Author response:

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

Reviewer #1 (Public review): 

This study presents cryoEM-derived structures of the Trypanosome aquaporin AQP2, in complex with its natural ligand, glycerol, as well as two trypanocidal drugs, pentamidine and melarsoprol, which use AQP2 as an uptake route. The structures are high quality, and the density for the drug molecules is convincing, showing a binding site in the centre of the AQP2 pore. 

The authors then continue to study this system using molecular dynamics simulations. Their simulations indicate that the drugs can pass through the pore and identify a weak binding site in the centre of the pore, which corresponds with that identified through cryoEM analysis. They also simulate the effect of drug resistance mutations, which suggests that the mutations reduce the affinity for drugs and therefore might reduce the likelihood that the drugs enter into the centre of the pore, reducing the likelihood that they progress through into the cell. 

While the cryoEM and MD studies are well conducted, it is a shame that the drug transport hypothesis was not tested experimentally. For example, did they do cryoEM with AQP2 with drug resistance mutations and see if they could see the drugs in these maps? They might not bind, but another possibility is that the binding site shifts, as seen in Chen et al. 

TbAQP2 from the drug-resistant mutants does not transport either melarsoprol or pentamidine and there was thus no evidence to suggest that the mutant TbAQP2 channels could bind either drug. Moreover, there is not a single mutation that is characteristic for drug resistance in TbAQP2: references 12–15 show a plethora of chimeric AQP2/3 constructs in addition to various point mutations in laboratory strains and field isolates. In reference 17 we describe a substantial number of SNPs that reduced pentamidine and melarsoprol efficacy to levels that would constitute clinical resistance to acceptable dosage regimen. It thus appears that there are many and diverse mutations that are able to modify the protein sufficiently to induce resistance, and likely in multiple different ways, including the narrowing of the pore, changes to interacting amino acids, access to the pore etc. We therefore did not attempt to determine the structures of the mutant channels because we did not think that in most cases we would see any density for the drugs in the channel, and we would be unable to define ‘the’ resistance mechanism if we did in the case of one individual mutant TbAQP2. Our MD data suggests that pentamidine binding affinity is in the range of 50-300 µM for the mutant TbAQP2s selected for that test (I110W and L258Y/L264R), i.e. >1000-fold higher than TbAQP2WT. Thus these structures will be exceedingly challenging to determine with pentamidine in the pore but, of course, until the experiment has been tried we will not know for sure.

Do they have an assay for measuring drug binding? 

We tried many years ago to develop a ³H-pentamidine binding assay to purified wild type TbAQP2 but we never got satisfactory results even though the binding should be in the doubledigit nanomolar range. This may be for any number of technical reasons and could also be partly because flexible di-benzamidines bind non-specifically to proteins at µM concentrations giving rise to high background. Measuring binding to the mutants was not tested given that they would be binding pentamidine in the µM range. If we were to pursue this further, then isothermal titration calorimetry (ITC) may be one way forward as this can measure µM affinity binding using unlabelled compounds, although it uses a lot of protein and background binding would need to be carefully assessed; see for example our work on measuring tetracycline binding to the tetracycline antiporter TetAB (https://doi.org/10.1016/j.bbamem.2015.06.026 ). Membrane proteins are also particularly tricky for this technique as the chemical activity of the protein solution must be identical to the chemical activity of the substrate solution which titrates in the molecule binding to the protein; this can be exceedingly problematic if any free detergent remains in the purified membrane protein. Another possibility may be fluorescence polarisation spectroscopy, although this would require fluorescently labelling the drugs which would very likely affect their affinity for TbAQP2 and how they interact with the wild type and mutant proteins – see the detailed SAR analysis in Alghamdi et al. 2020 (ref. 17). As you will appreciate, it would take considerable time and effort to set up an assay for measuring drug binding to mutants and is beyond the current scope of the current work.

I think that some experimental validation of the drug binding hypothesis would strengthen this paper. Without this, I would recommend the authors to soften the statement of their hypothesis (i.e, lines 65-68) as this has not been experimentally validated.

We agree with the referee that direct binding of drugs to the mutants would be very nice to have, but we have neither the time nor resources to do this. We have therefore softened the statement on lines 65-68 to read ‘Drug-resistant TbAQP2 mutants are still predicted to bind pentamidine, but the much weaker binding in the centre of the channel observed in the MD simulations would be insufficient to compensate for the high energy processes of ingress and egress, hence impairing transport at pharmacologically relevant concentrations.’ 

Reviewer #2 (Public review): 

Summary: 

The authors present 3.2-3.7 Å cryo-EM structures of Trypanosoma brucei aquaglyceroporin-2 (TbAQP2) bound to glycerol, pentamidine, or melarsoprol and combine them with extensive allatom MD simulations to explain drug recognition and resistance mutations. The work provides a persuasive structural rationale for (i) why positively selected pore substitutions enable diamidine uptake, and (ii) how clinical resistance mutations weaken the high-affinity energy minimum that drives permeation. These insights are valuable for chemotherapeutic re-engineering of diamidines and aquaglyceroporin-mediated drug delivery. 

My comments are on the MD part. 

Strengths: 

The study 

(1) Integrates complementary cryo-EM, equilibrium, applied voltage MD simulations, and umbrella-sampling PMFs, yielding a coherent molecular-level picture of drug permeation. 

(2) Offers direct structural rationalisation of long-standing resistance mutations in trypanosomes, addressing an important medical problem. 

Weaknesses: 

Unphysiological membrane potential. A field of 0.1 V nm ¹ (~1 V across the bilayer) was applied to accelerate translocation. From the traces (Figure 1c), it can be seen that the translocation occurred really quickly through the channel, suggesting that the field might have introduced some large changes in the protein. The authors state that they checked visually for this, but some additional analysis, especially of the residues next to the drug, would be welcome. 

This is a good point from the referee, and we thank them for raising it. It is common to use membrane potentials in simulations that are higher than the physiological value, although these are typically lower than used here. The reason we used the higher value was to speed sampling and it still took 1,400 ns for transport in the physiologically correct direction, and even then, only in 1/3 repeats. Hence this choice of voltage was probably necessary to see the effect. The exceedingly slow rate of pentamidine permeation seen in the MD simulation was consistent with the experimental observations, as discussed in Alghamdi et al (2020) [ref. 17] where we estimated that TbAQP2-mediated pentamidine uptake in T. brucei bloodstream forms proceeds at just 9.5×10⁵ molecules/cell/h; the number of functional TbAQP2 units in the plasma membrane is not known but their location is limited to the small flagellar pocket (Quintana et al. PLoS Negl Trop Dis 14, e0008458 (2020)). 

The referee is correct that it is important to make sure that the applied voltage is not causing issues for the protein, especially for residues in contact with the drug. We have carried out RMSF analysis to better test this. The data show that comparing our simulations with the voltage applied to the monomeric MD simulations + PNTM with no voltage reveals little difference in the dynamics of the drug-contacting residues. 

We have added these new data as Supplementary Fig12b with a new legend (lines1134-1138) 

‘b, RMSF calculations were run on monomeric TbAQP2 with either no membrane voltage or a 0.1V nm^-1 voltage applied (in the physiological direction). Shown are residues in contact with the pentamidine molecule, coloured by RMSF value. RMSF values are shown for residues Leu122, Phe226, Ile241, and Leu264. The data suggest the voltage has little impact on the flexibility or stability of the pore lining residues.’

We have also added the following text to the manuscript (lines 524-530):

‘Membrane potential simulations were run using the computational electrophysiology protocol. An electric field of 0.1 V/nm was applied in the z-axis dimension only, to create a membrane potential of about 1 V (see Fig. S10a). Note that this is higher than the physiological value of 87.1 ± 2.1 mV at pH 7.3 in bloodstream T. brucei, and was chosen to improve the sampling efficiency of the simulations. The protein and lipid molecules were visually confirmed to be unaffected by this voltage, which we quantify using RMSF analysis on pentamidine-contacting residues (Fig. S12b).’ 

Based on applied voltage simulations, the authors argue that the membrane potential would help get the drug into the cell, and that a high value of the potential was applied merely to speed up the simulation. At the same time, the barrier for translocation from PMF calculations is ~40 kJ/mol for WT. Is the physiological membrane voltage enough to overcome this barrier in a realistic time? In this context, I do not see how much value the applied voltage simulations have, as one can estimate the work needed to translocate the substrate on PMF profiles alone. The authors might want to tone down their conclusions about the role of membrane voltage in the drug translocation.

We agree that the PMF barriers are considerable, however we highlight that other studies have seen similar landscapes, e.g. PMID 38734677 which saw a barrier of ca. 10-15 kcal/mol (ca. 4060 kJ/mol) for PNTM transversing the channel. This was reduced by ca. 4 kcal/mol when a 0.4 V nm ¹ membrane potential was applied, so we expect a similar effect to be seen here. 

We have updated the Results to more clearly highlight this point and added the following text (lines 274-275):

We note that previous studies using these approaches saw energy barriers of a similar size, and that these are reduced in the presence of a membrane voltage[17,31].’ 

Pentamidine charge state and protonation. The ligand was modeled as +2, yet pKa values might change with the micro-environment. Some justification of this choice would be welcome. 

Pentamidine contains two diamidine groups and each are expected to have a pKa above 10 in solution (PMID: 20368397), suggesting that the molecule will carry a +2 charge. Using the +2 charge is also in line with previous MD studies (PMID: 32762841). We have added the following text to the Methods (lines 506-509):

‘The pentamidine molecule used existing parameters available in the CHARMM36 database under the name PNTM with a charge state of +2 to reflect the predicted pKas of >10 for these groups [73] and in line with previous MD studies[17].’

We note that accounting for the impact of the microenvironment is an excellent point – future studies might employ constant pH calculations to address this.

The authors state that this RMSD is small for the substrate and show plots in Figure S7a, with the bottom plot being presumably done for the substrate (the legends are misleading, though), levelling off at ~0.15 nm RMSD. However, in Figure S7a, we see one trace (light blue) deviating from the initial position by more than 0.2 nm - that would surely result in an RMSD larger than 0.15, but this is somewhat not reflected in the RMSD plots. 

The bottom plot of Fig. S9a (previously Fig. S7a) is indeed the RMSD of the drug (in relation to the protein). We have clarified the legend with the following text (lines 1037-1038): ‘… or for the pentamidine molecule itself, i.e. in relation to the Cα of the channel (bottom).’ 

With regards the second comment, we assume the referee is referring to the light blue trace from Fig S9c. These data are actually for the monomeric channel rather than the tetramer. We apologise for not making this clearer in the legend. We have added the word ‘monomeric’ (line 1041).

Reviewer #3 (Public review): 

Summary: 

Recent studies have established that trypanocidal drugs, including pentamidine and melarsoprol, enter the trypanosomes via the glyceroaquaporin AQP2 (TbAQP2). Interestingly, drug resistance in trypanosomes is, at least in part, caused by recombination with the neighbouring gene, AQP3, which is unable to permeate pentamidine or melarsoprol. The effect of the drugs on cells expressing chimeric proteins is significantly reduced. In addition, controversy exists regarding whether TbAQP2 permeates drugs like an ion channel, or whether it serves as a receptor that triggers downstream processes upon drug binding. In this study the authors set out to achieve three objectives: 

(1) to determine if TbAQP2 acts as a channel or a receptor,

We should clarify here that this was not an objective of the current manuscript as the transport activity has already been extensively characterised in the literature, as described in the introduction.

(2) to understand the molecular interactions between TbAQP2 and glycerol, pentamidine, and melarsoprol, and 

(3) to determine the mechanism by which mutations that arise from recombination with TbAQP3 result in reduced drug permeation. 

Indeed, all three objectives are achieved in this paper. Using MD simulations and cryo-EM, the authors determine that TbAQP2 likely permeates drugs like an ion channel. The cryo-EM structures provide details of glycerol and drug binding, and show that glycerol and the drugs occupy the same space within the pore. Finally, MD simulations and lysis assays are employed to determine how mutations in TbAQP2 result in reduced permeation of drugs by making entry and exit of the drug relatively more energy-expensive. Overall, the strength of evidence used to support the author's claims is solid. 

Strengths: 

The cryo-EM portion of the study is strong, and while the overall resolution of the structures is in the 3.5Å range, the local resolution within the core of the protein and the drug binding sites is considerably higher (~2.5Å). 

I also appreciated the MD simulations on the TbAQP2 mutants and the mechanistic insights that resulted from this data. 

Weaknesses: 

(1) The authors do not provide any empirical validation of the drug binding sites in TbAQP2. While the discussion mentions that the binding site should not be thought of as a classical fixed site, the MD simulations show that there's an energetically preferred slot (i.e., high occupancy interactions) within the pore for the drugs. For example, mutagenesis and a lysis assay could provide us with some idea of the contribution/importance of the various residues identified in the structures to drug permeation. This data would also likely be very valuable in learning about selectivity for drugs in different AQP proteins.

On a philosophical level, we disagree with the requirement for ‘validation’ of a structure by mutagenesis. It is unclear what such mutagenesis would tell us beyond what was already shown experimentally through ³H-pentamidine transport, drug sensitivity and lysis assays i.e. a given mutation will impact permeation to a certain extent. But on the structural level, what does mutagenesis tell us? If a bulky aromatic residue that makes many van der Waals interactions with the substrate is changed to an alanine residue and transport is reduced, what does this mean? It would confirm that the phenylalanine residue is very likely indeed making van der Waals contacts to the substrate, but we knew that already from the WT structure. And if it doesn’t have any effect? Well, it could mean that the van der Waals interactions with that particular residue are not that important or it could be that the substrate has changed its positions slightly in the channel and the new pose has similar energy of interactions to that observed in the wild type channel. Regardless of the result, any data from mutagenesis would be open to interpretation and therefore would not impact on the conclusions drawn in this manuscript. We might not learn anything new unless all residues interacting with the substrate are mutated, the structure of each mutant was determined and MD simulations were performed for all, which is beyond the scope of this work. Even then, the value for understanding clinical drug resistance would be limited, as this phenomenon has been linked to various chimeric rearrangements with adjacent TbAQP3 (references 12–15), each with a structure distinct from TbAQP2 with a single SNP. We also note that the recent paper by Chen et al. did not include any mutagenesis of the drug binding sites in TbAQP2 in their analysis of TbAQP2, presumably for similar reasons as discussed above.

(2) Given the importance of AQP3 in the shaping of AQP2-mediated drug resistance, I think a figure showing a comparison between the two protein structures/AlphaFold structures would be beneficial and appropriate

We agree that the comparison is of considerably interest and would contribute further to our understanding of the unique permeation capacities of TbAQP2. As such, we followed the reviewer’s suggestion and made an AlphaFold model of TbAQP3 and compared it to our structures of TbAQP2. The RMSD is 0.6 Å to the pentamidine-bound TbAQP2, suggesting that the fold of TbAQP3 has been predicted well, although the side chain rotamers cannot be assessed for their accuracy. Previous work has defined the selectivity filter of TbAQP3 to be formed by W102, R256, Y250. The superposition of the TbAQP3 model and the TbAQP2 pentamidine-bound structure shows that one of the amine groups is level with R256 and that there is a clash with Y250 and the backbone carbonyl of Y250, which deviates in position from the backbone of TbAQP2 in this region. There is also a clash with Ile252. 

Although these observations are indeed interesting, on their own they are highly preliminary and extensive further work would be necessary to draw any convincing conclusions regarding these residues in preventing uptake of pentamidine and melarsoprol. The TbAQP3 AlphaFold model would need to be verified by MD simulations and then we would want to look at how pentamidine would interact with the channel under different experimental conditions like we have done with TbAQP2. We would then want to mutate to Ala each of the residues singly and in combination and assess them in uptake assays to verify data from the MD simulations. This is a whole new study and, given the uncertainties surrounding the observations of just superimposing TbAQP2 structure and the TbAQP3 model, we feel that, regrettably, this is just too speculative to add to our manuscript. 

(3) A few additional figures showing cryo-EM density, from both full maps and half maps, would help validate the data. 

Two new Supplementary Figures have been made, on showing the densities for each of the secondary structure elements (the new Figure S5) and one for the half maps showing the ligands (the new Figure S6). All the remaining supplementary figures have been renamed accordingly.

(4) Finally, this paper might benefit from including more comparisons with and analysis of data published in Chen et al (doi.org/10.1038/s41467-024-48445-4), which focus on similar objectives. Looking at all the data in aggregate might reveal insights that are not obvious from either paper on their own. For example, melarsoprol binds differently in structures reported in the two respective papers, and this may tell us something about the energy of drug-protein interactions within the pore. 

We already made the comparisons that we felt were most pertinent and included a figure (Fig. 5) to show the difference in orientation of melarsoprol in the two structures. We do not feel that any additional comparison is sufficiently interesting to be included. As we point out, the structures are virtually identical (RMSD 0.6 Å) and therefore there are no further mechanistic insights we would like to make beyond the thorough discussion in the Chen et al paper.

Reviewer #1 (Recommendations for the authors): 

(1) Line 65 - I don't think that the authors have tested binding experimentally, and so rather than 'still bind', I think that 'are still predicted to bind' is more appropriate. 

Changed as suggested

(2) Line 69 - remove 'and' 

Changed as suggested

(3) Line 111 - clarify that it is the protein chain which is 'identical'. Ligands not. 

Changed to read ‘The cryo-EM structures of TbAQP2 (excluding the drugs/substrates) were virtually identical…

(4) Line 186 - make the heading of this section more descriptive of the conclusion than the technique? 

We have changed the heading to read: ‘Molecular dynamics simulations show impaired pentamidine transport in mutants’

Reviewer #2 (Recommendations for the authors): 

(1) Methods - a rate of 1 nm per ns is mentioned for pulling simulations, is that right? 

Yes, for the generation of the initial frames for the umbrella sampling a pull rate of 1 nm/ns was used in either an upwards or downwards z-dimension

(2) Figure S9 and S10 have their captions swapped. 

The captions have been swapped to their proper positions.

(3) Methods state "40 ns per window" yet also that "the first 50 ns of each window was discarded as equilibration". 

Well spotted - this line should have read “the first 5 ns of each window was discarded as equilibration”. This has been corrected (line 541).

Reviewer #3 (Recommendations for the authors): 

(1) Abstract, line 68-70: incomplete sentence.

The sentence has been re-written: ‘The structures of drug-bound TbAQP2 represent a novel paradigm for drug-transporter interactions and are a new mechanism for targeting drugs in pathogens and human cells.

(2) Line 312-313: The paper you mention here came out in May 2024 - a year ago. I appreciate that they reported similar structural data, but for the benefit of the readers and the field, I would recommend a more thorough account of the points by which the two pieces of work differ. Is there some knowledge that can be gleaned by looking at all the data in the two papers together? For example, you report a glycerol-bound structure while the other group provides an apo one. Are there any mechanistic insights that can be gained from a comparison?

We already made the comparisons that we felt were most pertinent and included a figure (Fig. 5) to show the difference in orientation of melarsoprol in the two structures. We do not feel that any additional comparison is sufficiently interesting to be included. As we point out, the structures are virtually identical (RMSD 0.6 Å) and therefore there are no further mechanistic insights we would like to make beyond the thorough discussion in the Chen et al paper.

(3) Similarly, you can highlight the findings from your MD simulations on the TbAQP2 drug resistance mutants, which are unique to your study. How can this data help with solving the drug resistance problem?

New drugs will need to be developed that can be transported by the mutant chimera AQP2s and the models from the MD simulations will provide a starting point for molecular docking studies. Further work will then be required in transport assays to optimise transport rather than merely binding. However, the fact that drug resistance can also arise through deletion of the AQP2 gene highlights the need for developing new drugs that target other proteins.

(4) A glaring question that one has as a reader is why you have not attempted to solve the structures of the drug resistance mutants, either in complex with the two compounds or in their apo/glycerol-bound form? To be clear, I am not requesting this data, but it might be a good idea to bring this up in the discussion.

TbAQP2 containing the drug-resistant mutants does not transport either melarsoprol or pentamidine (Munday et al., 2014; Alghamdi et al., 2020); there was thus no evidence to suggest that the mutant TbAQP2 channels could bind either drug. We therefore did not attempt to determine the structures of the mutant channels because we did not think that we would see any density for the drugs in the channel. Our MD data suggests that pentamidine binding affinity is in the range of 50-300 µM for the mutant TbAQP2, supporting the view that getting these structures would be highly challenging, but of course until the experiment is tried we will not know for sure.

We also do not think we would learn anything new about doing structures of the drug-free structures of the transport-negative mutants of TbAQP2. The MD simulations have given novel insights into why the drugs are not transported and we would rather expand effort in this direction and look at other mutants rather than expend further effort in determining new structures.

(5) Line 152-156: Is there a molecular explanation for why the TbAQP2 has 2 glycerol molecules captured in the selectivity filter while the PfAQP2 and the human AQP7 and AQP10 have 3?

The presence of glycerol molecules represents local energy minima for binding, which will depend on the local disposition of appropriate hydrogen bonding atoms and hydrophobic regions, in conjunction with the narrowness of the channel to effectively bind glycerol from all sides. It is noticeable that the extracellular region of the channel is wider in TbAQP2 than in AQP7 and AQP10, so this may be one reason why additional ordered glycerol molecules are absent, and only two are observed. Note also that the other structures were determined by X-ray crystallography, and the environment of the crystal lattice may have significantly decreased the rate of diffusion of glycerol, increasing the likelihood of observing their electron densities.

(6) I would also think about including the 8JY7 (TbAQP2 apo) structure in your analysis.

We included 8JY7 in our original analyses, but the results were identical to 8JY6 and 8JY8 in terms of the protein structure, and, in the absence of any modelled substrates in 8JY7 (the interesting part for our manuscript), we therefore have not included the comparison.

(7) I also think, given the importance of AQP3 in this context, it would be really useful to have a comparison with the AQP3 AlphaFold structure in order to examine why it does not permeate drugs.

We made an AlphaFold model of TbAQP3 and compared it to our structures of TbAQP2. The RMSD is 0.6 Å to the pentamidine-bound TbAQP2, suggesting that the fold of TbAQP3 has been predicted well, although the side chain rotamers cannot be assessed for their accuracy. Previous work has defined the selectivity filter of TbAQP3 to be formed by W102, R256, Y250. The superposition of the TbAQP3 model and the TbAQP2 pentamidine-bound structure shows that one of the amine groups is level with R256 and that there is a clash with Y250 and the backbone carbonyl of Y250, which deviates in position from the backbone of TbAQP2 in this region. There is also a clash with Ile252. 

Although these observations are interesting, on their own they are preliminary in the extreme and extensive further work will be necessary to draw any convincing conclusions regarding these residues in preventing uptake of pentamidine and melarsoprol. The TbAQP3 AlphaFold model would need to be verified by MD simulations and then we would want to look at how pentamidine would interact with the channel under different experimental conditions like we have done with TbAQP2. We would then want to mutate to Ala each of the residues singly and in combination and assess them in uptake assays to verify data from the MD simulations. This is a whole new study and, given the uncertainties surrounding the observations of just superimposing TbAQP2 structure and the TbAQP3 model, we feel this is just too speculative to add to our manuscript. 

(8) To validate the densities representing glycerol and the compounds, you should show halfmap densities for these. 

A new figure, Fig S6 has been made to show the half-map densities for the glycerol and drugs.

(9) I would also like to see the density coverage of the individual helices/structural elements. 

A new figure, Fig S5 has been made to show the densities for the structural elements.

(10) While the LigPlot figure is nice, I think showing the data (including the cryo-EM density) is necessary validation.

The LigPlot figure is a diagram (an interpretation of data) and does not need the densities as these have already been shown in Fig. 1c (the data).

(11) I would recommend including a figure that illustrates the points described in lines 123-134.

All of the points raised in this section are already shown in Fig. 2a, which was referred to twice in this section. We have added another reference to Fig.2a on lines 134-135 for completeness.

(12) Line 202: I would suggest using "membrane potential/voltage" to avoid confusion with mitochondrial membrane potential. 

We have changed this to ‘plasma membrane potential’ to differentiate it from mitochondrial membrane potential.

(13) Figure 4: Label C.O.M. in the panels so that the figure corresponds to the legend. 

We have altered the figure and added and explanation in the figure legend (lines 716-717):

‘Cyan mesh shows the density of the molecule across the MD simulation. and the asterisk shows the position of the centre of mass (COM).’

(14) Figure S2: Panels d and e appear too similar, and it is difficult to see the stick representation of the compound. I would recommend either using different colours or showing a close-up of the site.

We have clarified the figure by including two close-up views of the hot-spot region, one with melarsoprol overlaid and one with pentamidine overlaid

(15) Figure S2: Typo in legend: 8YJ7 should be 8JY7.

Changed as suggested  

(16) Figure S3 and Figure S4: Please clarify which parts of the process were performed in cryoSPARC and which in Relion. 

Figure S3 gives an overview of the processing and has been simplified to give the overall picture of the procedures. All of the details were included in the Methods section as other programmes are used, not just cryoSPARC and Relion. Given the complexities of the processing, we have referred the readers to the Methods section rather than giving confusing information in Fig. S3.

We have updated the figure legend to Fig. S4 as requested.

(17) Figure S9 and Figure S10: The legends are swapped in these two figures.

The captions have been swapped to their proper positions.

(18) For ease of orientation and viewing, I would recommend showing a vertical HOLE plot aligned with an image of the AQP2 pore. 

The HOLE plot has been re-drawn as suggest (Fig. S2)

Author response:

We are very pleased to hear the overall positive views and constructive criticisms of eLife Editors and Reviewers on our work. In particular, we appreciate their global assessment that the work is important for understanding how body plan cues shape sensorimotor behavioural patterns, that the strength of evidence is solid, and their views that our experimental toolkit will be useful to others. We also very much appreciate eLife’s assessment that our findings will be of broad interest to researchers studying neural circuits, developmental genetics, and the evolution of behaviour.

Regarding Reviewer 1, we thank them for their positive comments on the value of our study, highlighting that our paper addresses an important question using an elegant and innovative combination of methods, which leads to clear insights into the sensory biology of self-righting, which they consider shall be useful for others in the field. We are also very pleased to hear that they consider that our study makes a substantial contribution to understanding how animals correct their body position and that the manuscript is very clearly written and couched in interesting biology. In a revised version of the manuscript, we will consider some of the interesting points raised by Rev1, including the possibility of conducting new experiments using neuronal subset-specific Gal4s, to establish whether daIV sensory neurons are also acting in a regionally specific manner along the A-P axis.

Turning to the comments by Rev2, we are grateful to them for considering that our experimental design is elegant, and that it introduces innovative methods that will likely benefit the fly behavior community, and the results are robustly supported. In connection to other comments, in a revised manuscript we will consider addressing the question of whether normal levels of expression of the Hox gene Antennapedia within the daIV domain are essential for self-righting. We will also seek to add technical replicates to our Hox expression molecular analysis, amend typos and incorporate several of the constructive corrections mentioned.

Author response:

Reviewer #1:

Indicated the paper provided a strong analysis of RNAseq databases to provide a biological context and resource for the massive amounts of data in the field on RNA editing. The reviewer noted that future studies will be important to define the functional consequences of the individual edits and why the RNA editing rules we identified exist. We address these comments below.

(1) The reviewer wondered about the role of noncanonical editing to neuronal protein expression.

Indeed, the role of noncanonical editing has been poorly studied compared to the more common A-to-I ADAR-dependent editing. Most non-canonical coding edits we found actually caused silent changes at the amino acid level, suggesting evolutionary selection against this mechanism as a pathway for generating protein diversity. As such, we suspect that most of these edits are not altering neuronal function in significant ways. Two potential exceptions to this were non-canonical edits that altered conserved residues in the synaptic proteins Arc1 and Frequenin 1. The C-to-T coding edit in the activity-regulated Arc1 mRNA that encodes a retroviral-like Gag protein involved in synaptic plasticity resulted in a P124L amino acid change (see Author response image 1 panel A below). ~50% of total Arc1 mRNA was edited at this site in both Ib and Is neurons, suggesting a potentially important role if the P124L change alters Arc1 structure or function. Given Arc1 assembles into higher order viral-like capsids, this change could alter capsid formation or structure. Indeed, P124 lies in the hinge region separating the N- and C-terminal capsid assembly regions (panel B) and we hypothesize this change will alter the ability of Arc1 capsids to assemble properly. We plan to experimentally test this by rescuing Arc1 null mutants with edited versus unedited transgenes to see how the previously reported synaptic phenotypes are modified. We also plan to examine the ability of the change to alter Arc1 capsid assembly in a collaboration using CyroEM.

Author response image 1.

A. AlphaFold predictions of Drosophila Arc1 and Frq1 with edit site noted. B. Structure of the Drosophila Arc1 capsid. Monomeric Arc1 conformation within the capsid is shown on the right with the location of the edit site indicated.

The other non-canonical edit (G-to-A) that stood out was in Frequenin 1 (Frq1), a multi-EF hand containing Ca²⁺ binding protein that regulates synaptic transmission, that resulted in a G2E amino acid substitution (location within Frq1shown in panel A above). This glycine residue is conserved in all Frq homologs and is the site of N-myristoylation, a co-translational lipid modification to the glycine after removal of the initiator methionine by an aminopeptidase. Myristoylation tethers Frq proteins to the plasma membrane, with a Ca²⁺-myristoyl switch allowing some family members to cycle on and off membranes when the lipid domain is sequestered in the absence of Ca²⁺. Although the G2E edit is found at lower levels (20% in Ib MNs and 18% in Is MNs), it could create a pool of soluble Frq1 that alters it’s signaling. We plan to functionally assay the significance of this non-canonical edit as well. Compared to edits that alter amino acid sequence, determining how non canonical editing of UTRs might regulate mRNA dynamics is a harder question at this stage and will require more experimental follow-up.

(2) The reviewer noted the last section of the results might be better split into multiple parts as it reads as a long combination of two thoughts.

We agree with the reviewer that the last section is important, but it was disconnected a bit from the main story and was difficult for us to know exactly where to put it. All the data to that point in the paper was collected from our own PatchSeq analysis from individual larval motoneurons. We wanted to compare these results to other large RNAseq datasets obtained from pooled neuronal populations and felt it was best to include this at the end of the results section, as it no longer related to the rules of RNA editing within single neurons. We used these datasets to confirm many of our edits, as well as find evidence for some developmental and neuron-specific cell type edits. We also took advantage of RNAseq from neuronal datasets with altered activity to explore how activity might alter the editing machinery. We felt it better to include that data in this final section given it was not collected from our original PatchSeq approach.

Reviewer #2:

Noted the study provided a unique opportunity to identify RNA editing sites and rates specific to individual motoneuron subtypes, highlighting the RNAseq data was robustly analyzed and high-confidence hits were identified and compared to other RNAseq datasets. The reviewer provided some suggestions for future experiments and requested a few clarifications.

(1) The reviewer asked about Figure 1F and the average editing rate per site described later in the paper.

Indeed, Figure 1F shows the average editing rate for each individual gene for all the Ib and Is cells, so we primarily use that to highlight the variability we find in overall editing rate from around 20% for some sites to 100% for others. The actual editing rate for each site for individual neurons is shown in Figure 4D that plots the rate for every edit site and the overall sum rate for that neuron in particular.

(2) The reviewer also noted that it was unclear where in the VNC the individual motoneurons were located and how that might affect editing.

The precise segment of the larvae for every individual neuron that was sampled by Patch-seq was recorded and that data is accessible in the original Jetti et al 2023 paper if the reader wants to explore any potential anterior to posterior differences in RNA editing. Due to the technical difficulty of the Patch-seq approach, we pooled all the Ib and Is neurons from each segment together to get more statistical power to identify edit sites. We don’t believe segmental identify would be a major regulator of RNA editing, but cannot rule it out.

(3) The reviewer also wondered if including RNAs located both in the nucleus and cytoplasm would influence editing rate.

Given our Patch-seq approach requires us to extract both the cytoplasm and nucleus, we would be sampling both nuclear and cytoplasmic mRNAs. However, as shown in Figure 8 – figure supplement 3 D-F, the vast majority of our edits are found in both polyA mRNA samples and nascent nuclear mRNA samples from other datasets, indicating the editing is occurring co-transcriptionally and within the nucleus. As such, we don't think the inclusion of cytoplasmic mRNA is altering our measured editing rates for most sites. This may not be true for all non-canonical edits, as we did see some differences there, indicating some non-canonical editing may be happening in the cytoplasm as well.

Reviewer #3:

indicated the work provided a valuable resource to access RNA editing in single neurons. The reviewer suggested the value of future experiments to demonstrate the effects of editing events on neuronal function. This will be a major effort for us going forwards, as we indeed have already begun to test the role of editing in mRNAs encoding several presynaptic proteins that regulate synaptic transmission. The reviewer also had several other comments as discussed below.

(1) The reviewer noted that silent mutations could alter codon usage that would result in translational stalling and altered protein production.

This is an excellent point, as silent mutations in the coding region could have a more significant impact if they generate non-preferred rare codons. This is not something we have analyzed, but it certainly is worth considering in future experiments. Our initial efforts are on testing the edits that cause predictive changes in presynaptic proteins based on the amino acid change and their locale in important functional domains, but it is worth considering the silent edits as well as we think about the larger picture of how RNA editing is likely to impact not only protein function but also protein levels.

(2) The reviewer noted future studies could be done using tools like Alphafold to test if the amino acid changes are predicted to alter the structure of proteins with coding edits.

This is an interesting approach, though we don’t have much expertise in protein modeling at that level. We could consider adding this to future studies in collaboration with other modeling labs.

(3) The reviewer wondered if the negative correlation between edits and transcript abundance could indicate edits might be destabilizing the transcripts.

This is an interesting idea, but would need to be experimentally tested. For the few edits we have generated already to begin functionally testing, including our published work with editing in the C-terminus of Complexin, we haven’t seen a change in mRNA levels causes by these edits. However, it would not be surprising to see some edits reducing transcript levels. A set of 5’UTR edits we have generated in Syx1A seem to be reducing protein production and may be acting in such a manner.

(4) The reviewer wondered if the proportion of edits we report in many of the figures is normalized to the length of the transcript, as longer transcripts might have more edits by chance.

The figures referenced by the reviewer (1, 2 and 7) show the number of high-confidence editing sites that fall into the 5’ UTR, 3’ UTR, or CDS categories. Our intention here was to highlight that the majority of the high confidence edits that made it through the stringent filtering process were in the coding region. This would still be true if we normalized to the length of the given gene region. However, it would be interesting to know if these proportions match the expected proportions of edits in these gene regions given a random editing rate per gene region length across the Drosophila genome, although we did not do this analysis.    

(5) The reviewer noted that future studies could expand on the work to examine miRNA or other known RBP binding sites that might be altered by the edits.

This is another avenue we could pursue in the future. We did do this analysis for a few of the important genes encoding presynaptic proteins (these are the most interesting to us given the lab’s interest in the synaptic vesicle fusion machinery), but did not find anything obvious for this smaller subset of targets.

(6) The reviewer suggested sequence context for Adar could also be investigated for the hits we identified.

We haven’t pursued this avenue yet, but it would be of interest to do in the future. In a similar vein, it would be informative to identify intron-exon base pairing that could generate the dsDNA template on which ADAR acts.

(7) The reviewer noted the disconnect between Adar mRNA levels and overall editing levels reported in Figure 4A/B.

Indeed, the lack of correlation between overall editing levels and Adar mRNA abundance has been noted previously in many studies. For the type of single cell Patch-seq approach we took to generate our RNAseq libraries, the absolute amount of less abundant transcripts obtained from a single neuron can be very noisy. As such, the few neurons with no detectable Adar mRNA are likely to represent that single neuron noise in the sampling. Per the reviewer’s question, these figure panels only show A-to-I edits, so they are specific to ADAR.

(8) The reviewer notes the scale in Figure 5D can make it hard to visualize the actual impact of the changes.

The intention of Figure 5D was to address the question of whether sites with high Ib/Is editing differences were simply due to higher Ib or Is mRNA expression levels. If this was the case, then we would expect to see highly edited sites have large Ib/Is TPM differences. Instead, as the figure shows, the vast majority of highly-edited sites were in mRNAs that were NOT significantly different between Ib and Is (red dots in graph) and are therefore clustered together near “0 Difference in TPMs”. TPMs and editing levels for all edit sites can be found in Table 1, and a visualization of these data for selected sites is shown in Figure 5E.

Author response:

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

Reviewer #1 (Public review):

In this manuscript, Hoon Cho et al. present a novel investigation into the role of PexRAP, an intermediary in ether lipid biosynthesis, in B cell function, particularly during the Germinal Center (GC) reaction. The authors profile lipid composition in activated B cells both in vitro and in vivo, revealing the significance of PexRAP. Using a combination of animal models and imaging mass spectrometry, they demonstrate that PexRAP is specifically required in B cells. They further establish that its activity is critical upon antigen encounter, shaping B cell survival during the GC reaction. Mechanistically, they show that ether lipid synthesis is necessary to modulate reactive oxygen species (ROS) levels and prevent membrane peroxidation.

Highlights of the Manuscript:

The authors perform exhaustive imaging mass spectrometry (IMS) analyses of B cells, including GC B cells, to explore ether lipid metabolism during the humoral response. This approach is particularly noteworthy given the challenge of limited cell availability in GC reactions, which often hampers metabolomic studies. IMS proves to be a valuable tool in overcoming this limitation, allowing detailed exploration of GC metabolism.

The data presented is highly relevant, especially in light of recent studies suggesting a pivotal role for lipid metabolism in GC B cells. While these studies primarily focus on mitochondrial function, this manuscript uniquely investigates peroxisomes, which are linked to mitochondria and contribute to fatty acid oxidation (FAO). By extending the study of lipid metabolism beyond mitochondria to include peroxisomes, the authors add a critical dimension to our understanding of B cell biology.

Additionally, the metabolic plasticity of B cells poses challenges for studying metabolism, as genetic deletions from the beginning of B cell development often result in compensatory adaptations. To address this, the authors employ an acute loss-of-function approach using two conditional, cell-type-specific gene inactivation mouse models: one targeting B cells after the establishment of a pre-immune B cell population (Dhrs7b^f/f, huCD20-CreERT2) and the other during the GC reaction (Dhrs7b^f/f; S1pr2-CreERT2). This strategy is elegant and well-suited to studying the role of metabolism in B cell activation.

Overall, this manuscript is a significant contribution to the field, providing robust evidence for the fundamental role of lipid metabolism during the GC reaction and unveiling a novel function for peroxisomes in B cells. 

Comments on revisions:

There are still some discrepancies in gating strategies. In Fig. 7B legend (lines 1082-1083), they show representative flow plots of GL7+ CD95+ GC B cells among viable B cells, so it is not clear if they are IgDneg, as the rest of the GC B cells aforementioned in the text.

We apologize for missing this item in need of correction in the revision and sincerely thank the reviewer for the stamina and care in picking this up. The data shown in Fig. 7B represented cells (events) in the IgD^neg Dump^neg viable lymphoid gate. We will correct this omission/blemish in the final revision that becomes the version of record.

Western blot confirmation: We understand the limitations the authors enumerate. Perhaps an RT-qPCR analysis of the Dhrs7b gene in sorted GC B cells from the S1PR2-CreERT2 model could be feasible, as it requires a smaller number of cells. In any case, we agree with the authors that the results obtained using the huCD20-CreERT2 model are consistent with those from the S1PR2-CreERT2 model, which adds credibility to the findings and supports the conclusion that GC B cells in the S1PR2-CreERT2 model are indeed deficient in PexRAP.

We will make efforts to go back through the manuscript and highlight this limitation to readers, i.e., that we were unable to get genetic evidence to assess what degree of "counter-selection" applied to GC B cells in our experiments.

We agree with the referee that optimally to support the Imaging Mass Spectrometry (IMS) data showing perturbations of various ether lipids within GC after depletion of PexRAP, it would have been best if we could have had a qRT2-PCR that allowed quantitation of the Dhrs7b-encoded mRNA in flow-purified GC B cells, or the extent to which the genomic DNA of these cells was in deleted rather than 'floxed' configuration.

While the short half-life of ether lipid species leads us to infer that the enzymatic function remains reduced/absent, it definitely is unsatisfying that the money for experiments ran out in June and the lab members had to move to new jobs.

Lines 222-226: We believe the correct figure is 4B, whereas the text refers to 4C.

As for the 1st item, we apologize and will correct this error.

Supplementary Figure 1 (line 1147): The figure title suggests that the data on T-cell numbers are from mice in a steady state. However, the legend indicates that the mice were immunized, which means the data are not from steady-state conditions. 

We will change the wording both on line 1147 and 1152.

Reviewer #2 (Public review):

Summary:

In this study, Cho et al. investigate the role of ether lipid biosynthesis in B cell biology, particularly focusing on GC B cell, by inducible deletion of PexRAP, an enzyme responsible for the synthesis of ether lipids.

Strengths:

Overall, the data are well-presented, the paper is well-written and provides valuable mechanistic insights into the importance of PexRAP enzyme in GC B cell proliferation.

Weaknesses:

More detailed mechanisms of the impaired GC B cell proliferation by PexRAP deficiency remain to be further investigated. In minor part, there are issues for the interpretation of the data which might cause confusions by readers.

Comments on revisions:

The authors improved the manuscript appropriately according to my comments.

To re-summarize, we very much appreciate the diligence of the referees and Editors in re-reviewing this work at each cycle and helping via constructive peer review, along with their favorable comments and overall assessments. The final points will be addressed with minor edits since there no longer is any money for further work and the lab people have moved on.

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

Reviewer #1 (Public review):

In this manuscript, Sung Hoon Cho et al. presents a novel investigation into the role of PexRAP, an intermediary in ether lipid biosynthesis, in B cell function, particularly during the Germinal Center (GC) reaction. The authors profile lipid composition in activated B cells both in vitro and in vivo, revealing the significance of PexRAP. Using a combination of animal models and imaging mass spectrometry, they demonstrate that PexRAP is specifically required in B cells. They further establish that its activity is critical upon antigen encounter, shaping B cell survival during the GC reaction. 

Mechanistically, they show that ether lipid synthesis is necessary to modulate reactive oxygen species (ROS) levels and prevent membrane peroxidation.

Highlights of the Manuscript:

The authors perform exhaustive imaging mass spectrometry (IMS) analyses of B cells, including GC B cells, to explore ether lipid metabolism during the humoral response. This approach is particularly noteworthy given the challenge of limited cell availability in GC reactions, which often hampers metabolomic studies. IMS proves to be a valuable tool in overcoming this limitation, allowing detailed exploration of GC metabolism.

The data presented is highly relevant, especially in light of recent studies suggesting a pivotal role for lipid metabolism in GC B cells. While these studies primarily focus on mitochondrial function, this manuscript uniquely investigates peroxisomes, which are linked to mitochondria and contribute to fatty acid oxidation (FAO). By extending the study of lipid metabolism beyond mitochondria to include peroxisomes, the authors add a critical dimension to our understanding of B cell biology.

Additionally, the metabolic plasticity of B cells poses challenges for studying metabolism, as genetic deletions from the beginning of B cell development often result in compensatory adaptations. To address this, the authors employ an acute loss-of-function approach using two conditional, cell-type-specific gene inactivation mouse models: one targeting B cells after the establishment of a pre-immune B cell population (Dhrs7b^f/f, huCD20-CreERT2) and the other during the GC reaction (Dhrs7b^f/f; S1pr2-CreERT2). This strategy is elegant and well-suited to studying the role of metabolism in B cell activation.

Overall, this manuscript is a significant contribution to the field, providing robust evidence for the fundamental role of lipid metabolism during the GC reaction and unveiling a novel function for peroxisomes in B cells.

We appreciate these positive reactions and response, and agree with the overview and summary of the paper's approaches and strengths.

