TH, Verguts T. 2021. Dynamic expressions of confidence within an evidence accumulation framework. Cognition 207:104522. doi:10.1016/j.cognition.2020.104522

Pescetelli N, Yeung N. 2022. Benefits of spontaneous confidence alignment between dyad members. Collective Intelligence 1. doi:10.1177/26339137221126915

Sanders JI, Hangya B, Kepecs A. 2016. Signatures of a Statistical Computation in the Human Sense of Confidence. Neuron 90:499–506. doi:10.1016/j.neuron.2016.03.025

Author response:

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

Reviewer #1 (Public Review): 

Summary: 

This manuscript uses optical coherence tomography (OCT) to visualize tissue microstructures about 1-2 mm under the finger pad skin surface. Their geometric features are tracked and used to generate tissue strains upon skin surface indentation by a series of transparent stimuli both normal and tangential to the surface. Then movements of the stratum corneum and the upper portion of the viable epidermis are evaluated. Based upon this data, across a number of participants and ridges, around 300 in total, the findings report upon particular movements of these tissue microstructures in various loading states. A better understanding of the mechanics of the skin microstructures is important to understand how surface forces propagate toward the locations of mechanoreceptive end organs, which lie near the edge of the epidermis and dermis, from which tactile responses of at least two peripheral afferents originate. Indeed, the microstructures of the skin are likely to be important in shaping how neural afferents respond and enhance their sensitivity, receptive field characteristics, etc. 

Strengths: 

The use of OCT in the context of analyzing the movements of skin microstructures is novel. Also novel and powerful is the use of distinct loading cases, e.g., normal, tangential, and stimulus features, e.g., edges, and curves. I am unaware of other empirical visualization studies of this sort. They are state-of-the-art in this field.

Moreover, in addition to the empirical imaging observations, strain vectors in the tissues are calculated over time. 

Weaknesses: 

The interpretation of the results and their framing relative to the overall hypotheses/questions and prior works could be articulated more clearly. In particular, the major findings of the manuscript are in newly describing a central concept regarding "ridge flanks," but such structures are neither anatomically nor mechanistically defined in a clear fashion. For example, "... it appears that the primary components of ridge deformation and, potentially, neural responses are deformations of the ridge flanks and their relative movement, rather than overall bending of the ridges themselves." From an anatomical perspective, I think what the authors mean by "ridge flanks" is a differential in strain from one lateral side of a papillary ridge to the other. But is it unclear what about the continuous layers of tissue would cause such behaviors. Perhaps a sweat duct or some other structure (not visible to OCT) would subdivide the "flanks" of a papillary ridge somehow? If not due to particular anatomy, then is the importance of the "ridge flank" due to a mechanistic phenomenon of some sort? Given that the findings of the manuscript center upon the introduction of this new concept, I think a greater effort should be made to define what exactly are the "ridge flanks." It is clear from the results, especially the sliding case, that there is something important that the manuscript is getting at with this concept. 

We apologize for the confusion around our use of ‘ridge flanks’. To recap the overall goal briefly, we wanted to measure the deformation of papillary ridges and their associated sub-surface structures to different tactile stimuli. Capturing these deformations and comparing them against different proposed ideas, for example bending (horizontal shear) of the entire ridge versus differential deformations of different sub-parts, constrains neural activation mechanisms, has implications for how well tactile stimuli can be spatially resolved on the skin, and for whether sub-surface deformations can be easily predicted from surface movements alone. Our mesh was dense enough to compare the stratum corneum and the viable epidermis directly, where we expected some differences due to their previously documented mechanical differences, as well as the ridge flanks, which refers to the two (proximal and distal) sides of a single papillary ridge and their associated structure in the SC and VE (as correctly surmised by the reviewer). Differential behaviour across ridge flanks might be seen, because various observations of the surface of the stratum corneum had suggested mechanical differences between the papillary ridges and the grooves dividing them, potentially leading to differential deformations of these two halves depending on which direction they were facing tissue with different mechanical properties.

We now provide a clearer definition of ridge flanks in Figure 1 and in the main text. Importantly, existing prior research is better connected to our own investigation in the Introduction and we now specifically explain why we investigate ridge flanks.