However, several major points need to be addressed:

Major Comments:

Figures 1 and 2

The authors conclude, based on the results from these two figures, that PexRAP promotes the homeostatic maintenance and proliferation of B cells. In this section, the authors first use a tamoxifen-inducible full Dhrs7b knockout (KO) and afterwards Dhrs7bΔ/Δ-B model to specifically characterize the role of this molecule in B cells. They characterize the B and T cell compartments using flow cytometry (FACS) and examine the establishment of the GC reaction using FACS and immunofluorescence. They conclude that B cell numbers are reduced, and the GC reaction is defective upon stimulation, showing a reduction in the total percentage of GC cells, particularly in the light zone (LZ).

The analysis of the steady-state B cell compartment should also be improved. This includes a  more detailed characterization of MZ and B1 populations, given the role of lipid metabolism and lipid peroxidation in these subtypes.

Suggestions for Improvement:

B Cell compartment characterization: A deeper characterization of the B cell compartment in non-immunized mice is needed, including analysis of Marginal Zone (MZ) maturation and a more detailed examination of the B1 compartment. This is especially important given the role of specific lipid metabolism in these cell types. The phenotyping of the B cell compartment should also include an analysis of immunoglobulin levels on the membrane, considering the impact of lipids on membrane composition.

Although the manuscript is focused on post-ontogenic B cell regulation in Ab responses, we believe we will be able to polish a revised manuscript through addition of results of analyses suggested by this point in the review: measurement of surface IgM on and phenotyping of various B cell subsets, including MZB and B1 B cells, to extend the data in Supplemental Fig 1H and I. Depending on the level of support, new immunization experiments to score Tfh and analyze a few of their functional molecules as part of a B cell paper may be feasible.   

Addendum / update of Sept 2025: We added new data with more on MZB and B1 B cells, surface IgM, and on Tfh populations. 

GC Response Analysis Upon Immunization: The GC response characterization should include additional data on the T cell compartment, specifically the presence and function of Tfh cells. In Fig. 1H, the distribution of the LZ appears strikingly different. However, the authors have not addressed this in the text. A more thorough characterization of centroblasts and centrocytes using CXCR4 and CD86 markers is needed.

The gating strategy used to characterize GC cells (GL7+CD95+ in IgD− cells) is suboptimal. A more robust analysis of GC cells should be performed in total B220+CD138− cells.

We first want to apologize the mislabeling of LZ and DZ in Fig 1H. The greenish-yellow colored region (GL7⁺ CD35⁺) indicate the DZ and the cyan-colored region (GL7⁺ CD35⁺) indicates the LZ.    Addendum / update of Sept 2025: We corrected the mistake, and added new experimental data using the CD138 marker to exclude preplasmablasts.  

As a technical note, we experienced high background noise with GL7 staining uniquely with PexRAP deficient (Dhrs7b^f/f; Rosa26-CreER^T2) mice (i.e., not WT control mice). The high background noise of GL7 staining was not observed in B cell specific KO of PexRAP (Dhrs7b^f/f; huCD20-CreER^T2). Two formal possibilities to account for this staining issue would be if either the expression of the GL7 epitope were repressed by PexRAP or the proper positioning of GL7⁺ cells in germinal center region were defective in PexRAPdeficient mice (e.g., due to an effect on positioning cues from cell types other than B cells). In a revised manuscript, we will fix the labeling error and further discuss the GL7 issue, while taking care not to be thought to conclude that there is a positioning problem or derepression of GL7 (an activation antigen on T cells as well as B cells).

While the gating strategy for an overall population of GC B cells is fairly standard even in the current literature, the question about using CD138 staining to exclude early plasmablasts (i.e., analyze B220⁺ CD138^neg vs B220⁺ CD138⁺) is interesting. In addition, some papers like to use GL7⁺ CD38^neg for GC B cells instead of GL7⁺ Fas (CD95)⁺, and we thank the reviewer for suggesting the analysis of centroblasts and centrocytes. For the revision, we will try to secure resources to revisit the immunizations and analyze them for these other facets of GC B cells (including CXCR4/CD86) and for their GL7⁺ CD38^neg. B220⁺ CD138^- and B220⁺ CD138⁺ cell populations. 

We agree that comparison of the Rosa26-CreERT2 results to those with B cell-specific lossof-function raise a tantalizing possibility that Tfh cells also are influenced by PexRAP. Although the manuscript is focused on post-ontogenic B cell regulation in Ab responses, we hope to add a new immunization experiments that scores Tfh and analyzes a few of their functional molecules could be added to this B cell paper, depending on the ability to wheedle enough support / fiscal resources.  

Addendum / update of Sept 2025: Within the tight time until lab closure, and limited $$, we were able to do experiments that further reinforced the GC B cell data - including stains for DZ vs LZ sub-subsetting - and analyzed Tfh cells. We were not able to explore changes in functional antigenic markers on the GC B or Tfh cells. 

The authors claim that Dhrs7b supports the homeostatic maintenance of quiescent B cells in vivo and promotes effective proliferation. This conclusion is primarily based on experiments where CTV-labeled PexRAP-deficient B cells were adoptively transferred into μMT mice (Fig. 2D-F). However, we recommend reviewing the flow plots of CTV in Fig. 2E, as they appear out of scale. More importantly, the low recovery of PexRAP-deficient B cells post-adoptive transfer weakens the robustness of the results and is insufficient to conclusively support the role of PexRAP in B cell proliferation in vivo.

In the revision, we will edit the text and try to adjust the digitized cytometry data to allow more dynamic range to the right side of the upper panels in Fig. 2E, and otherwise to improve the presentation of the in vivo CTV result. However, we feel impelled to push back respectfully on some of the concern raised here. First, it seems to gloss over the presentation of multiple facets of evidence. The conclusion about maintenance derives primarily from Fig. 2C, which shows a rapid, statistically significant decrease in B cell numbers (extending the finding of Fig. 1D, a more substantial decrease after a bit longer a period). As noted in the text, the rate of de novo B cell production does not suffice to explain the magnitude of the decrease. 

In terms of proliferation, we will improve presentation of the Methods but the bottom line is that the recovery efficiency is not bad (comparing to prior published work) inasmuch as transferred B cells do not uniformly home to spleen. In a setting where BAFF is in ample supply in vivo, we transferred equal numbers of cells that were equally labeled with CTV and counted B cells. The CTV result might be affected by lower recovered B cell with PexRAP deficiency, generally, the frequencies of CTV^low divided population are not changed very much. However, it is precisely because of the pitfalls of in vivo analyses that we included complementary data with survival and proliferation in vitro. The proliferation was attenuated in PexRAP-deficient B cells in vitro; this evidence supports the conclusion that proliferation of PexRAP knockout B cells is reduced. It is likely that PexRAP deficient B cells also have defect in viability in vivo as we observed the reduced B cell number in PexRAP-deficient mice. As the reviewer noticed, the presence of a defect in cycling does, in the transfer experiments, limit the ability to interpret a lower yield of B cell population after adoptive transfer into µMT recipient mice as evidence pertaining to death rates. We will edit the text of the revision with these points in mind. 

In vitro stimulation experiments: These experiments need improvement. The authors have used anti-CD40 and BAFF for B cell stimulation; however, it would be beneficial to also include antiIgM in the stimulation cocktail. In Fig. 2G, CTV plots do not show clear defects in proliferation, yet the authors quantify the percentage of cells with more than three divisions. These plots should clearly display the gating strategy. Additionally, details about histogram normalization and potential defects in cell numbers are missing. A more in-depth analysis of apoptosis is also required to determine whether the observed defects are due to impaired proliferation or reduced survival. 

As suggested by reviewer, testing additional forms of B cell activation can help explore the generality (or lack thereof) of findings. We plan to test anti-IgM stimulation together with anti-CD40 + BAFF as well as anti-IgM + TLR7/8, and add the data to a revised and final manuscript. 

Addendum / update of Sept 2025: The revision includes results of new experiments in which anti-IgM was included in the stimulation cocktail, as well as further data on apoptosis and distinguishing impaired cycling / divisions from reduced survival .

With regards to Fig. 2G (and 2H), in the revised manuscript we will refine the presentation (add a demonstration of the gating, and explicate histogram normalization of FlowJo). 

It is an interesting issue in bioscience, but in our presentation 'representative data' really are pretty representative, so a senior author is reminded of a comment Tak Mak made about a reduction (of proliferation, if memory serves) to 0.7 x control. [His point in a comment to referees at a symposium related that to a salary reduction by 30% :) A mathematical alternative is to point out that across four rounds of division for WT cells, a reduction to  0.7x efficiency at each cycle means about 1/4 as many progeny.] 

We will try to edit the revision (Methods, Legends, Results, Discussion] to address better the points of the last two sentences of the comment, and improve the details that could assist in replication or comparisons (e.g., if someone develops a PexRAP inhibitor as potential therapeutic). 

For the present, please note that the cell numbers at the end of the cultures are currently shown in Fig 2, panel I. Analogous culture results are shown in Fig 8, panels I, J, albeit with harvesting at day 5 instead of day 4. So, a difference of ≥ 3x needs to be explained. As noted above, a division efficiency reduced to 0.7x normal might account for such a decrease, but in practice the data of Fig. 2I show that the number of PexRAP-deficient B cells at day 4 is similar to the number plated before activation, and yet there has been a reasonable amount of divisions. So cell numbers in the culture of mutant B cells are constant because cycling is active but decreased and insufficient to allow increased numbers ("proliferation" in the true sense) as programmed death is increased. In line with this evidence, Fig 8G-H document higher death rates [i.e., frequencies of cleaved caspase3⁺ cell and Annexin V⁺ cells] of PexRAP-deficient B cells compared to controls. Thus, the in vitro data lead to the conclusion that both decreased division rates and increased death operate after this form of stimulation. 

An inference is that this is the case in vivo as well - note that recoveries differed by ~3x (Fig. 2D), and the decrease in divisions (presentation of which will be improved) was meaningful but of lesser magnitude (Fig. 2E, F). 

Reviewer #2 (Public review):

Summary:

In this study, Cho et al. investigate the role of ether lipid biosynthesis in B cell biology, particularly focusing on GC B cell, by inducible deletion of PexRAP, an enzyme responsible for the synthesis of ether lipids.

Strengths:

Overall, the data are well-presented, the paper is well-written and provides valuable mechanistic insights into the importance of PexRAP enzyme in GC B cell proliferation.

We appreciate this positive response and agree with the overview and summary of the paper's approaches and strengths. 

Weaknesses:

More detailed mechanisms of the impaired GC B cell proliferation by PexRAP deficiency remain to be further investigated. In the minor part, there are issues with the interpretation of the data which might cause confusion for the readers.

Issues about contributions of cell cycling and divisions on the one hand, and susceptibility to death on the other, were discussed above, amplifying on the current manuscript text. The aggregate data support a model in which both processes are impacted for mature B cells in general, and mechanistically the evidence and work focus on the increased ROS and modes of death. Although the data in Fig. 7 do provide evidence that GC B cells themselves are affected, we agree that resource limitations had militated against developing further evidence about cycling specifically for GC B cells. We will hope to be able to obtain sufficient data from some specific analysis of proliferation in vivo (e.g., Ki67 or BrdU) as well as ROS and death ex vivo when harvesting new samples from mice immunized to analyze GC B cells for CXCR4/CD86, CD38, CD138 as indicated by Reviewer 1. As suggested by Reviewer 2, we will further discuss the possible mechanism(s) by which proliferation of PexRAP-deficient B cells is impaired. We also will edit the text of a revision where to enhance clarity of data interpretation - at a minimum, to be very clear that caution is warranted in assuming that GC B cells will exhibit the same mechanisms as cultures in vitro-stimulated B cells. 

Addendum / update of Sept 2025: We were able to obtain results of intravital BrdU incorporation into GC B cells to measure cell cycling rates. The revised manuscript includes these results as well as other new data on apoptosis / survival, while deleting the data about CD138 populations whose interpretation was reasonably questioned by the referees.  

Reviewer #1 (Recommendations for the authors):

We believe the evidence presented to support the role of PexRAP in protecting B cells from cell death and promoting B cell proliferation is not sufficiently robust and requires further validation in vivo. While the study demonstrates an increase in ether lipid content within the GC compartment, it also highlights a reduction in mature B cells in PexRAP-deficient mice under steady-state conditions. However, the IMS results (Fig. 3A) indicate that there are no significant differences in ether lipid content in the naïve B cell population. This discrepancy raises an intriguing point for discussion: why is PexRAP critical for B cell survival under steady-state conditions?

We thank the referee for all their care and input, and we agree that further intravital analyses could strengthen the work by providing more direct evidence of impairment of GC B cells in vivo. To revise and improve this manuscript before creation of a contribution of record, we performed new experiments to the limit of available funds and have both (i) added these new data and (ii) sharpened the presentation to correct what we believe to be one inaccurate point raised in the review. 

(A) Specifically, we immunized mice with a B cell-specific depletion of PexRAP (Dhrs7b^D/D-B mice) and measured a variety of readouts of the GC B cells' physiology in vivo: proliferation by intravital incorporation of BrdU, ROS in the viable GC B cell gate, and their cell death by annexin V staining directly ex vivo. Consistent with the data with in vitro activated B cells, these analyses showed increased ROS (new - Fig. 7D) and higher frequencies of Annexin V⁺ 7AAD⁺ in GC B cells (GL7⁺ CD38^- B cell-gate) of immunized Dhrs7b^D/D-B mice compared with WT controls (huCD20-CreERT2^+/-, Dhrs7b^+/+)  (new - Fig. 7E). Collectively, these results indicate that PexRAP aids (directly or indirectly) in controlling ROS in GC B cells and reduces B cell death, likely contributing to the substantially decreased overall GC B cell population. These new data are added to the revised manuscript in Figure 7.  

Moreover, in each of two independent experiments (each comprising 3 vs 3 immunized mice), BrdU⁺ events among GL7⁺ CD38^- (GC B cell)-gated cells were reduced in the B cell-specific PexRAP knockouts compared with WT controls (new, Fig. 7F and Supplemental Fig 6E). This result on cell cycle rates in vivo is presented with caution in the revised manuscript text because the absolute labeling fractions were somewhat different in Expt 1 vs Expt 2. This situation affords a useful opportunity to comment on the culture of "P values" and statistical methods. It is intriguing to consider how many successful drugs are based on research published back when the standard was to interpret a result of this sort more definitively despite a merged "P value" that was not a full 2 SD different from the mean. In the optimistic spirit of the eLife model, it can be for the attentive reader to decide from the data (new, Fig. 7F and Supplemental Fig 6E) whether to interpret the BrdU results more strongly that what we state in the revised text.  

(B) On the issue of whether or not the loss of PexRAP led to perturbations of the lipidome of B cells prior to activation, we have edited the manuscript to do a better job making this point more clear.  

We point out to readers that in the resting, pre-activation state abnormalities were detected in naive B cells, not just in activated and GC B cells. In brief, the IMS analysis and LC-MS-MS analysis detected statistically significant differences in some, but not all, the ether phospholipids species in PexRAP deficient cells (some of which was in Supplemental Figure 2 of the original version). 

With this appropriate and helpful concern having been raised, we realize that this important point merited inclusion in the main figures. We point specifically to a set of phosphatidyl choline ions shown in Fig. 3 (revised - panels A, B, D) of the revised manuscript (PC O-36:5; PC O-38:5; PC O-40:6 and -40:7). 

For this ancillary record (because a discourse on the limitations of each analysis), we will note issues such as the presence of many non-B cells in each pixel of the IMS analyses (so that some or many "true positives" will fail to achieve a "significant difference") and for the naive B cells, differential rates of synthesis, turnover, and conversion (e.g., addition of another 2-carbon unit or saturation / desaturation of one side-chain). To the extent the concern reflects some surprise and perhaps skepticism that what seem relatively limited differences (many species appear unaffected, etc), we share in the sentiment. But the basic observation is that there are differences, and a reasonable connection between the altered lipid profile and evidence of effects on survival or proliferation (i.e., integration of survival and cell cycling / division). 

Additionally, it would be valuable to evaluate the humoral response in a T-independent setting. This would clarify whether the role of PexRAP is restricted to GC B cells or extends to activated B cells in general. 

We agree that this additional set of experiments would be nice and would extend work incrementally by testing the generality of the findings about Ab responses. The practical problem is that money and time ran out while testing important items that strengthen the evidence about GC B cells. 

Finally, the manuscript would benefit from a thorough revision to improve its readability and clarity. Including more detailed descriptions of technical aspects, such as the specific stimuli and time points used in analyses, would greatly enhance the flow and comprehension of the study. Furthermore, the authors should review figure labeling to ensure consistency throughout the manuscript, and carefully cite the relevant references. For instance, S1PR2 CreERT2 mouse is established by Okada and Kurosaki (Shinnakasu et al ,Nat. Immunol, 2016)

We appreciate this feedback and comment, inasmuch as both the clarity and scholarship matter greatly to us for a final item of record. For the revision, we have given our best shot to editing the text in the hopes of improved clarity, reduction of discrepancies (helpfully noted in the Minor Comments), and further detail-rich descriptions of procedures. We also edited the figure labeling to give a better consistency. While we note that the appropriate citation of Shinnakasu et al (2016) was ref. #69 of the original and remains as a citation, we have rechecked other referencing and try to use citations with the best relevant references.  

Minor Comments: The labeling of plots in Fig. 2 should be standardized. For example, in Fig. 2C, D, and G, the same mouse strain is used, yet the Cre+ mouse is labeled differently in each plot. 

We agree and have tried to tighten up these features in the panels noted as well as more generally (e.g., Fig. 4, 5, 6, 7, 9; consistency of huCD20-CreERT2 / hCD20CreERT2).

According to the text, the results shown in Fig. 1G and H correspond to a full KO  (Dhrs7b^f/f; Rosa26-CreERT2 mice). However, Fig. 1H indicates that the bottom image corresponds to Dhrs7b^f/f, huCD20-CreERT2 mice (Dhrs7bΔ/Δ -B). 

We have corrected Fig. 1H to be labeled as Dhrs7b^Δ/Δ (with the data on Dhrs7b^Δ/Δ-B presented in Supplemental Figure 4A, which is correctly labeled). Thank you for picking up this error that crept in while using copy/paste in preparation of figure panels and failing to edit out the "-B"!  

Similarly, the gating strategy for GC cells in the text mentions IgD− cells, while the figure legend refers to total viable B cells. These discrepancies need clarification.

We believe we located and have corrected this issue in the revised manuscript.   

Figures 3 and 4. The authors claim that B cell expression of PexRAP is required to  achieve normal concentrations of ether phospholipids. 

Suggestions for Improvement: 

Lipid Metabolism Analysis: The analysis in Fig. 3 is generally convincing but could be strengthened by including an additional stimulation condition such as anti-IgM plus antiCD40. In Fig. 4C, the authors display results from the full KO model. It would be helpful to include quantitative graphs summarizing the parameters displayed in the images.

We have performed new experiments (anti-IgM + anti-CD40) and added the data to the revised manuscript (new - Supplemental Fig. 2H and Supplemental Fig 6, D & F). Conclusions based on the effects are not changed from the original. 

As a semantic comment and point of scientific process, any interpretation ("claim") can - by definition - only be taken to apply to the conditions of the experiment. Nonetheless, it is inescapable that at least for some ether P-lipids of naive, resting B cells, and for substantially more in B cells activated under the conditions that we outline, B cell expression of PexRAP is required. 

With regards to the constructive suggestion about a new series of lipidomic analyses, we agree that for activated B cells it would be nice and increase insight into the spectrum of conditions under which the PexRAP-deficient B cells had altered content of ether phospholipids. However, in light of the costs of metabolomic analyses and the lack of funds to support further experiments, and the accuracy of the point as stated, we prioritized the experiments that could fit within the severely limited budget. 

[One can add that our results provide a premise for later work to analyze a time course after activation, and to perform isotopomer (SIRM) analyses with [13] C-labeled acetate or glucose, so as to understand activation-induced increases in the overall   To revise the manuscript, we did however extrapolate from the point about adding BCR cross-linking to anti-CD40 as a variant form of activating the B cells for measurements of ROS, population growth, and rates of division (CTV partitioning). The results of these analyses, which align with and thereby strengthen the conclusions about these functional features from experiments with anti-CD40 but no anti-IgM, are added to Supplemental Fig 2H and Supplemental Fig 6D, F. 

Figures 5, 6, and 7

The authors claim that Dhrs7b in B cells shapes antibody affinity and quantity. They use two mouse models for this analysis: huCD20-CreERT2 and Dhrs7b f/f; S1pr2-CreERT2 mice. 

Suggestions for Improvement:

Adaptive immune response characterization: A more comprehensive characterization of the adaptive immune response is needed, ideally using the Dhrs7b f/f; S1pr2-CreERT2 model. This should include: Analysis of the GC response in B220+CD138− cells. Class switch recombination analysis. A detailed characterization of centroblasts, centrocytes, and Tfh populations. Characterization of effector cells (plasma cells and memory cells).

Within the limits of time and money, we have performed new experiments prompted by this constructive set of suggestions. 

Specifically, we analyzed the suggested read-outs in the huCD20-CreERT2, Dhrs7b^f/f model after immunization, recognizing that it trades greater signal-noise for the fact that effects are due to a mix of the impact on B cells during clonal expansion before GC recruitment and activities within the GC. In brief, the results showed that 

(a) the GC B cell population - defined as CD138^neg GL7⁺ CD38^lo/neg IgD^neg B cells - was about half as large for PexRAP-deficient B cells net of any early- or preplasmablasts (CD138⁺ events) (new - Fig 5G); 

(b) the frequencies of pre- / early plasmablasts (CD138⁺ GL7⁺ CD38^neg) events (see new - Fig. 6H, I; also, new Supplemental Fig 5D) were so low as to make it unlikely that our data with the S1pr2-CreERT2 model (in Fig 7B, C) would be affected meaningfully by analysis of the CD138 levels;

(c) There was a modest decrease in centrocytes (LZ) but not centroblasts (DZ) (new - Fig 5H, I) - consistent with the immunohistochemical data of Supplemental Fig. 5A-C). 

Because of time limitations (the "shelf life" of funds and the lab) and insufficient stock of the S1pr2-CreERT2, Dhrs7b^f/f mice as well as those that would be needed as adoptive transfer recipients because of S1PR2 expression in (GC-)Tfh, the experiments were performed instead with the huCD20-CreERT2, Dhrs7b^f/f model. We would also note that using this Cre transgene better harmonizes the centrocyte/centroblast and Tfh data with the existing data on these points in Supplemental Fig. 4. 

(d) Of note, the analyses of Tfh and GC-Tfh phenotype cells using the huCD20-CreERT2 B cell type-specific inducible Cre system to inactivate Dhrs7b (new - Supplemental Fig 1G-I; which, along with new - Supplemental Fig 5E) provide evidence of an abnormality that must stem from a function or functions of PexRAP in B cells, most likely GC B cells. Specifically, it is known that the GC-Tfh population proliferates and is supported by the GC B cells, and the results of B cell-specific deletion show substantial reductions in Tfh cells (both the GC-Tfh gating and the wider gate for plots of CXCR5/PD-1/ fluorescence of CD4 T cells 

Timepoint Consistency: The NP response (Fig. 5) is analyzed four weeks postimmunization, whereas SRBC (Supp. Fig. 4) and Fig. 7 are analyzed one week or nine days post-immunization. The NP system analysis should be repeated at shorter timepoints to match the peak GC reaction.

This comment may stem from a misunderstanding. As diagrammed in Fig. 5A, the experiments involving the NP system were in fact measured at 7 d after a secondary (booster) immunization. That timing is approximately the peak period and harmonizes with the 7 d used for harvesting SRBC-immunized mice. So in fact the data with each system were obtained at a similar time point. Of course the NP experiments involved a second immunization so that many plasma cell and Ab responses derived from memory B cells generated by the primary immunization. However, the field at present is dominated by the view that the vast majority of the GC B cells after this second immunization (which historically we perform with alum adjuvant) are recruited from the naive rather than the memory B cell pool. For the revised manuscript, we have taken care that the Methods, Legend, and Figure provide the information to readers, and expanded the statement of a rationale. 

It may seem a technicality but under NIH regulations we are legally obligated to try to minimize mouse usage. It also behooves researchers to use funds wisely. In line with those imperatives, we used systems that would simultaneously allow analyses of GC B cells, identification of affinity maturation (which is minimal in our hands at a 7 d time point after primary NP-carrier immunization), and a switched repertoire (also minimal), and where with each immunogen the GC were scored at 7-9 d after immunization (9 d refers to the S1pr2-CreERT2 experiments). Apart from the end of funding, we feel that what little might be learned from performing a series of experiments that involve harvests 7 d after a primary immunization with NP-ovalbumin cannot well be justified. 

In vitro plasma cell differentiation: Quantification is missing for plasma cell differentiation in vitro (Supp. Fig. 4). The stimulus used should also be specified in the figure legend. Given the use of anti-CD40, differentiation towards IgG1 plasma cells could provide additional insights.

As suggested by reviewer, we have added the results of quantifying the in vitro plasma cell differentiation in Supplemental Fig 6B. Also, we edited the Methods and Supplemental Figure Legend to give detailed information of in vitro stimulation. 

Proliferation and apoptosis analysis: The observed defects in the humoral response should be correlated with proliferation and apoptosis analyses, including Ki67 and Caspase markers.

As suggested by the review, we have performed new experiment and analyzed the frequencies of cell death by annexin V staining, and elected to use intravital uptake of BrdU as a more direct measurement of S phase / cell cycling component of net proliferation. The new results are now displayed in Figure 5 and Supplemental Fig. 5. 

Western blot confirmation: While the authors have demonstrated the absence of PexRAP protein in the huCD20-CreERT2 model, this has not been shown in GC B cells from the Dhrs7b f/f; S1pr2-CreERT2 model. This confirmation is necessary to validate the efficiency of Dhrs7b deletion.

We were unable to do this for technical reasons expanded on below. For the revision, we have edited in a bit of text more explicitly to alert readers to the potential impact of counter-selection on interpretation of the findings with GC B cells. Before entering the GC, B cells have undergone many divisions, so if there were major pre-GC counterselection, in all likelihood the GC B cells would PexRAP-sufficient. To recap from the original manuscript and the new data we have added, IMS shows altered lipid profiles in the GC B cells and the literature indicates that the lipids are short-lived, requiring de novo resynthesis. The BrdU, ROS, and annexin V data show that GC B cells are abnormal. Accordingly, abnormal GC B cells represent the parsimonious or straightforward interpretation of the new results with GC-Tfh cell prevalence. 

While we take these findings together to suggest that counterselection (i.e., a Western result showing normal levels of PexRAP in the GC B cells) seems unlikely, it is formally possible and would mean that the in situ defects of GC B cells arose due to environmental influences of the PexRAP-deficient B cells during the developmental history of the WT B cells observed in the GC. 

Having noted all that, we understand that concerns about counter-selection are an issue if a reader accepts the data showing that mutant (PexRAP-deficient) B cells tend to proliferate less and die more readily. Indeed, one can speculate that were we also to perform competition experiments in which the Ighb, Cd45.2 B cells (WT or Dhrs7b D/D) are mixed with equal numbers of Igha, Cd45.1 competitors, the differences would become much greater. With this in mind, Western blotting of flow-purified GC B cells might give a sense of how much counter-selection has occurred. 

That said, the Westerns need at least 2.5 x 10⁶ B cells (those in the manuscript used five million, 5  x 10⁶) and would need replication. Taken together with the observation that ~200,000 GC B cells (on average) were measured in each B cell-specific knockout mouse after immunization (Fig. 1, Fig 5) and taking into account yields from sorting, each Western would require some 20-25 tamoxifen-injected ___-CreERT2, Dhrs7b f/f mice, and about half again that number as controls. The expiry of funds prohibited the time and costs of generating that many mice (>70) and flow-purified GC B cells. 

Figure 8

The authors claim that Dhrs7b contributes to the modulation of ROS, impacting B cell proliferation.

Suggestions for Improvement:

GC ROS Analysis: The in vitro ROS analysis should be complemented by characterizing ROS and lipid peroxidation in the GC response using the Dhrs7b f/f; S1pr2-CreERT2 model. Flow cytometry staining with H2DCFDA, MitoSOX, Caspase-3, and Annexin V would allow assessment of ROS levels and cell death in GC B cells. 

While subject to some of the same practical limits noted above, we have performed new experiments in line with this helpful input of the reviewer, and added the helpful new data to the revised manuscript. Specifically, in addition to the BrdU and phenotyping analyses after immunization of huCD20-CreER^T2, Dhrs7b^f/f mice, DCFDA (ROS), MitoSox, and annexin V signals were measured for GC B cells. Although the mitoSox signals did not significantly differ for PexRAP-deficient GCB, the ROS and annexin V signals were substantially increased. We added the new data to Figure 5 and Supplemental Figure 5. Together with the decreased in vivo BrdU incorporation in GC B cells from Dhrs7b^D/D-B mice, these results are consistent with and support our hypothesis that PexRAP regulates B cell population growth and GC physiology in part by regulating ROS detoxification, survival and proliferation of B cells.  

Quantification is missing in Fig. 8E, and Fig. 8F should use clearer symbols for better readability. 

We added quantification for Fig 8E in Supplemental Fig 6E, and edited the symbols in Fig 8F for better readability.

Figure 9

The authors claim that Dhrs7b in B cells affects oxidative metabolism and ER mass. The  results in this section are well-performed and convincing.

Suggestion for Improvement:

Based on the results, the discussion should elaborate on the potential role of lipids in antigen presentation, considering their impact on mitochondria and ER function.

We very much appreciate the praise of the tantalizing findings about oxidative metabolism and ER mass, and will accept the encouragement that we add (prudently) to the Discussion section to make note of the points mentioned by the Reviewer, particularly now that (with their encouragement) we have the evidence that B cell-specific loss of PexRAP (with the huCD20-CreERT2 deletion prior to immunization) resulted in decreased (GC-)Tfh and somewhat lower GC B cell proliferation.  

Reviewer #2 (Recommendations for the authors):

The authors should investigate whether PexRAP-deficient GC B cells exhibit increased mitochondrial ROS and cell death ex vivo, as observed in in vitro cultured B cells.

We very much appreciate the work of the referee and their input. We addressed this helpful recommendation, in essence aligned with points from Reviewer 1, via new experiments (until the money ran out) and addition of data to the manuscript. To recap briefly, we found increased ROS in GC B cells along with higher fractions of annexin V positive cells; intriguingly, increased mtROS (MitoSox signal) was not detected, which contrasts with the results in activated B cells in vitro in a small way. To keep the text focused and not stray too far outside the foundation supported by data, this point may align with papers that provide evidence of differences between pre-GC and GC B cells (for instance with lack of Tfam or LDHA in B cells).    

It remains unclear whether the impaired proliferation of PexRAP-deficient B cells is primarily due to increased cell death. Although NAC treatment partially rescued the phenotype of reduced PexRAP-deficient B cell number, it did not restore them to control levels. Analysis of the proliferation capacity of PexRAP-deficient B cells following NAC treatment could provide more insight into the cause of impaired proliferation.

To add to the data permitting an assessment of this issue, we performed new experiments in which B cells were activated (BCR and CD40 cross-linking), cultured, and both the change in population and the CTV partitioning were measured in the presence or absence of NAC. The results, added to the revision as Supplemental Fig 6FH, show that although NAC improved cell numbers for PexRAP-deficient cells relative to controls, this compound did not increase divisions at all. We infer that the more powerful effect of this lipid synthesis enzyme is to promote survival rather than division  capacity. 

Primary antibody responses were assessed at only one time point (day 20). It would be valuable to examine the kinetics of antibody response at multiple time points (0, 1w, 2w, 3w, for example) to better understand the temporal impact of PexRAP on antibody production.

We thank the reviewer for this suggestion. While it may be that the kinetic measurement of Ag-specific antibody level across multiple time points would provide an additional mechanistic clue into the of impact PexRAP on antibody production, the end of sponsored funding and imminent lab closure precluded performing such experiments.   

CD138+ cell population includes both GC-experienced and GC-independent plasma cells (Fig. 7). Enumeration of plasmablasts, which likely consists of both PexRAP-deleted and undeleted cells (Fig. 7D and E), may mislead the readers such that PexRAP is dispensable for plasmablast generation. I would suggest removing these data and instead examining the number of plasmablasts in the experimental setting of Fig. 4A (huCD20-CreERT2-mediated deletion) to address whether PexRAP-deficiency affects plasmablast generation. 

We have eliminated the figure panels in question, since it is accurate that in the absence of a time-stamping or marking approach we have a limited ability to distinguish plasma cells that arose prior to inactivation of the Dhrs7b gene in B cells. In addition, we performed new experiments that were used to analyze the "early plasmablast" phenotype and added those data to the revision (Supplemental Fig 5D).

Author response:

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

Reviewer #1 (Public review): 

Summary:

The authors use the theory of planned behavior to understand whether or not intentions to use sex as a biological variable (SABV), as well as attitude (value), subjective norm (social pressure), and behavioral control (ability to conduct behavior), across scientists at a pharmacological conference. They also used an intervention (workshop) to determine the value of this workshop in changing perceptions and misconceptions. Attempts to understand the knowledge gaps were made.

Strengths:

The use of SABV is limited in terms of researchers using sex in the analysis as a variable of interest in the models (and not a variable to control). To understand how we can improve on the number of researchers examining the data with sex in the analyses, it is vital we understand the pressure points that researchers consider in their work. The authors identify likely culprits in their analyses. The authors also test an intervention (workshop) to address the main bias or impediments for researchers' use of sex in their analyses. 

Weaknesses:

There are a number of assumptions the authors make that could be revisited: 

(1) that all studies should contain across sex analyses or investigations. It is important to acknowledge that part of the impetus for SABV is to gain more scientific knowledge on females. This will require within sex analyses and dedicated research to uncover how unique characteristics for females can influence physiology and health outcomes. This will only be achieved with the use of female-only studies. The overemphasis on investigations of sex influences limits the work done for women's health, for example, as within-sex analyses are equally important.

The Sex and Gender Equity in Research (SAGER) guidelines (1) provide guidance that “Where the subjects of research comprise organisms capable of differentiation by sex, the research should be designed and conducted in a way that can reveal sex-related differences in the results, even if these were not initially expected.”.  This is a default position of inclusion where the sex can be determined and analysis assessing for sex related variability in response. This position underpins many of the funding bodies new policies on inclusion.   

However, we need to place this in the context of the driver of inclusion. The most common reason for including male and female samples is for those studies that are exploring the effect of a treatment and then the goal of inclusion is to assess the generalisability of the treatment effect (exploratory sex inclusion)(2). The second scenario is where sex is included because sex is one of the variables of interest and this situation will arise because there is a hypothesized sex difference of interest (confirmatory sex inclusion).  

We would argue that the SABV concept was introduced to address the systematic bias of only studying one sex when assessing treatment effect to improve the generalisability of the research.  Therefore, it isn’t directly to gain more scientific knowledge on females.  However, this strategy will highlight when the effect is very different between male and female subjects which will potentially generate sex specific hypotheses.  

Where research has a hypothesis that is specific to a sex (e.g. it is related to oestrogen levels) it would be appropriate to study only the sex of interest, in this case females. The recently published Sex Inclusive Research Framework gives some guidance here and allows an exemption for such a scenario classifying such proposals “Single sex study justified” (3).

We have added an additional paragraph to the introduction to clarify the objectives behind inclusion and how this assists the research process. 

(2) It should be acknowledged that although the variability within each sex is not different on a number of characteristics (as indicated by meta-analyses in rats and mice), this was not done on all variables, and behavioral variables were not included. In addition, across-sex variability may very well be different, which, in turn, would result in statistical sex significance. In addition, on some measures, there are sex differences in variability, as human males have more variability in grey matter volume than females. PMID: 33044802. 

The manuscript was highlighting the common argument used to exclude the use of females, which is that females are inherently more variable as an absolute truth. We agree there might be situations, where the variance is higher in one sex or another depending on the biology.  We have extended the discussion here to reflect this, and we also linked to the Sex Inclusive Research Framework (3) which highlights that in these situations researchers can utlise this argument provided it is supported with data for the biology of interest. 

(3) The authors need to acknowledge that it can be important that the sample size is increased when examining more than one sex. If the sample size is too low for biological research, it will not be possible to determine whether or not a difference exists. Using statistical modelling, researchers have found that depending on the effect size, the sample size does need to increase. It is important to bare this in mind as exploratory analyses with small sample size will be extremely limiting and may also discourage further study in this area (or indeed as seen the literature - an exploratory first study with the use of males and females with limited sample size, only to show there is no "significance" and to justify this as an reason to only use males for the further studies in the work. 

The reviewer raises a common problem: where researchers have frequently argued that if they find no sex differences in a pilot then they can proceed to study only one sex. The SAGER guidelines (1), and now funder guidelines (4, 5), challenge that position. Instead, the expectation is for inclusion as the default in all experiments (exploratory inclusion strategy) to allow generalisable results to be obtained. When the results are very different between the male and female samples, then this can be determined. This perspective shift (2) requires a change in mindset and understanding that the driver behind inclusion is of generalisability not exploration of sex differences. This has been added to the introduction as an additional paragraph exploring the drivers behind inclusion.  

We agree with the reviewer that if the researcher is interested in sex differences in an effect (confirmatory inclusion strategy, aka sex as a primary variable) then the N will need to be higher.  However, in this situation, one, of course, must have male and female samples in the same experiment to allow the simultaneous exploration to assess the dependency on sex. 

Reviewer #2 (Public review): 

Summary:

The investigators tested a workshop intervention to improve knowledge and decrease misconceptions about sex inclusive research. There were important findings that demonstrate the difficulty in changing opinions and knowledge about the importance of studying both males and females. While interventions can improve knowledge and decrease perceived barriers, the impact was small. 

Strengths:

The investigators included control groups and replicated the study in a second population of scientists. The results appear to be well substantiated. These are valuable findings that have practical implications for fields where sex is included as a biological variable to improve rigor and reproducibility. 

Thank you for assessment and highlighting these strengths.  We appreciate your recognition of the value and practical implications of this work. 

Weaknesses:

I found the figures difficult to understand and would have appreciated more explanation of what is depicted, as well as greater space between the bars representing different categories. 

We have improved the figures and figure legends to improve clarity. 

Reviewer #3 (Public review):

Summary:

This manuscript aims to determine cultural biases and misconceptions in inclusive sex research and evaluate the efficacy of interventions to improve knowledge and shift perceptions to decrease perceived barriers for including both sexes in basic research. 

Overall, this study demonstrates that despite the intention to include both sexes and a general belief in the importance of doing so, relatively few people routinely include both sexes. Further, the perceptions of barriers to doing so are high, including misconceptions surrounding sample size, disaggregation, and variability of females. There was also a substantial number of individuals without the statistical knowledge to appropriately analyze data in studies inclusive of sex. Interventions increased knowledge and decreased perception of barriers. 

Strengths:

(1) This manuscript provides evidence for the efficacy of interventions for changing attitudes and perceptions of research.

(2) This manuscript also provides a training manual for expanding this intervention to broader groups of researchers.

Thank you for highlighting these strengths. We appreciate your recognition that the intervention was effect in changing attitudes and perception. We deliberately chose to share the material to provide the resources to allow a wider engagement.  

Weaknesses:

The major weakness here is that the post-workshop assessment is a single time point, soon after the intervention. As this paper shows, intention for these individuals is already high, so does decreasing perception of barriers and increasing knowledge change behavior, and increase the number of studies that include both sexes? Similarly, does the intervention start to shift cultural factors? Do these contribute to a change in behavior? 

Measuring change in behaviour following an intervention is challenging and hence we had implemented an intention score as a proxy for behaviour. We appreciate the benefit of a long-term analysis, but it was beyond the scope of this study and would need a larger dataset size to allow for attrition. We agree that the strategy implemented has weaknesses. We have extended the limitation section in the discussion to include these. 

Reviewer #1 (Recommendations for the authors):  

I would ask them to think about alternative explanations and ask for free-form responses, and to revise with the caveats written above - sample size does need to be increased depending on effect size, and that within sex studies are also important. Not all studies should focus on sex influences.  

The inclusion of the additional paragraph in the introduction to clarify the objective of inclusion and the resulting impact on experimental design should address these recommendations.   

We have also added the free-form responses as an additional supplementary file.  

Reviewer #2 (Recommendations for the authors):  

This is an important set of studies. My only recommendation to improve the data presentation so that it is clear what is depicted and how the analyses were conducted. I know it is in the methods, but reminding the reader would be helpful.  

We have revisited the figures and included more information in the legends to explain the analysis and improve clarity.   

Reviewer #3 (Recommendations for the authors):  

There are parts in the introduction which read as contradictory and as such are confusing - for example, in the 3rd paragraph it states that little progress on sex inclusive research has been made, and in the following sentences it states that the proportion of published studies across sex has improved. The references in these two statements are from the same time range, so has this improved? Or not?  

The introduction does include a summation statement on the position: “Whilst a positive step forward, this proportion still represents a minority of studies, and notably this inclusion was not associated with an increase in the proportion of studies that included data analysed by sex.” We have reworded the text to ensure it is internally consistent with this summary statement and this should increase clarity.

In discussing the results, it is sometimes confusing what the percentages mean. For example, "the researchers reported only conducting sex inclusive research in <=55% of their studies over the past 5 years (55% in study 1 general population and 35% study 2 pre-assessment)." Does that mean 55% of people are conducting sex inclusive research, or does this mean only half of their studies? These two options have very different implications.

We agree that the sentence is confusing and it has been reworded.  

Addressing long-term assessments in attitude and action (ie, performing sex inclusive research) is a crucial addition, with data if possible, but at least substantive discussion.  

We have add this to the limitation section in the discussion

One minor but confusing point is the analogy comparing sex inclusive studies with attending the gym. The point is well taken - knowledge is not enough for behavior change. However, the argument here is that to increase sex inclusive research requires cultural change. To go to the gym, requires motivation.This seems like an oranges-to-lemons comparison (same family, different outcome when you bite into it).

At the core, both scenarios involve the challenge of changing established habits and cultural norms in action based on knowledge (the right thing to do). The exercise scenario is a primary example provided by the original authors to describe how aspects of the theory of planned behaviour (perceived behavioural control, attitude, and social norms) may influence behavioural change. Understanding which of these aspects may drive or influence change is why we used this framework to understand our study population.  We disagree that is an oranges-to-lemons comparison.

References

(1) Heidari S, Babor TF, De Castro P, Tort S, Curno M. Sex and Gender Equity in Research: rationale for the SAGER guidelines and recommended use. Res Integr Peer Rev. 2016;1:2.

(2) Karp NA. Navigating the paradigm shift of sex inclusive preclinical research and lessons learnt. Commun Biol. 2025;8(1):681.

(3) Karp NA, Berdoy M, Gray K, Hunt L, Jennings M, Kerton A, et al. The Sex Inclusive Research Framework to address sex bias in preclinical research proposals. Nat Commun. 2025;16(1):3763.

(4) MRC. Sex in experimental design - Guidance on new requirements https://www.ukri.org/councils/mrc/guidance-for-applicants/policies-and-guidance-forresearchers/sex-in-experimental-design/: UK Research and Innovation; 2022 [

(5) Clayton JA, Collins FS. Policy: NIH to balance sex in cell and animal studies. Nature. 2014;509(7500):282-3.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

Asthenospermia, characterized by reduced sperm motility, is one of the major causes of male infertility. The "9 + 2" arranged MTs and over 200 associated proteins constitute the axoneme, the molecular machine for flagellar and ciliary motility. Understanding the physiological functions of axonemal proteins, particularly their links to male infertility, could help uncover the genetic causes of asthenospermia and improve its clinical diagnosis and management. In this study, the authors generated Ankrd5 null mice and found that ANKRD5-/- males exhibited reduced sperm motility and infertility. Using FLAG-tagged ANKRD5 mice, mass spectrometry, and immunoprecipitation (IP) analyses, they confirmed that ANKRD5 is localized within the N-DRC, a critical protein complex for normal flagellar motility. However, transmission electron microscopy (TEM) and cryo-electron tomography (cryo-ET) of sperm from Ankrd5 null mice did not reveal significant structural abnormalities.