The OCT used herein cannot visualize deep and fully into what the manuscript refers to as a "ridge"(note others have previously broken apart this concept apart into "papillary", "intermediate" and "limiting" ridges) near locations of the mechanoreceptive end organs lie at the epidermal-dermal border. Therefore, the OCT must make inferences about the movements of these deeper tissues, but cannot see them directly, and it is the movements of these deeper tissues that are likely driving the intricacies of neural firing. Note the word "ridge" is used often in the manuscript's abstract, introduction, and discussion but the definition in Fig. 1 and elsewhere differs in important ways from prior works of Cauna (expert in anatomy). Therefore, the manuscript should clarify if "ridge" refers to the papillary ridge (visible at the exterior of the skin), intermediate ridge (defined by Cauna as what the authors refer to as the primary ridge), and limiting ridge (defined by Cauna as what the authors refer to as the secondary ridge). What the authors really mean (I think) is some combination of the papillary and intermediate ridge structures, but not the full intermediate ridge. The manuscript acknowledges this in the "Limitations and future work" section, stating that these ridges cannot be resolved. This is important because the manuscript is oriented toward tracking this structure. It sets up the narrative and hypotheses to evaluate the prior works of Cauna, Gerling, Swensson, and others who all directly addressed the movement of this anatomical feature which is key to understanding ultimately how stresses at these locations might move the peripheral end organs (i.e., Merkel cells, Meissner corpuscles). 

Thank you for these observations. Indeed, our terminology was not consistent. We have now switched to Cauna’s terminology and added additional labels in Figure 1, explaining all mentioned structures in the main text. We have also changed the language in many instances in the main text to make it clearer whether we are referring to individual anatomical ridges (papillary, limiting, etc.) or the whole structure. Additionally, it is now clearer from the start which features are tracked, and we specifically state  that intermediate ridges are excluded from our tracking.

Regarding the intermediate ridge, it indeed plays a big role in Cauna’s lever hypothesis. Given the intermediate ridge is excluded from our analysis, we can neither prove nor disprove this hypothesis in our current work. However, there are many mechanical mysteries to solve regarding the structures directly above, which are the main focus of this paper. We have rewritten the introduction to make these questions clearer. For example, Cauna observed pliability of the papillary ridges in surface experiments. Swensson found differential expression patterns of keratin in epidermis tissue in and above the intermediate ridges, but the direct mechanical consequences that are proposed in their paper concern the behaviour of papillary ridges, rather than relying on a mechanical role of intermediate ridges. Even Cauna’s lever idea implies specific deformation of the stratum corneum, which would be measurable in our study, as the upper handle of the ‘lever’ needs turning. We observed little movement in accordance with this idea, putting the lever mechanism into question. While this does not rule out a mechanical role of the intermediate ridge, these findings constrain its potential mechanisms.

Reviewer #2 (Public Review): 

Summary: 

The authors investigate sub-skin surface deformations to a number of different, relevant tactile stimuli, including pressure and moving stimuli. The results demonstrate and quantify the tension and compression applied from these types of touch to fingerprint ridges, where pressure flattens the ridges. Their study further revealed that on lateral movement, prominent vertical shearing occurred in ridge deformation, with somewhat inconsistent horizontal shear. This also shows how much the deeper skin layers are deformed in touch, meaning the activation of all cutaneous mechanoreceptors, as well as the possibility of other deeper non-cutaneous mechanoreceptors. 

Strengths: 

The paper has many strengths. As well as being impactful scientifically, the methods are sound and innovative, producing interesting and detailed results. The results reveal the intricate workings of the skin layers to pressure touch, as well as sliding touch over different conditions. This makes it applicable to many touch situations and provides insights into the differential movements of the skin, and thus the encoding of touch in regards to the function of fingerprints. The work is very clearly written and presented, including how their work relates to the literature and previous hypotheses about the function of fingerprint ridges. The figures are very well-presented and show individual and group data well. The additional supplementary information is informative and the video of the skin tracking demonstrates the experiments well. 

Weaknesses: 

There are very few weaknesses in the work, rather the authors detail well the limitations in the discussion. Therefore, this opens up lots of possibilities for future work. 

We thank the reviewer for these encouraging comments.

Impact/significance: 

Overall, the work will likely have a large impact on our understanding of the mechanics of the skin. The detail shown in the study goes beyond current understanding, to add profound insights into how the skin actually deforms and moves on contact and sliding over a surface, respectively. The method could be potentially applied in many other different settings (e.g. to investigate more complex textures, and how skin deformation changes with factors like dryness and aging). This fundamental piece of work could therefore be applied to understand skin changes and how these impact touch perception. It can further be applied to understand skin mechanoreceptor function better and model these. Finally, the importance of fingertip ridges is well-detailed, demonstrating how these play a role in directly shaping our touch perception and how they can shape the interactions we have with surfaces. 

Reviewer #3 (Public Review): 

Summary: 

The publication presents unique in-vivo images of the upper layer of the epidermis of the glabrous skin when a flat object compresses or slides on the fingertip. The images are captured using OCT, and are the process of recovering the strain that fingerprints experience during the mechanical stimulation. 

The most important finding is, in my opinion, that fingerprints undergo pure compression/tension without horizontal shear, hinting at the fact that the shear stress caused by the tangential load is transferred to the deeper tissues and ultimately to the mechanoreceptors (SA-I / RA-I). 

Strengths: 

Fascinating new insights into the mechanics of glabrous skin. To the best of my knowledge, this is the first experimental evidence of the mechanical deformation of fingerprints when subjected to dynamic mechanical stimulation. The OCT measurement allows an unprecedented measurement of the depth of the skin whereas previous works were limited to tracking the surface deformation.  - The robust data analysis reveals the continuum mechanics underlying the deformation of the fingerprint ridges. 

Weaknesses: 

I do not see any major weaknesses. The work is mainly experimental and is rigorously executed. Two points pique my curiosity, however: 

(1) How do the results presented in this study compare with previous finite element analysis? I am curious to know if the claim that the horizontal shear strain is transferred to the previous layer is also captured by these models. The reason is that the FEA models typically use homogeneous materials and whether or not the behavior in-silico and in-vivo matches would offer an idea of the nature of the stratum corneum. 

Very few modeling studies have examined combined normal and tangential loading of the fingertip. Additionally, results are often expressed in terms of Von Mises stresses, and not deformation [1,2], making direct comparison challenging. Nevertheless, one multilayered study [3] supports our finding that the largest deformations are found in deeper tissues.

(1) Shao, F., Childs, T. H. C., Barnes, C. J. & Henson, B. Finite element simulations of static and sliding contact between a human fingertip and textured surfaces. Tribology International 43, 2308–2316 (2010).

(2) Tang, W. et al. Investigation of mechanical responses to the tactile perception of surfaces with different textures using the finite element method. Advances in Mechanical Engineering 8, (2016).

(3) Amaied, E., Vargiolu, R., Bergheau, J. M. & Zahouani, H. Aging effect on tactile perception: Experimental and modelling studies. Wear 332–333, 715–724 (2015). 

(2) Was there a specific reason why the authors chose to track only one fingerprint? From the method section, it seems that nothing would have prevented tracking a denser point cloud and reconstructing the stain on a section of the skin rather than just one ridge. With such data, the author could extend their analysis to multiple ridges interaction and get a better sense of the behavior of the entire strip of skin. 

We apologise for the confusion regarding this point. While in our illustration and the accompanying videos, we only show a single tracked ridge for clarity, we do indeed track all visible ridges in every frame. As imaging slices were 4 mm wide, often 8-9 ridges were visible concurrently. However, during the sliding experiments the skin was sometimes dragged along with the stimulus, causing some ridges to disappear from view for certain periods and then re-enter the frame. This would make it difficult to expand the analysis to multiple ridges, but in any case, we found neighbouring ridges to behave very consistently within a given trial, so that their mechanical behaviour (relative to the tactile feature, if any) could be averaged in the analysis.

Reviewer #1 (Recommendations For The Authors): 

Discussion, line 213, "Thus, the primary mechanism through which the ridge conforms to the object involves the relative movement and shearing of the ridge flanks, rather than relying on the groves as articulated joints." I don't see this as definitely proven in the imaging and analysis. This could be a hypothesis to come from this work for further evaluation but is a quite strong statement not obviously supported by the evidence. 