Strengths:

The phenotypes observed in ANKRD5-/- mice, including reduced sperm motility and male infertility, are conversing. The authors demonstrated that ANKRD5 is an N-DRC protein that interacts with TCTE1 and DRC4. Most of the experiments are well designed and executed.

Weaknesses:

The last section of cryo-ET analysis is not convincing. "ANKRD5 depletion may impair buffering effect between adjacent DMTs in the axoneme".

"In WT sperm, DMTs typically appeared circular, whereas ANKRD5-KO DMTs seemed to be extruded as polygonal. (Fig. S9B,D). ANKRD5-KO DMTs seemed partially open at the junction between the A- and B-tubes (Fig. S9B,D)." In the TEM images of 4E, ANKRD5-KO DMTs look the same as WT. The distortion could result from suboptimal sample preparation, imaging or data processing. Thus, the subsequent analyses and conclusions are not reliable.

Thank you for your valuable advice. To validate the results of cryo-ET, we carefully analyzed the TEM results (previously we only focused on the global "9+2" structure of the axial filament) and found that deletion of ANKRD5 resulted in both normal and deformed DMT morphologies, which was consistent with the results observed by cryo-ET. At the same time, we have added the corresponding text and picture descriptions in the article:

The text description we added is: “Upon re-examining the TEM data in light of the Cryo-ET findings, similar abnormalities were observed in the TEM images (Fig.4E, Fig. S10B). Notably, both intact and deformed DMT structures were consistently observed in both TEM and STA analyses, with the deformation of the B-tube being more obvious (Fig.4E, Fig. S10). ”

This paper still requires significant improvements in writing and language refinement. Here is an example: "While N-DRC is critical for sperm motility, but the existence of additional regulators that coordinate its function remains unclear" - ill-formed sentences.

We appreciate the reviewer’s valuable comment regarding the clarity of our writing. The sentence cited (“While N-DRC is critical for sperm motility, but the existence of additional regulators that coordinate its function remains unclear”) was indeed ill-formed. We have revised it to improve readability and precision. The corrected version now reads:“Although the N-DRC is critical for sperm motility, whether additional regulatory components coordinate its function remains unclear.” We have carefully re-examined the manuscript and refined the language throughout to ensure clarity and conciseness.

Reviewer #2 (Public review):

Summary:

The manuscript investigates the role of ANKRD5 (ANKEF1) as a component of the N-DRC complex in sperm motility and male fertility. Using Ankrd5 knockout mice, the study demonstrates that ANKRD5 is essential for sperm motility and identifies its interaction with N-DRC components through IP-mass spectrometry and cryo-ET. The results provide insights into ANKRD5's function, highlighting its potential involvement in axoneme stability and sperm energy metabolism.

Strengths:

The authors employ a wide range of techniques, including gene knockout models, proteomics, cryo-ET, and immunoprecipitation, to explore ANKRD5's role in sperm biology.

Weaknesses:

“Limited Citations in Introduction: Key references on the role of N-DRC components (e.g.,DRC2, DRC4) in male infertility are missing, which weakens the contextual background.”

We appreciate the reviewer’s valuable suggestion. To address this concern, we have added the following sentence in the Introduction:

“Recent mammalian knockout studies further confirmed that loss of DRC2 or DRC4 results in severe sperm flagellar assembly defects, multiple morphological abnormalities of the sperm flagella (MMAF), and complete male infertility, highlighting their indispensable roles in spermatogenesis and reproduction [31].”

This addition introduces up-to-date evidence on DRC2 and DRC4 functions in male infertility and strengthens the contextual background as recommended.

Reviewer #1 (Recommendations for the authors):

"Male infertility impacts 8%-12% of the global male population, with sperm motility defects contributing to 40%-50% of these cases [2，3]. " Is reference 3 proper? I don't see "sperm motility defects contributing to 40%-50%" of male infertility.

Thank you for identifying this issue. You are correct—reference 3 does not support the statement about sperm motility defects comprising 40–50% of male infertility cases; it actually states:

“Male factor infertility is when an issue with the man’s biology makes him unable to impregnate a woman. It accounts for between 40 to 50 percent of infertility cases and affects around 7 percent of men.”

This was a misunderstanding on my part, and I apologize for the oversight.

To correct this, we have replaced the statement with more accurate references:

PMID: 33968937 confirms:

“Asthenozoospermia accounts for over 80% of primary male infertility cases.”

PMID: 33191078 defines asthenozoospermia (AZS) as reduced or absent sperm motility and notes it as a major cause of male infertility.

We have updated the manuscript accordingly:

In the Significance Statement: “Male infertility affects approximately 8%-12% of men globally, with defects in sperm motility accounting for over 80% of these cases.”

In the Introduction: “Male infertility affects approximately 8% to 12% of the global male population, with defects in sperm motility accounting for over 80% of these cases[2,3].”

Thank you again for your careful review and for giving us the opportunity to improve the accuracy of our manuscript.

"Rather than bypassing the issue with ICSI, infertility from poor sperm motility could potentially be treated or even cured through stimulation of specific signaling pathways or gene therapy." Need references.

We appreciate the reviewer’s insightful comment. In response, we have added three supporting references to the relevant sentence.

The first reference (PMID: 39932044) demonstrates that cBiMPs and the PDE-10A inhibitor TAK-063 significantly and sustainably improve motility in human sperm with low activity, including cryopreserved samples, without inducing premature acrosome reaction or DNA damage. The second reference (PMID: 29581387) shows that activation of the PKA/PI3K/Ca²⁺ signaling pathways can reverse reduced sperm motility. The third reference (PMID: 33533741) reports that CRISPR-Cas9-mediated correction of a point mutation in Tex11^PM/Y spermatogonial stem cells (SSCs) restores spermatogenesis in mice and results in the production of fertile offspring.

These references provide mechanistic support and demonstrate the feasibility of treating poor sperm motility through targeted pathway modulation or gene therapy, thus reinforcing the validity of our statement.

"Our findings indicate that ANKRD5 (Ankyrin repeat domain 5; also known as ANK5 or ANKEF1) interacts with N-DRC structure". The full name should be provided the first time ANKRD5 appears. Is ANKRD5 a component of N-DRC or does it interact with N-DRC?

We thank the reviewer for the valuable suggestion. In response, we have moved the full name “Ankyrin repeat domain 5; also known as ANK5 or ANKEF1” to the abstract where ANKRD5 first appears, and have removed the redundant mention from the main text.

Based on our experimental data, we consider ANKRD5 to be a novel component of the N-DRC (nexin-dynein regulatory complex), rather than merely an interacting partner. Therefore, we have revised the sentence in the main text to read:

“Here, we demonstrate that ANKRD5 is a novel N-DRC component essential for maintaining sperm motility.”

Fig 5E, numbers of TEM images should be added.

We thank the reviewer for the suggestion. We would like to clarify that Fig. 5E does not contain TEM images, and it is likely that the reviewer was referring to Fig. 4E instead.

In Fig. 4E, we conducted three independent experiments. In each experiment, 60 TEM cross-sectional images of sperm tails were analyzed for both Ankrd5 knockout and control mice.

The findings were consistent across all replicates.

We have updated the figure legend accordingly, which now reads:

“Transmission electron microscopy (TEM) of sperm tails from control and Ankrd5 KO mice. Cross-sections of the midpiece, principal piece, and end piece were examined. Red dashed boxes highlight regions of interest, and the magnified views of these boxed areas are shown in the upper right corner of each image. In three independent experiments, 20 sperm cross-sections per mouse were analyzed for each group, with consistent results observed.”

There are random "222" in the references. Please check and correct.

I sincerely apologize for the errors caused by the reference management software, which resulted in the insertion of random "222" and similar numbering issues in the reference list. I have carefully reviewed and corrected the following problems:

References 9, 11, 13, 26, 34, 63, and 64 had the number "222" mistakenly placed before the title; these have now been removed. References 15 and 18 had "111" incorrectly inserted before the title; this has also been corrected. Reference 36 had an erroneous "2" before the title and was found to be a duplicate of Reference 32; these have now been merged into a single citation. Additionally, References 22 and 26 were identified as duplicates of the same article and have been consolidated accordingly. 

All these issues have been resolved to ensure the reference list is accurate and properly formatted.

Reviewer #2 (Recommendations for the authors):

The authors have already addressed most of the issues I am concerned about.

In addition, we have also corrected some errors in the revised manuscript:

(1) In Figure 3G, the y-axis label was previously marked as “Sperm count in the oviduct (10⁶)”, which has now been corrected to “Sperm count in the oviduct”.

(2) All p-values have been reformatted to italic lowercase letters to comply with the journal style guidelines.

Figure 6 Legend: A typographical error in the figure legend has been corrected. The text previously read “(A) The differentially expressed proteins of Ankrd5^+/– and Ankrd5^+/- were identified...”. This has now been amended to “(A) The differentially expressed proteins of Ankrd5^+/– and Ankrd5^+/– were identified...” to correctly represent the comparison between heterozygous and homozygous knockout groups.

In the original Figure 4E, we added a zoom-in panel to the image to show the deformed DMT.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #2 (Public review): 

Summary: 

The paper describes the high-resolution structure of KdpFABC, a bacterial pump regulating intracellular potassium concentrations. The pump consists of a subunit with an overall structure similar to that of a canonical potassium channel and a subunit with a structure similar to a canonical ATP-driven ion pump. The ions enter through the channel subunit and then traverse the subunit interface via a long channel that lies parallel to the membrane to enter the pump, followed by their release into the cytoplasm. 

The work builds on the previous structural and mechanistic studies from the authors' and other labs. While the overall architecture and mechanism have already been established, a detailed understanding was lacking. The study provides a 2.1 Å resolution structure of the E1-P state of the transport cycle, which precedes the transition to the E2 state, assumed to be the ratelimiting step. It clearly shows a single K+ ion in the selectivity filter of the channel and in the canonical ion binding site in the pump, resolving how ions bind to these key regions of the transporter. It also resolves the details of water molecules filling the tunnel that connects the subunits, suggesting that K+ ions move through the tunnel transiently without occupying welldefined binding sites. The authors further propose how the ions are released into the cytoplasm in the E2 state. The authors support the structural findings through mutagenesis and measurements of ATPase activity and ion transport by surface-supported membrane (SSM) electrophysiology. 

Reviewer #3 (Public review): 

Summary: 

By expressing protein in a strain that is unable to phosphorylate KdpFABC, the authors achieve structures of the active wildtype protein, capturing a new intermediate state, in which the terminal phosphoryl group of ATP has been transferred to a nearby Asp, and ADP remains covalently bound. The manuscript examines the coupling of potassium transport and ATP hydrolysis by a comprehensive set of mutants. The most interesting proposal revolves around the proposed binding site for K+ as it exits the channel near T75. Nearby mutations to charged residues cause interesting phenotypes, such as constitutive uncoupled ATPase activity, leading to a model in which lysine residues can occupy/compete with K+ for binding sites along the transport pathway. 

Strengths: 

The high resolution (2.1 Å) of the current structure is impressive, and allows many new densities in the potassium transport pathway to be resolved. The authors are judicious about assigning these as potassium ions or water molecules, and explain their structural interpretations clearly. In addition to the nice structural work, the mechanistic work is thorough. A series of thoughtful experiments involving ATP hydrolysis/transport coupling under various pH and potassium concentrations bolsters the structural interpretations and lends convincing support to the mechanistic proposal. The SSME experiments are generally rigorous. 

Weaknesses: 

The present SSME experiments do not support quantitative comparisons of different mutants, as in Figures 4D and 5E. Only qualitative inferences can be drawn among different mutant constructs. 

Thank you to both reviewers for your thorough review of our work. We acknowledge the limitations of SSME experiments in quantitative comparison of mutants and have revised the manuscript to address this point. In addition, we have included new ATPase data from reconstituted vesicles which we believe will help to strengthen our contention that both ATPase and transport are equally affected by Val496 mutations.

Reviewer #2 (Recommendations for the authors): 

I have a minor editorial comment: 

Perhaps I am confused. However, in reference to the text in the Results: "Our WT complex displayed high levels of K+-dependent ATPase activity and generated robust transport currents (Fig. 1 - figure suppl. 1).", I do not see either K+-dependency of ATPase activity nor transport currents in Fig. 1 - figure suppl. 1. Perhaps the text needs to be edited for clarity. 

Thank you for pointing this out. This confusion was caused by our removal of a panel from the revised manuscript, which depicted K+-dependent transport currents. Although this panel is somewhat redundant, given inclusion of raw SSME traces from all the mutants, it has been replaced as Fig. 1 - figure supplement 1F, thus providing a thorough characterization of the preparation used for cryo-EM analysis and supporting the statement quoted by this reviewer.

Reviewer #3 (Recommendations for the authors): 

The authors have provided a detailed description of the SSME data collection, and followed rigorous protocols to ensure that the currents measured on a particular sensor remained stable over time. 

I still have reservations about the direct comparison of transport in the different mutants. Specifically, on page 6, the authors state that "The longer side chain of V496M reduces transport modestly with no effect on ATPase activity. V496R, which introduces positive charge, completely abolishes activity. V496W and V496H reduce both transport and ATPase activity by about half, perhaps due to steric hindrance for the former and partial protonation for the latter." And in figures 4D and 5B, by plotting all of the peak currents on the same graph, the authors are giving the data a quantitative veneer, when these different experiments really aren't directly comparable, especially in the absence of any controls for reconstitution efficiency. 

In terms of overall conclusions, for the more drastic mutant phenotypes, I think it is completely reasonable to conclude that transport is not observed. But a 2-fold difference could easily result from differences in reconstitution or sensor preparation. My suggestion would be to show example traces rather than a numeric plot in 4D/5E, to convey the qualitative nature of the mutant-to-mutant comparisons, and to re-write the text to acknowledge the shortcomings of mutant-to-mutant comparisons with SSME, and avoid commenting on the more subtle phenotypes, such as modest decreases and reductions by about half. 

Figure 4, supplement 1. What is S162D? I don't think it is mentioned in the main text. 

We agree with the reviewer's point that quantitative comparison of different mutants by SSME is compromised by ambiguity in reconstitution. However, we do not think that display of raw SSME currents is an effective way to communicate qualitative effects to the general reader, given the complexity of these data (e.g., distinction between transient binding current seen in V496R and genuine, steady-state transport current seen in WT). So we have taken a compromise approach. To start, we have removed the transport data from the main figure (Fig. 4). Luckily, we had frozen and saved the batch of reconstituted proteoliposomes from Val496 mutants that had been used for transport assays. We therefore measured ATPase activities from these proteoliposomes - after adding a small amount of detergent to prevent buildup of electrochemical gradients (1 mg/ml decylmaltoside which is only slightly more than the critical micelle concentration of 0.87 mg/ml). Differences in ATPase activity from these proteoliposomes were very similar to those measured prior to reconstitution (i.e., data in Fig. 4d) indicating that reconstitution efficiencies were comparable for the various mutants. Furthermore, differences in SSME currents are very similar to these ATPase activities, suggesting that Val496 mutants did not affect energy coupling. These data are shown in the revised Fig. 4 - figure suppl. 1a, along with the SSME raw data and size-exclusion chromatography elution profiles (Fig. 4 - figure suppl. 1b-g). We also altered the text to point out the concern over comparing transport data from different mutants (see below). We hope that this revised presentation adequately supports the conclusion that Val496 mutations - and especially the V496R substitution - influence the passage of K+ through the tunnel without affecting mechanics of the ATP-dependent pump. 

The paragraph in question now reads as follows (pg. 6-7, with additional changes to legends to Fig. 4 and Fig. 4 - figure suppl. 1):

"In order to provide experimental evidence for K+ transport through the tunnel, we made a series of substitutions to Val496 in KdpA. This residue resides near the widest part of the tunnel and is fully exposed to its interior (Fig. 4a). We made substitutions to increase its bulk (V496M and V496W) and to introduce charge (V496E, V496R and V496H). We used the AlphaFold-3 artificial intelligence structure prediction program (Jumper et al., 2021) to generate structures of these mutants and to evaluate their potential impact on tunnel dimensions. This analysis predicts that V496W and V496R reduce the radius to well below the 1.4 Å threshold required for passage of K+ or water (Fig. 4c); V496E and V496M also constrict the tunnel, but to a lesser extent. Measurements of ATPase and transport activity (Fig. 4d) show that negative charge (V496E) has no effect. The or a longer side chain of (V496M) reduces transport modestly with have no apparent effect on ATPase activity. V496R, which introduces positive charge, almost completely abolishes activity. V496W and V496H reduce both transport and ATPase activity by about half, perhaps due to steric hindrance for the former and partial protonation for the latter. Transport activity of these mutants was also measured, but quantitative comparisons are hampered by potential inconsistency in reconstitution of proteoliposomes and in preparation of sensors for SSME. To account for differences in reconstitution, we compared ATPase activity and transport currents taken from the same batch of vesicles (Fig. 4 - figure suppl. 1a).  These data show that differences in ATPase activity of proteoliposomes was consistent with differences measured prior to reconstitution (Fig. 4d). Transport activity, which was derived from multiple sensors, mirrored ATPase activity, indicating that the Val496 mutants did not affect energy coupling, but simply modulated turnover rate of the pump."

S162D was included as a negative control, together with D307A. However, given the inactive mutants discussed in Fig. 5 (Asp582 and Lys586 substitutions), these seem an unnecessary distraction and have been removed from Fig. 4 - figure suppl. 1.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

The study presents significant findings on the role of mitochondrial depletion in axons and its impact on neuronal proteostasis. It effectively demonstrates how the loss of axonal mitochondria and elevated levels of eIF2β contribute to autophagy collapse and neuronal dysfunction. The use of Drosophila as a model organism and comprehensive proteome analysis adds robustness to the findings.

In this revision, the authors have responded thoughtfully to previous concerns. In particular, they have addressed the need for a quantitative analysis of age-dependent changes in eIF2β and eIF2α. By adding western blot data from multiple time points (7 to 63 days), they show that eIF2β levels gradually increase until middle age, then decline. In milton knockdown flies, this pattern appears shifted, supporting the idea that mitochondrial defects may accelerate aging-related molecular changes. These additions clarify the temporal dynamics of eIF2β and improve the overall interpretation.

Other updates include appropriate corrections to figures and quantification methods. The authors have also revised some of their earlier mechanistic claims, presenting a more cautious interpretation of their findings.

Overall, this work provides new insights into how mitochondrial transport defects may influence aging-related proteostasis through eIF2β. The manuscript is now more convincing, and the revisions address the main points raised earlier. I find the updated version much improved.

Thank you so much for the review, insightful comments and encouragement. We appreciate it.  

Reviewer #2 (Public review):

In the manuscript, the authors aimed to elucidate the molecular mechanism that explains neurodegeneration caused by the depletion of axonal mitochondria. In Drosophila, starting with siRNA depletion of milton and Miro, the authors attempted to demonstrate that the depletion of axonal mitochondria induces the defect in autophagy. From proteome analyses, the authors hypothesized that autophagy is impacted by the abundance of eIF2β and the phosphorylation of eIF2α. The authors followed up the proteome analyses by testing the effects of eIF2β overexpression and depletion on autophagy. With the results from those experiments, the authors proposed a novel role of eIF2β in proteostasis that underlies neurodegeneration derived from the depletion of axonal mitochondria, which they suggest accelerates age-dependent changes rather than increasing their magnitude.

Strong caution is necessary regarding the interpretation of translational regulation resulting from the milton KD. The effect of milton KD on translation appears subtle, if present at all, in the puromycin incorporation experiments in both the initial and revised versions. Additionally, the polysome profiling data in the revised manuscript lack the clear resolution for ribosomal subunits, monosomes, and polysomes that is typically expected in publications.

Thank you so much for the review and insightful comments. We appreciate it.  

Reviewer #2 (Recommendations for the authors):

The revised manuscript demonstrates many improvements. The authors have provided a more comprehensive data set and a more detailed description of their results. Furthermore, their explanation of the Integrated Stress Response (ISR) has been corrected, and this correction is reflected in the data interpretation.

As in the public review, I maintained my emphasis on the weakness of the claim on suppressed global translation, since the data are the same in the initial and the revised versions.

Thank you for your review. We understand that further studies will be needed to elucidate the roles on mitochondrial distribution in global translation profile. We will keep working on it. 

A few suggestions for minor corrections.

(1) The order of figures in the revised version is disorganized.

Thank you for pointing it out. We corrected the order. 

(2) In Figure 1A, mitochondria is bound by milton, and kinesin is bound by Miro. Their roles should be opposite.

Thank you for pointing it out, and we are sorry for the oversight. We corrected it.

Author response:

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

Reviewer #1 (Recommendations for the authors): 

I will address here just some minor changes that would improve understanding, reproducibility, or cohesion with the literature.

(1) It would be good to mention that the prostatic vesicle of this study is named vesicula granulorum in (Steniböck, 1966) and granule vesicle in (Hooge et al, 2007).

We have now included this (line 90 of our revised manuscript).  

(2) A slightly more detailed discussion of the germline genes would be interesting. For example, a potential function of pa1b3-2 and cgnl1-2 based on the similarity to known genes or on the conserved domains.

Pa1b3-2 appears to encode an acetylhydrolase; cgnl1-2 is likely a cingulin family protein involved in cell junctions. However, given the evolutionary distance between acoels and model organisms in whom these genes have been studied, we believe it is premature to speculate on their function without substantial additional work. We believe this work would be more appropriate in a future publication focused on the molecular genetic underpinnings of Hofstenia’s reproductive systems and their development.  

(3) It is mentioned that the animals can store sperm while lacking a seminal bursa "given that H. miamia can lay eggs for months after a single mating" (line 635) - this could also be self-fertilization, according to the authors' other findings.

We agree that it is possible this is self-fertilization, and we believe we have represented this uncertainty accurately in the text. However, we do not think this is likely, because self-fertilization manifests as a single burst of egg laying (Fig. 6D). We discuss this in the Results (line 540). 

(4) A source should be given for the tree in Figure 7B. 

We have now included this source (line 736), and we apologize for the oversight.  

(5) Either in the Methods or in the Results section, it would be good to give more details on why actin and FMRFamide and tropomyosin are chosen for the immunohistochemistry studies.

We have now included more detail in the Methods (line 823). Briefly, these are previously-validated antibodies that we knew would label relevant morphology.

(6) In the Methods "a standard protocol hematoxylin eosin" is mentioned. Even if this is a fairly common technique, more details or a reference should be provided.

We have now included more detail, and a reference (lines 766-774).  

(7) Given the historical placement of Acoela within Platyhelminthes and the fact that the readers might not be very familiar with this group of animals, two passages can be confusing: line 499 and lines 674-678.

We have edited these sentences to clarify when we mean platyhelminthes, which addresses this confusion.  

(8) A small addition to Table S1: Amphiscolops langerhansi also presents asexual reproduction through fission ([1], cited in [2]]).

Thanks. We have included this in Table S1.

(a) Hanson, E. D. 1960. 'Asexual Reproduction in Acoelous Turbellaria'. The Yale Journal of Biology and Medicine 33 (2): 107-11.

(b) Hendelberg, Jan, and Bertil Åkesson. 1991. 'Studies of the Budding Process in Convolutriloba Retrogemma (Acoela, Platyhelminthes)'. In Turbellarian Biology: Proceedings of the Sixth International Symposium on the Biology of the Turbellaria, Held at Hirosaki, Japan, 7-12 August 1990, 11-17. Springer. 

Reviewer #2 (Recommendations for the authors): 

I do not have any major comments on the manuscript. By default, I feel descriptive studies are a critical part of the advancement of science, particularly if the data are of great quality - as is the case here. The manuscript addresses various topics and describes these adequately. My minor point would be that in some sections, it feels like one could have gone a bit deeper. I highlighted three examples in the weakness section above (deeper analysis of markers for germline; modes of oogenesis/spermatogenesis; or proposed model for sperm storage). For instance, ultrastructural data might have been informative. But as said, I don't see this as a major problem, more a "would have been nice to see".

We have responded to these points in detail above.

Author response:

Reviewer #1 (Public review):

Major Comments:

(1) The abstract frames progressive renal dysfunction as a "central, disease-modifying feature" in both Gba1b and Parkin models, with systemic consequences including water retention, ionic hypersensitivity, and worsened neuro phenotypes. While the data demonstrates renal degeneration and associated physiological stress, the causal contribution of renal defects versus broader organismal frailty is not fully disentangled. Please consider adding causal experiments (e.g., temporally restricted renal rescue/knockdown) to directly establish kidney-specific contributions.

We concur that this would help strengthen our conclusions. However, manipulating Gba1b in a tissue-specific manner remains challenging due to its propensity for secretion via extracellular vesicles (ECVs). Leo Pallanck and Marie Davis have elegantly shown that ectopic Gba1b expression in neurons and muscles (tissues with low predicted endogenous expression) is sufficient to rescue major organismal phenotypes. Consistent with this, we have been unable to generate clear tissue-specific phenotypes using Gba1b RNAi.

We will pursue more detailed time-course experiments of the progression of renal pathology, (water weight, renal stem cell proliferation, redox defects, etc.) with the goal of identifying earlier-onset phenotypes that potentially drive dysfunction.

(2) The manuscript shows multiple redox abnormalities in Gba1b mutants (reduced whole fly GSH, paradoxical mitochondrial reduction with cytosolic oxidation, decreased DHE, increased lipid peroxidation, and reduced peroxisome density/Sod1 mislocalization). These findings support a state of redox imbalance, but the driving mechanism remains broad in the current form. It is unclear if the dominant driver is impaired glutathione handling or peroxisomal antioxidant/β-oxidation deficits or lipid peroxidation-driven toxicity, or reduced metabolic flux/ETC activity. I suggest adding targeted readouts to narrow the mechanism.

We agree that we have not yet established a core driver of redox imbalance. Identifying one is likely to be challenging, especially as our RNA-sequencing data from aged Gba1b^⁻/⁻ fly heads (Atilano et al., 2023) indicate that several glutathione S-transferases (GstD2, GstD5, GstD8, and GstD9) are upregulated. We can attempt overexpression of GSTs, which has been elegantly shown by Leo Pallanck to ameliorate pathology in Pink1/Parkin mutant fly brains. However, mechanisms that specifically suppress lipid peroxidation or its associated toxicity, independently of other forms of redox damage, remain poorly understood in Drosophila. Our position is there probably will not be one dominant driver of redox imbalance. Notably, CytB5 overexpression has been shown to reduce lipid peroxidation (Chen et al., 2017), and GstS1 has been reported to conjugate glutathione to the toxic lipid peroxidation product 4-HNE (Singh et al., 2001). Additionally, work from the Bellen lab demonstrated that overexpression of lipases, bmm or lip4, suppresses lipid peroxidation-mediated neurodegeneration (Liu et al., 2015). We will therefore test the effects of over-expressing CytB5, bmm and lip4 in Gba1b^⁻/⁻ flies to help further define the mechanism.

(3) The observation that broad antioxidant manipulations (Nrf2 overexpression in tubules, Sod1/Sod2/CatA overexpression, and ascorbic acid supplementation) consistently shorten lifespan or exacerbate phenotypes in Gba1b mutants is striking and supports the idea of redox fragility. However, these interventions are broad. Nrf2 influences proteostasis and metabolism beyond redox regulation, and Sod1/Sod2/CatA may affect multiple cellular compartments. In the absence of dose-response testing or controls for potential off-target effects, the interpretation that these outcomes specifically reflect redox dyshomeostasis feels ahead of the data. I suggest incorporating narrower interpretations (e.g., targeting lipid peroxidation directly) to clarify which redox axis is driving the vulnerability.

We are in agreement that Drosophila Cnc exhibits functional conservation with both Nrf1 and Nrf2, which have well-established roles in proteostasis and lysosomal biology that may exacerbate pre-existing lysosomal defects in Gba1b mutants. In our manuscript, Nrf2 manipulation forms part of a broader framework of evidence, including dietary antioxidant ascorbic acid and established antioxidant effectors CatA, Sod1, and Sod2. Together, these data indicate that Gba1b mutant flies display a deleterious response to antioxidant treatments or manipulations. To further characterise the redox state, we will quantify lipid peroxidation using Bodipy 581/591 and assess superoxide levels via DHE staining under our redox-altering experimental conditions.

As noted above, we will attempt to modulate lipid peroxidation directly through CytB5 and GstS1 overexpression, acknowledging the caveat that this approach may not fully dissociate lipid peroxidation from other aspects of redox stress. We have also observed detrimental effects of PGC1α on the lifespan of Gba1b^⁻/⁻ flies and will further investigate its impact on redox status in the renal tubules.

(4) This manuscript concludes that nephrocyte dysfunction does not exacerbate brain pathology. This inference currently rests on a limited set of readouts: dextran uptake and hemolymph protein as renal markers, lifespan as a systemic measure, and two brain endpoints (LysoTracker staining and FK2 polyubiquitin accumulation). While these data suggest that nephrocyte loss alone does not amplify lysosomal or ubiquitin stress, they may not fully capture neuronal function and vulnerability. To strengthen this conclusion, the authors could consider adding functional or behavioral assays (e.g., locomotor performance)

We will address this suggestion by performing DAM activity assays and climbing assays in the Klf15; Gba1b^⁻/⁻ double mutants.

(5) The manuscript does a strong job of contrasting Parkin and Gba1b mutants, showing impaired mitophagy in Malpighian tubules, complete nephrocyte dysfunction by day 28, FRUMS clearance defects, and partial rescue with tubule-specific Parkin re-expression. These findings clearly separate mitochondrial quality control defects from the lysosomal axis of Gba1b. However, the mechanistic contrast remains incomplete. Many of the redox and peroxisomal assays are only presented for Gba1b. Including matched readouts across both models (e.g., lipid peroxidation, peroxisome density/function, Grx1-roGFP2 compartmental redox status) would make the comparison more balanced and strengthen the conclusion that these represent distinct pathogenic routes.

We agree that park^⁻/⁻ mutants have been characterised in greater detail than park^⁻/⁻. The primary aim of our study was not to provide an exhaustive characterisation of park¹/¹, but rather to compare key shared and distinct mechanisms underlying renal dysfunction. We have included several relevant readouts for park^⁻/⁻ tubules (e.g., Figure 7D and 8H: mito-Grx1-roGFP2; Figure 8J: lipid peroxidation using BODIPY 581/591). To expand our characterisation of park¹/¹ flies, we will express the cytosolic Grx1 reporter and the peroxisomal marker YFP::Pts.

(6) Rapamycin treatment is shown to rescue several renal phenotypes in Gba1b mutants (water retention, RSC proliferation, FRUMS clearance, lipid peroxidation) but not in Parkin, and mitophagy is not restored in Gba1b. This provides strong evidence that the two models engage distinct pathogenic pathways. However, the therapeutic interpretation feels somewhat overstated. Human relevance should be framed more cautiously, and the conclusions would be stronger with mechanistic markers of autophagy (e.g., Atg8a, Ref(2)p flux in Malpighian tubules) or with experiments varying dose, timing, and duration (short-course vs chronic rapamycin).

We will measure Atg8a, polyubiquitin, and Ref(2)P levels in Gba1b^⁻/⁻ and park^¹/¹ tubules following rapamycin treatment. In our previous study focusing on the gut (Atilano et al., 2023), we showed that rapamycin treatment increased lysosomal area, as assessed using LysoTracker^TM. We will extend this analysis to the renal tubules following rapamycin exposure. Another reviewer requested that we adopt more cautious language regarding the clinical translatability of this work, and we will amend this in Version 2.

(7) Several systemic readouts used to support renal dysfunction (FRUMS clearance, salt stress survival) could also be influenced by general organismal frailty. To ensure these phenotypes are kidney-intrinsic, it would be helpful to include controls such as tissue-specific genetic rescue in Malpighian tubules or nephrocytes, or timing rescue interventions before overt systemic decline. This would strengthen the causal link between renal impairment and the observed systemic phenotypes.

As noted in our response to point 1, we currently lack reliable approaches to manipulate Gba1b in a tissue-specific manner. However, we agree that it is important to distinguish kidney-intrinsic dysfunction from generalised organismal frailty. In the park model, we have already performed renal cell-autonomous rescue: re-expression of Park specifically in Malpighian tubule principal cells (C42-Gal4) throughout adulthood partially normalises water retention, whereas brain-restricted Park expression has no effect on renal phenotypes. Because rescuing Park only in the renal tubules is sufficient to correct a systemic fluid-handling phenotype in otherwise mutant animals, these findings indicate that the systemic defects are driven, at least in part, by renal dysfunction rather than nonspecific organismal frailty.

To strengthen this causal link, we will now extend this same tubule-specific Park rescue (C42-Gal4 and the high-fidelity Malpighian tubule driver CG31272-Gal4) to additional systemic readouts raised by the reviewer. Specifically, we will assay FRUMS clearance and salt stress survival in rescued versus non-rescued park mutants to determine whether renal rescue also mitigates these systemic phenotypes.

Reviewer #2 (Public review):

(1) The authors claim that: "renal system dysfunction negatively impacts both organismal and neuronal health in Gba1b-/- flies, including autophagic-lysosomal status in the brain." This statement implies that renal impairments drive neurodegeneration. However, there is no direct evidence provided linking renal defects to neurodegeneration in this model. It is worth noting that Gba1b-/- flies are a model for neuronopathic Gaucher disease (GD): they accumulate lipids in their brains and present with neurodegeneration and decreased survival, as shown by Kinghorn et al. (The Journal of Neuroscience, 2016, 36, 11654-11670) and by others, which the authors failed to mention (Davis et al., PLoS Genet. 2016, 12: e1005944; Cabasso et al., J Clin Med. 2019, 8:1420; Kawasaki et al., Gene, 2017, 614:49-55).

With the caveats noted in the responses below, we show that driving Nrf2 expression using the renal tubular driver C42 results in decreased survival, more extensive renal defects, and increased brain pathology in Gba1b^⁻/⁻ flies, but not in healthy controls. This suggests that a healthy brain can tolerate renal dysfunction without severe pathological consequences. Our findings therefore indicate that in Gba1b^⁻/⁻ flies, there may be an interaction between renal defects and brain pathology. We do not explicitly claim that renal impairments drive neurodegeneration; rather, we propose that manipulations exacerbating renal dysfunction can have organism-wide effects, ultimately impacting the brain.

The reviewer is correct that our Gba1b^⁻/⁻ fly model represents a neuronopathic GD model with age-related pathology. Indeed, we reproduce the autophagic-lysosomal defects previously reported (Kinghorn et al., 2016) in Figure 5. We agree that the papers cited by the reviewer merit inclusion, and in Version 2 we will incorporate them into the following pre-existing sentence in the Results:

“The gut and brain of Gba1b^⁻/⁻ flies, similar to macrophages in GD patients, are characterised by enlarged lysosomes (Kinghorn et al., 2016; Atilano et al., 2023).”

(2) The authors tested brain pathology in two experiments:

(a) To determine the consequences of abnormal nephrocyte function on brain health, they measured lysosomal area in the brain of Gba1b-/-, Klf15LOF, or stained for polyubiquitin. Klf15 is expressed in nephrocytes and is required for their differentiation. There was no additive effect on the increased lysosomal volume (Figure 3D) or polyubiquitin accumulation (Figure 3E) seen in Gba1b-/- fly brains, implying that loss of nephrocyte viability itself does not exacerbate brain pathology.

(b) The authors tested the consequences of overexpression of the antioxidant regulator Nrf2 in principal cells of the kidney on neuronal health in Gba1b-/- flies, using the c42-GAL4 driver. They claim that "This intervention led to a significant increase in lysosomal puncta number, as assessed by LysoTrackerTM staining (Figure 5D), and exacerbated protein dyshomeostasis, as indicated by polyubiquitin accumulation and increased levels of the ubiquitin-autophagosome trafficker Ref(2)p/p62 in Gba1b-/- fly brains (Figure 5E). Interestingly, Nrf2 overexpression had no significant effect on lysosomal area or ubiquitin puncta in control brains, demonstrating that the antioxidant response specifically in Gba1b-/- flies negatively impacts disease states in the brain and renal system."Notably, c42-GAL4 is a leaky driver, expressed in salivary glands, Malpighian tubules, and pericardial cells (Beyenbach et al., Am. J. Cell Physiol. 318: C1107-C1122, 2020). Expression in pericardial cells may affect heart function, which could explain deterioration in brain function.

Taken together, the contribution of renal dysfunction to brain health remains debatable.

Based on the above, I believe the title should be changed to: Redox Dyshomeostasis Links Renal and Neuronal Dysfunction in Drosophila Models of Gaucher disease. Such a title will reflect the results presented in the manuscript

We agree that C42-Gal4 is a leaky driver; unfortunately, this was true for all commonly used Malpighian tubule drivers available when we began the study. A colleague has recommended CG31272-Gal4 from the Perrimon lab’s recent publication (Xu et al., 2024) as a high-fidelity Malpighian tubule driver. If it proves to maintain principal-cell specificity throughout ageing in our hands, we will repeat key experiments using this driver.

(3) The authors mention that Gba1b is not expressed in the renal system, which means that no renal phenotype can be attributed directly to any known GD pathology. They suggest that systemic factors such as circulating glycosphingolipids or loss of extracellular vesicle-mediated delivery of GCase may mediate renal toxicity. This raises a question about the validity of this model to test pathology in the fly kidney. According to Flybase, there is expression of Gba1b in renal structures of the fly.

Our evidence suggesting that Gba1b is not substantially expressed in renal tissue is based on use of the Gba1b-CRIMIC-Gal4 line, which fails to drive expression of fluorescently tagged proteins in the Malpighian tubules and we have previously shown there is no expression within the nephrocytes with this driver line (Atilano et al., 2023). This does not exclude the possibility that Gba1b functions within the tubules. Notably, Leo Pallanck has provided compelling evidence that Gba1b is present in extracellular vesicles (ECVs) and given the role of the Malpighian tubules in haemolymph filtration, these cells are likely exposed to circulating ECVs. The lysosomal defects observed in Gba1b^⁻/⁻ tubules therefore suggest a potential role for Gba1b in this tissue.  

John Vaughan and Thomas Clandinin have developed mCherry- and Lamp1.V5-tagged Gba1b constructs. We intend to express these in tissues shown by the Pallanck lab to release ECVs (e.g., neurons and muscle) and examine whether the protein can be detected in the tubules.

(4) It is worth mentioning that renal defects are not commonly observed in patients with Gaucher disease. Relevant literature: Becker-Cohen et al., A Comprehensive Assessment of Renal Function in Patients With Gaucher Disease, J. Kidney Diseases, 2005, 46:837-844.

We have identified five references indicating that renal involvement, while rare, does occur in association with GD. We agree that this is a valid citation and will include it in the revised introductory sentence:

“However, renal dysfunction remains a rare symptom in GD patients (Smith et al., 1978; Chander et al., 1979; Siegel et al., 1981; Halevi et al., 1993).”

(5) In the discussion, the authors state: "Together, these findings establish renal degeneration as a driver of systemic decline in Drosophila models of GD and PD..." and go on to discuss a brain-kidney axis in PD. However, since this study investigates a GD model rather than a PD model, I recommend omitting this paragraph, as the connection to PD is speculative and not supported by the presented data.

Our position is that Gba1b^⁻/⁻ represents a neuronopathic Gaucher disease model with mechanistic relevance to PD. The severity of GBA1 mutations correlates with the extent of GBA1/GCase loss of function and, consequently, with increased PD risk. Likewise, biallelic park^⁻/⁻ mutants cause a severe and heritable form of PD, and the Drosophila park^⁻/⁻ model is a well-established and widely recognised system that has been instrumental in elucidating how Parkin and Pink1 mutations drive PD pathogenesis.

We therefore see no reason to omit this paragraph. While some aspects are inherently speculative, such discussion is appropriate and valuable when addressing mechanisms underlying a complex and incompletely understood disease, provided interpretations remain measured. At no point do we claim that our work demonstrates a direct brain-renal axis. Rather, our data indicate that renal dysfunction is a disease-modifying feature in these models, aligning with emerging epidemiological evidence linking PD and renal impairment.

(6) The claim: "If confirmed, our findings could inform new biomarker strategies and therapeutic targets for GBA1 mutation carriers and other at-risk groups. Maintaining renal health may represent a modifiable axis of intervention in neurodegenerative disease," extends beyond the scope of the experimental evidence. The authors should consider tempering this statement or providing supporting data.

(7) The conclusion, "we uncover a critical and previously overlooked role for the renal system in GD and PD pathogenesis," is too strong given the data presented. As no mechanistic link between renal dysfunction and neurodegeneration has been established, this claim should be moderated.

We agree that these sections may currently overstate our findings. In Version 2, we will revise them to ensure our claims remain balanced, while retaining the key points that arise from our data and clearly indicating where conclusions require confirmation (“if confirmed”) or additional study (“warrants further investigation”).

“If confirmed, our findings could inform new biomarker strategies and therapeutic targets for patients with GD and PD. Maintaining renal health may represent a modifiable axis of intervention in these diseases.”

“We uncover a notable and previously underappreciated role for the renal system in GD and PD, which now warrants further investigation.”

(8) The relevance of Parkin mutant flies is questionable, and this section could be removed from the manuscript.

We intend to include the data for the Parkin loss-of-function mutants, as these provide essential support for the PD-related findings discussed in our manuscript. To our knowledge, this represents the first demonstration that Parkin mutants display defects in Malpighian tubule function and water homeostasis. We therefore see no reason to remove these findings. Furthermore, as Reviewer 1 specifically requested additional experiments using the Park fly model, we plan to incorporate these analyses in the revised manuscript.

Minor comments:

(1)  Figure 1G: The FRUMS assay is not shown for Gba1b-/- flies.

The images in Figure 1G illustrate representative stages of dye clearance. We have quantified the clearance time course for both genotypes. During this process, the tubules of Gba1b^⁻/⁻ flies, similar to controls, sequentially resemble each of the three example images. As the Gba1b^⁻/⁻ tubules appear morphologically identical to controls, differing only in population-level clearance dynamics, we do not feel that including additional example images would provide further informative value.

(2) In panels D and F of Figure 2, survival of control and Gba1b-/- flies in the presence of 4% NaCl is presented. However, longevity is different (up to 10 days in D and ~3 days in F for control). The authors should explain this.

We agree. In our experience, feeding-based stress survival assays show considerable variability between experiments, and we therefore interpret results only within individual experimental replicates. We have observed similar variability in oxidative stress, starvation, and xenobiotic survival assays, which may reflect batch-specific or environmental effects.

(3) In Figure 7F, the representative image does not correspond to the quantification; the percentage of endosome-negative nephrocytes seems to be higher for the control than for the park1/1 flies. Please check this.

The example images are correctly oriented. Typically, an endosome-negative nephrocyte shows no dextran uptake, whereas an endosome-positive nephrocyte displays a ring of puncta around the cell periphery. In park¹/¹ mutants, dysfunctional nephrocytes exhibit diffuse dextran staining throughout the cell, accompanied by diffuse DAPI signal, indicating a complete loss of membrane integrity and likely cell death. We have 63× images from the preparations shown in Figure 7F demonstrating this. In Version 2, we will include apical and medial z-slices of the nephrocytes to illustrate these findings (to be added as supplementary   data).

(4) In Figure 7H, the significance between control and park1/1 flies in the FRUMS assay is missing.

We observe significant dye clearance from the haemolymph; however, the difference in complete clearance from the tubules does not reach statistical significance. This may speculatively reflect alterations in specific aspects of tubule function, where absorption and transcellular flux are affected, but subsequent clearance from the tubule lumen remains intact. We do not feel that our current data provide sufficient resolution to draw detailed conclusions about tubule physiology at this level.