We have rephrased this statement as a proposal for further testing:

“Therefore, we propose that the primary mechanism through which a ridge conforms to an object might involve the relative movement and shearing of the ridge flanks, rather than relying on the grooves as articulated joints.”

Discussion, line 220, "Our findings strongly indicate that the majority of the surface movement of the skin was observed by deeper tissue rather than surface layers of the skin." But since there are no measurements of such tissues, or of collagen bundle tightening, etc. it is not obvious to me how this can be proven as it is not directly observable and was not modeled. 

We have reworded this paragraph to be more cautious and have included potential avenues for future testing of this idea:

“It is possible that the majority of the surface movement of the skin was absorbed by deeper tissues rather than the surface layers of the skin imaged in the present study. If that is the case, recent modeling work has suggested that tissue deformations are highly dependent on the orientation of collagen fibers in these tissues (Duprez et al., 2024), which might be amenable to tracking in future OCT work to test this idea directly. Additionally, previous work investigating tactile afferent responses to tangential skin movements has reported strong activation of SA-2 receptors, thought to measure skin stretch mainly in deeper tissues (Saal et al., 2025), providing further indirect evidence.”

Figure 1, A. As noted elsewhere, there are issues with the naming of the anatomy, and there is no definition of the concept of "ridge flanks." Also, it does not indicate the depth point to which OCT can resolve. 

We have updated and expanded the labels in Figure 1A to clarify the anatomy (along with changes in the text described above). Figure 1C now includes a sentence about the resolvability of features below the mesh:

“Detail view of a single OCT frame showing ridged skin structure and clear boundary between the stratum corneum and viable epidermis. A mesh covering the stratum corneum and the upper part of the viable epidermis (without the intermediate ridge) is overlaid spanning a single papillary ridge. The border between the viable epidermis and dermis is less clearly delineated, but some deeper features are resolved less well.”

The concept of a ridge flank is now illustrated in Figure 1B(i) and Figure 1B(iv), and referred to in both the caption and main text. Updated figure caption text:

“These deformations need not apply to the whole ridge structure but might affect different parts separately, e.g. via shearing in different directions across both ridge flanks  as shown on the far right

(see darker shading to highlight a single ridge flank).”

Updated text in the main manuscript:

“Additionally, if there are indeed mechanical differences between papillary ridges and their neighbouring grooves at the level of the stratum corneum, this might result in differential movements of the two sides of each papillary ridge, here referred to as ridge flanks (see Figure 1B-iv, right, for a potential example).”

Note that Figure 4B also includes an illustration of this concept.

Figure 1, B. This mechanical representation does not capture the entirety of the papillary-intermediate ridge unit in question, as set up by the authors in the introduction. Also, in the caption it is not ridge deformation, but upper SC and VE deformation. And the OCT cannot resolve the whole ridge. 

We have reworded the figure caption”

“Potential deformations of the tracked ridge structure, including the stratum corneum and the bulk of the viable epidermis, during tactile interactions, with arrows indicating the directions of relative deformation. [...]”

Importantly, the main manuscript text has been rewritten in the introduction section to clarify our research question and how much of the sub-surface ridge structure is tracked:

“From a mechanical standpoint, these conflicting interpretations raise the question of how the outermost two skin layers typically deform at the resolution of single papillary ridges, whether by tension, compression, or shear (see examples in Figure 1B). Additionally, such deformations might apply to individual papillary ridges and all their sub-surface structures equally, for example horizontal shearing that bends the papillary ridge in a certain direction, while levering its sub-surface aspects in the opposite direction. Conversely, individual parts of the ridge structure might deform differently. For example, the viable epidermis might deform to a different extent or in different directions due to its lower stiffness and different morphology. Additionally, if there are indeed mechanical differences between papillary ridges and their neighbouring grooves at the level of the stratum corneum, this might result in differential movements of the two sides of each papillary ridge, here referred to as ridge flanks (see Figure 1B-iv, right, for a potential example). To empirically address these questions, we employed Optical Coherence Tomography (OCT) to precisely measure the sub-surface deformation of individual fingerprint ridges in response to a variety of mechanical events. Specifically, we focused on the stratum corneum and the bulk of the viable epidermis (excluding intermediate ridges), which could be robustly resolved and tracked by our setup.”

Figure 1, C: While it is noted in the caption that the locations of the intermediate and limiting ridges, as well as the collagen bundles, are clearly visible, it is not clear to me, although the caption uses these words. This is especially the case below the orange mesh. From the picture, and because this is not labeled, it leaves it up to my interpretation, it seems like the secondary ridge (limiting) is larger than the primary (intermediate). 

We have reworded the caption as follows:

“Detail view of a single OCT frame showing ridged skin structure and clear boundary between the stratum corneum and viable epidermis. A mesh covering the stratum corneum and the upper part of the viable epidermis (without the intermediate ridge) is overlaid spanning a single papillary ridge. The border between the viable epidermis and dermis is less clearly delineated.”

Indeed, while the intermediate ridge was often visible in the OCT images, its size was rather inconsistent and it could appear as larger or smaller than the limiting ridge, while in histological images it is generally shown as larger (however note that there is somewhat limited data). This difference might be due to imaging artifacts, e.g. limited visibility into the deeper tissues, might reflect individual differences between participants, or could indicate that intermediate ridges are not of a consistent height in the (out-of-plane) direction along a given ridge. We have clarified this in the Limitations section of the Discussion:

“[...] while we could confidently track landmarks associated with the stratum corneum, we could not reliably identify intermediate ridges in the viable epidermis, though they were visible in some of the frames, limiting the depth of the fitted mesh. We hypothesize that the additional depth of these ridges combined with their slender morphology might have degraded the signal. 3D OCT imaging (see below) might help to resolve these features in future work and settle open questions regarding their precise morphology.”

Figure 1, D, and E: How do these measurements compare with the literature? They seem reasonable to me based on a cursory review, but there is a need to directly compare, especially since measurements in this context with the OCT are novel and could be valuable. 

We have clarified this in the main text and added more references to the existing literature:

“We measured an average ridge width of 0.47 mm across participants (Figure 1D), consistent with previous studies (Moore, 1989; Ohler and Cummins, 1942). Average skin layer thickness was 0.38 mm for the stratum corneum and 0.12 mm for the viable epidermis across our dataset (Figure 1E), again in agreement with previous studies using both in vivo imaging and ex vivo histology (Fruhstorfer et al., 2000; Lintzeri et al., 2022; Maiti et al., 2020).”

Abstract 4th sentence's structure makes me think that hundreds of individual fingerprint ridges can be tracked at the same time. Perhaps it could be tweaked to clearly indicate that hundreds were tracked between trials between participants. 

We have changed the sentence to now read:

“Here, we used optical coherence tomography to image and track sub-surface deformations of hundreds of individual fingerprint ridges across ten participants and four individual contact events at high spatial resolution in vivo.”

Introduction, 1st sentence, the fingertip per se is not an organ, though the skin is an organ. 

Changed the wording from “organ” to “structure”.

Introduction, 1st sentence, "... that convert skin deformations ..." Need to add word skin to be clear. 

Done.

Introduction, 3rd paragraph, "Alternately, the grooves may be stiffer or less ...". In this paragraph, and this sentence in particular, Cauna is cited and the words groves and ridges are used. But this is not adequately explained. Cauna had distinct terminology, where he referred to papillary, intermediate, and limiting ridges, that exist in addition to ready ridges. It is important because the manuscript uses the word "ridges" in a non-specific way. This is done not just here but throughout the manuscript, and is central to the questions which can be addressed with OCT. 

Anatomy has been better defined and more extensively labelled in Figure 1A, including labels for ‘papillary ridges’ and ‘grooves’. We have reworded this paragraph to better explain the concepts and how they relate to the subsequent analyses in the paper

“Consequently, the mechanical response of the skin below its immediate surface remains largely unknown, leading to conflicting interpretations in the literature. For instance, it has been proposed that the papillary ridges are stiffer than the neighbouring grooves (Swensson et al., 1998), which might imply that normal loading of the skin might not affect the ridges’ profile appreciably. Conversely, other observations have suggested that the grooves are relatively stiff, allowing the papillary ridges to deform considerably (Cauna, 1954; Johansson and LaMotte, 1983). However, the sub-surface consequences of this putative pliability during object contact or stick-to-slip transitions (see e.g. Delhaye et al., 2016) are unclear: the whole ridge structure might bend as proposed in Cauna’s lever mechanism (Cauna, 1954), but this view has proved controversial (see e.g. Gerling and Thomas, 2008), with direct empirical evidence lacking.”