Reviewer #3 (Public review):

Weaknesses:

The paper relies mostly on the biallelic Gba1b mutant, which may reflect dysfunction in Gaucher's patients, though this has yet to be fully explored. The claims for the heterozygous allele and a role in Parkinson's is a little more tenuous, making assumptions that heterozygosity is a similar but milder phenotype than the full loss-of-function.

We agree with the reviewer that studying heterozygotes may provide valuable insight into GBA1-associated PD. We will therefore assess whether subtle renal defects are detectable in Gba1b^⁻/⁻ heterozygotes. We clearly state that GBA1 mutations act as a risk factor for PD rather than a Mendelian inherited cause. Consistent with findings from Gba heterozygous mice, Gba1b^⁻/⁻ flies display minimal phenotypes (Kinghorn et al. 2016), and any observable effects are expected to be very mild and age dependent.

(1) Figure 1c, the loss of stellate cells. What age are the MTs shown? Is this progressive or developmental?

These experiments were conducted on flies that were three weeks of age, as were all manipulations unless otherwise stated. We will ensure that this information is clearly indicated in the figure legends in Version 2. We did not observe changes in stellate cell number at three days of age, and this result will be included in the supplementary material in Version 2. Our data therefore suggest that this is a progressive phenotype.

(2) I might have missed this, but for Figure 3, do the mutant flies start with a similar average weight, or are they bloated?

We will perform an age-related time course of water weight in response to Reviewer 1’s comments. For all experiments, fly eggs are age-matched and seeded below saturation density to ensure standardised conditions. Gba1b mutant flies do not exhibit any defects in body size or timing of eclosion.

(3) On 2F, add to the graph that 4% NaCl (or if it is KCL) is present for all conditions, just to make the image self-sufficient to read.

Many thanks for the suggestion. We agree that this will increase clarity and will make this amendment in Version 2 of the manuscript

(4) P13 - rephrase, 'target to either the mitochondria or the cytosol' (as it is phrased, it sounds as though you are doing both at the same time).

We agree and we plan to revise the sentence as follows:

Original:

“To further evaluate the glutathione redox potential (E_GSH) in MTs, we utilised the redox-sensitive green, fluorescent biosensor Grx1-roGFP2, targeted to both the mitochondria and cytosol (Albrecht et al., 2011).”

Revised:

“To further evaluate the glutathione redox potential (E_GSH) in MTs, we utilised the redox-sensitive fluorescent biosensor Grx1-roGFP2, targeted specifically to either the mitochondria or the cytosol using mito- or cyto-tags, respectively (Albrecht et al., 2011).”

(5) In 6F - the staining appears more intense in the Park mutant - perhaps add asterisks or arrowheads to indicate the nephrocytes so that the reader can compare the correct parts of the image?

Reviewer 2 reached the same interpretation. Typically, an endosome-negative nephrocyte shows no dextran uptake, whereas an endosome-positive nephrocyte displays a ring of puncta around the cell periphery. In park¹/¹ mutants, dysfunctional nephrocytes exhibit diffuse dextran staining throughout the cell, accompanied by diffuse DAPI signal, indicative of a complete loss of membrane integrity and likely cell death. We have 63× images from the preparations shown in Figure 7F demonstrating this, and in Version 2 we will include apical and medial z-slices of the nephrocytes to illustrate these findings (to be added as supplementary data).

(6) In the main results text - need some description/explanation of the SOD1 v SOD2 distribution (as it is currently understood) in the cell - SOD2 being predominantly mitochondrial. This helps arguments later on.

Thank you for this suggestion. We plan to amend the text as follows:

“Given that Nrf2 overexpression shortens lifespan in Gba1b^⁻/⁻ flies, we investigated the effects of overexpressing its downstream antioxidant targets, Sod1, Sod2, and CatA, both ubiquitously using the tub-Gal4 driver and with c42-Gal4, which expresses in PCs.”

to:

“Given that Nrf2 overexpression shortens lifespan in Gba1b^⁻/⁻ flies, we investigated the effects of overexpressing its downstream antioxidant targets, Sod1, Sod2, and CatA, both ubiquitously using the tub-Gal4 driver and with c42-Gal4, which expresses in PCs. Sod1 and CatA function primarily in the cytosol and peroxisomes, whereas Sod2 is localised to the mitochondria. Sod1 and Sod2 catalyse the dismutation of superoxide radicals to hydrogen peroxide, while CatA subsequently degrades hydrogen peroxide to water and oxygen.”

(7) Figure 1G, what age are the flies? Same for 3D and E, 4C,D,E, 5B - please check the ages of flies for all of the imaging figures; this information appears to have been missed out.

As stated above, all experiments were conducted on three-week-old flies unless otherwise specified. In Version 2 of the manuscript, we will ensure this information is included consistently in the figure legends to prevent any potential confusion.

Author response:

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

Reviewer #1:

Specifically, the authors need to define the DFG conformation using criteria accepted in the field, for example, see https://klifs.net/index.php.

We thank the reviewer for this suggestion. In the manuscript, we use pseudodihedral and bond angle-based DFG definitions that have been previously established by literature cited in the study (re-iterated below) to unambiguously define the side-chain conformational states of the DFG motif. As we are interested in the specific mechanics of DFG flips under different conditions, we’ve found that the descriptors defined below are sufficient to distinguish between DFG states and allow a more direct comparison with previously-reported results in the literature using different methods.

We amended the text to be more clear as to those definitions and their choice:

DFG angle definitions:

Phe382/Cg, Asp381/OD2, Lys378/O

Source: Structural Characterization of the Aurora Kinase B "DFG-flip" Using Metadynamics. Lakkaniga NR, Balasubramaniam M, Zhang S, Frett B, Li HY. AAPS J. 2019 Dec 18;22(1):14. doi: 10.1208/s12248-019-0399-6. PMID: 31853739; PMCID: PMC7905835.

“Finally, we chose the angle formed by Phe382's gamma carbon, Asp381's protonated side chain oxygen (OD2), and Lys378's backbone oxygen as PC3 based on observations from a study that used a similar PC to sample the DFG flip in Aurora Kinase B using metadynamics \cite{Lakkaniga2019}. This angular PC3 should increase or decrease (based on the pathway) during the DFG flip, with peak differences at intermediate DFG configurations, and then revert to its initial state when the flip concludes.”

DFG pseudodihedral definitions:

Ala380/Cb, Ala380/Ca, Asp381/Ca, Asp381/Cg

Ala380/Cb, Ala380/CA, Phe382/CA, Phe382Cg

Source: Computational Study of the “DFG-Flip” Conformational Transition in c-Abl and c-Src Tyrosine Kinases. Yilin Meng, Yen-lin Lin, and Benoît Roux The Journal of Physical Chemistry B 2015 119 (4), 1443-1456 DOI: 10.1021/jp511792a

“For downstream analysis, we used two pseudodihedrals previously defined in the existing Abl1 DFG flip simulation literature \cite{Meng2015} to identify and discriminate between DFG states. The first (dihedral 1) tracks the flip state of Asp381, and is formed by the beta carbon of Ala380, the alpha carbon of Ala380, the alpha carbon of Asp381, and the gamma carbon of Asp381. The second (dihedral 2) tracks the flip state of Phe382, and is formed by the beta carbon of Ala380, the alpha carbon of Ala380, the alpha carbon of Phe381, and the gamma carbon of Phe381. These pseudodihedrals, when plotted in relation to each other, clearly distinguish between the initial DFG-in state, the target DFG-out state, and potential intermediate states in which either Asp381 or Phe381 has flipped.”

Convergence needs to be demonstrated for estimating the population difference between different conformational states.

We agree that demonstrating convergence is important for accurate estimations of population differences between conformational states. However, as the DFG flip is a complex and concerted conformational change with an energy barrier of 30 kcal/mol [1], and considering the traditional limitations of methods like weighted ensemble molecular dynamics (WEMD), it would take an unrealistic amount of GPU time (months) to observe convergence in our simulations. As discussed in the text (see examples below), we caveat our energy estimations by explicitly mentioning that the state populations we report are not converged and are indicative of a much larger energy barrier in the mutant.

“These relative probabilities qualitatively agree with the large expected free energy barrier for the DFG-in to DFG-out transition (~32 kcal/mol), and with our observation of a putative metastable DFG-inter state that is missed by NMR experiments due to its low occupancy.”

“As an important caveat, it is unlikely that the DFG flip free energy barriers of over 70 kcal/mol estimated for the Abl1 drug-resistant variants quantitatively match the expected free energy barrier for their inactivation. Rather, our approximate free energy barriers are a symptom of the markedly increased simulation time required to sample the DFG flip in the variants relative to the wild-type, which is a strong indicator of the drastically reduced propensity of the variants to complete the DFG flip. Although longer WE simulations could allow us to access the timescales necessary for more accurately sampling the free energy barriers associated with the DFG flip in Abl1's drug-resistant compound mutants, the computational expense of running WE for 200 iterations is already large (three weeks with 8 NVIDIA RTX3900 GPUs for one replicate); this poses a logistical barrier to attempting to sample sufficient events to be able to fully characterize how the reaction path and free energy barrier change for the flip associated with the mutations. Regardless, the results of our WE simulations resoundingly show that the Glu255Lys/Val and Thr315Ile compound mutations drastically reduce the probability for DFG flip events in Abl1.”

(1) Conformational states dynamically populated by a kinase determine its function. Tao Xie et al., Science 370, eabc2754 (2020). DOI:10.1126/science.abc2754

The DFG flip needs to be sampled several times to establish free energy difference.

Our simulations have captured thousands of correlated and dozens of uncorrelated DFG flip events. The per-replicate free energy differences are computed based on the correlated transitions. Please consult the WEMD literature (referenced below and in the manuscript, references 34 and 36) for more information on how WEMD allows the sampling of multiple such events and subsequent estimation of probabilities:

Zuckermann et al (2017) 10.1146/annurev-biophys-070816-033834

Chong et al (2021) 10.1021/acs.jctc.1c01154

The free energy plots do not appear to show an intermediate state as claimed.

Both the free energy plots and the representative/anecdotal trajectories analyzed in the study show a saddle point when Asp381 has flipped but Phe382 has not (which defines the DFG-inter state), we observe a distinct change in probability when going to the pseudodihedral values associated with DFG-inter to DFG-up or DFG-out. We removed references to the putative state S1 as we we agree with the reviewer that its presence is unlikely given the data we show.

The trajectory length of 7 ns in both Figure 2 and Figure 4 needs to be verified, as it is extremely short for a DFG flip that has a high free energy barrier.

We appreciate this point. To clarify, the 7 ns segments corresponds to a collated trajectory extracted from the tens of thousands of walkers that compose the WEMD ensemble, and represent just the specific moment at which the dihedral flips occur rather than the entire flip process. On average, our WEMD simulations sample over 3 us of aggregate simulation time before the first DFG flip event is observed, in line with a high energy barrier. This is made clear in the manuscript excerpt below: “Over an aggregate simulation time of over 20 $\mu$s, we have collected dozens of uncorrelated and unbiased inactivation events, starting from the lowest energy conformation of the Abl1 kinase core (PDB 6XR6) \cite{Xie2020}.”

The free energy scale (100 kT) appears to be one order of magnitude too large.

As discussed in the text and quoted in response to comment 2, the exponential splitting nature of WEMD simulations (where the probability of individual walkers are split upon crossing each bin threshold) often leads to unrealistically high energy barriers for rare events. This is not unexpected, and as discussed in the text, we consider that value to be a qualitative measurement of the decreased probability of a DFG flip in Abl1 mutants, and not a direct measurement of energy barriers.

Setting the DFG-Asp to the protonated state is not justified, because in the DFG-in state, the DFG-Asp is clearly deprotonated.

According to previous publications, DFG-Asp is frequently protonated in the DFG-in state of Abl1 kinase. For instance, as quoted from Hanson, Chodera, et al., Cell Chem Bio (2019), “C onsistent with previous simulations on the DFG-Asp-out/in interconversion of Abl kinase we only observe the DFG flip with protonated Asp747 ( Shan et al., 2009 ). We showed previously that the pKa for the DFG-Asp in Abl is elevated at 6.5.”

Finally, the authors should discuss their work in the context of the enormous progress made in theoretical studies and mechanistic understanding of the conformational landscape of protein kinases in the last two decades, particularly with regard to the DFG flip. and The study is not very rigorous. The major conclusions do not appear to be supported. The claim that it is the first unbiased simulation to observe DFG flip is not true. For example, Hanson, Chodera et al (Cell Chem Biol 2019), Paul, Roux et al (JCTC 2020), and Tsai, Shen et al (JACS 2019) have also observed the DFG flip.

We thank the reviewer for pointing out these issues. We have revised the manuscript to better contextualize our claims within the limitations of the method and to acknowledge previous work by Hanson, Chodera et al., Paul, Roux et al., and Tsai, Shen et al.

The updated excerpt is described below

“Through our work, we have simulated an ensemble of DFG flip pathways in a wild-type kinase and its variants with atomistic resolution and without the use of biasing forces, also reporting the effects of inhibitor-resistant mutations in the broader context of kinase inactivation likelihood with such level of detail. “

Reviewer #2:

I appreciated the discussion of the strengths/weaknesses of weighted ensemble simulations. Am I correct that this method doesn't do anything to explicitly enhance sampling along orthogonal degrees of freedom? Maybe a point worth mentioning if so.

Yes, this is correct. We added a sentence to WEMD summary section of Results and Discussion discussing it.

“As a supervised enhanced sampling method, WE employs progress coordinates (PCs) to track the time-dependent evolution of a system from one or more basis states towards a target state. Although weighted ensemble simulations are unbiased in the sense that no biasing forces are added over the course of the simulations, the selection of progress coordinates and the bin definitions can potentially bias the results towards specific pathways \cite{Zuckerman2017}. Additionally, traditional WEMD simulations do not explicitly enhance sampling along orthogonal degrees of freedom (those not captured by the progress coordinates). In practice, this means that insufficient PC definitions can lead to poor sampling.”

I don't understand Figure 3C. Could the authors instead show structures corresponding to each of the states in 3B, and maybe also a representative structure for pathways 1 and 2?

We have remade Figure 3. We removed 3B and accompanying discussion as upon review we were not confident on the significance of the LPATH results where it pertains to the probability of intermediate states. We replaced 3B with a summary of the pathways 1 and 2 in regards to the Phe382 flip (which is the most contrasting difference).

Why introduce S1 and DFG-inter? And why suppose that DFG-inter is what corresponds to the excited state seen by NMR?

As a consequence of dropping the LPATH analysis, we also removed mentions to S1 as it further analysis made it hard to distinguish from DFG-in, For DFG-inter, we mention that conformation because (a) it is shared by both flipping mechanisms that we have found, and (b) it seems relevant for pharmacology, as it has been observed in other kinases such as Aurora B (PDB 2WTV), as Asp381 flipping before Phe382 creates space in the orthosteric kinase pocket which could be potentially targeted by an inhibitor.

It would be nice to have error bars on the populations reported in Figure 3.

Agreed, upon review we decided do drop the populations as we were not confident on the significance of the LPATH results where it pertains to the probability of intermediate states.

I'm confused by the attempt to relate the relative probabilities of states to the 32 kca/mol barrier previously reported between the states. The barrier height should be related to the probability of a transition. The DFG-out state could be equiprobable with the DFG-in state and still have a 32 kcal/mol barrier separating them.

Thanks for the correction, we agree with the reviewer and have amended the discussion to reflect this. Since we are starting our simulations in the DFG-in state, the probability of walkers arriving in DFG-out in our steady state WEMD simulations should (assuming proper sampling) represent the probability of the transition. We incorrectly associated the probability of the DFG-out state itself with the probability of the transition.

How do the relative probabilities of the DFG-in/out states compare to experiments, like NMR?

Previous NMR work has found the population of apo DFG in (PDB 6XR6) in solution to be around 88% for wild-type ABL1, and 6% for DFG out (PDB 6XR7). The remaining 6% represents post-DFG-out state (PDB 6XRG) where the activation loop has folded in near the hinge, which we did not simulate due to the computational cost associated with it. The same study reports the barrier height from DFG-in to DFG-out to be estimated at around 30 kcal/mol.

(1) Conformational states dynamically populated by a kinase determine its function. Tao Xie et al., Science 370, eabc2754 (2020). DOI:10.1126/science.abc2754

(we already have that in the text, just need to quote here)

“Do the staggered and concerted DFG flip pathways mentioned correspond to pathways 1 and 2 in Figure 3B, or is that a concept from previous literature?”

Yes, we have amended Figure 3B to be clearer. In previous literature both pathways have been observed [1], although not specifically defined.

Source: Computational Study of the “DFG-Flip” Conformational Transition in c-Abl and c-Src Tyrosine Kinases. Yilin Meng, Yen-lin Lin, and Benoît Roux The Journal of Physical Chemistry B 2015 119 (4), 1443-1456 DOI: 10.1021/jp511792a

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary

Query: In this manuscript, the authors introduce Gcoupler, a Python-based computational pipeline designed to identify endogenous intracellular metabolites that function as allosteric modulators at the G protein-coupled receptor (GPCR) - Gα protein interface. Gcoupler is comprised of four modules:

I. Synthesizer - identifies protein cavities and generates synthetic ligands using LigBuilder3

II. Authenticator - classifies ligands into high-affinity binders (HABs) and low-affinity binders (LABs) based on AutoDock Vina binding energies

III. Generator - trains graph neural network (GNN) models (GCM, GCN, AFP, GAT) to predict binding affinity using synthetic ligands

IV. BioRanker - prioritizes ligands based on statistical and bioactivity data

The authors apply Gcoupler to study the Ste2p-Gpa1p interface in yeast, identifying sterols such as zymosterol (ZST) and lanosterol (LST) as modulators of GPCR signaling. Our review will focus on the computational aspects of the work. Overall, we found the Gcoupler approach interesting and potentially valuable, but we have several concerns with the methods and validation that need to be addressed prior to publication/dissemination.

We express our gratitude to Reviewer #1 for their concise summary and commendation of our work. We sincerely apologize for the lack of sufficient detail in summarizing the underlying methods employed in Gcoupler, as well as its subsequent experimental validations using yeast, human cell lines, and primary rat cardiomyocyte-based assays.

We wish to state that substantial improvements have been made in the revised manuscript, every section has been elaborated upon to enhance clarity. Please refer to the point-by-point response below and the revised manuscript.

Query: (1) The exact algorithmic advancement of the Synthesizer beyond being some type of application wrapper around LigBuilder is unclear. Is the grow-link approach mentioned in the methods already a component of LigBuilder, or is it custom? If it is custom, what does it do? Is the API for custom optimization routines new with the Synthesizer, or is this a component of LigBuilder? Is the genetic algorithm novel or already an existing software implementation? Is the cavity detection tool a component of LigBuilder or novel in some way? Is the fragment library utilized in the Synthesizer the default fragment library in LigBuilder, or has it been customized? Are there rules that dictate how molecule growth can occur? The scientific contribution of the Synthesizer is unclear. If there has not been any new methodological development, then it may be more appropriate to just refer to this part of the algorithm as an application layer for LigBuilder.

We appreciate Reviewer #1's constructive suggestion. We wish to emphasize that

(1) The LigBuilder software comprises various modules designed for distinct functions. The Synthesizer in Gcoupler strategically utilizes two of these modules: "CAVITY" for binding site detection and "BUILD" for de novo ligand design.

(2) While both modules are integral to LigBuilder, the Synthesizer plays a crucial role in enabling their targeted, automated, and context-aware application for GPCR drug discovery.

(3) The CAVITY module is a structure-based protein binding site detection program, which the Synthesizer employs for identifying ligand binding sites on the protein surface.

(4) The Synthesizer also leverages the BUILD module for constructing molecules tailored to the target protein, implementing a fragment-based design strategy using its integrated fragment library.

(5) The GROW and LINK methods represent two independent approaches encompassed within the aforementioned BUILD module.

Author response image 1.

Schematic representation of the key strategy used in the Synthesizer module of Gcoupler.

Our manuscript details the "grow-link" hybrid approach, which was implemented using a genetic algorithm through the following stages:

(1) Initial population generation based on a seed structure via the GROW method.

(2) Selection of "parent" molecules from the current population for inclusion in the mating pool using the LINK method.

(3) Transfer of "elite" molecules from the current population to the new population.

(4) Population expansion through structural manipulations (mutation, deletion, and crossover) applied to molecules within the mating pool.

Please note, the outcome of this process is not fixed, as it is highly dependent on the target cavity topology and the constraint parameters employed for population evaluation. Synthesizer customizes generational cycles and optimization parameters based on cavity-specific constraints, with the objective of either generating a specified number of compounds or comprehensively exploring chemical diversity against a given cavity topology.

While these components are integral to LigBuilder, Synthesizer's innovation lies

(1) in its programmatic integration and dynamic adjustment of these modules.

(2) Synthesizer distinguishes itself not by reinventing these algorithms, but by their automated coordination, fine-tuning, and integration within a cavity-specific framework.

(3) It dynamically modifies generation parameters according to cavity topology and druggability constraints, a capability not inherently supported by LigBuilder.

(4) This renders Synthesizer particularly valuable in practical scenarios where manual optimization is either inefficient or impractical.

In summary, Synthesizer offers researchers a streamlined interface, abstracting the technical complexities of LigBuilder and thereby enabling more accessible and reproducible ligand generation pipelines, especially for individuals with limited experience in structural or cheminformatics tools.

Query: (2) The use of AutoDock Vina binding energy scores to classify ligands into HABs and LABs is problematic. AutoDock Vina's energy function is primarily tuned for pose prediction and displays highly system-dependent affinity ranking capabilities. Moreover, the HAB/LAB thresholds of -7 kcal/mol or -8 kcal/mol lack justification. Were these arbitrarily selected cutoffs, or was benchmarking performed to identify appropriate cutoffs? It seems like these thresholds should be determined by calibrating the docking scores with experimental binding data (e.g., known binders with measured affinities) or through re-scoring molecules with a rigorous alchemical free energy approach.

We again express our gratitude to Reviewer #1 for these inquiries. We sincerely apologize for the lack of sufficient detail in the original version of the manuscript. In the revised manuscript, we have ensured the inclusion of a detailed rationale for every threshold utilized to prioritize high-affinity binders. Please refer to the comprehensive explanation below, as well as the revised manuscript, for further details.

We would like to clarify that:

(1) The Authenticator module is not solely reliant on absolute binding energy values for classification. Instead, it calculates binding energies for all generated compounds and applies a statistical decision-making layer to define HAB and LAB classes.

(2) Rather than using fixed thresholds, the module employs distribution-based methods, such as the Empirical Cumulative Distribution Function (ECDF), to assess the overall energy landscape of the compound set. We then applied multiple statistical tests to evaluate the HAB and LAB distributions and determine an optimal, data-specific cutoff that balances class sizes and minimizes overlap.

(3) This adaptive approach avoids rigid thresholds and instead ensures context-sensitive classification, with safeguards in place to maintain adequate representation of both classes for downstream model training, and in this way, the framework prioritizes robust statistical reasoning over arbitrary energy cutoffs and aims to reduce the risks associated with direct reliance on Vina scores alone.

(4) To assess the necessity and effectiveness of the Authenticator module, we conducted a benchmarking analysis where we deliberately omitted the HAB and LAB class labels, treating the compound pool as a heterogeneous, unlabeled dataset. We then performed random train-test splits using the Synthesizer-generated compounds and trained independent models.

(5) The results from this approach demonstrated notably poorer model performance, indicating that arbitrary or unstructured data partitioning does not effectively capture the underlying affinity patterns. These experiments highlight the importance of using the statistical framework within the Authenticator module to establish meaningful, data-driven thresholds for distinguishing High- and Low-Affinity Binders. The cutoff values are thus not arbitrary but emerge from a systematic benchmarking and validation process tailored to each dataset.

Please note: While calibrating docking scores with experimental binding affinities or using rigorous methods like alchemical free energy calculations can improve precision, these approaches are often computationally intensive and reliant on the availability of high-quality experimental data, a major limitation in many real-world screening scenarios.

In summary, the primary goal of Gcoupler is to enable fast, scalable, and broadly accessible screening, particularly for cases where experimental data is sparse or unavailable. Incorporating such resource-heavy methods would not only significantly increase computational overhead but also undermine the framework’s intended usability and efficiency for large-scale applications. Instead, our workflow relies on statistically robust, data-driven classification methods that balance speed, generalizability, and practical feasibility.

Query: (3) Neither the Results nor Methods sections provide information on how the GNNs were trained in this study. Details such as node features, edge attributes, standardization, pooling, activation functions, layers, dropout, etc., should all be described in detail. The training protocol should also be described, including loss functions, independent monitoring and early stopping criteria, learning rate adjustments, etc.

We again thank Reviewer #1 for this suggestion. We would like to mention that in the revised manuscript, we have added all the requested details. Please refer to the points below for more information.

(1) The Generator module of Gcoupler is designed as a flexible and automated framework that leverages multiple Graph Neural Network architectures, including Graph Convolutional Model (GCM), Graph Convolutional Network (GCN), Attentive FP, and Graph Attention Network (GAT), to build classification models based on the synthetic ligand datasets produced earlier in the pipeline.

(2) By default, Generator tests all four models using standard hyperparameters provided by the DeepChem framework (https://deepchem.io/), offering a baseline performance comparison across architectures. This includes pre-defined choices for node features, edge attributes, message-passing layers, pooling strategies, activation functions, and dropout values, ensuring reproducibility and consistency. All models are trained with binary cross-entropy loss and support default settings for early stopping, learning rate, and batch standardization where applicable.

(3) In addition, Generator supports model refinement through hyperparameter tuning and k-fold cross-validation (default: 3 folds). Users can either customize the hyperparameter grid or rely on Generator’s recommended parameter ranges to optimize model performance. This allows for robust model selection and stability assessment of tuned parameters.

(4) Finally, the trained models can be used to predict binding probabilities for user-supplied compounds, making it a comprehensive and user-adaptive tool for ligand screening.

Based on the reviewer #1 suggestion, we have now added a detailed description about the Generator module of Gcoupler, and also provided relevant citations regarding the DeepChem workflow.

Query: (4) GNN model training seems to occur on at most 500 molecules per training run? This is unclear from the manuscript. That is a very small number of training samples if true. Please clarify. How was upsampling performed? What were the HAB/LAB class distributions? In addition, it seems as though only synthetically generated molecules are used for training, and the task is to discriminate synthetic molecules based on their docking scores. Synthetic ligands generated by LigBuilder may occupy distinct chemical space, making classification trivial, particularly in the setting of a random split k-folds validation approach. In the absence of a leave-class-out validation, it is unclear if the model learns generalizable features or exploits clear chemical differences. Historically, it was inappropriate to evaluate ligand-based QSAR models on synthetic decoys such as the DUD-E sets - synthetic ligands can be much more easily distinguished by heavily parameterized ligand-based machine learning models than by physically constrained single-point docking score functions.

We thank reviewer #1 for these detailed technical queries. We would like to clarify that:

(1) The recommended minimum for the training set is 500 molecules, but users can add as many synthesized compounds as needed to thoroughly explore the chemical space related to the target cavity.

(2) Our systematic evaluation demonstrated that expanding the training set size consistently enhanced model performance, especially when compared to AutoDock docking scores. This observation underscores the framework's scalability and its ability to improve predictive accuracy with more training compounds.

(3) The Authenticator module initially categorizes all synthesized molecules into HAB and LAB classes. These labeled molecules are then utilized for training the Generator module. To tackle class imbalance, the class with fewer data points undergoes upsampling. This process aims to achieve an approximate 1:1 ratio between the two classes, thereby ensuring balanced learning during GNN model training.

(4) The Authenticator module's affinity scores are the primary determinant of the HAB/LAB class distribution, with a higher cutoff for HABs ensuring statistically significant class separation. This distribution is also indirectly shaped by the target cavity's topology and druggability, as the Synthesizer tends to produce more potent candidates for cavities with favorable binding characteristics.

(5) While it's true that synthetic ligands may occupy distinct chemical space, our benchmarking exploration for different sites on the same receptor still showed inter-cavity specificity along with intra-cavity diversity of the synthesized molecules.

(6) The utility of random k-fold validation shouldn't be dismissed outright; it provides a reasonable estimate of performance under practical settings where class boundaries are often unknown. Nonetheless, we agree that complementary validation strategies like leave-class-out could further strengthen the robustness assessment.

(7) We agree that using synthetic decoys like those from the DUD-E dataset can introduce bias in ligand-based QSAR model evaluations if not handled carefully. In our workflow, the inclusion of DUD-E compounds is entirely optional and only considered as a fallback, specifically in scenarios where the number of low-affinity binders (LABs) synthesized by the Synthesizer module is insufficient to proceed with model training.

(8) The primary approach relies on classifying generated compounds based on their derived affinity scores via the Authenticator module. However, in rare cases where this results in a heavily imbalanced dataset, DUD-E compounds are introduced not as part of the core benchmarking, but solely to maintain minimal class balance for initial model training. Even then, care is taken to interpret results with this limitation in mind. Ultimately, our framework is designed to prioritize data-driven generation of both HABs and LABs, minimizing reliance on synthetic decoys wherever possible.

Author response image 2.

Scatter plots depicting the segregation of High/Low-Affinity Metabolites (HAM/LAM) (indicated in green and red) identified using Gcoupler workflow with 100% training data. Notably, models trained on lesser training data size (25%, 50%, and 75% of HAB/LAB) severely failed to segregate HAM and LAM (along Y-axis). X-axis represents the binding affinity calculated using IC4-specific docking using AutoDock.

Based on the reviewer #1’s suggestion, we have now added all these technical details in the revised version of the manuscript.

Query: (5) Training QSAR models on docking scores to accelerate virtual screening is not in itself novel (see here for a nice recent example: https://www.nature.com/articles/s43588-025-00777-x), but can be highly useful to focus structure-based analysis on the most promising areas of ligand chemical space; however, we are perplexed by the motivation here. If only a few hundred or a few thousand molecules are being sampled, why not just use AutoDock Vina? The models are trained to try to discriminate molecules by AutoDock Vina score rather than experimental affinity, so it seems like we would ideally just run Vina? Perhaps we are misunderstanding the scale of the screening that was done here. Please clarify the manuscript methods to help justify the approach.

We acknowledge the effectiveness of training QSAR models on docking scores for prioritizing chemical space, as demonstrated by the referenced study (https://www.nature.com/articles/s43588-025-00777-x) on machine-learning-guided docking screen frameworks.

We would like to mention that:

(1) While such protocols often rely on extensive pre-docked datasets across numerous protein targets or utilize a highly skewed input distribution, training on as little as 1-10% of ligand-protein complexes and testing on the remainder in iterative cycles.

(2) While powerful for ultra-large libraries, this approach can introduce bias towards the limited training set and incur significant overhead in data curation, pre-computation, and infrastructure.

(3) In contrast, Gcoupler prioritizes flexibility and accessibility, especially when experimental data is scarce and large pre-docked libraries are unavailable. Instead of depending on fixed docking scores from external pipelines, Gcoupler integrates target-specific cavity detection, de novo compound generation, and model training into a self-contained, end-to-end framework. Its QSAR models are trained directly on contextually relevant compounds synthesized for a given binding site, employing a statistical classification strategy that avoids arbitrary thresholds or precomputed biases.

(4) Furthermore, Gcoupler is open-source, lightweight, and user-friendly, making it easily deployable without the need for extensive infrastructure or prior docking expertise. While not a complete replacement for full-scale docking in all use cases, Gcoupler aims to provide a streamlined and interpretable screening framework that supports both focused chemical design and broader chemical space exploration, without the computational burden associated with deep learning docking workflows.

(5) Practically, even with computational resources, manually running AutoDock Vina on millions of compounds presents challenges such as format conversion, binding site annotation, grid parameter tuning, and execution logistics, all typically requiring advanced structural bioinformatics expertise.

(6) Gcoupler's Authenticator module, however, streamlines this process. Users only need to input a list of SMILES and a receptor PDB structure, and the module automatically handles compound preparation, cavity mapping, parameter optimization, and high-throughput scoring. This automation reduces time and effort while democratizing access to structure-based screening workflows for users without specialized expertise.

Ultimately, Gcoupler's motivation is to make large-scale, structure-informed virtual screening both efficient and accessible. The model serves as a surrogate to filter and prioritize compounds before deeper docking or experimental validation, thereby accelerating targeted drug discovery.

Query: (6) The brevity of the MD simulations raises some concerns that the results may be over-interpreted. RMSD plots do not reliably compare the affinity behavior in this context because of the short timescales coupled with the dramatic topological differences between the ligands being compared; CoQ6 is long and highly flexible compared to ZST and LST. Convergence metrics, such as block averaging and time-dependent MM/GBSA energies, should be included over much longer timescales. For CoQ6, the authors may need to run multiple simulations of several microseconds, identify the longest-lived metastable states of CoQ6, and perform MM/GBSA energies for each state weighted by each state's probability.

We appreciate Reviewer #1's suggestion regarding simulation length, as it is indeed crucial for interpreting molecular dynamics (MD) outcomes. We would like to mention that:

(1) Our simulation strategy varied based on the analysis objective, ranging from short (~5 ns) runs for preliminary or receptor-only evaluations to intermediate (~100 ns) and extended (~550 ns) runs for receptor-ligand complex validation and stability assessment.

(2) Specifically, we conducted three independent 100 ns MD simulations for each receptor-metabolite complex in distinct cavities of interest. This allowed us to assess the reproducibility and persistence of binding interactions. To further support these observations, a longer 550 ns simulation was performed for the IC4 cavity, which reinforced the 100 ns findings by demonstrating sustained interaction stability over extended timescales.

(3) While we acknowledge that even longer simulations (e.g., in the microsecond range) could provide deeper insights into metastable state transitions, especially for highly flexible molecules like CoQ6, our current design balances computational feasibility with the goal of screening multiple cavities and ligands.

(4) In our current workflow, MM/GBSA binding free energies were calculated by extracting 1000 representative snapshots from the final 10 ns of each MD trajectory. These configurations were used to compute time-averaged binding energies, incorporating contributions from van der Waals, electrostatic, polar, and non-polar solvation terms. This approach offers a more reliable estimate of ligand binding affinity compared to single-point molecular docking, as it accounts for conformational flexibility and dynamic interactions within the binding cavity.

(5) Although we did not explicitly perform state-specific MM/GBSA calculations weighted by metastable state probabilities, our use of ensemble-averaged energy estimates from a thermally equilibrated segment of the trajectory captures many of the same benefits. We acknowledge, however, that a more rigorous decomposition based on metastable state analysis could offer finer resolution of binding behavior, particularly for highly flexible ligands like CoQ6, and we consider this a valuable direction for future refinement of the framework.

Reviewer #2 (Public review):

Summary:

Query: Mohanty et al. present a new deep learning method to identify intracellular allosteric modulators of GPCRs. This is an interesting field for e.g. the design of novel small molecule inhibitors of GPCR signalling. A key limitation, as mentioned by the authors, is the limited availability of data. The method presented, Gcoupler, aims to overcome these limitations, as shown by experimental validation of sterols in the inhibition of Ste2p, which has been shown to be relevant molecules in human and rat cardiac hypertrophy models. They have made their code available for download and installation, which can easily be followed to set up software on a local machine.

Strengths:

Clear GitHub repository

Extensive data on yeast systems

We sincerely thank Reviewer #2 for their thorough review, summary, and appreciation of our work. We highly value their comments and suggestions.

Weaknesses:

Query: No assay to directly determine the affinity of the compounds to the protein of interest.

We thank Reviewer #2 for raising these insightful questions. During the experimental design phase, we carefully accounted for validating the impact of metabolites in the rescue response by pheromone.

We would like to mention that we performed an array of methods to validate our hypothesis and observed similar rescue effects. These assays include:

a. Cell viability assay (FDA/PI Flourometry-based)

b. Cell growth assay

c. FUN1^TM-based microscopy assessment

d. Shmoo formation assays

e. Mating assays

f. Site-directed mutagenesis-based loss of function

g. ransgenic reporter-based assay

h. MAPK signaling assessment using Western blot.

i. And via computational techniques.

Concerning the in vitro interaction studies of Ste2p and metabolites, we made significant efforts to purify Ste2p by incorporating a His tag at the N-terminal. Despite dedicated attempts over the past year, we were unsuccessful in purifying the protein, primarily due to our limited expertise in protein purification for this specific system. As a result, we opted for genetic-based interventions (e.g., point mutants), which provide a more physiological and comprehensive approach to demonstrating the interaction between Ste2p and the metabolites.

Author response image 3.

(a) Affinity purification of Ste2p from Saccharomyces cerevisiae. Western blot analysis using anti-His antibody showing the distribution of Ste2p in various fractions during the affinity purification process. The fractions include pellet, supernatant, wash buffer, and sequential elution fractions (1–4). Wild-type and ste2Δ strains served as positive and negative controls, respectively. (b) Optimization of Ste2p extraction protocol. Ponceau staining (left) and Western blot analysis using anti-His antibody (right) showing Ste2p extraction efficiency. The conditions tested include lysis buffers containing different concentrations of CHAPS detergent (0.5%, 1%) and glycerol (10%, 20%).

Furthermore, in addition to the clarification above, we have added the following statement in the discussion section to tone down our claims: “A critical limitation of our study is the absence of direct binding assays to validate the interaction between the metabolites and Ste2p. While our results from genetic interventions, molecular dynamics simulations, and docking studies strongly suggest that the metabolites interact with the Ste2p-Gpa1 interface, these findings remain indirect. Direct binding confirmation through techniques such as surface plasmon resonance, isothermal titration calorimetry, or co-crystallization would provide definitive evidence of this interaction. Addressing this limitation in future work would significantly strengthen our conclusions and provide deeper insights into the precise molecular mechanisms underlying the observed phenotypic effects.”

We request Reviewer #2 to kindly refer to the assays conducted on the point mutants created in this study, as these experiments offer robust evidence supporting our claims.

Query: In conclusion, the authors present an interesting new method to identify allosteric inhibitors of GPCRs, which can easily be employed by research labs. Whilst their efforts to characterize the compounds in yeast cells, in order to confirm their findings, it would be beneficial if the authors show their compounds are active in a simple binding assay.

We express our gratitude and sincere appreciation for the time and effort dedicated by Reviewer #2 in reviewing our manuscript. We are confident that our clarifications address the reviewer's concerns.

Reviewer #3 (Public review):

Summary:

Query: In this paper, the authors introduce the Gcoupler software, an open-source deep learning-based platform for structure-guided discovery of ligands targeting GPCR interfaces. Overall, this manuscript represents a field-advancing contribution at the intersection of AI-based ligand discovery and GPCR signaling regulation.

Strengths:

The paper presents a comprehensive and well-structured workflow combining cavity identification, de novo ligand generation, statistical validation, and graph neural network-based classification. Notably, the authors use Gcoupler to identify endogenous intracellular sterols as allosteric modulators of the GPCR-Gα interface in yeast, with experimental validations extending to mammalian systems. The ability to systematically explore intracellular metabolite modulation of GPCR signaling represents a novel and impactful contribution. This study significantly advances the field of GPCR biology and computational ligand discovery.

We thank and appreciate Reviewer #3 for vesting time and efforts in reviewing our manuscript and for appreciating our efforts.

Recommendations for the authors:

Reviewing Editor Comments:

We encourage the authors to address the points raised during revision to elevate the assessment from "incomplete" to "solid" or ideally "convincing." In particular, we ask the authors to improve the justification for their methodological choices and to provide greater detail and clarity regarding each computational layer of the pipeline.

We are grateful for the editors' suggestions. We have incorporated significant revisions into the manuscript, providing comprehensive technical details to prevent any misunderstandings. Furthermore, we meticulously explained every aspect of the computational workflow.

Reviewer #2 (Recommendations for the authors):

Query: Would it be possible to make the package itself pip installable?

Yes, it already exists under the testpip repository and we have now migrated it to the main pip. Please access the link from here: https://pypi.org/project/gcoupler/

Query: I am confused by the binding free energies reported in Supplementary Figure 8. Is the total DG reported that of the protein-ligand complex? If that is the case, the affinities of the ligands would be extremely high. They are also very far off from the reported -7 kcal/mol active/inactive cut-off.

We thank Reviewer #2 for this query. We would like to mention that we have provided a detailed explanation in the point-by-point response to Reviewer #2's original comment. Briefly, to clarify, the -7 kcal/mol active/inactive cutoff mentioned in the manuscript refers specifically to the docking-based binding free energies (ΔG) calculated using AutoDock or AutoDock Vina, which are used for compound classification or validation against the Gcoupler framework.

In contrast, the binding free energies reported in Supplementary Figure 8 are obtained through the MM-GBSA method, which provides a more detailed and physics-based estimate of binding affinity by incorporating solvation and enthalpic contributions. It is well-documented in the literature that MM-GBSA tends to systematically underestimate absolute binding free energies when compared to experimental values (10.2174/1568026616666161117112604; Table 1).

Author response image 4.

Scatter plot comparing the predicted binding affinity calculated by Docking and MM/GBSA methods, against experimental ΔG (10.1007/s10822-023-00499-0)

Our use of MM-GBSA is not to match experimental ΔG directly, but rather to assess relative binding preferences among ligands. Despite its limitations in predicting absolute affinities, MM-GBSA is known to perform better than docking for ranking compounds by their binding potential. In this context, an MM-GBSA energy value still reliably indicates stronger predicted binding, even if the numerical values appear extremely higher than typical experimental or docking-derived cutoffs.

Thus, the two energy values, docking-based and MM-GBSA, serve different purposes in our workflow. Docking scores are used for classification and thresholding, while MM-GBSA energies provide post hoc validation and a higher-resolution comparison of binding strength across compounds.

To corroborate their findings, can the authors include direct binding affinity assays for yeast and human Ste2p? This will help in establishing whether the observed phenotypic effects are indeed driven by binding of the metabolites.

We thank Reviewer #2 for raising these insightful questions. During the experimental design phase, we carefully accounted for validating the impact of metabolites in the rescue response by pheromone.

We would like to mention that we performed an array of methods to validate our hypothesis and observed similar rescue effects. These assays include:

a. Cell viability assay (FDA/PI Flourometry- based)

b. Cell growth assay

c. FUN1^TM-based microscopy assessment

d. Shmoo formation assays

e. Mating assays

f. Site-directed mutagenesis-based loss of function

g. Transgenic reporter-based assay

h. MAPK signaling assessment using Western blot.

i. And via computational techniques.

Concerning the in vitro interaction studies of Ste2p and metabolites, we made significant efforts to purify Ste2p by incorporating a His tag at the N-terminal. Despite dedicated attempts over the past year, we were unsuccessful in purifying the protein, primarily due to our limited expertise in protein purification for this specific system. As a result, we opted for genetic-based interventions (e.g., point mutants), which provide a more physiological and comprehensive approach to demonstrating the interaction between Ste2p and the metabolites.

Furthermore, in addition to the clarification above, we have added the following statement in the discussion section to tone down our claims: “A critical limitation of our study is the absence of direct binding assays to validate the interaction between the metabolites and Ste2p. While our results from genetic interventions, molecular dynamics simulations, and docking studies strongly suggest that the metabolites interact with the Ste2p-Gpa1 interface, these findings remain indirect. Direct binding confirmation through techniques such as surface plasmon resonance, isothermal titration calorimetry, or co-crystallization would provide definitive evidence of this interaction. Addressing this limitation in future work would significantly strengthen our conclusions and provide deeper insights into the precise molecular mechanisms underlying the observed phenotypic effects.”

We request Reviewer #2 to kindly refer to the assays conducted on the point mutants created in this study, as these experiments offer robust evidence supporting our claims.

Did the authors perform expression assays to make sure the mutant proteins were similarly expressed to wt?

We thank reviewer #2 for this comment. We would like to mention that:

(1) In our mutants (S75A, T155D, L289K)-based assays, all mutants were generated using integration at the same chromosomal TRP1 locus under the GAL1 promoter and share the same C-terminal CYC1 terminator sequence used for the reconstituted wild-type (rtWT) construct, thus reducing the likelihood of strain-specific expression differences.

(2) Furthermore, all strains were grown under identical conditions using the same media, temperature, and shaking parameters. Each construct underwent the same GAL1 induction protocol in YPGR medium for identical durations, ensuring uniform transcriptional activation across all strains and minimizing culture-dependent variability in protein expression.

(3) Importantly, both the rtWT and two of the mutants (T155D, L289K) retained α-factor-induced cell death (PI and FUN1-based fluorometry and microscopy; Figure 4c-d) and MAPK activation (western blot; Figure 4e), demonstrating that the mutant proteins are expressed at levels sufficient to support signalling.

Reviewer #3 (Recommendations for the authors):

My comments that would enhance the impact of this method are:

(1) While the authors have compared the accuracy and efficiency of Gcoupler to AutoDock Vina, one of the main points of Gcoupler is the neural network module. It would be beneficial to have it evaluated against other available deep learning ligand generative modules, such as the following: 10.1186/s13321-024-00829-w, 10.1039/D1SC04444C.

Thank you for the observation. To clarify, our benchmarking of Gcoupler’s accuracy and efficiency was performed against AutoDock, not AutoDock Vina. This choice was intentional, as AutoDock is one of the most widely used classical techniques in computer-aided drug design (CADD) for obtaining high-resolution predictions of ligand binding energy, binding poses, and detailed atomic-level interactions with receptor residues. In contrast, AutoDock Vina is primarily optimized for large-scale virtual screening, offering faster results but typically with lower resolution and limited configurational detail.

Since Gcoupler is designed to balance accuracy with computational efficiency in structure-based screening, AutoDock served as a more appropriate reference point for evaluating its predictions.

We agree that benchmarking against other deep learning-based ligand generative tools is important for contextualizing Gcoupler’s capabilities. However, it's worth noting that only a few existing methods focus specifically on cavity- or pocket-driven de novo drug design using generative AI, and among them, most are either partially closed-source or limited in functionality.

While PocketCrafter (10.1186/s13321-024-00829-w) offers a structure-based generative framework, it differs from Gcoupler in several key respects. PocketCrafter requires proprietary preprocessing tools, such as the MOE QuickPrep module, to prepare protein pocket structures, limiting its accessibility and reproducibility. In addition, PocketCrafter’s pipeline stops at the generation of cavity-linked compounds and does not support any further learning from the generated data.

Similarly, DeepLigBuilder (10.1039/D1SC04444C) provides de novo ligand generation using deep learning, but the source code is not publicly available, preventing direct benchmarking or customization. Like PocketCrafter, it also lacks integrated learning modules, which limits its utility for screening large, user-defined libraries or compounds of interest.

Additionally, tools like AutoDesigner from Schrödinger, while powerful, are not publicly accessible and hence fall outside the scope of open benchmarking.

Author response table 1.

Comparison of de novo drug design tools. SBDD refers to Structure-Based Drug Design, and LBDD refers to Ligand-Based Drug Design.

In contrast, Gcoupler is a fully open-source, end-to-end platform that integrates both Ligand-Based and Structure-Based Drug Design. It spans from cavity detection and molecule generation to automated model training using GNNs, allowing users to evaluate and prioritize candidate ligands across large chemical spaces without the need for commercial software or advanced coding expertise.

(2) In Figure 2, the authors mention that IC4 and IC5 potential binding sites are on the direct G protein coupling interface ("This led to the identification of 17 potential surface cavities on Ste2p, with two intracellular regions, IC4 and IC5, accounting for over 95% of the Ste2p-Gpa1p interface (Figure 2a-b, Supplementary Figure 4j-n)..."). Later, however, in Figure 4, when discussing which residues affect the binding of the metabolites the most, the authors didn't perform MD simulations of mutant STE2 and just Gpa1p (without metabolites present). It would be beneficial to compare the binding of G protein with and without metabolites present, as these interface mutations might be affecting the binding of G protein by itself.

Thank you for this insightful suggestion. While we did not perform in silico MD simulations of the mutant Ste2-Gpa1 complex in the absence of metabolites, we conducted experimental validation to functionally assess the impact of interface mutations. Specifically, we generated site-directed mutants (S75A, L289K, T155D) and expressed them in a ste2Δ background to isolate their effects.

As shown in the Supplementary Figure, these mutants failed to rescue cells from α-factor-induced programmed cell death (PCD) upon metabolite pre-treatment. This was confirmed through fluorometry-based viability assays, FUN1^TM staining, and p-Fus3 signaling analysis, which collectively monitor MAPK pathway activation (Figure 4c–e).

Importantly, the induction of PCD in response to α-factor in these mutants demonstrates that G protein coupling is still functionally intact, indicating that the mutations do not interfere with Gpa1 binding itself. However, the absence of rescue by metabolites strongly suggests that the mutated residues play a direct role in metabolite binding at the Ste2p–Gpa1p interface, thus modulating downstream signaling.

While further MD simulations could provide structural insight into the isolated mutant receptor–G protein interaction, our experimental data supports the functional relevance of metabolite binding at the identified interface.

(3) While the experiments, performed by the authors, do support the hypothesis that metabolites regulate GPCR signaling, there are no experiments evaluating direct biophysical measurements (e.g., dissociation constants are measured only in silicon).

We thank Reviewer #3 for raising these insightful comments. We would like to mention that we performed an array of methods to validate our hypothesis and observed similar rescue effects. These assays include:

a. Cell viability assay (FDA/PI Flourometry- based)

b. Cell growth assay

c. FUN1^TM-based microscopy assessment

d. Shmoo formation assays

e. Mating assays

f. Site-directed mutagenesis-based loss of function

g. Transgenic reporter-based assay

h. MAPK signaling assessment using Western blot.

i. And via computational techniques.

Concerning the direct biophysical measurements of Ste2p and metabolites, we made significant efforts to purify Ste2p by incorporating a His tag at the N-terminal, with the goal of performing Microscale Thermophoresis (MST) and Isothermal Titration Calorimetry (ITC) measurements. Despite dedicated attempts over the past year, we were unsuccessful in purifying the protein, primarily due to our limited expertise in protein purification for this specific system. As a result, we opted for genetic-based interventions (e.g., point mutants), which provide a more physiological and comprehensive approach to demonstrating the interaction between Ste2p and the metabolites.

Furthermore, in addition to the clarification above, we have added the following statement in the discussion section to tone down our claims: “A critical limitation of our study is the absence of direct binding assays to validate the interaction between the metabolites and Ste2p. While our results from genetic interventions, molecular dynamics simulations, and docking studies strongly suggest that the metabolites interact with the Ste2p-Gpa1 interface, these findings remain indirect. Direct binding confirmation through techniques such as surface plasmon resonance, isothermal titration calorimetry, or co-crystallization would provide definitive evidence of this interaction. Addressing this limitation in future work would significantly strengthen our conclusions and provide deeper insights into the precise molecular mechanisms underlying the observed phenotypic effects.”

(4) The authors do not discuss the effects of the metabolites at their physiological concentrations. Overall, this manuscript represents a field-advancing contribution at the intersection of AI-based ligand discovery and GPCR signaling regulation.

We thank reviewer #3 for this comment and for recognising the value of our work. Although direct quantification of intracellular free metabolite levels is challenging, several lines of evidence support the physiological relevance of our test concentrations.

- Genetic validation supports endogenous relevance: Our genetic screen of 53 metabolic knockout mutants showed that deletions in biosynthetic pathways for these metabolites consistently disrupted the α-factor-induced cell death, with the vast majority of strains (94.4%) resisting the α-factor-induced cell death, and notably, a subset even displayed accelerated growth in the presence of α‑factor. This suggests that endogenous levels of these metabolites normally provide some degree of protection, supporting their physiological role in GPCR regulation.

- Metabolomics confirms in vivo accumulation: Our untargeted metabolomics analysis revealed that α-factor-treated survivors consistently showed enrichment of CoQ6 and zymosterol compared to sensitive cells. This demonstrates that these metabolites naturally accumulate to protective levels during stress responses, validating their biological relevance.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

This study investigates the sex determination mechanism in the clonal ant Ooceraea biroi, focusing on a candidate complementary sex determination (CSD) locus-one of the key mechanisms supporting haplodiploid sex determination in hymenopteran insects. Using whole genome sequencing, the authors analyze diploid females and the rarely occurring diploid males of O. biroi, identifying a 46 kb candidate region that is consistently heterozygous in females and predominantly homozygous in diploid males. This region shows elevated genetic diversity, as expected under balancing selection. The study also reports the presence of an lncRNA near this heterozygous region, which, though only distantly related in sequence, resembles the ANTSR lncRNA involved in female development in the Argentine ant, Linepithema humile (Pan et al. 2024). Together, these findings suggest a potentially conserved sex determination mechanism across ant species. However, while the analyses are well conducted and the paper is clearly written, the insights are largely incremental. The central conclusion - that the sex determination locus is conserved in ants - was already proposed and experimentally supported by Pan et al. (2024), who included O. biroi among the studied species and validated the locus's functional role in the Argentine ant. The present study thus largely reiterates existing findings without providing novel conceptual or experimental advances.

Although it is true that Pan et al., 2024 demonstrated (in Figure 4 of their paper) that the synteny of the region flanking ANTSR is conserved across aculeate Hymenoptera (including O. biroi), Reviewer 1’s claim that that paper provides experimental support for the hypothesis that the sex determination locus is conserved in ants is inaccurate. Pan et al., 2024 only performed experimental work in a single ant species (Linepithema humile) and merely compared reference genomes of multiple species to show synteny of the region, rather than functionally mapping or characterizing these regions.

Other comments:

The mapping is based on a very small sample size: 19 females and 16 diploid males, and these all derive from a single clonal line. This implies a rather high probability for false-positive inference. In combination with the fact that only 11 out of the 16 genotyped males are actually homozygous at the candidate locus, I think a more careful interpretation regarding the role of the mapped region in sex determination would be appropriate. The main argument supporting the role of the candidate region in sex determination is based on the putative homology with the lncRNA involved in sex determination in the Argentine ant, but this argument was made in a previous study (as mentioned above).

Our main argument supporting the role of the candidate region in sex determination is not based on putative homology with the lncRNA in L. humile. Instead, our main argument comes from our genetic mapping (in Fig. 2), and the elevated nucleotide diversity within the identified region (Fig. 4). Additionally, we highlight that multiple genes within our mapped region are homologous to those in mapped sex determining regions in both L. humile and Vollenhovia emeryi, possibly including the lncRNA.

In response to the Reviewer’s assertion that the mapping is based on a small sample size from a single clonal line, we want to highlight that we used all diploid males available to us. Although the primary shortcoming of a small sample size is to increase the probability of a false negative, small sample sizes can also produce false positives. We used two approaches to explore the statistical robustness of our conclusions. First, we generated a null distribution by randomly shuffling sex labels within colonies and calculating the probability of observing our CSD index values by chance (shown in Fig. 2). Second, we directly tested the association between homozygosity and sex using Fisher’s Exact Test (shown in Supplementary Fig. S2). In both cases, the association of the candidate locus with sex was statistically significant after multiple-testing correction using the Benjamini-Hochberg False Discovery Rate. These approaches are clearly described in the “CSD Index Mapping” section of the Methods.

We also note that, because complementary sex determination loci are expected to evolve under balancing selection, our finding that the mapped region exhibits a peak of nucleotide diversity lends orthogonal support to the notion that the mapped locus is indeed a complementary sex determination locus.

The fourth paragraph of the results and the sixth paragraph of the discussion are devoted to explaining the possible reasons why only 11/16 genotyped males are homozygous in the mapped region. The revised manuscript will include an additional sentence (in what will be lines 384-388) in this paragraph that includes the possible explanation that this locus is, in fact, a false positive, while also emphasizing that we find this possibility to be unlikely given our multiple lines of evidence.

In response to Reviewer 1’s suggestion that we carefully interpret the role of the mapped region in sex determination, we highlight our careful wording choices, nearly always referring to the mapped locus as a “candidate sex determination locus” in the title and throughout the manuscript. For consistency, the revised manuscript version will change the second results subheading from “The O. biroi CSD locus is homologous to another ant sex determination locus but not to honeybee csd” to “O. biroi’s candidate CSD locus is homologous to another ant sex determination locus but not to honeybee csd,” and will add the word “candidate” in what will be line 320 at the beginning of the Discussion, and will change “putative” to “candidate” in what will be line 426 at the end of the Discussion.

In the abstract, it is stated that CSD loci have been mapped in honeybees and two ant species, but we know little about their evolutionary history. But CSD candidate loci were also mapped in a wasp with multi-locus CSD (study cited in the introduction). This wasp is also parthenogenetic via central fusion automixis and produces diploid males. This is a very similar situation to the present study and should be referenced and discussed accordingly, particularly since the authors make the interesting suggestion that their ant also has multi-locus CSD and neither the wasp nor the ant has tra homologs in the CSD candidate regions. Also, is there any homology to the CSD candidate regions in the wasp species and the studied ant?

In response to Reviewer 1’s suggestion that we reference the (Matthey-Doret et al. 2019) study in the context of diploid males being produced via losses of heterozygosity during asexual reproduction, the revised manuscript will include (in what will be lines 123-126) the highlighted portion of the following sentence: “Therefore, if O. biroi uses CSD, diploid males might result from losses of heterozygosity at sex determination loci (Fig. 1C), similar to what is thought to occur in other asexual Hymenoptera that produce diploid males (Rabeling and Kronauer 2012; Matthey-Doret et al. 2019).”

We note, however, that in their 2019 study, Matthey-Doret et al. did not directly test the hypothesis that diploid males result from losses of heterozygosity at CSD loci during asexual reproduction, because the diploid males they used for their mapping study came from inbred crosses in a sexual population of that species.

We address this further below, but we want to emphasize that we do not intend to argue that O. biroi has multiple CSD loci. Instead, we suggest that additional, undetected CSD loci is one possible explanation for the absence of diploid males from any clonal line other than clonal line A. In response to Reviewer 1’s suggestion that we reference the (Matthey-Doret et al. 2019) study in the context of multilocus CSD, the revised manuscript version will include the following additional sentence in the fifth paragraph of the discussion (in what will be lines 372-374): “Multi-locus CSD has been suggested to limit the extent of diploid male production in asexual species under some circumstances (Vorburger 2013; Matthey-Doret et al. 2019).”

Regarding Reviewer 2’s question about homology between the putative CSD loci from the (Matthey-Doret et al. 2019) study and O. biroi, we note that there is no homology. The revised manuscript version will have an additional Supplementary Table (which will be the new Supplementary Table S3) that will report the results of this homology search. The revised manuscript will also include the following additional sentence in the Results, in what will be lines 172-174: “We found no homology between the genes within the O. biroi CSD index peak and any of the genes within the putative L. fabarum CSD loci (Supplementary Table S3).”

The authors used different clonal lines of O. biroi to investigate whether heterozygosity at the mapped CSD locus is required for female development in all clonal lines of O. biroi (L187-196). However, given the described parthenogenesis mechanism in this species conserves heterozygosity, additional females that are heterozygous are not very informative here. Indeed, one would need diploid males in these other clonal lines as well (but such males have not yet been found) to make any inference regarding this locus in other lines.

We agree that a full mapping study including diploid males from all clonal lines would be preferable, but as stated earlier in that same paragraph, we have only found diploid males from clonal line A. We stand behind our modest claim that “Females from all six clonal lines were heterozygous at the CSD index peak, consistent with its putative role as a CSD locus in all O. biroi.” In the revised manuscript version, this sentence (in what will be lines 199-201) will be changed slightly in response to a reviewer comment below: “All females from all six clonal lines (including 26 diploid females from clonal line B) were heterozygous at the CSD index peak, consistent with its putative role as a CSD locus in all O. biroi.”

Reviewer #2 (Public review):

The manuscript by Lacy et al. is well written, with a clear and compelling introduction that effectively conveys the significance of the study. The methods are appropriate and well-executed, and the results, both in the main text and supplementary materials, are presented in a clear and detailed manner. The authors interpret their findings with appropriate caution.

This work makes a valuable contribution to our understanding of the evolution of complementary sex determination (CSD) in ants. In particular, it provides important evidence for the ancient origin of a non-coding locus implicated in sex determination, and shows that, remarkably, this sex locus is conserved even in an ant species with a non-canonical reproductive system that typically does not produce males. I found this to be an excellent and well-rounded study, carefully analyzed and well contextualized.

That said, I do have a few minor comments, primarily concerning the discussion of the potential 'ghost' CSD locus. While the authors acknowledge (line 367) that they currently have no data to distinguish among the alternative hypotheses, I found the evidence for an additional CSD locus presented in the results (lines 261-302) somewhat limited and at times a bit difficult to follow. I wonder whether further clarification or supporting evidence could already be extracted from the existing data. Specifically:

We agree with Reviewer 2 that the evidence for a second CSD locus is limited. In fact, we do not intend to advocate for there being a second locus, but we suggest that a second CSD locus is one possible explanation for the absence of diploid males outside of clonal line A. In our initial version, we intentionally conveyed this ambiguity by titling this section “O. biroi may have one or multiple sex determination loci.” However, we now see that this leads to undue emphasis on the possibility of a second locus. In the revised manuscript, we will split this into two separate sections: “Diploid male production differs across O. biroi clonal lines” and “O. biroi lacks a tra-containing CSD locus.”

(1) Line 268: I doubt the relevance of comparing the proportion of diploid males among all males between lines A and B to infer the presence of additional CSD loci. Since the mechanisms producing these two types of males differ, it might be more appropriate to compare the proportion of diploid males among all diploid offspring. This ratio has been used in previous studies on CSD in Hymenoptera to estimate the number of sex loci (see, for example, Cook 1993, de Boer et al. 2008, 2012, Ma et al. 2013, and Chen et al., 2021). The exact method might not be applicable to clonal raider ants, but I think comparing the percentage of diploid males among the total number of (diploid) offspring produced between the two lineages might be a better argument for a difference in CSD loci number.

We want to re-emphasize here that we do not wish to advocate for there being two CSD loci in O. biroi. Rather, we want to explain that this is one possible explanation for the apparent absence of diploid males outside of clonal line A. We hope that the modifications to the manuscript described in the previous response help to clarify this.

Reviewer 2 is correct that comparing the number of diploid males to diploid females does not apply to clonal raider ants. This is because males are vanishingly rare among the vast numbers of females produced. We do not count how many females are produced in laboratory stock colonies, and males are sampled opportunistically. Therefore, we cannot report exact numbers. However, we will add the highlighted portion of the following sentence (in what will be lines 268-270) to the revised manuscript: “Despite the fact that we maintain more colonies of clonal line B than of clonal line A in the lab, all the diploid males we detected came from clonal line A.”

(2) If line B indeed carries an additional CSD locus, one would expect that some females could be homozygous at the ANTSR locus but still viable, being heterozygous only at the other locus. Do the authors detect any females in line B that are homozygous at the ANTSR locus? If so, this would support the existence of an additional, functionally independent CSD locus.

We thank the reviewer for this suggestion, and again we emphasize that we do not want to argue in favor of multiple CSD loci. We just want to introduce it as one possible explanation for the absence of diploid males outside of clonal line A.

The 26 sequenced diploid females from clonal line B are all heterozygous at the mapped locus, and the revised manuscript will clarify this in what will be lines 199-201. Previously, only six of those diploid females were included in Supplementary Table S2, and that will be modified accordingly.

(3) Line 281: The description of the two tra-containing CSD loci as "conserved" between Vollenhovia and the honey bee may be misleading. It suggests shared ancestry, whereas the honey bee csd gene is known to have arisen via a relatively recent gene duplication from fem/tra (10.1038/nature07052). It would be more accurate to refer to this similarity as a case of convergent evolution rather than conservation.

In the sentence that Reviewer 2 refers to, we are representing the assertion made in the (Miyakawa and Mikheyev 2015) paper in which, regarding their mapping of a candidate CSD locus that contains two linked tra homologs, they write in the abstract: “these data support the prediction that the same CSD mechanism has indeed been conserved for over 100 million years.” In that same paper, Miyakawa and Mikheyev write in the discussion section: “As ants and bees diverged more than 100 million years ago, sex determination in honey bees and V. emeryi is probably homologous and has been conserved for at least this long.”

As noted by Reviewer 2, this appears to conflict with a previously advanced hypothesis: that because fem and csd were found in Apis mellifera, Apis cerana, and Apis dorsata, but only fem was found in Mellipona compressipes, Bombus terrestris, and Nasonia vitripennis, that the csd gene evolved after the honeybee (Apis) lineage diverged from other bees (Hasselmann et al. 2008). However, it remains possible that the csd gene evolved after ants and bees diverged from N. vitripennis, but before the divergence of ants and bees, and then was subsequently lost in B. terrestris and M. compressipes. This view was previously put forward based on bioinformatic identification of putative orthologs of csd and fem in bumblebees and in ants [(Schmieder et al. 2012), see also (Privman et al. 2013)]. However, subsequent work disagreed and argued that the duplications of tra found in ants and in bumblebees represented convergent evolution rather than homology (Koch et al. 2014). Distinguishing between these possibilities will be aided by additional sex determination locus mapping studies and functional dissection of the underlying molecular mechanisms in diverse Aculeata.

Distinguishing between these competing hypotheses is beyond the scope of our paper, but the revised manuscript will include additional text to incorporate some of this nuance. We will include these modified lines below (in what will be lines 287-295), with the additions highlighted:

“A second QTL region identified in V. emeryi (V.emeryiCsdQTL1) contains two closely linked tra homologs, similar to the closely linked honeybee tra homologs, csd and fem (Miyakawa and Mikheyev 2015). This, along with the discovery of duplicated tra homologs that undergo concerted evolution in bumblebees and ants (Schmieder et al. 2012; Privman et al. 2013) has led to the hypothesis that the function of tra homologs as CSD loci is conserved with the csd-containing region of honeybees (Schmieder et al. 2012; Miyakawa and Mikheyev 2015). However, other work has suggested that tra duplications occurred independently in honeybees, bumblebees, and ants (Hasselmann et al. 2008; Koch et al. 2014), and it remains to be demonstrated that either of these tra homologs acts as a primary CSD signal in V. emeryi.”

(4) Finally, since the authors successfully identified multiple alleles of the first CSD locus using previously sequenced haploid males, I wonder whether they also observed comparable allelic diversity at the candidate second CSD locus. This would provide useful supporting evidence for its functional relevance.

As is already addressed in the final paragraph of the results and in Supplementary Fig. S4, there is no peak of nucleotide diversity in any of the regions homologous to V.emeryiQTL1, which is the tra-containing candidate sex determination locus (Miyakawa and Mikheyev 2015). In the revised manuscript, the relevant lines will be 307-310. We want to restate that we do not propose that there is a second candidate CSD locus in O. biroi, but we simply raise the possibility that multi-locus CSD *might* explain the absence of diploid males from clonal lines other than clonal line A (as one of several alternative possibilities).

Overall, these are relatively minor points in the context of a strong manuscript, but I believe addressing them would improve the clarity and robustness of the authors' conclusions.

Reviewer #3 (Public review):

Summary:

The sex determination mechanism governed by the complementary sex determination (CSD) locus is one of the mechanisms that support the haplodiploid sex determination system evolved in hymenopteran insects. While many ant species are believed to possess a CSD locus, it has only been specifically identified in two species. The authors analyzed diploid females and the rarely occurring diploid males of the clonal ant Ooceraea biroi and identified a 46 kb CSD candidate region that is consistently heterozygous in females and predominantly homozygous in males. This region was found to be homologous to the CSD locus reported in distantly related ants. In the Argentine ant, Linepithema humile, the CSD locus overlaps with an lncRNA (ANTSR) that is essential for female development and is associated with the heterozygous region (Pan et al. 2024). Similarly, an lncRNA is encoded near the heterozygous region within the CSD candidate region of O. biroi. Although this lncRNA shares low sequence similarity with ANTSR, its potential functional involvement in sex determination is suggested. Based on these findings, the authors propose that the heterozygous region and the adjacent lncRNA in O. biroi may trigger female development via a mechanism similar to that of L. humile. They further suggest that the molecular mechanisms of sex determination involving the CSD locus in ants have been highly conserved for approximately 112 million years. This study is one of the few to identify a CSD candidate region in ants and is particularly noteworthy as the first to do so in a parthenogenetic species.

Strengths:

(1) The CSD candidate region was found to be homologous to the CSD locus reported in distantly related ant species, enhancing the significance of the findings.

(2) Identifying the CSD candidate region in a parthenogenetic species like O. biroi is a notable achievement and adds novelty to the research.

Weaknesses

(1) Functional validation of the lncRNA's role is lacking, and further investigation through knockout or knockdown experiments is necessary to confirm its involvement in sex determination.

See response below.

(2) The claim that the lncRNA is essential for female development appears to reiterate findings already proposed by Pan et al. (2024), which may reduce the novelty of the study.

We do not claim that the lncRNA is essential for female development in O. biroi, but simply mention the possibility that, as in L. humile, it is somehow involved in sex determination. We do not have any functional evidence for this, so this is purely based on its genomic position immediately adjacent to our mapped candidate region. We agree with the reviewer that the study by Pan et al. (2024) decreases the novelty of our findings. Another way of looking at this is that our study supports and bolsters previous findings by partially replicating the results in a different species.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

L307-308 should state homozygous for either allele in THE MAJORITY of diploid males.

This will be fixed in the revised manuscript, in what will be line 321.

Reviewer #3 (Recommendations for the authors):

The association between heterozygosity in the CSD candidate region and female development in O. biroi, along with the high sequence homology of this region to CSD loci identified in two distantly related ant species, is not sufficient to fully address the evolution of the CSD locus and the mechanisms of sex determination.

Given that functional genetic tools, such as genome editing, have already been established in O. biroi, I strongly recommend that the authors investigate the role of the lncRNA through knockout or knockdown experiments and assess its impact on the sex-specific splicing pattern of the downstream tra gene.

Although knockout experiments of the lncRNA would be illuminating, the primary signal of complementary sex determination is heterozygosity. As is clearly stated in our manuscript and that of (Pan et al. 2024), it does not appear to be heterozygosity within the lncRNA that induces female development, but rather heterozygosity in non-transcribed regions linked to the lncRNA. Therefore, future mechanistic studies of sex determination in O. biroi, L. humile, and other ants should explore how homozygosity or heterozygosity of this region impacts the sex determination cascade, rather than focusing (exclusively) on the lncRNA.

With this in mind, we developed three sets of guide RNAs that cut only one allele within the mapped CSD locus, with the goal of producing deletions within the highly variable region within the mapped locus. This would lead to functional hemizygosity or homozygosity within this region, depending on how the cuts were repaired. We also developed several sets of PCR primers to assess the heterozygosity of the resultant animals. After injecting 1,162 eggs over several weeks and genotyping the hundreds of resultant animals with PCR, we confirmed that we could induce hemizygosity or homozygosity within this region, at least in ~1/20 of the injected embryos. Although it is possible to assess the sex-specificity of the splice isoform of tra as a proxy for sex determination phenotypes (as done by (Pan et al. 2024)), the ideal experiment would assess male phenotypic development at the pupal stage. Therefore, over several more weeks, we injected hundreds more eggs with these reagents and reared the injected embryos to the pupal stage. However, substantial mortality was observed, with only 12 injected eggs developing to the pupal stage. All of these were female, and none of them had been successfully mutated.

In conclusion, we agree with the reviewer that functional experiments would be useful, and we made extensive attempts to conduct such experiments. However, these experiments turned out to be extremely challenging with the currently available protocols. Ultimately, we therefore decided to abandon these attempts.  

We opted not to include these experiments in the paper itself because we cannot meaningfully interpret their results. However, we are pleased that, in this response letter, we can include a brief description for readers interested in attempting similar experiments.

Since O. biroi reproduces parthenogenetically and most offspring develop into females, observing a shift from female- to male-specific splicing of tra upon early embryonic knockout of the lncRNA would provide much stronger evidence that this lncRNA is essential for female development. Without such functional validation, the authors' claim (lines 36-38) seems to reiterate findings already proposed by Pan et al. (2024) and, as such, lacks sufficient novelty.

We have responded to the issue of “lack of novelty” above. But again, the actual CSD locus in both O. biroi and L. humile appears to be distinct from (but genetically linked to) the lncRNA, and we have no experimental evidence that the putative lncRNA in O. biroi is involved in sex determination at all. Because of this, and given the experimental challenges described above, we do not currently intend to pursue functional studies of the lncRNA.

References

Hasselmann M, Gempe T, Schiøtt M, Nunes-Silva CG, Otte M, Beye M. 2008. Evidence for the evolutionary nascence of a novel sex determination pathway in honeybees. Nature 454:519–522.

Koch V, Nissen I, Schmitt BD, Beye M. 2014. Independent Evolutionary Origin of fem Paralogous Genes and Complementary Sex Determination in Hymenopteran Insects. PLOS ONE 9:e91883.

Matthey-Doret C, van der Kooi CJ, Jeffries DL, Bast J, Dennis AB, Vorburger C, Schwander T. 2019. Mapping of multiple complementary sex determination loci in a parasitoid wasp. Genome Biology and Evolution 11:2954–2962.

Miyakawa MO, Mikheyev AS. 2015. QTL mapping of sex determination loci supports an ancient pathway in ants and honey bees. PLOS Genetics 11:e1005656.

Pan Q, Darras H, Keller L. 2024. LncRNA gene ANTSR coordinates complementary sex determination in the Argentine ant. Science Advances 10:eadp1532.

Privman E, Wurm Y, Keller L. 2013. Duplication and concerted evolution in a master sex determiner under balancing selection. Proceedings of the Royal Society B: Biological Sciences 280:20122968.

Rabeling C, Kronauer DJC. 2012. Thelytokous parthenogenesis in eusocial Hymenoptera. Annual Review of Entomology 58:273–292.

Schmieder S, Colinet D, Poirié M. 2012. Tracing back the nascence of a new sex-determination pathway to the ancestor of bees and ants. Nature Communications 3:1–7.

Vorburger C. 2013. Thelytoky and Sex Determination in the Hymenoptera: Mutual Constraints. Sexual Development 8:50–58.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review): 

Jiang et al. present a measure of phenological lag by quantifying the effects of abiotic constraints on the differences between observed and expected phenological changes, using a combination of previously published phenology change data for 980 species, and associated climate data for study sites. They found that, across all samples, observed phenological responses to climate warming were smaller than expected responses for both leafing and flowering spring events. They also show that data from experimental studies included in their analysis exhibited increased phenological lag compared to observational studies, possibly as a result of reduced sensitivity to climatic changes. Furthermore, the authors present evidence that spatial trends in phenological responses to warming may differ than what would be expected from phenological sensitivity, due to the seasonal timing of when warming occurs. Thus, climate change may not result in geographic convergences of phenological responses. This study presents an interesting way to separate the individual effects of climate change and other abiotic changes on the phenological responses across sites and species. 

Strengths: 

A straightforward mathematical definition of phenological lag allows for this method to potentially be applied in different geographic contexts. Where data exists, other researchers can partition the effects of various abiotic forcings on phenological responses that differ from those expected from warming sensitivity alone. 

Identifying phenological lag, and associated contributing factors, provides a method by which more nuanced predictions of phenological responses to climate change can be made. Thus, this study could improve ecological forecasting models. 

Weaknesses: 

The analysis here could be more robust. A more thorough examination of phenological lag would provide stronger evidence that the framework presented has utility. The differences in phenologica lag by study approach, species origin, region, and growth form are interesting, and could be expanded. For example, the authors have the data to explore the relationships between phenological lag and the quantitative variables included in the final model (altitude, latitude, mean annual temperature) and other spatial or temporal variables. This would also provide stronger evidence for the author's claims about potential mechanisms that contribute to phenological lag. 

We did examine the relationships of phenological lag with geographic or climatic variables in our analyses. Other than the weak correlations with latitude and altitude cited in the discussion section (lines 292-293), phenological lag was not related to mean annual temperature or long-term precipitation for both leafing and flowering.  

The authors include very little data visualizations, and instead report results and model statistics in tables. This is difficult to interpret and may obscure underlying patterns in the data. Including visual representations of variable distributions and between-variable relationships, in addition to model statistics, provides stronger evidence than model statistics alone. 

Table 2 shows the influences of geographic or climatic variables, particularly those related to drivers of spring phenology, i.e., budburst temperature, forcing change, and phenological lag, on phenological changes. As quantitative contributions of these drivers have been extracted, the influences of remaining variables are either minor or insignificant. Thus, examination of variable distributions, which has been done in previous syntheses, is probably not necessary.         

Some of independent variables were apparently correlated (r <0.6), e.g., MAT with altitude and latitude, budburst temperature with forcing change and spring warming, and forcing change with spring warming.

Reviewer #3 (Public review): 

Summary: 

The authors developed a new phenological lag metric and applied this analytical framework to a global dataset to synthesize shifts in spring phenology and assess how abiotic constraints influence spring phenology. 

Strengths: 

The dataset developed in this study is extensive, and the phenological lag metric is valuable. 

Weaknesses: 

The stability of the method used in this study needs improvement, particularly in the calculation of forcing requirements. In addition, the visualization of the results (such as Table 1) should be enhanced. 

Not clear how to improve the calculation of forcing accumulation.    

Recommendations for the authors: 

Editor (Recommendations for the authors): 

To improve the robustness of the metric and the conclusions drawn, we recommend that the authors: 

Test the sensitivity of their results to different base temperature thresholds and to nonlinear forcing response models, even for a subset of species. The proposed framework relies on an accurate understanding of species-specific thermal responses, which remain poorly resolved.

Different above-zero base temperatures have been used previously, although justifications are mostly following previous work. As we indicated in our first responses, the use of above-zero base temperatures underestimates forcing from low temperatures, which has more impacts on species with early spring phenology or in areas of cold climate due to greater proportions of forcing accumulations from low temperatures. The use of high base temperatures can lead to an interpretation that early season species require little or no forcing to break buds, which is biologically incorrect. Thus, the use of above-zero base temperatures would be more appropriate for particular locations or species than for meta-analysis across different spring phenology and climatic conditions. 

The research on multiple warming is limited in terms of levels of warming used (mostly one and occasionally two) for assessing non-linear forcing responses. This can be the focus of future work.  

Our framework is based on drivers of spring phenology and not dependent on “accurate understanding of species-specific thermal responses”. However, a good understanding of species- and site-specific responses to phenological constraints (e.g., insufficient winter chilling, photoperiod, and environmental stresses) does help determine the nature of phenological lag. All these are explained in our paper.     

Analyze relationships between phenological lag and additional geographic or climatic gradients already available in the dataset (e.g., latitude, mean annual temperature, interannual variability). 

We did examine the relationships of phenological lag with geographic or climatic variables in our analyses. Other than the weak correlations with latitude and altitude cited in the discussion section (lines 292-293), phenological lag was not related to mean annual temperature or long-term precipitation for both leafing and flowering.  

Our objective is to understand changes in spring phenology and differences in plant phenological responses across different functional groups or climatic regions, although our approach can be used to study interannual variability of spring phenology. Our metadata are compiled for comparing warmer vs control treatments (often multiyear averages), not for assessing interannual variability.      

Improve data visualization to better convey how phenological lag varies across environmental and biological contexts. 

See responses above.

Consider incorporating explicit uncertainty estimates around phenological lag calculations.  These steps would improve the interpretability and generalizability of the framework, helping it move from a useful heuristic to a more robust and empirically grounded analytical tool. 

The calculation of phenological lag is based on drivers of spring phenology with uncertainty depending primarily on uncertainty in phenological observations. Previous uncertainty assessments can be used here (see a few selected studies below).   

Alles, G.R., Comba, J.L., Vincent, J.M., Nagai, S. and Schnorr, L.M., 2020. Measuring phenology uncertainty with large scale image processing. Ecological Informatics, 59, p.101109.

Liu G, Chuine I, Denéchère R, Jean F, Dufrêne E, Vincent G, Berveiller D, Delpierre N. Higher sample sizes and observer intercalibration are needed for reliable scoring of leaf phenology in trees. Journal of Ecology. 2021 Jun;109(6):2461-74.

Tang, J., Körner, C., Muraoka, H., Piao, S., Shen, M., Thackeray, S.J. and Yang, X., 2016.Emerging opportunities and challenges in phenology: a review. Ecosphere, 7(8), p.e01436. 

Nagai, S., Inoue, T., Ohtsuka, T., Yoshitake, S., Nasahara, K.N. and Saitoh, T.M., 2015. Uncertainties involved in leaf fall phenology detected by digital camera. Ecological Informatics, 30, pp.124-132.

Author response:

The following is the authors’ response to the previous reviews

Reviewer#1 (Public Review):

In the current article, Octavia Soegyono and colleagues study "The influence of nucleus accumbens shell D1 and D2 neurons on outcome-specific Pavlovian instrumental transfer", building on extensive findings from the same lab. While there is a consensus about the specific involvement of the Shell part of the Nucleus Accumbens (NAc) in specific stimulus-based actions in choice settings (and not in General Pavlovian instrumental transfer - gPIT, as opposed to the Core part of the NAc), mechanisms at the cellular and circuitry levels remain to be explored. In the present work, using sophisticated methods (rat Cre-transgenic lines from both sexes, optogenetics and the well-established behavioral paradigm outcome-specific PIT - sPIT), Octavia Soegyono and colleagues decipher the diOerential contribution of dopamine receptors D1 and D2 expressing-spiny projection neurons (SPNs).

After validating the viral strategy and the specificity of the targeting (immunochemistry and electrophysiology), the authors demonstrate that while both NAc Shell D1- and D2SPNs participate in mediating sPIT, NAc Shell D1-SPNs projections to the Ventral Pallidum (VP, previously demonstrated as crucial for sPIT), but not D2-SPNs, mediates sPIT. They also show that these eOects were specific to stimulus-based actions, as valuebased choices were left intact in all manipulations.

This is a well-designed study and the results are well supported by the experimental evidence. The paper is extremely pleasant to read and add to the current literature.

We thank the Reviewer for their positive assessment.

Comments on revisions:  

We thank the authors for their detailed responses and for addressing our comments and concerns.

To further improve consistency and transparency, we kindly request that the authors provide, for Supplemental Figures S1-S4, panels E (raw data for lever presses during the PIT test), the individual data points together with the corresponding statistical analyses in the figure legends.

Panel E of Figures S1-S4 now includes the individual data points. The outcome-specific data have already been analysed, and we report these analyses in the main manuscript. These analyses are more informative than those requested by the Reviewer since they report the net eFects of the stimuli on choice between actions while controlling for potential individual baseline instrumental performance. All data remain fully transparent and are publicly available on an online repository in accordance with eLife policies (see relevant section in Materials and Methods).  

In addition, regarding Supplemental Figure S3, panel E, we note the absence of a PIT eOect in the eYFP group under the ON condition, which appears to diOer from the net response reported in the main Figure 5, panel B. Could the authors clarify this apparent discrepancy?

We apologize for the error, which has now been corrected. 

We also note a discrepancy between the authors' statement in their response ("40 rats excluded based on post-mortem analyses") and the number of excluded animals reported in the Materials and Methods section, which adds up to 47. We kindly ask the authors to clarify this point for consistency.

We thank the Reviewer for identifying the error reported in our initial response. The total number of animals excluded was 47, as reported in the manuscript. 

Finally, as a minor point, we suggest indicating the total number of animals used in the study in the Materials and Methods section.

The total number of animals has been included in the Materials and Methods section.

Reviewer #2 (Public Review):

Summary:

This manuscript by Soegyono et a. describes a series of experiments designed to probe the involvement of dopamine D1 and D2 neurons within the nucleus accumbens shell in outcome-specific Pavlovian-instrumental transfer (osPIT), a well-controlled assay of cueguided action selection based on congruent outcome associations. They used an optogenetic approach to phasically silence NAc shell D1 (D1-Cre mice) or D2 (A2a-Cre mice) neurons during a subset of osPIT trials. Both manipulations disrupted cue-guided action selection but had no eOects on negative control measures/tasks (concomitant approach behavior, separate valued guided choice task), nor were any osPIT impairments found in reporter only control groups. Separate experiments revealed that selective inhibition of NAc shell D1 but not D2 inputs to ventral pallidum were required for osPIT expression, thereby advancing understanding of the basal ganglia circuitry underpinning this important aspect of decision making.

Strengths:

The combinatorial viral and optogenetic approaches used here were convincingly validated through anatomical tract-tracing and ex vivo electrophysiology. The behavioral assays are sophisticated and well-controlled to parse cue and value guided action selection. The inclusion of reporter only control groups is rigorous and rules out nonspecific eOects of the light manipulation. The findings are novel and address a critical question in the literature. Prior work using less decisive methods had implicated NAc shell D1 neurons in osPIT but suggested that D2 neurons may not be involved. The optogenetic manipulations used in the current study provides a more direct test of their involvement and convincingly demonstrate that both populations play an important role. Prior work had also implicated NAc shell connections to ventral pallidum in osPIT, but the current study reveals the selective involvement of D1 but not D2 neurons in this circuit. The authors do a good job of discussing their findings, including their nuanced interpretation that NAc shell D2 neurons may contribute to osPIT through their local regulation of NAc shell microcircuitry.

We thank the Reviewer for their positive assessment.

Weaknesses:

The current study exclusively used an optogenetic approach to probe the function of D1 and D2 NAc shell neurons. Providing a complementary assessment with chemogenetics or other appropriate methods would strengthen conclusions, particularly the novel demonstration for D2 NAc shell involvement. Likewise, the null result of optically inhibiting D2 inputs to ventral pallidum leaves open the possibility that a more complete or sustained disruption of this pathway may have impaired osPIT.

We acknowledge the reviewer's valuable suggestion that demonstrating NAc-S D1- and D2-SPNs engagement in outcome-specific PIT through another technique would strengthen our optogenetic findings. Several approaches could provide this validation. Chemogenetic manipulation, as the reviewer suggested, represents one compelling option. Alternatively, immunohistochemical assessment of phosphorylated histone H3 at serine 10 (P-H3) oFers another promising avenue, given its established utility in reporting striatal SPNs plasticity in the dorsal striatum (Matamales et al., 2020). We hope to complete such an assessment in future work since it would address the limitations of previous work that relied solely on ERK1/2 phosphorylation measures in NAc-S SPNs (Laurent et al., 2014). The manuscript was modified to report these future avenues of research (page 12). 

Regarding the null result from optical silencing of D2 terminals in the ventral pallidum, we agree with the reviewer's assessment. While we acknowledge this limitation in the current manuscript (page 13), we aim to address this gap in future studies to provide a more complete mechanistic understanding of the circuit.

Conclusions:

The research described here was successful in providing critical new insights into the contributions of NAc D1 and D2 neurons in cue-guided action selection. The authors' data interpretation and conclusions are well reasoned and appropriate. They also provide a thoughtful discussion of study limitations and implications for future research. This research is therefore likely to have a significant impact on the field.

We thank the Reviewer for their positive assessment.

Comments on revisions:

I have reviewed the rebuttal and revised manuscript and have no remaining concerns.

We are pleased to have addressed the Reviewer’s query.

References

Laurent, V., Bertran-Gonzalez, J., Chieng, B. C., & Balleine, B. W. (2014). δ-Opioid and Dopaminergic Processes in Accumbens Shell Modulate the Cholinergic Control of Predictive Learning and Choice. J Neurosci, 34(4), 1358-1369. https://doi.org/10.1523/JNEUROSCI.4592-13.2014

Matamales, M., McGovern, A. E., Mi, J. D., Mazzone, S. B., Balleine, B. W., & BertranGonzalez, J. (2020). Local D2- to D1-neuron transmodulation updates goal-directed learning in the striatum. Science, 367(6477), 549-555. https://doi.org/10.1126/science.aaz5751

Author response:

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

Reviewer #1 (Public review): 

This paper describes a number of patterns of epistasis in a large fitness landscape dataset recently published by Papkou et al. The paper is motivated by an important goal in the field of evolutionary biology to understand the statistical structure of epistasis in protein fitness landscapes, and it capitalizes on the unique opportunities presented by this new dataset to address this problem. 