Figure 1. Avoid red-green dots for colorblind accessibility. PMMA is not in the caption. 

We have switched the colors of the mechanoreceptors in panel A to a colorblind-friendly scheme. We now also specify the material of the plates in the figure 1 caption.

Results, line 102. "... papillary ridge structure...." Is this the ridge to which is being referred? 

In conjunction with the updated labeling in Figure 1A, we have updated the terminology throughout the paper to be more consistent.

Results, line 99. "We noted a small increase in the area of the strateum corneum, which was likely an artifact due to the fit of the mesh to the ridge's curvature ..." There is very little discussion of Fig. F's finding related to an increase in area in the SC and decrease in the VE. It makes me question if this finding in this panel is an artifact. With stiff tissue like stratum corneum, how would the area increase? 

This finding could be a measurement artifact or it could be the result of skin from neighbouring regions pushing into the imaged space. We have reworded the brief description in the Results:

“We noted a small increase in the area of the stratum corneum, which was possibly an artifact due to the imperfect fit of the mesh to the ridge's curvature (but see Discussion for an alternative explanation).”

Additionally, we have added a short section in the Discussion in the Limitations section:

“Some of our tactile interactions might have caused skin deformations out-of-plane that were thus not measurable. For example, the slight increase in thickness of the stratum corneum under normal load might be explained as a measurement artifact due to the coarse nature of the mesh fitted, but could alternatively reflect tissue from out-of-plane regions pushing into the imaged space. Indeed, recent surface measurements of the skin's behaviour during initial object contact have reported compression of the skin in the plane parallel to its surface (Doumont et al., 2025), which would result in increasing thickness, assuming that the stratum corneum is incompressible. Future studies could consider creating three-dimensional reconstructions of the fingerprint structure to study such effects.”

Figure 3. The colors used in slip and stick are not colorblind accessible. 

We have changed the background colors in Figure 3A,B,C to a colorblind accessible version.

Results, line 151, "Thus, most of this shearing must be sustained by deeper tissues." But there are no direct observations as such. Also, in the next sentence, "collagen fiber bundles" are referred to in a non-specific way. This section is highly speculative with no systematic visualization of these structures, and should probably be moved to the discussion. 

We have reworded this sentence to be more cautious. We have now also highlighted collagen fiber bundles visible in the figure. Systematic analysis of these is beyond the scope of the present study, as these were not tracked, but might be possible in future studies. The reworded sentence reads as follows:

“Thus, it is possible that shearing is sustained by deeper tissues, an effect that could be tested in future studies by directly tracking the angle and orientation of collagen fiber bundles anchoring the epidermis to deeper tissues (see highlighted examples in Figure 3B).”

Results, line 161, " Horizontal shear ..." do you mean surface shear, per the Fig. 1 definition? 

For consistency, we have changed the labels to ‘Horizontal shear’ and ‘Vertical shear’ in Figure 1A(iii) and Figure 1A(iv) as these are the terms used throughout the paper.

Discussion, line 198, "... flatten even at relatively low forces." This is an interesting point and it would be useful to note how low exactly. 

We have reworded this sentence to better reflect the findings described earlier:

“We found that individual ridges tended to flatten considerably at relatively low forces of 0.5 N, with higher forces increasing deformations only moderately.”

Reviewer #2 (Recommendations For The Authors): 

Minor comments that could improve the paper even further 

In the abstract, it may be good to specify that the stimuli were all applied to the finger, this was not an active, self-generated tactile interaction, e.g. change 'in response to a variety of tactile stimuli' to 'in response to a variety of passively-applied tactile stimuli'. 

Done.

Comment on the grey/blue colours in the figures. I like the combination of blue/orange for different conditions, but sometimes the blue is very difficult to see against the grey background. Is there any way of making the grey background shading lighter and/or the blue darker/more vivid?