The paper reports some interesting previously unobserved patterns that may have implications for our understanding of fitness landscapes and protein evolution. In particular, Figure 5 is very intriguing. However, I have two major concerns detailed below. First, I found the paper rather descriptive (it makes little attempt to gain deeper insights into the origins of the observed patterns) and unfocused (it reports what appears to be a disjointed collection of various statistics without a clear narrative. Second, I have concerns with the statistical rigor of the work. 

(1) I think Figures 5 and 7 are the main, most interesting, and novel results of the paper. However, I don't think that the statement "Only a small fraction of mutations exhibit global epistasis" accurately describes what we see in Figure 5. To me, the most striking feature of this figure is that the effects of most mutations at all sites appear to be a mixture of three patterns. The most interesting pattern noted by the authors is of course the "strong" global epistasis, i.e., when the effect of a mutation is highly negatively correlated with the fitness of the background genotype. The second pattern is a "weak" global epistasis, where the correlation with background fitness is much weaker or non-existent. The third pattern is the vertically spread-out cluster at low-fitness backgrounds, i.e., a mutation has a wide range of mostly positive effects that are clearly not correlated with fitness. What is very interesting to me is that all background genotypes fall into these three groups with respect to almost every mutation, but the proportions of the three groups are different for different mutations. In contrast to the authors' statement, it seems to me that almost all mutations display strong global epistasis in at least a subset of backgrounds. A clear example is C>A mutation at site 3. 

(1a) I think the authors ought to try to dissect these patterns and investigate them separately rather than lumping them all together and declaring that global epistasis is rare. For example, I would like to know whether those backgrounds in which mutations exhibit strong global epistasis are the same for all mutations or whether they are mutation- or perhaps positionspecific. Both answers could be potentially very interesting, either pointing to some specific site-site interactions or, alternatively, suggesting that the statistical patterns are conserved despite variation in the underlying interactions. 

(1b) Another rather remarkable feature of this plot is that the slopes of the strong global epistasis patterns seem to be very similar across mutations. Is this the case? Is there anything special about this slope? For example, does this slope simply reflect the fact that a given mutation becomes essentially lethal (i.e., produces the same minimal fitness) in a certain set of background genotypes? 

(1c) Finally, how consistent are these patterns with some null expectations? Specifically, would one expect the same distribution of global epistasis slopes on an uncorrelated landscape? Are the pivot points unusually clustered relative to an expectation on an uncorrelated landscape? 

(1d) The shapes of the DFE shown in Figure 7 are also quite interesting, particularly the bimodal nature of the DFE in high-fitness (HF) backgrounds. I think this bimodality must be a reflection of the clustering of mutation-background combinations mentioned above. I think the authors ought to draw this connection explicitly. Do all HF backgrounds have a bimodal DFE? What mutations occupy the "moving" peak? 

(1e) In several figures, the authors compare the patterns for HF and low-fitness (LF) genotypes. In some cases, there are some stark differences between these two groups, most notably in the shape of the DFE (Figure 7B, C). But there is no discussion about what could underlie these differences. Why are the statistics of epistasis different for HF and LF genotypes? Can the authors at least speculate about possible reasons? Why do HF and LF genotypes have qualitatively different DFEs? I actually don't quite understand why the transition between bimodal DFE in Figure 7B and unimodal DFE in Figure 7C is so abrupt. Is there something biologically special about the threshold that separates LF and HF genotypes? My understanding was that this was just a statistical cutoff. Perhaps the authors can plot the DFEs for all backgrounds on the same plot and just draw a line that separates HF and LF backgrounds so that the reader can better see whether the DFE shape changes gradually or abruptly.

(1f) The analysis of the synonymous mutations is also interesting. However I think a few additional analyses are necessary to clarify what is happening here. I would like to know the extent to which synonymous mutations are more often neutral compared to non-synonymous ones. Then, synonymous pairs interact in the same way as non-synonymous pair (i.e., plot Figure 1 for synonymous pairs)? Do synonymous or non-synonymous mutations that are neutral exhibit less epistasis than non-neutral ones? Finally, do non-synonymous mutations alter epistasis among other mutations more often than synonymous mutations do? What about synonymous-neutral versus synonymous-non-neutral. Basically, I'd like to understand the extent to which a mutation that is neutral in a given background is more or less likely to alter epistasis between other mutations than a non-neutral mutation in the same background. 

(2) I have two related methodological concerns. First, in several analyses, the authors employ thresholds that appear to be arbitrary. And second, I did not see any account of measurement errors. For example, the authors chose the 0.05 threshold to distinguish between epistasis and no epistasis, but why this particular threshold was chosen is not justified. Another example: is whether the product s12 × (s1 + s2) is greater or smaller than zero for any given mutation is uncertain due to measurement errors. Presumably, how to classify each pair of mutations should depend on the precision with which the fitness of mutants is measured. These thresholds could well be different across mutants. We know, for example, that low-fitness mutants typically have noisier fitness estimates than high-fitness mutants. I think the authors should use a statistically rigorous procedure to categorize mutations and their epistatic interactions. I think it is very important to address this issue. I got very concerned about it when I saw on LL 383-388 that synonymous stop codon mutations appear to modulate epistasis among other mutations. This seems very strange to me and makes me quite worried that this is a result of noise in LF genotypes. 

Thank you for your review of the manuscript. In the revised version, we have addressed both major criticisms, as detailed below.

When carefully examining the plots in Figure 5 independently, we indeed observe that the fitness effect of a mutation on different genetic backgrounds can be classified into three characteristic patterns. Our reasoning for these patterns is as follows:

Strong correlation: Typically observed when the mutation is lethal across backgrounds. Linear regression of mutations exhibiting strong global epistasis shows slopes close to −1 and pivot points near −0.7 (Table S4). Since the reported fitness threshold is −0.508, these mutations push otherwise functional backgrounds into the non-functional range, consistent with lethal effects.

Weak correlation: Observed when a mutation has no significant effect on fitness across backgrounds, consistent with neutrality.

No correlation: Out of the 261,333 reported variants, 243,303 (93%) lie below the fitness threshold of −0.508, indicating that the low-fitness region is densely populated by nonfunctional variants. The “strong correlation” and “weak correlation” lines intersect in this zone. Most mutations in this region have little effect (neutral), but occasional abrupt fitness increases correspond to “resurrecting” mutations, the converse of lethal changes. For example, mutations such as X→G at locus 4 or X→A at locus 5 restore function, while the reverse changes (e.g. C→A at locus 3) are lethal.

Thus, the “no-correlation” pattern is largely explained by mutations that reverse the effect of lethal changes, effectively resurrecting non-functional variants. In the revised manuscript, we highlight these nuances within the broader classification of fitness effect versus background fitness (pp. 10–13).

Additional analyses included in the revision:

Synonymous vs. non-synonymous pairs: We repeated the Figure 1 analysis for synonymous–synonymous pairs. As expected, synonymous pairs exhibit lower overall frequencies of epistasis, consistent with their greater neutrality. However, the qualitative spectrum remains similar: positive and negative epistasis dominate, while sign epistasis is rare (Supplementary Figs. S6–S7, S9–S10).

Fitness effect vs. epistasis change: We tested whether the mean fitness effect of a mutation correlates with the percent of cases in which it changes the nature of epistasis. No correlation was found (R² ≈ 0.11), and this analysis is now included in the revised manuscript.

Epistasis-modulating ability: Non-synonymous mutations more frequently alter the interactions between other mutations than synonymous substitutions. Within synonymous substitutions, the subset with measurable fitness effects disproportionately contributes to epistasis modulation. Thus, the ability of synonymous substitutions to modulate epistasis arises primarily from the non-neutral subset.

These analyses clarify the role of synonymous mutations in reshaping epistasis on the folA landscape.

Revision of statistical treatment of epistasis:

In our original submission, we used an arbitrary threshold of 0.05 to classify the presence or absence of epistasis, following Papkou et al., who based conclusions on a single experimental replicate. However, as the reviewer correctly noted, this does not adequately account for measurement variability across different genotypes.

In the revised manuscript, we adopt a statistically rigorous framework that incorporates replicate-based error directly. Specifically, we now use the mean fitness across six independent replicates, together with the corresponding standard deviation, to classify fitness peaks and epistasis. This eliminates arbitrary thresholds and ensures that epistatic classifications reflect the precision of measurements for each genotype.

This revision led to both quantitative and qualitative changes:

For high-fitness genotypes, the core patterns of higher-order (“fluid”) epistasis remain robust (Figures 2–3).

For low-fitness genotypes, incorporating replicate-based error removed spurious fluidity effects, yielding a more accurate characterization of epistasis (Figures 2–3; Supplementary Figs. S6–S7, S9–S10).

We describe these methodological changes in detail in the revised Methods section and provide updated code.

Together, these revisions directly address the reviewer’s concerns. They improve the statistical rigor of our analysis, strengthen the robustness of our conclusions, and underscore the importance of accounting for measurement error in large-scale fitness landscape studies—a point we now emphasize in the manuscript.

Reviewer #2 (Public review): 

Significance: 

This paper reanalyzes an experimental fitness landscape generated by Papkou et al., who assayed the fitness of all possible combinations of 4 nucleotide states at 9 sites in the E. coli DHFR gene, which confers antibiotic resistance. The 9 nucleotide sites make up 3 amino acid sites in the protein, of which one was shown to be the primary determinant of fitness by Papkou et al. This paper sought to assess whether pairwise epistatic interactions differ among genetic backgrounds at other sites and whether there are major patterns in any such differences. They use a "double mutant cycle" approach to quantify pairwise epistasis, where the epistatic interaction between two mutations is the difference between the measured fitness of the double-mutant and its predicted fitness in the absence of epistasis (which equals the sum of individual effects of each mutation observed in the single mutants relative to the reference genotype). The paper claims that epistasis is "fluid," because pairwise epistatic effects often differs depending on the genetic state at the other site. It also claims that this fluidity is "binary," because pairwise effects depend strongly on the state at nucleotide positions 5 and 6 but weakly on those at other sites. Finally, they compare the distribution of fitness effects (DFE) of single mutations for starting genotypes with similar fitness and find that despite the apparent "fluidity" of interactions this distribution is well-predicted by the fitness of the starting genotype. 

The paper addresses an important question for genetics and evolution: how complex and unpredictable are the effects and interactions among mutations in a protein? Epistasis can make the phenotype hard to predict from the genotype and also affect the evolutionary navigability of a genotype landscape. Whether pairwise epistatic interactions depend on genetic background - that is, whether there are important high-order interactions -- is important because interactions of order greater than pairwise would make phenotypes especially idiosyncratic and difficult to predict from the genotype (or by extrapolating from experimentally measured phenotypes of genotypes randomly sampled from the huge space of possible genotypes). Another interesting question is the sparsity of such high-order interactions: if they exist but mostly depend on a small number of identifiable sequence sites in the background, then this would drastically reduce the complexity and idiosyncrasy relative to a landscape on which "fluidity" involves interactions among groups of all sites in the protein. A number of papers in the recent literature have addressed the topics of high-order epistasis and sparsity and have come to conflicting conclusions. This paper contributes to that body of literature with a case study of one published experimental dataset of high quality. The findings are therefore potentially significant if convincingly supported. 

Validity: 

In my judgment, the major conclusions of this paper are not well supported by the data. There are three major problems with the analysis. 

(1) Lack of statistical tests. The authors conclude that pairwise interactions differ among backgrounds, but no statistical analysis is provided to establish that the observed differences are statistically significant, rather than being attributable to error and noise in the assay measurements. It has been established previously that the methods the authors use to estimate high-order interactions can result in inflated inferences of epistasis because of the propagation of measurement noise (see PMID 31527666 and 39261454). Error propagation can be extreme because first-order mutation effects are calculated as the difference between the measured phenotype of a single-mutant variant and the reference genotype; pairwise effects are then calculated as the difference between the measured phenotype of a double mutant and the sum of the differences described above for the single mutants. This paper claims fluidity when this latter difference itself differs when assessed in two different backgrounds. At each step of these calculations, measurement noise propagates. Because no statistical analysis is provided to evaluate whether these observed differences are greater than expected because of propagated error, the paper has not convincingly established or quantified "fluidity" in epistatic effects. 

(2) Arbitrary cutoffs. Many of the analyses involve assigning pairwise interactions into discrete categories, based on the magnitude and direction of the difference between the predicted and observed phenotypes for a pairwise mutant. For example, the authors categorize as a positive pairwise interaction if the apparent deviation of phenotype from prediction is >0.05, negative if the deviation is <-0.05, and no interaction if the deviation is between these cutoffs. Fluidity is diagnosed when the category for a pairwise interaction differs among backgrounds. These cutoffs are essentially arbitrary, and the effects are assigned to categories without assessing statistical significance. For example, an interaction of 0.06 in one background and 0.04 in another would be classified as fluid, but it is very plausible that such a difference would arise due to error alone. The frequency of epistatic interactions in each category as claimed in the paper, as well as the extent of fluidity across backgrounds, could therefore be systematically overestimated or underestimated, affecting the major conclusions of the study. 

(3) Global nonlinearities. The analyses do not consider the fact that apparent fluidity could be attributable to the fact that fitness measurements are bounded by a minimum (the fitness of cells carrying proteins in which DHFR is essentially nonfunctional) and a maximum (the fitness of cells in which some biological factor other than DHFR function is limiting for fitness). The data are clearly bounded; the original Papkou et al. paper states that 93% of genotypes are at the low-fitness limit at which deleterious effects no longer influence fitness. Because of this bounding, mutations that are strongly deleterious to DHFR function will therefore have an apparently smaller effect when introduced in combination with other deleterious mutations, leading to apparent epistatic interactions; moreover, these apparent interactions will have different magnitudes if they are introduced into backgrounds that themselves differ in DHFR function/fitness, leading to apparent "fluidity" of these interactions. This is a well-established issue in the literature (see PMIDs 30037990, 28100592, 39261454). It is therefore important to adjust for these global nonlinearities before assessing interactions, but the authors have not done this. 

This global nonlinearity could explain much of the fluidity claimed in this paper. It could explain the observation that epistasis does not seem to depend as much on genetic background for low-fitness backgrounds, and the latter is constant (Figure 2B and 2C): these patterns would arise simply because the effects of deleterious mutations are all epistatically masked in backgrounds that are already near the fitness minimum. It would also explain the observations in Figure 7. For background genotypes with relatively high fitness, there are two distinct peaks of fitness effects, which likely correspond to neutral mutations and deleterious mutations that bring fitness to the lower bound of measurement; as the fitness of the background declines, the deleterious mutations have a smaller effect, so the two peaks draw closer to each other, and in the lowest-fitness backgrounds, they collapse into a single unimodal distribution in which all mutations are approximately neutral (with the distribution reflecting only noise). Global nonlinearity could also explain the apparent "binary" nature of epistasis. Sites 4 and 5 change the second amino acid, and the Papkou paper shows that only 3 amino acid states (C, D, and E) are compatible with function; all others abolish function and yield lower-bound fitness, while mutations at other sites have much weaker effects. The apparent binary nature of epistasis in Figure 5 corresponds to these effects given the nonlinearity of the fitness assay. Most mutations are close to neutral irrespective of the fitness of the background into which they are introduced: these are the "non-epistatic" mutations in the binary scheme. For the mutations at sites 4 and 5 that abolish one of the beneficial mutations, however, these have a strong background-dependence: they are very deleterious when introduced into a high-fitness background but their impact shrinks as they are introduced into backgrounds with progressively lower fitness. The apparent "binary" nature of global epistasis is likely to be a simple artifact of bounding and the bimodal distribution of functional effects: neutral mutations are insensitive to background, while the magnitude of the fitness effect of deleterious mutations declines with background fitness because they are masked by the lower bound. The authors' statement is that "global epistasis often does not hold." This is not established. A more plausible conclusion is that global epistasis imposed by the phenotype limits affects all mutations, but it does so in a nonlinear fashion. 

In conclusion, most of the major claims in the paper could be artifactual. Much of the claimed pairwise epistasis could be caused by measurement noise, the use of arbitrary cutoffs, and the lack of adjustment for global nonlinearity. Much of the fluidity or higher-order epistasis could be attributable to the same issues. And the apparently binary nature of global epistasis is also the expected result of this nonlinearity. 

We thank the reviewer for raising this important concern. We fully agree that the use of arbitrary thresholds in the earlier version of the manuscript, together with the lack of an explicit treatment of measurement error, could compromise the rigor of our conclusions. To address this, we have undertaken a thorough re-analysis of the folA landscape.

(1)  Incorporating measurement error and avoiding noise-driven artifacts

In the original version, we followed Papkou et al. in using a single experimental replicate and applying fixed thresholds to classify epistasis. As the reviewer correctly notes, this approach allows noise to propagate from single-mutant measurements to double-mutant effects, and ultimately to higher-order epistasis.

In the revised analysis, we now:

Use the mean fitness across all six independent replicates for each genotype.

Incorporate the corresponding standard deviation as a measure of experimental error.

Classify epistatic interactions only when differences between a genotype and its neighbors exceed combined error margins, rather than using a fixed cutoff.

This ensures that observed changes in epistasis are statistically distinguishable from noise. Details are provided in the revised Methods section and updated code.

(2) Replacing arbitrary thresholds with error-based criteria

Previously, we used an arbitrary ±0.05 cutoff to define the presence/absence of epistasis. As the reviewer notes, this could misclassify interactions (e.g. labeling an effect as “fluid” when the difference lies within error). In the revised framework, these thresholds have been eliminated. Instead, interactions are classified based on whether their distributions overlap within replicate variance.

This approach scales naturally with measurement precision, which differs between high-fitness and low-fitness genotypes, and removes the need for a universal cutoff.

(3) Consequences of re-analysis

Implementing this revised framework produced several important updates:

High-fitness backgrounds: The qualitative picture of higher-order (“fluid”) epistasis remains robust. The patterns reported originally are preserved.

Low-fitness backgrounds: Accounting for replicate variance revealed that part of the previously inferred “fluidity” arose from noise. These spurious effects are now removed, giving a more conservative but more accurate view of epistasis in non-functional regions.

Fitness peaks: Our replicate-aware analysis identifies 127 peaks, compared to 514 in Papkou et al. Importantly, all 127 peaks occur in functional regions of the landscape. This difference highlights the importance of replicate-based error treatment: relying on a single run without demonstrating repeatability can yield artifacts.

(4) Addressing bounding effects and terminology

We also agree with the reviewer that bounding effects, arising from the biological limits of fitness, can create apparent nonlinearities in the genotype–phenotype map. To clarify this, we made the following changes:

Terminology: We now use the term higher-order epistasis instead of fluid epistasis, emphasizing that the observed background-dependence involves more than two mutations and cannot be explained by global nonlinearities alone.

We also clarify the definitions of sign-epistasis used in this work.

By replacing arbitrary cutoffs with replicate-based error estimates and by explicitly considering bounding effects, we have substantially increased the rigor of our analysis. While this reanalysis led to both quantitative and qualitative changes in some regions, the central conclusion remains unchanged: higher-order epistasis is pervasive in the folA landscape, especially in functional backgrounds.

All analysis scripts and codes are provided as Supplementary Material.

Reviewer #3 (Public review): 

Summary: 

The authors have studied a previously published large dataset on the fitness landscape of a 9 base-pair region of the folA gene. The objective of the paper is to understand various aspects of epistasis in this system, which the authors have achieved through detailed and computationally expensive exploration of the landscape. The authors describe epistasis in this system as "fluid", meaning that it depends sensitively on the genetic background, thereby reducing the predictability of evolution at the genetic level. However, the study also finds two robust patterns. The first is the existence of a "pivot point" for a majority of mutations, which is a fixed growth rate at which the effect of mutations switches from beneficial to deleterious (consistent with a previous study on the topic). The second is the observation that the distribution of fitness effects (DFE) of mutations is predicted quite well by the fitness of the genotype, especially for high-fitness genotypes. While the work does not offer a synthesis of the multitude of reported results, the information provided here raises interesting questions for future studies in this field. 

Strengths: 

A major strength of the study is its detailed and multifaceted approach, which has helped the authors tease out a number of interesting epistatic properties. The study makes a timely contribution by focusing on topical issues like the prevalence of global epistasis, the existence of pivot points, and the dependence of DFE on the background genotype and its fitness. The methodology is presented in a largely transparent manner, which makes it easy to interpret and evaluate the results. 

The authors have classified pairwise epistasis into six types and found that the type of epistasis changes depending on background mutations. Switches happen more frequently for mutations at functionally important sites. Interestingly, the authors find that even synonymous mutations in stop codons can alter the epistatic interaction between mutations in other codons. Consistent with these observations of "fluidity", the study reports limited instances of global epistasis (which predicts a simple linear relationship between the size of a mutational effect and the fitness of the genetic background in which it occurs). Overall, the work presents some evidence for the genetic context-dependent nature of epistasis in this system. 

Weaknesses: 

Despite the wealth of information provided by the study, there are some shortcomings of the paper which must be mentioned. 

(1) In the Significance Statement, the authors say that the "fluid" nature of epistasis is a previously unknown property. This is not accurate. What the authors describe as "fluidity" is essentially the prevalence of certain forms of higher-order epistasis (i.e., epistasis beyond pairwise mutational interactions). The existence of higher-order epistasis is a well-known feature of many landscapes. For example, in an early work, (Szendro et. al., J. Stat. Mech., 2013), the presence of a significant degree of higher-order epistasis was reported for a number of empirical fitness landscapes. Likewise, (Weinreich et. al., Curr. Opin. Genet. Dev., 2013) analysed several fitness landscapes and found that higher-order epistatic terms were on average larger than the pairwise term in nearly all cases. They further showed that ignoring higher-order epistasis leads to a significant overestimate of accessible evolutionary paths. The literature on higher-order epistasis has grown substantially since these early works. Any future versions of the present preprint will benefit from a more thorough contextual discussion of the literature on higher-order epistasis.

(2) In the paper, the term 'sign epistasis' is used in a way that is different from its wellestablished meaning. (Pairwise) sign epistasis, in its standard usage, is said to occur when the effect of a mutation switches from beneficial to deleterious (or vice versa) when a mutation occurs at a different locus. The authors require a stronger condition, namely that the sum of the individual effects of two mutations should have the opposite sign from their joint effect. This is a sufficient condition for sign epistasis, but not a necessary one. The property studied by the authors is important in its own right, but it is not equivalent to sign epistasis. 

(3) The authors have looked for global epistasis in all 108 (9x12) mutations, out of which only 16 showed a correlation of R^2 > 0.4. 14 out of these 16 mutations were in the functionally important nucleotide positions. Based on this, the authors conclude that global epistasis is rare in this landscape, and further, that mutations in this landscape can be classified into one of two binary states - those that exhibit global epistasis (a small minority) and those that do not (the majority). I suspect, however, that a biologically significant binary classification based on these data may be premature. Unsurprisingly, mutational effects are stronger at the functional sites as seen in Figure 5 and Figure 2, which means that even if global epistasis is present for all mutations, a statistical signal will be more easily detected for the functionally important sites. Indeed, the authors show that the means of DFEs decrease linearly with background fitness, which hints at the possibility that a weak global epistatic effect may be present (though hard to detect) in the individual mutations. Given the high importance of the phenomenon of global epistasis, it pays to be cautious in interpreting these results. 

(4) The study reports that synonymous mutations frequently change the nature of epistasis between mutations in other codons. However, it is unclear whether this should be surprising, because, as the authors have already noted, synonymous mutations can have an impact on cellular functions. The reader may wonder if the synonymous mutations that cause changes in epistatic interactions in a certain background also tend to be non-neutral in that background. Unfortunately, the fitness effect of synonymous mutations has not been reported in the paper. 

(5) The authors find that DFEs of high-fitness genotypes tend to depend only on fitness and not on genetic composition. This is an intriguing observation, but unfortunately, the authors do not provide any possible explanation or connect it to theoretical literature. I am reminded of work by (Agarwala and Fisher, Theor. Popul. Biol., 2019) as well as (Reddy and Desai, eLife, 2023) where conditions under which the DFE depends only on the fitness have been derived. Any discussion of possible connections to these works could be a useful addition.  

We thank the reviewer for the summary of our work and for highlighting both its strengths and areas for improvement. We have carefully considered the points raised and revised the manuscript accordingly. The revised version:

(1) Clarifies the conceptual framework. We emphasize the distinction between background-dependent, higher-order epistasis and global nonlinearities. To avoid ambiguity, we have replaced the term “fluid” epistasis with higher-order epistasis throughout, in line with prior literature (e.g. Szendro et al., 2013; Weinreich et al., 2013). We now explicitly situate our results in the context of these studies and clarify our definitions of epistasis, correcting the earlier error where “strong sign epistasis” was used in place of “sign epistasis.”

(2) Improves statistical rigor. We now incorporate replicate variance and statistical error criteria in place of arbitrary thresholds. This ensures that classification of epistasis reflects experimental precision rather than fixed, arbitrary cutoffs.

(3) Expands treatment of synonymous mutations. We now explicitly analyze synonymous mutations, separating those that are neutral from those that are non-neutral. Our results show that non-neutral synonymous mutations are disproportionately responsible for altering epistatic interactions, while neutral synonymous mutations rarely do so. We also report the fitness effects of synonymous mutations directly and include new analyses showing that there is no correlation between the mean fitness effect of a synonymous mutation and the frequency with which it alters epistasis (Supplementary Fig. S11).

These revisions strengthen both the rigor and the clarity of the manuscript. We hope they address the reviewer’s concerns and make the significance of our findings, particularly the siteresolved quantification of higher-order epistasis in the folA landscape, including in synonymous mutations, more apparent.

Reviewing Editor Comments: 

Key revision suggestions: 

(1) Please quantify the impact of measurement noise on your conclusions, and perform statistical analysis to determine whether the observed differences of epistasis due to different backgrounds are statistically significant. 

(2) Please investigate how your conclusions depend on the cutoffs, and consider choosing them based on statistical criteria. 

(3) Please reconsider the possible role of global epistasis. In particular, the effect of bounds on fitness values. All reviewers are concerned that all claims, including about global epistasis, may be consistent with a simple null model where most low fitness genotypes are non-functional and variation in their fitness is simply driven by measurement noise. Please provide a convincing argument rejecting this model. 

More generally, we recommend that you consider all suggestions by reviewers, including those about results, but also those about terminology and citing relevant works. 

Thank you for your guidance. We have substantially revised the manuscript to incorporate the reviewers’ suggestions. In addition to addressing the three central issues raised, we have refined terminology, expanded the discussion of prior work, and clarified the presentation of our main results. We believe these changes significantly strengthen both the rigor and the impact of the study. We are grateful to the Reviewing Editor and reviewers for their constructive feedback.

In the revised manuscript, we address the three major points as follows:

(1) Quantifying measurement noise and statistical significance. We now use the average of six independent experimental runs for each genotype, together with the corresponding standard deviations, to explicitly quantify measurement uncertainty. Pairwise and higher-order epistasis are assessed relative to these error estimates, rather than against fixed thresholds. This ensures that differences across genetic backgrounds are statistically distinguishable from noise.

(2) Replacing arbitrary cutoffs with statistical criteria. We have eliminated the use of arbitrary thresholds. Instead, classification of interactions (positive, negative, or neutral epistasis) is based on whether fitness differences exceed replicate variance. This approach scales naturally with measurement precision. While some results change quantitatively for high-fitness backgrounds and qualitatively for low-fitness backgrounds, our central conclusions remain robust.

(3) Analysis of synonymous mutations. We now separately analyze synonymous mutations to test their role in altering epistasis. Our results show that there is no correlation between the average fitness effect of a synonymous mutation and the frequency with which it changes epistatic interactions.

We have revised terminology for clarity (replacing “fluid” with higher-order epistasis) and updated the Discussion to place our work in the broader context of the literature on higher-order epistasis.

Finally, we have rewritten the entire manuscript to improve clarity, refine the narrative flow, and ensure that the presentation more crisply reflects the subject of the study

Reviewer #1 (Recommendations for the authors): 

MINOR COMMENTS 

(1) Lines 102-107. Papkou's definition of non-functional genotypes makes sense since it is based on the fact that some genotypes are statistically indistinguishable in terms of fitness from mutants with premature stop codons in folA. It doesn't really matter whether to call them low fitness or non-functional, but it would be helpful to explain the basis for this distinction. 

Thank you for raising this point. To maintain consistency with the original dataset and analysis, we retain Papkou et al.’s nomenclature and refer to these genotypes as “functional” or “non-functional.” 

(2) Lines 111-112. I think the authors need to briefly explain here how they define the absence of epistasis. They do so in the Methods, but this information is essential and needs to be conveyed to the reader in the Results as well. 

Thank you for the suggestion. We agree that this definition is essential for readers to follow the Results. In the revised manuscript, we have added a brief explanation at the start of the Results section clarifying how we define the absence of epistasis. Specifically, we now state that two mutations are considered non-epistatic when the observed fitness of the double mutant is statistically indistinguishable (within error of six replicates) from the additive expectation based on the single mutants. This ensures that the Results section is selfcontained, while full details remain in the Methods.

(3) Lines 142 and elsewhere. The authors introduce the qualifier "fluid" to describe the fact that the value or sign of pairwise epistasis changes across genetic backgrounds. I don't see a need for this new terminology, since it is already captured adequately by the term "higher-order epistasis". The epistasis field is already rife with jargon, and I would prefer if new terms were introduced only when absolutely necessary. 

Thank you for this helpful suggestion. We agree that introducing new terminology is unnecessary here. In the revised manuscript, we have replaced the term “fluid” epistasis with “higher-order epistasis” throughout, to align with established usage and avoid adding jargon.

(4) Figure 6. I don't think this is the best way of showing that the pivot points are clustered. A histogram would be more appropriate and would take less space. However it would allow the authors to display a null distribution to demonstrate that this clustering is indeed surprising. 

(5) Lines 320-321. Mann-Whitney U tests whether one distribution is systematically shifted up or down relative to the other. Please change the language here. It looks like the authors also performed the Kolmogorov-Smirnoff test, which is appropriate, but it doesn't look like the results are reported anywhere. Please report. 

(6) Lines 330-334. The fact that HF genotypes seem to have more similar DFEs than LF genotypes is somewhat counterintuitive. Could this be an artifact of the fact that any two random HF genotypes are more similar to each other than any two randomly sampled LF genotypes? 

(7) Lines 427. The sentence "The set of these selected variants are assigned their one hamming distance neighbours to construct a new 𝑛-base sequence space" is confusing. I think it is pretty clear how to construct a n-base sequence space, and this sentence adds more confusion than it removes. 

Thank you for raising this point. To maintain consistency with the original dataset and analysis, we retain Papkou et al.’s nomenclature and refer to these genotypes as “functional” or “non-functional.” 

We now start the results section of the manuscript with a brief description of how each type of epistasis is defined. Specifically, we now state that two mutations are considered non-epistatic when the observed fitness of the double mutant is statistically indistinguishable (within the error of six replicates) from the additive expectation based on the single mutants. This ensures that the Results section is self-contained, while full details remain in the Methods.

We also agree that introducing new terminology is unnecessary. In the revised manuscript, we have replaced the term “fluid” epistasis with “higher-order epistasis” throughout, to align with established usage and avoid adding jargon. Finally, we concur that the identified sentence was unnecessary and potentially confusing; it has been removed from the revised manuscript to improve clarity. In fact, we have rewritten the entire manuscript for better flow and readability. 

Reviewer #2 (Recommendations for the authors): 

(1) Supplementary Figure S2A and S3 seem to be the same. 

(3) The classification scheme for reciprocal sign/single sign/other sign epistasis differs from convention and should be made more explicit or renamed. 

(4) Re the claim that high and low fitness backgrounds have different frequencies of the various types of epistasis: 

Are the frequency distributions of the different types of epistasis statistically different between high and low fitness backgrounds statistically significant? It seems that they follow similar general patterns, and the sample size is much smaller for high fitness backgrounds so more variance in their distributions is expected. 

Do bounding of fitness measurements play a role in generating the differences in types of epistasis seen in high vs. low-fitness backgrounds? If many variants are at the lower bound of the fitness assay, then positive epistasis might simply be less detectable for these backgrounds (which seems to be the biggest difference between high/low fitness backgrounds). 

(5) In Figure 4B, points are not independent, because the mutation effects are calculated for all mutations in all backgrounds, rather than with reference to a single background or fluorescence value. The same mutations are therefore counted many times. 

(6) It is not clear how the "pivot growth rate" was calculated or what the importance of this metric is. 

(7) In the introduction, the justification for reanalyzing the Papkou et al dataset in particular is not clear. 

(8) Epistasis at the nucleotide level is expected because of the genetic code: fitness and function are primarily affected by amino acid changes, and nucleotide mutations will affect amino acids depending on the state at other nucleotide sites in the same codon. For the most part, this is not explicitly taken account of in the paper. I recommend separating apparent epistasis due to the genetic code from that attributable to dependence among codons. 

Thank you for noting this. Figure S2A shows results for high-fitness peaks only, whereas Figure S3 shows results for all peaks across the landscape. We have now made this distinction explicit in the figure legends and main text of the revised manuscript. 

In the revised analysis, peaks are defined using the average fitness across six experimental replicates along with the corresponding standard deviation. Each genotype is compared with all single-step neighbors, and it is classified as a peak only if its mean fitness is significantly higher than all neighbors (p < 0.05). This procedure explicitly accounts for measurement error and replaces the arbitrary thresholding used previously. Full details are now described in the Methods.

To avoid confusion, we now state our definitions explicitly at the start of the analysis. We have now corrected our definition in the text. We define sign epistasis as a one where at least one mutation switches from being beneficial to deleterious. 

We have clarified our motivation in the Introduction. The Papkou et al. dataset is the most comprehensive experimental map of a complete 9-bp region of folA and provides six independent replicates, making it uniquely suited for testing hypotheses about backgrounddependent epistasis. Importantly, Papkou et al. based their conclusions on a single run, whereas our reanalysis incorporates replicate means and variances, leading to substantive differences—for example, a reduction in reported peaks from 514 to 127. By recalibrating the analysis, we provide a more rigorous account of this landscape and highlight how methodological choices affect conclusions.

We also agree that some nucleotide-level epistasis reflects the structure of the genetic code (i.e., codon degeneracy and context-dependence of amino acid substitutions). In the revised manuscript, we explicitly separate epistasis attributable to codon structure from epistasis arising among codons. For example, synonymous mutations that alter epistasis within codons are treated separately from those affecting interactions across codons, and this distinction is now clearly indicated in the Results.

Reviewer #3 (Recommendations for the authors): 

(1) The analysis of peak density and accessibility in the paragraph starting on line 96 seems a bit out of context. Its connection with the various forms of epistasis treated in the rest of the paper is unclear. 

(2) As mentioned in the Public Review, the term 'sign epistasis' has been used in a non-standard way. My suggestion would be to use a different term. Even a slightly modified term, such as "strong sign epistasis", should help to avoid any confusion. 

(3)  mentioned in the public review that it is not clear whether the synonymous mutations that change the type of epistasis also tend to be non-neutral. This issue could be addressed by computing, for example, the fitness effects of all synonymous mutations for backgrounds and mutation pairs where a switch in epistasis occurs, and comparing it with fitness effects where no such switch occurs. 

(4) Do the authors have any proposal for why synonymous mutations seem to cause more frequent changes in epistasis in low-fitness backgrounds? Related to this, is there any systematic difference between the types of switch caused by synonymous mutations in the low- versus high-fitness backgrounds? 

(5) It is unclear exactly how the pivot points were determined, especially since the data for many mutations is noisy. The protocol should be provided in the Methods section. 

(6) Line 303: possible typo, "accurate" --> "inaccurate". 

(7) The value of Delta used for the "phenotypic DFE" has not been mentioned in the main text (including Methods).

We agree that the connection needed to be clearer. In the revised manuscript, we (i) relocate and retitle this material as a brief “Landscape overview” preceding the epistasis analyses, (ii) explicitly link multi-peakedness and path accessibility to epistasis (e.g., multi-peak structure implies the presence of sign/reciprocal-sign epistasis; accessibility is shaped by background-dependent effects), and (iii) move derivations to the Supplement. We also recomputed peak density and accessibility using replicate-averaged fitness with replicate SDs, so the overview and downstream epistasis sections now use a single, error-aware landscape (updated in Figs. 1–3, with cross-references in the text).

We have aligned our terminology and now state definitions upfront. 

After replacing fixed cutoffs with replicate-based error criteria, switches are more frequent in high-fitness backgrounds (Fig. 3). Mechanistically, near the lower fitness bound, deleterious effects are masked (global nonlinearity), reducing apparent switching. Functional/high-fitness backgrounds allow both beneficial and deleterious outcomes, so background-dependent (higher-order) interactions manifest more readily. Switch types also vary by background fitness: high-fitness backgrounds show more sign/strong-sign switches, whereas low-fitness backgrounds show mostly magnitude reclassifications (Fig. 3C; Supplement Fig. Sx).

Finally, we corrected a typo by replacing “accurate” with “inaccurate” and now define Δ (equal to 0.05) in the main text (in Results and Figure 8 caption).

Author response:

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

Reviewer #1 (Public review):

Summary:

Dendrotweaks provides its users with a solid tool to implement, visualize, tune, validate, understand, and reduce single-neuron models that incorporate complex dendritic arbors with differential distribution of biophysical mechanisms. The visualization of dendritic segments and biophysical mechanisms therein provide users with an intuitive way to understand and appreciate dendritic physiology.

Strengths:

(1) The visualization tools are simplified, elegant, and intuitive.

(2) The ability to build single-neuron models using simple and intuitive interfaces.

(3) The ability to validate models with different measurements.

(4) The ability to systematically and progressively reduce morphologically-realistic neuronal models.

Weaknesses:

(1) Inability to account for neuron-to-neuron variability in structural, biophysical, and physiological properties in the model-building and validation processes.

We agree with the reviewer that it is important to account for neuron-to-neuron variability. The core approach of DendroTweaks, and its strongest aspect, is the interactive exploration of how morpho-electric parameters affect neuronal activity. In light of this, variability can be achieved through the interactive updating of the model parameters with widgets. In a sense, by adjusting a widget (e.g., channel distribution or kinetics), a user ends up with a new instance of a cell in the parameter space and receives almost real-time feedback on how this change affected neuronal activity. This approach is much simpler than implementing complex optimization protocols for different parameter sets, which would detract from the interactivity aspect of the GUI. In its revised version, DendroTweaks also accounts for neuron-to-neuron morphological variability, as channel distributions are now based on morphological domains (rather than the previous segment-specific approach). This makes it possible to apply the same biophysical configuration across various morphologies. Overall, both biophysical and morphological variability can be explored within DendroTweaks. 

(2) Inability to account for the many-to-many mapping between ion channels and physiological outcomes. Reliance on hand-tuning provides a single biased model that does not respect pronounced neuron-to-neuron variability observed in electrophysiological measurements.

We acknowledge the challenge of accounting for degeneracy in the relation between ion channels and physiological outcomes and the importance of capturing neuron-to-neuron variability. One possible way to address this, as we mention in the Discussion, is to integrate automated parameter optimization algorithms alongside the existing interactive hand-tuning with widgets. In its revised version, DendroTweaks can integrate with Jaxley (Deistler et al., 2024) in addition to NEURON. The models created in DendroTweaks can now be run with Jaxley (although not all types of models, see the limitations in the Discussion), and their parameters can be optimized via automated and fast gradient-based parameter optimization, including optimization of heterogeneous channel distributions. In particular, a key advantage of integrating Jaxley with DendroTweaks was its NMODL-to-Python converter, which significantly reduced the need to manually re-implement existing ion channel models for Jaxley (see here: https://dendrotweaks.readthedocs.io/en/latest/tutorials/convert_to_jaxley.html).

(1) Michael Deistler, Kyra L. Kadhim, Matthijs Pals, Jonas Beck, Ziwei Huang, Manuel Gloeckler, Janne K. Lappalainen, Cornelius Schröder, Philipp Berens, Pedro J. Gonçalves, Jakob H. Macke Differentiable simulation enables large-scale training of detailed biophysical models of neural dynamics bioRxiv 2024.08.21.608979; doi:https://doi.org/10.1101/2024.08.21.608979

Lack of a demonstration on how to connect reduced models into a network within the toolbox.

Building a network of reduced models is an exciting direction, yet beyond the scope of this manuscript, whose primary goal is to introduce DendroTweaks and highlight its capabilities. DendroTweaks is designed for single-cell modeling, aiming to cover its various aspects in great detail. Of course, we expect refined single-cell models, both detailed and simplified, to be further integrated into networks. But this does not need to occur within DendroTweaks. We believe this network-building step is best handled by dedicated network simulation platforms. To facilitate the network-building process, we extended the exporting capabilities of DendroTweaks. To enable the export of reduced models in DendroTweaks’s modular format, as well as in plain simulator code, we implemented a method to fit the resulting parameter distributions to analytical functions (e.g., polynomials). This approach provided a compact representation, requiring a few coefficients to be stored in order to reproduce a distribution, independently of the original segmentation. The reduced morphologies can be exported as SWC files, standardized ion channel models as MOD files, and channel distributions as JSON files. Moreover, plain NEURON code (Python) to instantiate a cell class can be automatically generated for any model, including the reduced ones. Finally, to demonstrate how these exported models can be integrated into larger simulations, we implemented a "toy" network model in a Jupyter notebook included as an example in the GitHub repository. We believe that these changes greatly facilitate the integration of DendroTweaks-produced models into networks while also allowing users to run these networks on their favorite platforms.

(4) Lack of a set of tutorials, which is common across many "Tools and Resources" papers, that would be helpful in users getting acquainted with the toolbox.

This is an important point that we believe has been addressed fully in the revised version of the tool and manuscript. As previously mentioned, the lack of documentation was due to the software's early stage. We have now added comprehensive documentation, which is available at https://dendrotweaks.readthedocs.io. This extensive material includes API references, 12 tutorials, 4 interactive Jupyter notebooks, and a series of video tutorials, and it is regularly updated with new content. Moreover, the toolbox's GUI with example models is available through our online platform at https://dendrotweaks.dendrites.gr.  

Reviewer #2 (Public review):

The paper by Makarov et al. describes the software tool called DendroTweaks, intended for the examination of multi-compartmental biophysically detailed neuron models. It offers extensive capabilities for working with very complex distributed biophysical neuronal models and should be a useful addition to the growing ecosystem of tools for neuronal modeling.

Strengths

(1) This Python-based tool allows for visualization of a neuronal model's compartments.

(2) The tool works with morphology reconstructions in the widely used .swc and .asc formats.

(3) It can support many neuronal models using the NMODL language, which is widely used for neuronal modeling.

(4) It permits one to plot the properties of linear and non-linear conductances in every compartment of a neuronal model, facilitating examination of the model's details.

(5) DendroTweaks supports manipulation of the model parameters and morphological details, which is important for the exploration of the relations of the model composition and parameters with its electrophysiological activity.

(6) The paper is very well written - everything is clear, and the capabilities of the tool are described and illustrated with great attention to detail.

Weaknesses

(1) Not a really big weakness, but it would be really helpful if the authors showed how the performance of their tool scales. This can be done for an increasing number of compartments - how long does it take to carry out typical procedures in DendroTweaks, on a given hardware, for a cell model with 100 compartments, 200, 300, and so on? This information will be quite useful to understand the applicability of the software.

DendroTweaks functions as a layer on top of a simulator. As a result, its performance scales in the same way as for a given simulator. The GUI currently displays the time taken to run a simulation (e.g., in NEURON) at the bottom of the Simulation tab in the left menu. While Bokeh-related processing and rendering also consume time, this is not as straightforward to measure. It is worth noting, however, that this time is short and approximately equivalent to rendering the corresponding plots elsewhere (e.g., in a Jupyter notebook), and thus adds negligible overhead to the total simulation time. 

(2) Let me also add here a few suggestions (not weaknesses, but something that can be useful, and if the authors can easily add some of these for publication, that would strongly increase the value of the paper).

(3) It would be very helpful to add functionality to read major formats in the field, such as NeuroML and SONATA.

We agree with the reviewer that support for major formats will substantially improve the toolbox, ensuring the reproducibility and reusability of the models. While integration with these formats has not been fully implemented, we have taken several steps to ensure elegant and reproducible model representation. Specifically, we have increased the modularity of model components and developed a custom compact data format tailored to single-cell modeling needs. We used a JSON representation inspired by the Allen Cell Types Database schema, modified to account for non-constant distributions of the model parameters. We have transitioned from a representation of parameter distributions dependent on specific segmentation graphs and sections to a more generalized domain-based distribution approach. In this revised methodology, segment groups are no longer explicitly defined by segment identifiers, but rather by specification of anatomical domains and conditional expressions (e.g., “select all segments in the apical domain with the maximum diameter < 0.8 µm”). Additionally, we have implemented the export of experimental protocols into CSV and JSON files, where the JSON files contain information about the stimuli (e.g., synaptic conductance, time constants), and the CSV files store locations of recording sites and stimuli. These features contribute toward a higher-level, structured representation of models, which we view as an important step toward eventual compatibility with standard formats such as NeuroML and SONATA. We have also initiated a two-way integration between DendroTweaks and SONATA. We developed a converter from DendroTweaks to SONATA that automatically generates SONATA files to reproduce models created in DendroTweaks. Additionally, support for the DendroTweaks JSON representation of biophysical properties will be added to the SONATA data format ecosystem, enabling models with complex dendritic distributions of channels. This integration is still in progress and will be included in the next version of DendroTweaks. While full integration with these formats is a goal for future releases, we believe the current enhancements to modularity and exportability represent a significant step forward, providing immediate value to the community.

(4) Visualization is available as a static 2D projection of the cell's morphology. It would be nice to implement 3D interactive visualization.

We offer an option to rotate a cell around the Y axis using a slider under the plot. This is a workaround, as implementing a true 3D visualization in Bokeh would require custom Bokeh elements, along with external JavaScript libraries. It's worth noting that there are already specialized tools available for 3D morphology visualization. In light of this, while a 3D approach is technically feasible, we advocate for a different method. The core idea of DendroTweaks’ morphology exploration is that each section is “clickable”, allowing its geometric properties to be examined in a 2D "Section" view. Furthermore, we believe the "Graph" view presents the overall cell topology and distribution of channels and synapses more clearly.

(5) It is nice that DendroTweaks can modify the models, such as revising the radii of the morphological segments or ionic conductances. It would be really useful then to have the functionality for writing the resulting models into files for subsequent reuse.

This functionality is fully available in local installations. Users can export JSON files with channel distributions and SWC files after morphology reduction through the GUI. Please note that for resource management purposes, file import/export is disabled on the public online demo. However, it can be enabled upon local installation by modifying the configuration file (app/default_config.json). In addition, it is now possible to generate plain NEURON (Python) code to reproduce a given model outside the toolbox (e.g., for network simulations). Moreover, it is now possible to export the simulation protocols as CSV files for locations of stimuli and recordings and JSON files for stimuli parameters.

(6) If I didn't miss something, it seems that DendroTweaks supports the allocation of groups of synapses, where all synapses in a group receive the same type of Poisson spike train. It would be very useful to provide more flexibility. One option is to leverage the SONATA format, which has ample functionality for specifying such diverse inputs.

Currently, each population of “virtual” neurons that form synapses on the detailed cell shares the same set of parameters for both biophysical properties of synapses (e.g., reversal potential, time constants) and presynaptic "population" activity (e.g., rate, onset). The parameter that controls an incoming Poisson spike train is the rate, which is indeed shared across all synapses in a population. Unfortunately, the current implementation lacks the capability to simulate complex synaptic inputs with heterogeneous parameters across individual synapses or those following non-uniform statistical distributions (the present implementation is limited to random uniform distributions). We have added this information in the Discussion (3. Discussion - 3.2 Limitations and future directions - ¶.5) to make users aware of the limitations. As it requires a substantial amount of additional work, we plan to address such limitations in future versions of the toolbox.

(7) "Each session can be saved as a .json file and reuploaded when needed" - do these files contain the whole history of the session or the exact snapshot of what is visualized when the file is saved? If the latter, which variables are saved, and which are not? Please clarify.

In the previous implementation, these files captured the exact snapshot of the model's latest state. In the new version, we adopted a modular approach where the biophysical configuration (e.g., channel distributions) and stimulation protocols are exported to separate files. This allows the user to easily load and switch the stimulation protocols for a given model. In addition, the distribution of parameters (e.g., channel conductances) is now based on the morphological domains and is agnostic of the exact morphology (i.e., sections and segments), which allows the same JSON files with biophysical configurations to be reused across multiple similar morphologies. This also allows for easy file exchange between the GUI and the standalone version.

Joint recommendations to Authors:

The reviewers agreed that the paper is well written and that DendroTweaks offers a useful collection of tools to explore models of single-cell biophysics. However, the tooling as provided with this submission has critical limitations in the capabilities, accessibility, and documentation that significantly limit the utility of DendroTweaks. While we recognize that it is under active development and features may have changed already, we can only evaluate the code and documentation available to us here.

We thank the reviewers for their positive evaluation of the manuscript and express our sincere appreciation for their feedback. We acknowledge the limitations they have pointed out and have addressed most of these concerns in our revised version.

In particular, we would emphasize:

(1) While the features may be rich, the documentation for either a user of the graphical interface or the library is extremely sparse. A collection of specific tutorials walking a GUI user through simple and complex model examples would be vital for genuine uptake. As one category of the intended user is likely to be new to computational modeling, it would be particularly good if this documentation could also highlight known issues that can arise from the naive use of computational techniques. Similarly, the library aspect needs to be documented in a more standard manner, with docstrings, an API function list, and more didactic tutorials for standard use cases.

DendroTweaks now features comprehensive documentation. The standalone Python library code is well-documented with thorough docstrings. The overall code modularity and readability have improved. The documentation is created using the widely adopted Sphinx generator, making it accessible for external contributors, and it is available via ReadTheDocs https://dendrotweaks.readthedocs.io/en/latest/index.html. The documentation provides a comprehensive set of tutorials (6 basic, 6 advanced) covering all key concepts and workflows offered by the toolbox. Interactive Jupyter notebooks are included in the documentation, along with the quick start guide. All example models also have corresponding notebooks that allow users to build the model from scratch.

The toolbox has its own online platform, where a quick-start guide for the GUI is available https://dendrotweaks.dendrites.gr/guide.html. We have created video tutorials for the GUI covering the basic use cases. Additionally, we have added tips and instructions alongside widgets in the GUI, as well as a status panel that displays application status, warnings, and other information. Finally, we plan to familiarize the community with the toolbox by organizing online and in-person tutorials, as the one recently held at the CNS*2025 conference (https://cns2025florence.sched.com/event/25kVa/building-intuitive-and-efficient-biophysicalmodels-with-jaxley-and-dendrotweaks). Moreover, the toolbox was already successfully used for training young researchers during the Taiwan NeuroAI 2025 Summer School, founded by Ching-Lung Hsu. The feedback was very positive.

(2) The paper describes both a GUI web app and a Python library. However, the code currently mixes these two in a way that largely makes sense for the web app but makes it very difficult to use the library aspect. Refactoring the code to separate apps and libraries would be important for anyone to use the library as well as allowing others to host their own DendroTweak servers. Please see the notes from the reviewing editor below for more details.

The code in the previous `app/model` folder, responsible for the core functionality of the toolbox, has been extensively refactored and extended, and separated into a standalone library. The library is included in the Python package index (PyPI, https://pypi.org/project/dendrotweaks).

Notes from the Reviewing Editor Comments (Recommendations for the authors):

(1) While one could import morphologies and use a collection of ion channel models, details of synapse groups and stimulation approaches appeared to be only configurable manually in the GUI. The ability to save and load full neuron and simulation states would be extremely useful for reproducibility and sharing data with collaborators or as an interactive data product with a publication. There is a line in the text about saving states as json files (also mentioned by Reviewer #2), but I could see no such feature in the version currently online.

We decided to reserve the online version for demonstration and educational purposes, with more example models being added over time. However, this functionality is available upon local installation of the app (and after specifying it in the ‘default_config.json’ in the root directory of the app). We’ve adopted a modular model representation to store separately morphology, channel models, biophysical parameters, and stimulation protocols.

(2) Relatedly, GUI exploration of complex data is often a precursor to a more automated simulation run. An easy mechanism to go from a user configuration to scripting would be useful to allow the early strength of GUIs to feed into the power of large-scale scripting.

Any model could be easily exported to a modular DendroTweaks representation and later imported either in the GUI or in the standalone version programmatically. This ensures a seamless transition between the two use cases.

(3) While the paper discusses DendroTweaks as both a GUI and a python library, the zip file of code in the submission is not in good form as a library. Back-end library code is intermingled with front-end web app code, which limits the ability to install the library from a standard python interface like PyPI. API documentation is also lacking. Functions tend to not have docstrings, and the few that do, do not follow typical patterns describing parameters and types.

As stated above, all these issues have been resolved in the new version of the toolbox. The library code is now housed in a separate repository https://github.com/Poirazi-Lab/DendroTweaks and included in PyPI https://pypi.org/project/dendrotweaks. The classes and public methods follow Numpy-style docstrings, and the API reference is available in the documentation: https://dendrotweaks.readthedocs.io/en/latest/genindex.html.

(4) Library installation is very difficult. The requirements are currently a lockfile, fully specifying exact versions of all dependencies. This is exactly correct for web app deployment to maintain consistency, but is not feasible in the context of libraries where you want to have minimal impact on a user's environment. Refactoring the library from the web app is critical for making DendroTweaks usable in both forms described in the paper.

The lockfile makes installation more or less impossible on computer setups other than that of the author. Needless to say, this is not acceptable for a tool, and I would encourage the authors to ask other people to attempt to install their code as they describe in the text. For example, attempting to create a conda environment from the environment.yml file on an M1 MacBook Pro failed because it could not find several requirements. I was able to get it to install within a Linux docker image with the x86 platform specified, but this is not generally viable. To make this be the tool it is described as in text, this must be resolved. A common pattern that would work well here is to have a requirements lockfile and Docker image for the web app that imports a separate, more minimally restrictive library package with that could be hosted on PyPI or, less conveniently, through conda-forge.

The installation of the standalone library is now straightforward via pip install dendrotweaks.On the Windows platform, however, manual installation of NEURON is required as described          in the official NEURON documentation https://nrn.readthedocs.io/en/8.2.6/install/install_instructions.html#windows.

(5) As an aside, to improve potential uptake, the authors might consider an MIT-style license rather than the GNU Public License unless they feel strongly about the GPL. Many organizations are hesitant to build on GPL software because of the wide-ranging demands it places on software derived from or using GPL code.

We thank the editor for this suggestion. We are considering changing the licence to MPL 2.0. It will maintain copyleft restrictions only on the package files while allowing end-users to freely choose their own license for any derived work, including the models, generated data files, and code that simply imports and uses our package.

Reviewer #1 (Recommendations for the authors):

(1) Abstract: Neurons rely on the interplay between dendritic morphology and ion channels to transform synaptic inputs into a sequence of somatic spikes. Technically, this would have to be morphology, ion channels, pumps, transporters, exchangers, buffers, calcium stores, and other molecules. For instance, if the calcium buffer concentration is large, then there would be less free calcium for activating the calcium-activated potassium channels. If there are different chloride co-transporters - NKCC vs. KCC - expressed in the neuron or different parts of the neuron, that would alter the chloride reversal for all the voltage- or ligand-gated chloride channels in the neuron. So, while morphology and ion channels are two important parts of the transformation, it would be incorrect to ignore the other components that contribute to the transformation. The statement might be revised to make these two components as two critical components.

The phrase “Two critical components” was added as it was suggested by the reviewer.

(2) Section 2.1 - The overall GUI looks intuitive and simple.

(3) Section 2.2

(a) The Graph view of morphology, especially accounting for the specific d_lambda is useful.

(b) "Note that while microgeometry might not significantly affect the simulation at a low spatial resolution (small number of segments) due to averaging, it can introduce unexpected cell behavior at a higher level of spatial discretization."

It might be good to warn the users that the compartmentalization and error analyses are with reference to the electrical lambda. If users have to account for calcium microdomains, these analyses wouldn't hold given the 2 orders of magnitude differences between the electrical and the calcium lambdas (e.g., Zador and Koch, J Neuroscience, 1994). Please sensitize users that the impact of active dendrites in regulating calcium microdomains and signaling is critical when it comes to plasticity models in morphologically realistic structures.

We thank the reviewer for this important point. We have clarified in the text that our spatial discretization specifically refers to the electrical length constant. We acknowledge that electrical and chemical processes operate on fundamentally different spatial and temporal scales, which requires special consideration when modeling phenomena like synaptic plasticity. We have sensitized users about this distinction. However, we do not address such examples in the manuscript, thus leaving the detailed discussion of non-electrical compartmentalization beyond the scope of this work.

(c) I am not very sure if the "smooth" tool for diameters that is illustrated is useful. Users shouldn't consider real variability in morphology as artifacts of reconstruction. As mentioned above, while this might not be an issue with electrical compartmentalization, calcium compartmentalization will severely be affected by small changes in morphology. Any model that incorporates calcium-gated channels should appropriately compartmentalize calcium. Without this, the spread of activation of calcium-dependent conductances would be an overestimate. Even small changes in cellular shape and curvature can have large impacts when it comes to signaling in terms of protein aggregation and clustering.

Although this functionality is still available in the toolbox, we have removed the emphasis from it in the manuscript. Nevertheless, for the purpose of addressing the reviewer’s comment, we provide an example when this “smoothening” might be needed:please see Figure S1 from Tasciotti et al. 2025.

(2) Simone Tasciotti, Daniel Maxim Iascone, Spyridon Chavlis, Luke Hammond, Yardena Katz, Attila Losonczy, Franck Polleux, Panayiota Poirazi. From Morphology to Computation: How Synaptic Organization Shapes Place Fields in CA1 Pyramidal Neurons bioRxiv 2025.05.30.657022; doi: https://doi.org/10.1101/2025.05.30.657022

(4) Section 2.3

(a) The graphical representation of channel gating kinetics is very useful.

(b) Please warn the users that experimental measurements of channel gating kinetics are extremely variable. Taking the average of the sigmoids or the activation/deactivation/inactivation kinetics provides an illusion that each channel subtype in a given cell type has fixed values of V_1/2, k, delta, and tau, but it is really a range obtained from several experiments. The heterogeneity is real and reflects cell-to-cell variability in channel gating kinetics, not experimental artifacts. Please sensitize the readers that there is not a single value for these channel parameters.

This is a fair comment, and it refers to a general problem in neuronal modeling. In DendroTweaks, we follow the approach widely used in the community that indeed doesn't account for heterogeneity. We added a paragraph in the revised manuscript's Discussion (3. Discussion - 3.3 Limitations and future directions - ¶.3) to address this issue.

(5) Section 2.4

(a) Same as above: Please sensitize users that the gradients in channel conductances are measured as an average of measurements from several different cells. This gradient need not be present in each neuron, as there could be variability in location-dependent measurements across cells. The average following a sigmoid doesn't necessarily mean that each neuron will have the channel distributed with that specific sigmoid (or even a sigmoid!) with the specific parametric values that the average reported. This is extremely important because there is an illusion that the gradient is fixed across cells and follows a fixed functional form.

We added this information to our Discussion in the same paragraph mentioned above.

(b) Please provide an example where the half-maximal voltage of a channel varies as a function of distance (such as Poolos et al., Nature Neuroscience, 2002 or Migliore et al., 1999; Colbert and Johnston, 1997). This might require a step-like function in some scenarios. An illustration would be appropriate because people tend to assume that channel gating kinetics are similar throughout the dendrite. Again, please mention that these shifts are gleaned from the average and don't really imply that each neuron must have that specific gradient, given neuron-to-neuron variability in these measurements.

We thank the reviewer for the provided literature, which we now cite when describing parameter distributions (2. Results - 2.4 Distributing ion channels - ¶.1). Please note that DendroTweaks' programming interface and data format natively support non-linear distribution of kinetic parameters alongside the channel conductances. As for the step-like function, users can either directly apply the built-in step-like distribution function or create it by combining two constant distributions.

(6) Section 2.5

(a) It might be useful to provide a mechanism for implementing the normalization of unitary conductances at the cell body, (as in Magee and Cook, 2000; Andrasfalvy et al., J Neuroscience, 2001). Specifically, users should be able to compute AMPAR conductance values at each segment which would provide a somatic EPSP value of 0.2 mV.

This functionality is indeed useful and will be added in future releases. Currently, it has been mentioned in the list of known limitations when working with synaptic inputs (3. Discussion - 3.3 Limitations and future directions - ¶.5).

(b) Users could be sensitized about differences in decay time constants of GABA_A receptors that are associated with parvalbamin vs. somatostatin neurons. As these have been linked to slow and fast gamma oscillations and different somatodendritic locations along different cell types, this might be useful (e.g., 10.1016/j.neuron.2017.11.033;10.1523/jneurosci.0261-20.2020; 10.7554/eLife.95562.1; 10.3389/fncel.2023.1146278).

We thank the reviewer for highlighting this important biological detail. DendroTweaks enables users to define model parameters specific to their cell type of interest. For practical reasons, we leave the selection of biologically relevant parameters to the users. However, we will consider adding an explicit example in our tutorials to showcase the toolbox's flexibility in this regard.

(7) Section 2.6

While reducing the morphological complexity has its advantages, users of this tool should be sensitized in this section about how the reduction does not capture all the complexity of the dendritic computation. For instance, the segregation/amplification properties of Polsky et al., 2004, Larkum et al., 2009 would not be captured by a fully reduced model. An example across different levels of reductions, implementing simulations in Figure 7F (but for synapses on the same vs. different branches), would be ideal. Demonstrate segregation/amplification in the full model for the same set of synapses - coming on the same branch/different branch (linear integration of synapses on different branches and nonlinear integration of synapses on the same branch). Then, show that with different levels of reduction, this segregation/amplification vanishes in the reduced model. In addition, while impedance-based approaches account for account for electrical computation, calcium-based computation is not something that is accountable with reduced models, given the small lambda_calcium values. Given the importance of calcium-activated conductances in electrical behaviour, this becomes extremely important to account for and sensitize users to. The lack of such sensitization results in presumptuous reductions that assume that all dendritic computation is accounted for by reduced models!

We agree with the reviewer that reduction leads to a loss in the complexity of dendritic computation. This has been stated in both the original algorithm paper (Amsalem et al., 2020) and in our manuscript (e.g., 3. Discussion - 3.2 Comparison to existing modeling software - ¶.6). In fact, to address this problem, we extended the functionality of neuron_reduce to allow for multiple levels of morphology reduction. Our motivation for integrating morphology reduction in the toolbox was to leverage the exploratory power of DendroTweaks to assess how different degrees of reduction alter cell integrative properties, determining which computations are preserved, which are lost, and at what specific reduction level these changes occur. Nevertheless, to address this comment, we've made it more explicit in the Discussion that reduction inevitably alters integrative properties and, at a certain level, leads to loss of dendritic computations.

(8) Section 2.7

(a) The validation process has two implicit assumptions:

(i) There is only one value of physiological measurements that neurons and dendrites are endowed with. The heterogeneity in these measurements even within the same cell type is ignored. The users should be allowed to validate each measurement over a range rather than a single value. Users should be sensitized about the heterogeneity of physiological measurements.

(ii) The validation process is largely akin to hand-tuning models where a one-to-one mapping of channels to measurements is assumed. For instance, input resistance can be altered by passive properties, by Ih, and by any channel that is active under resting conditions. Firing rate and patterns can be changed by pretty much every single ion channel that expresses along the somatodendritic axis.

An updated validation process that respects physiological heterogeneities in measurements and accounts for global dependencies would be more appropriate. Please update these to account for heterogeneities and many-to-many mappings between channels and measurements. An ideal implementation would be to incorporate randomized search procedures (across channel parameters spanning neuron-to-neuron variability in channel conductances/gating properties) to find a population of models that satisfy all physiological constraints (including neuron-to-neuron variability in each physiological measurement), rather than reliance on procedures that are akin to hand-tuning models. Such population-based approaches are now common across morphologically-realistic models for different cell types (e.g., Rathour and Narayanan, PNAS, 2014; Basak and Narayanan, J Physiology, 2018; Migliore et al., PLoS Computational Biology, 2018; Basak and Narayanan, Brain Structure and Function, 2020; Roy and Narayanan, Neural Networks, 2021; Roy and Narayanan, J Physiology, 2023; Arnaudon et al., iScience, 2023; Reva et al., Patterns, 2023; Kumari and Narayanan, J Neurophysiology, 2024) and do away with the biases introduced by hand-tuning as well as the assumption of one-to-one mapping between channels and measurements.

We appreciate the reviewer’s comment and the suggested alternatives to our validation process. We have extended the discussion on these alternative approaches (3. Discussion - 2. Comparison to existing modeling software - ¶.5). However, it is important to note that neither one-value nor one-to-one mapping assumption is imposed in our approach. It is true that validation is performed on a given model instance with fixed single-value parameters. However, users can discover heterogeneity and degeneracy in their models via interactive exploration. In the GUI, a given parameter can be changed, and the influence of this change on model output can be observed in real time. Validation can be run after each change to see whether the model output still falls within a biologically plausible regime or not. This is, of course, time-consuming and less efficient than any automated parameter optimization.

However, and importantly, this is the niche of DendroTweaks. The approach we provide here can indeed be referred to as model hand-tuning. This is intentional: we aim to complement black-box optimization by exposing the relationship between parameters and model outputs. DendroTweaks is not aimed at automated parameter optimization and is not meant to provide the user with parameter ranges automatically. The built-in validation in DendroTweaks is intended as a lightweight, fast feedback tool to guide manual tuning of dendritic model parameters so as to enhance intuitive understanding and assess the plausibility of outputs, not as a substitute for comprehensive model validation or optimization. The latter can be done using existing frameworks, designed for this purpose, as mentioned by the reviewer. 

(b) Users could be asked to wait for RMP to reach steady state. For instance, in some of the traces in Figure 7, the current injection is provided before RMP reaches steady-state. In the presence of slow channels (HCN or calcium-activated channels), the RMP can take a while to settle down. Users might be sensitized about this. This would also bring to attention the ability of several resting channels in modulating RMP, and the need to wait for steady-state before measurements are made.

We agree with the observation and updated the validation process accordingly. We have added functionality for simulation stabilization, allowing users to pre-run a simulation before the main simulation time. For example, model.run(duration=1000, prerun_time=300) could be used to stabilize the model for a period of 300 ms before running the main simulation for 1 s.

(c) Strictly speaking, it is incorrect to obtain membrane time constant by fitting a single exponential to the initial part of the sag response (Figure 7A). This may be confirmed in the model by setting HCN to zero (strictly all active channel conductances to zero), obtaining the voltage-response to a pulse current, fitting a double exponential (as Rall showed, for a finite cable or for a real neuron, a single exponential would yield incorrect values for the tau) to the voltage response, and mapping membrane time constant to the slower of the two time-constants (in the double exponential fit). This value will be very different from what is obtained in Figure 7A. Please correct this, with references to Rall's original papers and to electrophysiological papers that use this process to assess membrane properties of neurons and their dendrites (e.g., Stuart and Spruston, J Neurosci, 1998; Golding and Spruston, J Physiology, 2005).

We updated the algorithm for calculating the membrane time constant based on the reviewer's suggestions and added the suggested references. The time constant is now obtained in a model with blocked HCN channels (setting maximal conductance to 0) via a double exponential fit, taking the slowest component.

(9) Section 3

(a) May be good to emphasize the many-to-many mapping between ion channels and neuronal functions here in detail, and on how to explore this within the Dendrotweaks framework.

We have added a paragraph in the Discussion that addresses both the problems of heterogeneity and degeneracy in biological neurons and neuronal models (3. Discussion - 3.3 Limitations and future directions - ¶.3)

(b) May be good to have a specific section either here or in results about how the different reduced models can actually be incorporated towards building a network.

As mentioned earlier, building a network of reduced models is a promising new direction. However, it is beyond the scope of this manuscript, whose primary goal is to introduce DendroTweaks and highlight its capabilities. DendroTweaks is designed for single-cell modeling and provides export capabilities that allow integrating it into broader workflows, including network modeling. We have added a paragraph in the manuscript (3. Discussion - 3.1 Conceptual and implementational accessibility - ¶.2) that addresses how DendroTweaks could be used alongside other software, in particular for scaling up single-cell models to the network level.

(10) Section 4

(a) Section 4.3: In the second sentence (line 568), the "first Kirchhoff's law" within parentheses immediately after Q=CV gives an illusion that Q=CV is the first Kirchhoff's law! Please state that this is with reference to the algebraic sum of currents at a node.

We have corrected the equations and apologize for this oversight. 

(b) Table 1: In the presence of active ion channels, input resistance, membrane time constant, and voltage attenuation are not passive properties. Input resistance is affected by any active channel that is active at rest (HCN, Kir, A-type K+ through the window current, etc). The same holds for membrane time constant and voltage attenuation as well. This could be made clear by stating if these measurements are obtained in the presence or absence of active ion channels. In real neurons, all these measurements are affected by active ion channels; so, ideally, these are also active properties, not passive! Also, please mention that in the presence of resonating channels (e.g., HCN, M-type K+), a single exponential fit won't be appropriate to obtain tau, given the presence of sag.

We thank the reviewer for pointing out this ambiguity. What the term “Passive” means in Table 1 (e.g., for the input resistance, R_in) is that the minimal set of parameters needed to validate R_in are the passive ones (i.e., Cm, Ra, and Leak). We have changed the table listing to reflect this.

Reviewer #2 (Recommendations for the authors):

(1) Figure 2B and the caption to Figure 2F show and describe the diameter of the sections, whereas the image in Figure 2F shows the radius. Which is the correct one?

The reason for this is that Figure 2B shows the sections' geometry as it is represented in NEURON, i.e., with diameters, while Figure 2F shows the geometry as it is represented in an SWC file (as these changes are made based on the SWC file). Nevertheless, as mentioned earlier, we decided to remove panel F from the figure in the new version, to present a more important panel on tree graph representations.

(2) "Each segment can be viewed as an equivalent RC circuit representing a part of the membrane". The example in Figure 2B is perhaps a relatively simple case. For more complex cases where multiple nonlinear conductances are present in each section, would it be possible to show each of these conductances explicitly? If yes, it would be nice to illustrate that.

We would like to clarify that "can be viewed" here was intended to mean "can be considered," and we have updated the text accordingly. The schematic RC circuits were added to the corresponding figure for illustration purposes only and are not present in the GUI, as this would indeed be impractical for multiple conductances.

(3) Some extra citations could be added. For example, it is a little strange that BRIAN2 is mentioned, but NEST is not. It might be worth mentioning and citing it. Also, the Allen Cell Types Database is mentioned, but no citation for it is given. It could be useful to add such citations (https://doi.org/10.1038/s41593-019-0417-0, https://doi.org/10.1038/s41467-017-02718-3).

Brian 2 is extensively used in our lab on its own and as a foundation of the Dendrify library (Pagkalos et al., 2023). As stated in the discussion, we are considering bridging reduced Hodgkin-Huxley-type models to Dendrify leaky integrate-and-fire type models. For these reasons, Brian 2 is mentioned in the discussion. However, we acknowledge that our previous overview omitted references to some key software, which have now been added to the updated manuscript. We appreciate the reviewer providing references that we had overlooked.

(3) Pagkalos, M., Chavlis, S. & Poirazi, P. Introducing the Dendrify framework for incorporating dendrites to spiking neural networks. Nat Commun 14, 131 (2023). https://doi.org/10.1038/s41467-022-35747-8

Author response:

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

Reviewing Editor Comments:

The study design used reversal learning (i.e. the CS+ becomes the CS- and vice versa), while the title mentions 'fear learning and extinction'. In my opinion, the paper does not provide insight into extinction and the title should be changed.

Thank you for this important point. We agree that our paradigm focuses more directly on reversal learning than on standard extinction, as the test phases represent extinction in the absence of a US but follow a reversal phase. To better reflect the core of our investigation, we have changed the title.

Proposed change in manuscript (Title): Original Title: Distinct representational properties of cues and contexts shape fear learning and extinction 

New Title: Distinct representational properties of cues and contexts shape fear and reversal learning

Secondly, the design uses 'trace conditioning', whereas the neuroscientific research and synaptic/memory models are rather based on 'delay conditioning'. However, given the limitations of this design, it would still be possible to make the implications of this paper relevant to other areas, such as declarative memory research.

This is an excellent point, and we thank you for highlighting it. Our design, where a temporal gap exists between the CS offset and US onset, is indeed a form of trace conditioning. We also agree that this feature, particularly given the known role of the hippocampus in trace conditioning, strengthens the link between our findings and the broader field of episodic memory.

Proposed change in manuscript (Methods, Section "General procedure and stimuli"): We inserted the following text (lines 218-220): "It is important to note that the temporal gap between the CS offset and potential US delivery (see Figure 1A) indicates that our paradigm employs a trace conditioning design. This form of learning is known to be hippocampus-dependent and has been distinguished from delay conditioning.

Proposed change in manuscript (Discussion): We added the following to the discussion (lines 774-779): "Furthermore, our use of a trace conditioning paradigm, which is known to engage the hippocampus more than delay conditioning does, may have facilitated the detection of item-specific, episodiclike memory traces and their interaction with context. This strengthens the relevance of our findings for understanding the interplay between aversive learning and mechanisms of episodic memory."

The strength of the evidence at this point would be described as 'solid'. In order to increase the strength (to convincing), analyses including FWE correction would be necessary. I think exploratory (and perhaps some FDR-based) analyses have their valued place in papers, but I agree that these should be reported as such. The issue of testing multiple independent hypotheses also needs to be addressed to increase the strength of evidence (to convincing). Evaluating the design with 4 cues could lead to false positives if, for example, current valence, i.e. (CS++ and CS-+) > (CS+- and CS--), and past valence (CS++ > CS+-) > (CS-+ > CS--) are tested as independent tests within the same data set. Authors need to adjust their alpha threshold.

We fully agree. As summarized in our general response, we have implemented two major changes to our statistical approach to address these concerns comprehensively. These, are stated above, are the following:

(1) Correction for Multiple Hypotheses: We previously used FWER-corrected p-values that were obtained through permutation testing. We have now applied a Bonferroni adjustment to the FWER-corrected threshold (previously 0.05) used in our searchlight analyses. For instance, in the acquisition phase, since 2 independent tests (contrasts) were conducted, the significance threshold of each of these searchlight maps was set to p <0.025 (after FWE-correction estimated through non-parametric permutation testing); in reversal, 4 tests were conducted, hence the significance threshold was set to p<0.0125. This change is now clearly described in the Methods section (section “Searchlight approach” (lines 477484). This change had no impact on our searchlight results, given that all clusters that were previously as significant with the previous FWER alpha of 0.05 were also significant at the new, Bonferroni-adjusted thresholds; we also now report the cluster-specific corrected p-values in the cluster tables in Supplementary Material.

(2) ROI Analyses: Our ROI-based analyses used FDR-based correction for within each item reinstatement/generalized reinstatement pair of each ROI. We now explicitly state in the abstract, methods and results sections that these ROI-based analyses are exploratory and secondary to the primary whole-brain results, given that the correction method used is more liberal, in accordance with the exploratory character of these analyses.

We are confident that these changes ensure both the robustness and transparency of our reported findings.

Reviewer #1 (Public Review):

(1) I had a difficult time unpacking lines 419-420: "item stability represents the similarity of the neural representation of an item to other representations of this same item."

We thank the reviewer for pointing out this lack of clarity. We have revised the definition to be more intuitive and have ensured it is introduced earlier in the manuscript.

Proposed change in manuscript (Introduction, lines 144-150): We introduced the concept earlier and more clearly: "Furthermore, we can measure the consistency of a neural pattern for a given item across multiple presentations. This metric, which we refer to as “item stability”, quantifies how consistently a specific stimulus (e.g., the image of a kettle) is represented in the brain across multiple repetitions of the same item. Higher item stability has been linked to successful episodic memory encoding (Xue et al., 2010)."

Proposed change in manuscript (Methods, Section "Item stability and generalization of cues"): Original text: "Thus, item stability represents the similarity of the neural representation of an item to other representations of this same item (Xue, 2018), or the consistency of neural activity across repetitions (Sommer et al., 2022)."

Revised text (lines 434-436): "Item stability is defined as the average similarity of neural patterns elicited by multiple presentations of the same item (e.g., the kettle). It therefore measures the consistency of an item's neural representation across repeated encounters."

(2) The authors use the phrase "representational geometry" several times in the paper without clearly defining what they mean by this.

We apologize for this omission. We have now added a clear and concise definition of "representational geometry" in the Introduction, citing the foundational work by Kriegeskorte et al. (2008).

Proposed change in manuscript (Introduction): We inserted the following text (lines 117-125): " By contrast, multivariate pattern analyses (MVPA), such as representational similarity analysis (RSA; Kriegeskorte et al., 2008) has emerged as a powerful tool to investigate the content and structure of these representations (e.g., Hennings et al., 2022). This approach allows us to characterize the “representational geometry” of a set of items – that is, the structure of similarities and dissimilarities between their associated neural activity patterns. This geometry reveals how the brain organizes information, for instance, by clustering items that are conceptually similar while separating those that are distinct."

(3) The abstract is quite dense and will likely be challenging to decipher for those without a specialized knowledge of both the topic (fear conditioning) and the analytical approach. For instance, the goal of the study is clearly articulated in the first few sentences, but then suddenly jumps to a sentence stating "our data show that contingency changes during reversal induce memory traces with distinct representational geometries characterized by stable activity patterns across repetitions..." this would be challenging for a reader to grok without having a clear understanding of the complex analytical approach used in the paper.

We agree with your assessment. We have rewritten it to be more accessible to a general scientific audience, by focusing on the conceptual findings rather than methodological jargon.

Proposed change in manuscript (Abstract): We revised the abstract to be clearer. It now reads: " When we learn that something is dangerous, a fear memory is formed. However, this memory is not fixed and can be updated through new experiences, such as learning that the threat is no longer present. This process of updating, known as extinction or reversal learning, is highly dependent on the context in which it occurs. How the brain represents cues, contexts, and their changing threat value remains a major question. Here, we used functional magnetic resonance imaging and a novel fear learning paradigm to track the neural representations of stimuli across fear acquisition, reversal, and test phases. We found that initial fear learning creates generalized neural representations for all threatening cues in the brain’s fear network. During reversal learning, when threat contingencies switched for some of the cues, two distinct representational strategies were observed. On the one hand, we still identified generalized patterns for currently threatening cues, whereas on the other hand, we observed highly stable representations of individual cues (i.e., item-specific) that changed their valence, particularly in the precuneus and prefrontal cortex. Furthermore, we observed that the brain represents contexts more distinctly during reversal learning. Furthermore, additional exploratory analyses showed that the degree of this context specificity in the prefrontal cortex predicted the subsequent return of fear, providing a potential neural mechanism for fear renewal. Our findings reveal that the brain uses a flexible combination of generalized and specific representations to adapt to a changing world, shedding new light on the mechanisms that support cognitive flexibility and the treatment of anxiety disorders via exposure therapy."

(4) Minor: I believe it is STM200 not the STM2000.

Thank you for pointing this out. We have corrected it in the Methods section.

Proposed change in manuscript (Methods, Page 5, Line 211): Original: STM2000 -> Corrected: STM200

(5) Line 146: "...could be particularly fruitful as a means to study the influence of fear reversal or extinction on context representations, which have never been analyzed in previous fear and extinction learning studies." I direct the authors to Hennings et al., 2020, Contextual reinstatement promotes extinction generalization in healthy adults but not PTSD, as an example of using MVPA to decipher reinstatement of the extinction context during test.

Thank for pointing us towards this relevant work. We have revised the sentence to reflect the state of the literature more accurately.

Proposed change in manuscript (Introduction, Page 3): Original text: "...which have never been analyzed in previous fear and extinction learning studies." 

Revised text (lines 154-157): "...which, despite some notable exceptions (e.g., Hennings et al., 2020), have been less systematically investigated than cue representations across different learning stages."

(6) This is a methodological/conceptual point, but it appears from Figure 1 that the shock occurs 2.5 seconds after the CS (and context) goes off the screen. This would seem to be more like a trace conditioning procedure than a standard delay fear conditioning procedure. This could be a trivial point, but there have been numerous studies over the last several decades comparing differences between these two forms of fear acquisition, both behaviorally and neurally, including differences in how trace vs delay conditioning is extinguished.

Thank you for this pertinent observation; this was also pointed out by the editor. As detailed in our response to the editor, we now explicitly acknowledge that our paradigm uses a trace conditioning design, and have added statements to this effect in the Methods and Discussion sections (lines 218-220, and 774-779).

(7) In Figure 4, it would help to see the individual data points derived from the model used to test significance between the different conditions (reinstatement between Acq, reversal, and test-new).

We agree that this would improve the transparency of our results. We have revised Figure 4 to include individual data points, which are now plotted over the bar graphs. 

Reviewer #2 (Public Review & Recommendations)

Use a more stringent method of multiple comparison correction: voxel-wise FWE instead of FDR; Holm-Bonferroni across multiple hypothesis tests. If FDR is chosen then the exploratory character of the results should be transparently reported in the abstract.

Thank you for these critical comments regarding our statistical methods. As detailed in the general response and response to the editor (Comment 3), we have thoroughly revised our approach to ensure its rigor. We now clarify that our whole-brain analyses consistently use FWER-corrected pvalues. Additionally, the significance of these FWER-corrected p-values (obtained through permutation testing), which were previously considered significant against a default threshold of 0.05, are now compared with a Bonferroni-adjusted threshold equal to the number of tested contrasts in each experimental phase. We have modified the revised manuscript accordingly, in the methods section (lines 473-484) and in the supplementary material, where we added the p-values (FWER-corrected) of each cluster, evaluated against the new Bonferroni-adjusted thresholds. It is to be of note that this had no impact on our searchlight results, given that all clusters that were previously reported as significant with the alpha threshold of 0.05 were also significant at the new, corrected thresholds.

Proposed change in manuscript (Methods): We revised the relevant paragraphs (lines 473-484): "Significance corresponding to the contrast between conditions of the maps of interest was FWER-corrected using nonparametric permutation testing at the cluster level (10,000 permutations) to estimate significant cluster size. Additionally, we adjusted the alpha threshold against which we assessed the significance of the cluster-specific FWERcorrected p-values using Bonferroni correction. In this order, we divided the default alpha corrected threshold of 0.05 by the number of statistical comparisons that were conducted in each experimental phase. For example, for fear acquisition, we compared the CS+>CS- contrast for both item stability and cue generalization, resulting in 2 comparisons and hence a corrected alpha threshold of 0.025. Only clusters that had a FWER-corrected p-value below the Bonferroni-adjusted threshold were deemed significant. All searchlight analyses were restricted within a gray matter mask.”

The authors report fMRI results from line 96 onwards; all of these refer exclusively to mass-univariate fMRI which could be mentioned more transparently... The authors contrast "activation fMRI" with "RSA" (line 112). Again, I would suggest mentioning "mass-univariate fMRI", and contrasting this with "multivariate" fMRI, of which RSA is just one flavour. For example, there is some work that is clear and replicable, demonstrating human amygdala involvement in fear conditioning using SVM-based analysis of highresolution amygdala signals (one paper is currently cited in the discussion).

Thank you for this important clarification. We have revised the manuscript to incorporate your suggestions. We now introduce our initial analyses as "mass-univariate" and contrast them with the "multivariate pattern analysis" (MVPA) approach of RSA.

Proposed change in manuscript (Introduction): We revised the relevant paragraphs (lines 113-125): " While mass-univariate functional magnetic resonance imaging (fMRI) activation studies have been instrumental in identifying the brain regions involved in fear learning and extinction, they are insensitive to the patterns of neural activity that underlie the stimulus-specific representations of threat cues and contexts. Contrastingly, multivariate pattern analyses methods, such as representational similarity analysis (RSA; Kriegeskorte et al., 2008), have emerged as a powerful tool to investigate the content and structure of these representations (e.g., Hennings et al., 2022). This approach allows us to characterize the “representational geometry” of a set of items – i.e., the structure of similarities and dissimilarities between their associated neural activity patterns. This geometry reveals how the brain organizes information, for instance, by clustering items that are conceptually similar while separating those that are distinct.”

Line 177: unclear how incomplete data was dealt with. If there are 30 subjects and 9 incomplete data sets, then how do they end up with 24 in the final sample?

We apologize for the unclear wording in our original manuscript. We have clarified the participant exclusion pipeline in the Methods section.

Proposed change in manuscript (Methods, Section "Participants"): Original text: "The number of participants with usable fMRI data for each phase was as follows: N = 30 for the first phase of day one, N = 29 for the second phase of day one, N = 27 for the first phase of day two, and N = 26 for the second phase of day two. Of the 30 participants who completed the first session, four did not return for the second day and thus had incomplete data across the four experimental phases. An additional two participants were excluded from the analysis due to excessive head movement (>2.5 mm in any direction). This resulted in a final sample of 24 participants (8 males) between 18 and 32 years of age (mean: 24.69 years, standard deviation: 3.6) with complete, low-motion fMRI data for all analyses." 

Revised text: "The number of participants with usable fMRI data for each phase was as follows: N = 30 for the first phase of day one, N = 29 for the second phase of day one, N = 27 for the first phase of day two, and N = 26 for the second phase of day two. An additional two participants were excluded from the analysis due to excessive head movement (>2.5 mm in any direction). This resulted in a final sample of 24 participants (8 males) between 18 and 32 years of age (mean: 24.69 years, standard deviation: 3.6) with complete, low-motion fMRI data for all analyses."

Typo in line 201.  

Thank you for your comment. We have re-examined line 201 (“interval (Figure 1A). A total of eight CSs were presented during each phase and”) and the surrounding text but were unable to identify a clear typographical error in the provided quote. However, in the process of revising the manuscript for clarity, we have rephrased this section.

it would be good to see all details of the US calibration procedure, and the physical details of the electric shock (e.g. duration, ...).

Thank you for your comment. We have expanded the Methods section to include these important details.

Proposed change in manuscript (Methods, Section "General procedure and stimuli"): We inserted the following text (lines 225-230): "Electrical stimulation was delivered via two Ag/AgCl electrodes attached to the distal phalanx of the index and middle fingers of the non-dominant hand. he intensity of the electrical stimulation was calibrated individually for each participant prior to the experiment. Using a stepping procedure, the voltage was gradually increased until the participant rated the sensation as 'unpleasant but not painful'.

"beta series modelling" is a jargon term used in some neuroimaging software but not others. In essence, the authors use trial-by-trial BOLD response amplitude estimates in their model. Also, I don't think this requires justification - using the raw BOLD signal would seem outdated for at least 15 years.

Thank you for this helpful suggestion. We have simplified the relevant sentences for improved clarity.

Proposed change in manuscript (Methods, Section "RSA"): Original text: "...an approach known as beta-series modeling (Rissman et al., 2004; Turner et al., 2012)." 

Revised text (lines 391-393): "...an approach that allows for the estimation of trial-by-trial BOLD response amplitudes, often referred to as beta-series modeling (Rissman et al., 2004). Specifically, we used a Least Square Separate (LSS) approach..."