We have changed the color of the SC mesh to a darker shade of blue, which is more easily distinguished from the grey background. This applies to figures 2B/C, 3D, 4A/B/D/E, and all supplementary figures.

Methods. Could you please add a little more detail about exactly where the images were taken, e.g. in the exact middle of the fingerpad, at the fingertip? Did you line up the skin fingerprint ridges to be in a plane? It is just to better understand how the stimulus moved against the skin, which itself is rounded, and whether it was at a point where the ridges were relatively linear or curved. 

We have added the following text in the “Experimental set-up” section of the Methods:

“The participant's finger was secured in a finger holder, which was positioned in such a way that the flat part of the fingertip distal to the whorl made initial contact with the plate as it was lowered onto the fingertip. The scanner was positioned such that its scan path aligned with the distal-proximal axis of the plate, targeting the centre line of the fingerpad so that the fingerprint ridges were oriented orthogonally to the line scan.”

and

“For these experiments, imaging focused on the central flat part of the contact area, such that all fingerprint ridges visible in the imaged region were in contact with the plate throughout the trial.”

Methods. There is no section about statistics, yet you do use them in the paper. It may be good to add a few details in the methods to outline the package you used to do the statistics, as well as why you chose the tests you carried out. 

We have added a new Statistics section at the end of the Methods:

“Statistical tests were run in Python using the scipy.stats package. As distributions were skewed, we used non-parametric analyses throughout the study. Bonferroni corrections were used when multiple comparisons were made.”

A very minor point. Discussion, line 210: 'In this study...' is vague, which study exactly? It is preferable to be more precise, e.g. 'In the present/current study...'. 

Fixed.

Discussion. One point you may want to add is the possibility of looking at other skin regions. For example, would this approach work on the palm, on border glabrous/hairy skin, on various hairy skin sites, and on the foot? The possibilities could be endless if it could be applied anywhere, but it may depend on the technical positioning and skin itself. However, it would be interesting to know. 

We have added the following text at the end of the Discussion section:

“Finally, while we focused on the fingertip only, many other skin regions present interesting mechanical challenges waiting to be explored. The general ridged structure observed on the fingertip is common to all glabrous skin, but the local ridge mechanics might still differ: glabrous skin on the foot sole exhibits some morphological differences in order to support large weights that might well influence its mechanical response (Boyle et al., 2019). For example, the morphology of transverse ridges (running orthogonal to and connecting limiting with intermediate ridges) differs across regions on the foot sole (Nagashima and Tsuchida, 2011) and very likely from the hand (Yamada et al., 1996). Our method should be directly applicable to study deformations of these ridges, though three-dimensional observations might be needed to resolve some of the open questions. Hairy skin in contrast differs from glabrous skin in that the stratum corneum is much thinner. It also lacks the clearly organised ridge structure, but exhibits more loosely oriented skin folds instead, which very likely also serve a mechanical function (Leyva-Mendivil et al., 2015) and in principle are amenable to study using OCT.”

In the last lines of the discussion, you mention the possible effects of skin moisturization. The Tomlinson et al. paper refers to the hydration of the skin with regard to water, which I would say is a slightly different factor. I think you can mention this paper and talk about the water level of the skin/hydration, but also add specifically that moisturization (i.e. by an emollient, humectant, or occlusive substance) is another factor to consider (e.g. effects found by Dione et al, 2023 Sci Rep). Overall, these two points relate to the dryness of the skin and the humidity of surfaces being contacted, therefore you could expand on both. 

Thank you for the correction! We now mention both skin hydration and moisturization separately in this section.

I found [m23] “Make Peace with Social Media” by Amanda Baughan (2022) really interesting because it challenges the idea that social media is automatically bad for mental health. Instead of calling it an addiction, Baughan suggests treating it more like a relationship — one that you can manage, improve, and set boundaries for. I think this approach is a lot healthier than the “digital detox” mindset, which feels unrealistic for people who rely on social media for community or work.

Her perspective connects to the “Healing your social media” section in the chapter, especially the idea of replacing “I should” with “I enjoy.” It made me realize that guilt-based thinking about screen time doesn’t help — awareness and intention do. Personally, this made me reflect on how I use social media to learn and connect with people who share my goals, rather than just scroll out of habit.

I would argue you can never really know anyone 😵‍💫