I found the use of "Pavlovian trace" a bit confusing. The authors are coming from memory research where "memory trace" is often used; however, in associative learning the term "trace conditioning" means something else. Perhaps this can be explained upon first occurrence, and "memory trace" instead of "Pavlovian trace" might be more common.

We are grateful for this comment, as it highlights a critical point of potential confusion, especially given that we now acknowledge our paradigm uses a trace conditioning design. To eliminate this ambiguity, we have replaced all instances of "Pavlovian trace" with "lingering fear memory trace" throughout the manuscript (lines 542 and 599).

I would suggest removing evaluative statements from the results (repeated use of "interesting").

Thank you for this valuable suggestion. We have reviewed the Results section and removed subjective evaluative words to maintain a more objective tone. 

Line 882: one of these references refers to a multivariate BOLD analysis using SVM, not explicitly using temporal information in the signal (although they do show session-by-session information).

Thank you for this correction. We have re-examined the cited paper (Bach et al., 2011) and removed its inclusion in the text accordingly.

Author response:

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

Reviewer #1 (Public review):

Summary:

The study explores the use of Transport-based morphometry (TBM) to predict hematoma expansion and growth 24 hours post-event, leveraging Non-Contrast Computed Tomography (NCCT) scans combined with clinical and location-based information. The research holds significant clinical potential, as it could enable early intervention for patients at high risk of hematoma expansion, thereby improving outcomes. The study is well-structured, with detailed methodological descriptions and a clear presentation of results. However, the practical utility of the predictive tool requires further validation, as the current findings are based on retrospective data. Additionally, the impact of this tool on clinical decision-making and patient outcomes needs to be further investigated.

Strengths:

(1) Clinical Relevance: The study addresses a critical need in clinical practice by providing a tool that could enhance diagnostic accuracy and guide early interventions, potentially improving patient outcomes.

(2) Feature Visualization: The visualization and interpretation of features associated with hematoma expansion risk are highly valuable for clinicians, aiding in the understanding of model-derived insights and facilitating clinical application.

(3) Methodological Rigor: The study provides a thorough description of methods, results, and discussions, ensuring transparency and reproducibility.

Weaknesses:

(1) The limited sample size in this study raises concerns about potential model overfitting. While the reported AUCROC of 0.71 may be acceptable for clinical use, the robustness of the model could be further enhanced by employing techniques such as k-fold crossvalidation. This approach, which aggregates predictive results across multiple folds, mimics the consensus of diagnoses from multiple clinicians and could improve the model's reliability for clinical application. Additionally, in clinical practice, the utility of the model may depend on specific conditions, such as achieving high specificity to identify patients at risk of hematoma expansion, thereby enabling timely interventions. Consequently, while AUC is a commonly used metric, it may not fully capture the model's clinical applicability. The authors should consider discussing alternative performance metrics, such as specificity and sensitivity, which are more aligned with clinical needs. Furthermore, evaluating the model's performance in real-world clinical scenarios would provide valuable insights into its practical utility and potential impact on patient outcomes.

We thank the reviewer for these thoughtful comments. We agree that k-fold cross validation is a valid approach to reduce bias associated with overfitting and account for variability in the dataset composition. During the training and optimization process, this was employed within the VISTA dataset where data were shuffled at random and separated into independent training (60%) and internal validation (40%) datasets. This process was repeated 1000 times, to generate 1000 different training and internal validation splits. Statistical analyses and data visualization were performed independently on each of the 1000 cross-validation samples, and the mean results with corresponding 95% confidence intervals are presented. The p-values were averaged using the Fisher’s method. We have included this information in the methods section. [Page 22; Paragraph 1, Lines 8-10]. External validation was performed on the ERICH dataset and analyzed only once. We chose not to perform k-fold cross validation with the test dataset in attempt to assess the model’s generalizability to unseen data from a different patient cohort. However, we agree that taking advantage of the full 1,066 ERICH cases for model validation would improve the strength of our conclusions regarding the model’s robustness. This has been included in the discussion. [Page 15; Paragraph 1; Lines 11-14].

We agree that the AUC alone will not effectively describe the clinical applicability of the intended model. We have added the sensitivity and specificity metrics for the TBM’s performance in the external dataset to the discussion. The design of the present study was primarily a pre-clinical methodological study. However, we have suggested that future external validation studies should seek to identify ideal sensitivity and specificity thresholds when evaluating the model’s translatability to a clinical setting. [Page 11; Paragraph 2; Line 22 and Page 12; Paragraph 1; Lines 2-4]. We agree that future validation studies should also assess the model’s performance in a real-world clinical setting and have emphasized this point in the discussion. [Page 13; Paragraph 2; Lines 22-23 and Page 14; Paragraph 1; Lines 1-4].

(2) The authors compared the performance of TBM with clinical and location-based information, as well as other machine learning methods. While this comparison highlights the relative strengths of TBM, the study would benefit from providing concrete evidence on how this tool could enhance clinicians' ability to assess hematoma expansion in practice. For instance, it remains unclear whether integrating the model's output with a clinician's own assessment would lead to improved diagnostic accuracy or decisionmaking. Investigating this aspect-such as through studies evaluating the combined performance of clinician judgment and model predictions-could significantly enhance the tool's practical value.

We thank the reviewer for this suggestion. The present study intended to suggest potential advantages of the TBM method with comparison to alternate clinician-based and machine learning methods. While we agree that the TBM method warrants further evaluation in a realworld clinical setting to determine its practical utility, we propose that further optimization of TBM is first needed to improve its predictive accuracy. 

In developing TBM, our eventual goal is to produce a prediction tool, which can identify patients at risk for hematoma expansion early in the disease course, who may benefit from intervention with surgical and/or medical therapies. Current clinician-based risk stratification methods are highly variable in accuracy, inefficient, and require subjective interpretation of the NCCT scan. Our eventual goal is to aid clinical decision making with an automated, accurate and efficient model. In follow up work, we will study how to combine information derived from imaging and TBM with other assessment tools and clinical data in order to best inform clinicians. This has been incorporated into the discussion. [Page 14; Paragraph 1; Lines 1-4].

Reviewer #2 (Public review):

Summary:

The author presents a transport-based morphometry (TBM) approach for the discovery of noncontrast computed tomography (NCCT) markers of hematoma expansion risk in spontaneous intracerebral hemorrhage (ICH) patients. The findings demonstrate that TBM can quantify hematoma morphological features and outperforms existing clinical scoring systems in predicting 24-hour hematoma expansion. In addition, the inversion model can visualize features, which makes it interpretable. In conclusion, this research has clinical potential for ICH risk stratification, improving the precision of early interventions.

Strengths:

TBM quantifies hematoma morphological changes using the Wasserstein distance, which has a well-defined physical meaning. It identifies features that are difficult to detect through conventional visual inspection (such as peripheral density distribution and density heterogeneity), which provides evidence supporting the "avalanche effect" hypothesis in hematoma expansion pathophysiology.

Weaknesses:

(1) As a methodology-focused study, the description of the methods section somewhat lacks depth and focus, which may make it challenging for readers to fully grasp the overall structure and workflow of the approach. For instance, the manuscript lacks a systematic overview of the entire process, from NCCT image input to the final prediction output. A potential improvement would be to include a workflow figure at the beginning of the manuscript, summarizing the proposed method and subsequent analytical procedures. This would help readers better understand the mechanism of the model.

We thank the reviewer for this suggestion. We have included a figure detailing the TBM workflow to improve reader understanding. [Figure 1, Page 5; Paragraph 2; Lines 19-20 and Page 30; Paragraph 1].

(2) The description of the comparison algorithms could be more detailed. Since TBM directly utilizes NCCT images as input for prediction, while SVM and K-means are not inherently designed to process raw imaging data, it would be beneficial to clarify which specific features or input data were used for these comparison models. This would better highlight the effectiveness and advantages of the TBM method.

We thank the reviewer for this suggestion. We have included additional details of the comparison with machine learning models in the methods section. While we used PCA on the extracted transport maps and raw image data for dimensionality reduction prior to classification, we agree that the machine learning methods described may not have been optimally tuned to examine the data in the format in which it was presented. Future studies should aim to compare TBM with optimized machine and deep learning methods to determine TBM’s potential as an automated clinical risk stratification tool. We have added this to the limitations section of the discussion. [Page 14; Paragraph 2; Lines 22-23 and Page 15; Paragraph 1; Lines 1-2].

(3) The relatively small training and testing dataset may limit the model's performance and generalizability. Notably, while the study mentions that 1,066 patients from the ERICH dataset met the inclusion criteria, only 170 were randomly selected for the test set. Leveraging the full 1,066 ERICH cases for model training and internal validation might potentially enhance the model's robustness and performance.

We thank the reviewer for this suggestion. As the reviewer highlights, the intention of the manuscript was to present a methodologically focused study which led to our small validation cohort of 170 patients from the ERICH dataset. It is our intention to further optimize and validate the TBM method in a future larger study which is underway, taking full advantage of the ERICH dataset. This has been incorporated into the discussion section. [Page 15; Paragraph 1; Lines 1114].

(4) Some minor textual issues need to be checked and corrected, such as line 16 in the abstract "Incorporating these traits into a v achieved an AUROC of 0.71 ...".

We thank the reviewer for this comment. The typographical error has been corrected. 

(5) Some figures need to be reformatted (e.g., the x-axis in Figure 2 a is blocked).

We thank the reviewer for this comment. This was intentional to demonstrate that the X-axis in Figure 2a and 2b are identical and thereby highlight image features corresponding to the regression line on the graph.

Author response:

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

Reviewer #1 (Public review):

While the authors have largely ruled out zebrin II as the key protein underlying PC vulnerability or resistance to age-related loss, the molecular basis of this phenomenon remains unidentified. This reviewer acknowledges the complexity of this investigation and considers it a minor issue, as the manuscript thoughtfully discusses the gap and highlights it as a future direction.

We appreciate the reviewer’s acknowledgement of the complexity of determining the molecular basis of differential Purkinje cell vulnerability. Moreover, we acknowledge that zebrin II expression/identity is not the only factor in determining vulnerability; rather, the compartmentalized map as a whole may dictate these differences. We are eager to shed light on this issue through future study.

In cases where no PC loss is observed in aged mice (Figure 1F), it is unclear whether these PCs undergo morphological degeneration, such as thickened axons and shrunken dendrites. Further characterization of these resilient PCs would help understand why the aged mice without PC loss still exhibit motor deficits (Figure 7).

Thank you for the excellent idea of examining Purkinje cell morphology in aged mice without Purkinje cell loss. Upon looking for hallmarks of neurodegeneration, such as shrunken dendrites and axonal swellings, in aged mice without Purkinje cell loss, we observed minimal axonal pathology and no shrinkage of the molecular layer.  However, we note that while the features we examined are wellstudied hallmarks of degeneration, they are specific rather than exhaustive, and subtle morphological characteristics that are beyond our methods’ detection may change. We have added these new results to Figure 2C and added these notes to the manuscript.

The histologic analysis is based on mice with different genetic backgrounds. For example, the PC-specific reporter mice include two strains: Pcp2-Cre; Ai32 and Pcp2-Cre; Ai40D. These genetic variations may contribute to the heterogeneity of PC loss (Figure 1). To improve clarity, please add the genetic background details to Table 1.

We have added the genetic backgrounds of all mice used in the study to Table 1.

Please indicate from which lobule in the anterior or posterior human cerebellum the images in Figure 8 were taken.

Unfortunately, because of the limitations of human postmortem tissue collection (in some cases, we are provided with a very small block that was collected after the pathologist completed their primary duty for that individual), we cannot with full certainty distinguish the lobules from which the images were taken. However, we are grateful that, upon our request, the pathologists were able to collect tissue mainly from the vermis, which is where we wished to begin, knowing that the vermis in rodents and non-human primates typically has the clearest and most well-studied pattern. That said, this is an important issue that we are addressing for future studies.

Reviewer #2 (Public review):

(1) Limited strain diversity: The study exclusively uses C57BL/6J mice despite known genetic and motor differences even the closely related strains like C57BL/6N.

Thank you for pointing out this limitation of our study. We chose to limit this initial study to C57BL/6J mice based on their widespread use as a background strain on many currently maintained lines. That said, our study intentionally included several different crosses to provide genetic variability, even though C57BL/6J is still the predominant genetic background. In addition to the motor differences in genetic strains, we are also particularly interested in the differences in cerebellar morphology across strains (Inouye and Oda, 1980; Sillitoe and Joyner, 2007). Our use of mice maintained on the C57BL/6J background leaves open an exciting future direction: investigating age-related Purkinje cell loss in mice of different inbred and outbred strains. Given the importance of the topic, we have included new text in the discussion to alert the reader to this limitation of our study and to highlight interesting differences across strains that will be important to disentangle in our future work.

(2) No correlation quantified between the degree of PC loss, aging, and motor performance.

We sought to conduct a broad overview of motor problems that might be caused by age-related Purkinje cell loss, rather than a comprehensive investigation of how motor behavior changes with advancing Purkinje cell loss. Therefore, we agree with the reviewer’s comment, and we have added text to indicate that stronger correlations between these domains would be best tackled with deeper behavioral phenotyping conducted over time to match the potentially cooccurring progressive changes in cerebellar morphology, with a focus on Purkinje cell degeneration and eventual loss.

(3) It has not been demonstrated whether the neurodegenerative changes are indeed observed in zebrin-negative PCs.

We have added Supplementary Figure 4, which includes an example of reduced dendritic density and loss of Purkinje cell somata in zebrin II-negative stripes in lobules II and III. Please also see Figure 4B for an example of reduced dendritic density in zebrin II-negative Purkinje cells in lobules III and IV.

(4) The mechanisms of why only a subset of mice show PC loss remain unexplored and not discussed.

We agree that our manuscript would benefit from discussion of why some aged mice are resistant to age-related Purkinje cell loss. We have elaborated upon possible reasons for this differential vulnerability in the discussion.

(5) Linkages with normal human aging and cerebellar function are not well supported. While motor behavioral assays captured phenotypes that mimic aged people, correlation with PC loss is demonstrated to be absent in mice. It remains unclear whether this PC loss phenomenon is universal or specific to a particular individual; and whether specific to a human PC subtype.

In our study, we sought to show that patterned age-related Purkinje cell loss presents a promising area for future research in humans. We agree that further study is needed to solidify a link between age-related Purkinje cell loss in mice and humans and the implications for motor function. The reviewer raises a fair criticism that reflects the current state of knowledge: studies that link cerebellar aging to  motor function and cognitive decline in humans are few, as are studies of the cellular-level morphological changes of cerebellar aging –there is a pressing need for deeper study of human tissue. To address the issue raised by the reviewer, we have included new text to the discussion of our manuscript indicating these gaps in knowledge. 

(6) Analyses in the paraflocculus are currently not easy to understand. This lobule has heterogeneous PC subtypes, developmentally or molecularly. Zebrin-weak and Zebrinintense PCs are known to be arranged in stripes, which resembles the pattern of developmentally defined PC subsets (Fujita et al., 2014, Plos one; Fujita et al., 2012, J Neurosci). In the data presented, it is hard to appreciate whether the viewing angle is consistent relative to the angle of the paraflocculus. This may be a limitation of the analysis of the paraflocculus in general, that the orientation of this lobule is so susceptible to fixation and dissection. Discrepancy between PC loss stripe and zebrin pattern may be an overstatement, because appropriate analyses on the paraflocculus would require a rigorously standardized analytic method.

Thank you for your valuable insights on the complexity of analyzing the paraflocculus. We have altered our language to more accurately reflect the nuanced zebrin II expression pattern of this region. We also agree with and very much appreciate your advice that “analyses on the paraflocculus would require a rigorously standardized analytic method.” We have added these arguments to the revised manuscript text.

Reviewer #3 (Public review):

(1) In Figure 3, the authors use Pcp2-CRE mice to drive GFP expression in Purkinje cells in order to avoid the confounding variable of loss of calbindin expression in aging Purkinje cells. The authors go on to say, "we argue that calbindin expression alone is not a reliable, sufficient indicator of Purkinje cell loss". However, in Figure 4, the authors return to calbindin staining alone to assess the correlation of Purkinje cell loss with zebrin-II expression. Could the authors comment on why zebrin-II co-staining experiments were not performed in GFP reporter mice to avoid potential confounds of calbindin expression? Without this experiment, should readers accept the data presented in Figure 4 as a "reliable, sufficient indicator of Purkinje cell loss", given the author's prior claim?

This is a very good point, thank you. We agree that the data presented in Figure 4 alone would not be a sufficient indicator of Purkinje cell loss. However, we prefaced our calbindin and zebrin II co-staining with calbindin and GFP costaining (Figure 3), which showed that Purkinje cell-specific reporter expression revealed the same pattern of Purkinje cell loss as calbindin expression, and Neutral Red staining (Figure 2 and Supplementary Figure 3B), which confirmed the loss of Purkinje cells independent of immunofluorescence. For this reason, we feel confident that the data in Figure 4 is representative of the striped pattern of age-related Purkinje cell loss. Still, we see and agree with the reviewer’s comment, and therefore, to further show the correlation of Purkinje cell loss with zebrin II expression, we have added a new Supplementary Fig. 4, which shows co-staining of calbindin, GFP, and zebrin II.

(2) Throughout the manuscript, there is a considerable reliance on the authors' interpretation of imaging data with no accompanying quantification (categorization of "striped" or "non-striped" PC loss, correlation of GFP/calbindin/zebrin-II staining, etc.). While this may be difficult to obtain, the results would be much stronger with a quantitative approach to support the stated categorizations/observations.

Thank you for your suggestion. Quantifying stripe properties has been a challenging task for the field, given the regionalized features of stripe compartmentalization that make its complex architecture tricky to measure in its typical organization within the 3D anatomy of lobules and fissures and even harder to interpret when there are abnormalities. However, to quantitatively support our categorization of “striped” and “non-striped” Purkinje loss and the observed correlation between calbindin and GFP expression in aged mice, we have quantified the mediolateral pixel intensity across lobules II-IV, in which Purkinje cell loss reliably occurs in zebrin II-negative stripes. The results can be found in Supplementary Figure 1B and Supplementary Figure 3.

Reviewer #1 (Recommendations for the authors):

(1) In Figure 1, both staining artifacts and PC degeneration appear in light color. Please clarify how these two were differentiated.

Thank you for your comment, which raises an important point about distinguishing staining artifacts from Purkinje cell degeneration. Cerebellar patterning is symmetrical across the midline, so asymmetrical abnormalities are one clue that differentiates staining artifacts from the degenerative pattern. Another indicator of a staining artifact seen in wholemount preparations is the gradual fading of the stain (seen in some hemispheres in Figure 1), which is caused by continuous rubbing of the cerebellum against the tube during the staining process. In some cases, such as in Figure 1F, the cerebellum was damaged during the dissection of the meninges after staining, and in such cases the accidental removal of cerebellar tissue (molecular layer) reveals unstained tissue beneath the surface of the cerebellum. This type of staining artifact can be identified by a missing chunk of tissue surrounded by stained Purkinje cells, compared to the smooth, unmarred tissue where PCs have degenerated. We have added new text to the results (the legends) to clarify these critical points for the reader.

(2) In Figure 7C, please consider changing "Aged without stripes" to "Aged without PC loss" to be consistent with the labeling used in other panels.

Thank you for pointing out this discrepancy. We have made the suggested changes.

Reviewer #3 (Recommendations for the authors):

Could the authors comment on why zebrin-II co-staining experiments were not performed in GFP reporter mice to avoid potential confounds of calbindin expression? Without this experiment, should readers accept the data presented in Figure 4 as a "reliable, sufficient indicator of Purkinje cell loss", given the author's prior claim?

Thank you for this recommendation; we appreciate this advice. As we described above, our response to this suggestion reads:

This is a very good point, thank you. We agree that the data presented in Figure 4 alone would not be a sufficient indicator of Purkinje cell loss. However, we prefaced our calbindin and zebrin II co-staining with calbindin and GFP costaining (Figure 3), which showed that Purkinje cell-specific reporter expression revealed the same pattern of Purkinje cell loss as calbindin expression, and Neutral Red staining (Figure 2 and Supplementary Figure 3B), which confirmed the loss of Purkinje cells independent of immunofluorescence. For this reason, we feel confident that the data in Figure 4 is representative of the striped pattern of age-related Purkinje cell loss. Still, we see and agree with the reviewer’s comment, and therefore to further show the correlation of Purkinje cell loss with zebrin II expression, we have added a new Supplementary Fig. 4, which shows co-staining of calbindin, GFP, and zebrin II.

Author response:

The following is the authors’ response to the original reviews

Reviewing Editor Comments:

Recommendations for improvement:

(1) Address data presentation, editing, and other issues of lack of clarity as pointed out by the reviewers.

We have now addressed all comments from reviewers that identify editing errors and lack of clarity issues. Regarding data presentation we have made some changes, for example including a combined heatmap to show consistency between row names (Figure 2 - figure supplement 2), but also kept some stylistic features such as the balance between main and supplemental figures that we think fits more naturally with the story of the paper.

(2) Inclusion of requested and critical details in the methodology section, an important component for broad applicability of a new methodology by other investigators.

We have added the requested details to the methods section, specifically the RCA protocol.

(3) More in-depth discussion of the limitations of the methodology and approach to capture important but more complex components of tissues of interest, for example, sexual dimorphism.

We have now edited the ‘pitfalls of study’ section in the discussion to include further detail of the limitations of the number of genes that can be used to deeply profile transcriptomic types, including sexual dimorphism. Regarding its use in other tissues of interest, we have now included a reference in the discussion (Bintu et al., 2025) where a similar strategy has been used to profile cells in the olfactory epithelium and olfactory bulb. We have also used hamFISH in other brain areas (as commented in our public reviews responses) but as this is unpublished work we will refrain from mentioning it in the main text.

Reviewer #1 (Recommendations for the authors):

The manuscript by Edwards et al. would benefit from minor revisions. Here, we outline several points that could / should be addressed:

(1) General balance of data presentation between main and supplementary figures

(a) quantifications were often missing from main figures and only presented in the supplements

Thank you for raising this point. We believe that the balance of panels between the main and supplemental figures matches our story and results section well with quantifications included in the main figures where appropriate.

(b) more informative figure legends in supplements (e.g.: Supplementary Figure I - Figure 3)

We have now revised the figure legends and added more description where appropriate.

(c) missing subpanel in Figure 3; figure legend describes 3H, which is missing in the figure

We thank the reviewer for pointing this out and have now amended the subpanel.

stand-alone figure on inhibitory neuron cluster i3 cells

We agree that this is an important characterisation of i3 cells but decided to place this figure in the supplement as it does not fall within the main storyline (defining transcriptomic characterisation of cell types in a multimodal fashion), but rather acts as accessory information for those specifically interested in these inhibitory cell types.

statistical tests used (e.g.: Figure 1 C -, Supplementary Figure 3 - Figure 2)/ graphs shown (Supplementary Figure 1 - 1 D)

The statistical tests used are described in the figure legends.

t-SNE dimensionality reduction of positional parameters

Explanations of the t-SNE dimensionality reduction of positional parameters can be found in the materials and methods.

(d) heatmaps similarly informative and more convincing

We have included an extra heatmap (Figure 2 - figure supplement 2) in response to Reviewer 3’s comment (see below) in order to more easily follow genes across all the different clusters. We hope this helps to make the heatmaps more convincing and informative.

code availability

Code availability is described in the methods section of the manuscript.

page 6, 3rd paragraph wrong description of PMCo abbreviation

We thank the reviewer for identifying the mistake and we have now amended it.

Reviewer #2 (Recommendations for the authors):

The pre-existing scRNA-seq dataset on which the manuscript is based is an older Drop-seq dataset for which minimal QC information is provided. The authors should include QC information (genes/cells and UMIs/cells) in the Methods. Moreover, the Seurat clustering of these cells and depiction of marker genes in feature plots are not shown.

It is therefore difficult to determine how the authors selected their 31 genes for their hamFISH panel, or how selective they are to the original Drop-seq clusters.

The QC information of this dataset can be found in the original publication (Chen et al., 2019) with our clustering methods described in the materials and methods section. We have not included individual gene names in our heatmap plots for presentation purposes (there are over 200 rows), but the data and cluster descriptions can be found in supplemental tables.

Reviewer #3 (Recommendations for the authors):

(1) The imaging modality is not entirely clear in the methods. The microscopy technique is referenced to prior work and involves taking z-stacks, but analysis appears to be done on maximum z-projections, which seems like it would introduce the risk of false attribution of gene expression to cells that are overlapping in "z".

Thank you for pointing out the technical limitation of the microscopy. For imaging we used epifluorescence microscopy with 14x 500 nm z-steps to collect our raw data and generate a maximum intensity projection for further analysis. Because of the thin sections (10 um) used for the imaging, the overlap between cells in z is expected to be minimal. However, we cannot completely rule out misattribution raised in the comment. The method section contains this information.

(2) Supplemental Figure 1 - Figure Supplement 2B: RCA looks significantly different when compared to v2 smFISH from the representative image, although it is written as comparable. Additionally, there is no information about RCA mentioned in the Materials and Methods section. Supplemental Figure 1 - Figure Supplement 2B: The figure label for RCA is missing.

By comparable we are referring to the intensity rather than pattern as mentioned in the results section. We did not analyze the number of spots. It is true that the pattern of RCA signal is much sparser due to its inherent insensitivity compared with hamFISH. We thank the reviewer for identifying the lack of a methodological RCA description and have amended the manuscript to include this. We have also now amended the missing RCA label in the figure.

(3) Figure 2C and associated supplement: The rows (each gene) are not consistent across the subpanels (i.e. they do not line up left-to-right), this makes it difficult for the reader to follow the patterns that distinguish the cell types in each subset.

We have done this as we believe it makes for an easier interpretation of inhibitory vs excitatory clusters for the reader. However, we agree with the reviewer that one may wish to look at the dataset as a whole with a consistent gene order, and we have now provided this in the corresponding supplemental figure.  

(4) "Consistent with previous work, most inhibitory classes are localized in the dorsal and ventral subdivisions of the MeA, whereas excitatory neurons occupy primarily the ventral MeA (Figure 2D, Figure 2 - Figure Supplement 2C, Figure 1D)". - The reference to Figure 1D seems to be an error.

We thank the reviewer for identifying the mistake, and we have now amended it.

(5) Supplemental Figure 2 - Figure Supplement 1, "published by Chen et al." - should have a proper reference number to be compatible with the rest of the manuscript. Also, the lack of gene info makes it difficult to understand Panel A. Finally, the text on Panel B refers to "hamMERFISH" which seems an error.

We thank the reviewer for identifying the mistake on Panel B, it has now been amended. We have also changed the reference format. Regarding the lack of gene information in panel A, it is difficult to present all row names due to the large number of rows (>200), but this information can be found in supplemental table 2.

(6) Supplemental Figure 2 - Figure Supplement 1: there are thin dividing lines drawn on each section, but these are not described or defined, making it difficult to understand what is being delineated.

We thank the reviewer for identifying this omission and have now edited to figure legend to contain a description.

(7) Page 4, "...we found 26 clusters in cells that are positive for Slc32a1 (inhibitory) or Slc17a6 (encoding Vglut2 and therefore excitatory) positive (Figure 2 - figure supplement 1A, Table S2)."

This seems to be an error as Figure 2 - figure supplement 1A does not show this.

We double-checked that this description describes the panel accurately.

(8) "The clustering revealed that inhibitory and excitatory classes generally have different spatial properties (Figure 1E, left), although the salt-and-pepper, sparse nature of e10 (Nts+) cells is more similar to inhibitory cells than other excitatory classes".

The references to Figure 1E's should be to Figure 2E.

We thank the reviewer for identifying the mistake, and we have now amended it.

(9) "Comparison of the proportion of all cells that are cluster X vs projection neurons labelled by CTB that are cluster X". Please explain cluster X in this context.

We have now rephrased this sentence in the figure legend for clarity.

(10) Figure 3 - figure supplement 3: There appears to be quite a bit of heterogeneity in the patterns of activity across clusters even within behavioral contexts (e.g. the bottom 2 animals paired with females). It might be worth commenting on (or quantifying) whether there were any evident differences in the social behaviors observed (e.g. mating or not?) in individuals demonstrating these patterns.

We thank the reviewer for this observation. We unfortunately did not quantify the behaviors, but we agree that more work is needed to link the pattern of c-fos activity with incrementally measured behavioral variables. At least, we did not include animals that did not display the anticipated social behaviours (as described in the materials and methods) in the in situ transcriptomic profiling work.

Author response:

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

Reviewer #1 (Public Review):

In the current article, Octavia Soegyono and colleagues study "The influence of nucleus accumbens shell D1 and D2 neurons on outcome-specific Pavlovian instrumental transfer", building on extensive findings from the same lab. While there is a consensus about the specific involvement of the Shell part of the Nucleus Accumbens (NAc) in specific stimulus-based actions in choice settings (and not in General Pavlovian instrumental transfer - gPIT, as opposed to the Core part of the NAc), mechanisms at the cellular and circuitry levels remain to be explored. In the present work, using sophisticated methods (rat Cre-transgenic lines from both sexes, optogenetics, and the well-established behavioral paradigm outcome-specific PIT-sPIT), Octavia Soegyono and colleagues decipher the diNerential contribution of dopamine receptors D1 and D2 expressing spiny projection neurons (SPNs). 

After validating the viral strategy and the specificity of the targeting (immunochemistry and electrophysiology), the authors demonstrate that while both NAc Shell D1- and D2SPNs participate in mediating sPIT, NAc Shell D1-SPNs projections to the Ventral Pallidum (VP, previously demonstrated as crucial for sPIT), but not D2-SPNs, mediates sPIT. They also show that these eNects were specific to stimulus-based actions, as valuebased choices were left intact in all manipulations. 

This is a well-designed study, and the results are well supported by the experimental evidence. The paper is extremely pleasant to read and adds to the current literature.

We thank the Reviewer for their positive assessment. 

Reviewer 2 (Public Review):

Summary: 

This manuscript by Soegyono et al. describes a series of experiments designed to probe the involvement of dopamine D1 and D2 neurons within the nucleus accumbens shell in outcome-specific Pavlovian-instrumental transfer (osPIT), a well-controlled assay of cueguided action selection based on congruent outcome associations. They used an optogenetic approach to phasically silence NAc shell D1 (D1-Cre mice) or D2 (A2a-Cre mice) neurons during a subset of osPIT trials. Both manipulations disrupted cue-guided action selection but had no eNects on negative control measures/tasks (concomitant approach behavior, separate valued guided choice task), nor were any osPIT impairments found in reporter-only control groups. Separate experiments revealed that selective inhibition of NAc shell D1 but not D2 inputs to ventral pallidum was required for osPIT expression, thereby advancing understanding of the basal ganglia circuitry underpinning this important aspect of decision making.

Strengths: 

The combinatorial viral and optogenetic approaches used here were convincingly validated through anatomical tract-tracing and ex vivo electrophysiology. The behavioral assays are sophisticated and well-controlled to parse cue and value-guided action selection. The inclusion of reporter-only control groups is rigorous and rules out nonspecific eNects of the light manipulation. The findings are novel and address a critical question in the literature. Prior work using less decisive methods had implicated NAc shell D1 neurons in osPIT but suggested that D2 neurons may not be involved. The optogenetic manipulations used in the current study provide a more direct test of their involvement and convincingly demonstrate that both populations play an important role. Prior work had also implicated NAc shell connections to ventral pallidum in osPIT, but the current study reveals the selective involvement of D1 but not D2 neurons in this circuit. The authors do a good job of discussing their findings, including their nuanced interpretation that NAc shell D2 neurons may contribute to osPIT through their local regulation of NAc shell microcircuitry. 

We thank the Reviewer for their positive assessment. 

Weaknesses: 

The current study exclusively used an optogenetic approach to probe the function of D1 and D2 NAc shell neurons. Providing a complementary assessment with chemogenetics or other appropriate methods would strengthen conclusions, particularly the novel demonstration of D2 NAc shell involvement. Likewise, the null result of optically inhibiting D2 inputs to the ventral pallidum leaves open the possibility that a more complete or sustained disruption of this pathway may have impaired osPIT.

We acknowledge the reviewer's valuable suggestion that demonstrating NAc-S D1- and D2-SPNs engagement in outcome-specific PIT through another technique would strengthen our optogenetic findings. Several approaches could provide this validation. Chemogenetic manipulation, as the reviewer suggested, represents one compelling option. Alternatively, immunohistochemical assessment of phosphorylated histone H3 at serine 10 (P-H3) oMers another promising avenue, given its established utility in reporting striatal SPNs plasticity in the dorsal striatum (Matamales et al., 2020). We hope to complete such an assessment in future work since it would address the limitations of previous work that relied solely on ERK1/2 phosphorylation measures in NAc-S SPNs (Laurent et al., 2014). The manuscript was modified to report these future avenues of research (page 12). 

Regarding the null result from optical silencing of D2 terminals in the ventral pallidum, we agree with the reviewer's assessment. While we acknowledge this limitation in the current manuscript (page 13), we aim to address this gap in future studies to provide a more complete mechanistic understanding of the circuit.

Reviewer 3 (Public Review):

Summary:

The authors present data demonstrating that optogenetic inhibition of either D1- or D2MSNs in the NAc Shell attenuates expression of sensory-specific PIT while largely sparing value-based decision on an instrumental task. They also provide evidence that SS-PIT depends on D1-MSN projections from the NAc-Shell to the VP, whereas projections from D2-MSNs to the VP do not contribute to SS-PIT.

Strengths:

This is clearly written. The evidence largely supports the authors' interpretations, and these eNects are somewhat novel, so they help advance our understanding of PIT and NAc-Shell function.

We thank the Reviewer for their positive assessment. 

Weaknesses:

I think the interpretation of some of the eNects (specifically the claim that D1-MSNs do not contribute to value-based decision making) is not fully supported by the data presented.

We appreciate the reviewer's comment regarding the marginal attenuation of valuebased choice observed following NAc-S D1-SPN silencing. While this manipulation did produce a slight reduction in choice performance, the behavior remained largely intact. We are hesitant to interpret this marginal eMect as evidence for a direct role of NAc-S D1SPNs in value-based decision-making, particularly given the substantial literature demonstrating that NAc-S manipulations typically preserve such choice behavior (Corbit et al., 2001; Corbit & Balleine, 2011; Laurent et al., 2012). Furthermore, previous work has shown that NAc-S D1 receptor blockade impairs outcome-specific PIT while leaving value-based choice unaMected (Laurent et al., 2014). We favor an alternative explanation for our observed marginal reduction. As documented in Supplemental Figure 1, viral transduction extended slightly into the nucleus accumbens core (NAc-C), a region established as critical for value-based decision-making (Corbit et al., 2001; Corbit & Balleine, 2011; Laurent et al., 2012; Parkes et al., 2015). The marginal impairment may therefore reflect inadvertent silencing of a small number of  NAc-C D1-SPNs rather than a functional contribution from NAc-S D1-SPNs. Future studies specifically targeting larger NAc-C D1-SPN populations would help clarify this possibility and provide definitive resolution of this question.

Reviewer 1 (Recommendations for the Author):

My main concerns and comments are listed below.

(1) Could the authors provide the "raw" data of the PIT tests, such as PreSame vs Same vs PreDiNerent vs DiNerent? Could the authors clarify how the Net responding was calculated? Was it Same minus PreSame & DiNerent minus PreDiNerent, or was the average of PreSame and PreDiNerent used in this calculation?

The raw data for PIT testing across all experiments are now included in the Supplemental Figures (Supplemental Figures S1E, S2E, S3E, and S4E). Baseline responding was quantified as the average number of lever presses per minute for both actions during the two-minute period (i.e., average of PreSame and PreDiMerent) preceding each stimulus presentation. This methodology has been clarified in the revised manuscript (page 7).

(2) While both sexes are utilized in the current study, no statistical analysis is provided. Can the authors please comment on this point and provide these analyses (for both training and tests)?

As noted in the original manuscript, the final sample sizes for female and male rats were insuMicient to provide adequate statistical power for sex-based analyses (page 15). To address this limitation, we have now cited a previous study from our laboratory (Burton et al., 2014) that conducted such analyses with suMicient power in identical behavioural tasks. That study identified only marginal sex diMerences in performance, with female rats exhibiting slightly higher magazine entry rates during Pavlovian conditioning. Importantly, no diMerences were observed in outcome-specific PIT or value-based choice performance between sexes.

(3) Regarding Figure 1 - Anterograde tracing in D1-Cre and A2a-Cre rats (from line 976), I have one major and one minor question:

(3.1) I do not understand the rationale of showing anterograde tracing from the Dorsal Striatum (DS) as this region is not studied in the current work. Moreover, sagittal micrographs of D1-Cre and A2a-Cre would be relevant here. Could the authors please provide these micrographs and explain the rationale for doing tracing in DS?

We included dorsal striatum (DS) tracing data as a reference because the projection patterns of D1 and D2 SPNs in this region are well-established and extensively characterized, in contrast to the more limited literature on these cell types in the NAc-S. Regarding the comment about sagittal micrographs, we are uncertain of the specific concern as these images are presented in Figure 1B.

If the reviewer is requesting sagittal micrographs for NAc-S anterograde tracing, we did not employ this approach because: (1) the NAc-S and ventral pallidum are anatomically adjacent regions and (2) the medial-lateral coordinates of the ventral pallidum and lateral hypothalamus do not align optimally with those of the NAc-S, limiting the utility of sagittal analysis for these projections.

(3.2) There is no description about how the quantifications were done: manually? Automatically? What script or plugin was used? If automated, what were the thresholding conditions? How many brain sections along the anteroposterior axis? What was the density of these subpopulations? Can the authors include a methodological section to address this point?

We apologize for the omission of quantification methods used to assess viral transduction specificity. This methodological description has now been added to the revised manuscript (page 22). Briefly, we employed a manual procedure in two sections per rat, and cell counts were completed in a defined region of interest located around the viral infusion site.

(4) Lex A & Hauber (2008) Dopamine D1 and D2 receptors in the nucleus accumbens core and shell mediate Pavlovian-instrumental transfer. Learning & memory 15:483- 491, should be cited and discussed. It also seems that the contribution of the main dopaminergic source of the brain, the ventral tegmental area, is not cited, while it has been investigated in PIT in at least 3 studies regarding sPIT only, notably the VP-VTA pathway (Leung & Balleine 2015, accurately cited already).

We did not include the Lex & Hauber (2008) study because its experimental design (single lever and single outcome) prevents diMerentiation between the eMects of Pavlovian stimuli on action performance (general PIT) versus action selection (outcome-specific PIT, as examined in the present study). Drawing connections between their findings and our results would require speculative interpretations regarding whether their observed eMects reflect general or outcome-specific PIT mechanisms, which could distract from the core findings reported in the article.

Several studies examining the role of the VTA in outcome-specific PIT were referenced in the manuscript's introduction. Following the reviewer's recommendation, these references have also been incorporated into the discussion section (page 13). 

(5) While not directly the focus of this study, it would be interesting to highlight the accumbens dissociation between General vs Specific PIT, and how the dopaminergic system (diNerentially?) influences both forms of PIT.

We agree with the reviewer that the double dissociation between nucleus accumbens core/shell function and general/specific PIT is an interesting topic. However, the present manuscript does not examine this dissociation, the nucleus accumbens core, or general PIT. Similarly, our study does not directly investigate the dopaminergic system per se. We believe that discussing these topics would distract from our core findings and substantially increase manuscript length without contributing novel data directly relevant to these areas. 

(6) While authors indicate that conditioned response to auditory stimuli (magazine visits) are persevered in all groups, suggesting intact sensitivity to the general motivational properties of reward-predictive stimuli (lines 344, 360), authors can't conclude about the specificity of this behavior i.e. does the subject use a mental representation of O1 when experiencing S1, leading to a magazine visits to retrieve O1 (and same for S2-O2), or not? Two food ports would be needed to address this question; also, authors should comment on the fact that competition between instrumental & pavlovian responses does not explain the deficits observed.

We agree with the Reviewer that magazine entry data cannot be used to draw conclusions about specificity, and we do not make such claims in our manuscript. We are therefore unclear about the specific concern being raised. Following the Reviewer’s recommendation, we have commented on the fact that response competition could not explain the results obtained (page 11, see also supplemental discussion). 

The minor comments are listed below.

(7) A high number of rats were excluded (> 32 total), and the number of rats excluded for NAc-S D1-SPNs-VP is not indicated.

We apologize for omitting the number of rats excluded from the experiment examining NAc-S D1-SPN projections to the ventral pallidum. This information has been added to the revised manuscript (page 22).

(7.1) Can authors please comment on the elevated number of exclusions?

A total of 133 rats were used across the reported experiments, with 40 rats excluded based on post-mortem analyses. This represents an attrition rate of approximately 30%, which we consider reasonable given that most animals received two separate viral infusions and two separate fiber-optic cannula implantations, and that the inclusion of both female and male rats contributed to some variability in coordinates and so targeting. 

(7.2) Can authors please present the performance of these animals during the tasks (OFF conditions, and for control ones, both ON & OFF conditions)?

Rats were excluded after assessing the spread of viral infusions, placement of fibre-optic cannulas and potential damage due to the surgical procedures (page 21). The requested data are presented below and plotted in the same manner as in Figures 3-6. The pattern of performance in excluded animals was highly variable. 

Author response image 1.

(8) For tracing, only males were used, and for electrophysiology, only females were used.

(8.1) Can authors please comment on not using both sexes in these experiments? 

We agree that equal allocation of female and male rats in the experiments presented in Figures 1-2 would have been preferable. Animal availability was the sole factor determining these allocations. Importantly, both female and male D1-Cre and A2A-Cre rats were used for the NAc-S tracing studies, and no sex diMerences were observed in the projection patterns. The article describing the two transgenic lines of rats did not report any sex diMerence (Pettibone et al., 2019). 

(8.2) Is there evidence in the literature that the electrophysiological properties of female versus male SPNs could diNer?

The literature indicates that there is no sex diMerence in the electrophysiological properties of NAc-S SPNs (Cao et al., 2018; Willett et al., 2016).  

(8.3) It seems like there is a discrepancy between the number of animals used as presented in the Figure 2 legend versus what is described in the main text. In the Figure legend, I understand that 5 animals were used for D1-Cre/DIO-eNpHR3.0 validation, and 7 animals for A2a-Cre/DIO-eNpHR3.0; however, the main text indicates the use of a total of 8 animals instead of the 12 presented in the Figure legend. Can authors please address this mismatch or clarify?

The number of rats reported in the main text and Figure 2 legend was correct. However, recordings sometimes involved multiple cells from the same animal, and this aspect of the data was incorrectly reported and generated confusion. We have clarified the numbers in both the main text and Figure 2 legend to distinguish between animal counts and cell counts. 

(9) Overall, in the study, have the authors checked for outliers?

Performance across all training and testing stages was inspected to identify potential behavioral outliers in each experiment. Abnormal performance during a single session within a multi-session stage was not considered suMicient grounds for outlier designation. Based on these criteria, no subjects remaining after post-mortem analyses exhibited performance patterns warranting exclusion through statistical outlier analysis. However, we have conducted the specific analyses requested by the Reviewer, as described below. 

(9.1) In Figure 3, it seems that one female in the eYFP group, in the OFF situation, for the diNerent condition, has a higher level of responding than the others. Can authors please confirm or refute this visual observation with the appropriate statistical analysis?

Statistical analysis (z-score) confirmed the reviewer's observation regarding responding of the diMerent action in the OFF condition for this subject (|z| = 2.58). Similar extreme responding was observed in the ON condition (|z| = 2.03). Analyzing responding on the diMerent action in isolation is not informative in the context of outcome-specific PIT. Additional analyses revealed |z| < 2 when examining the magnitude of choice discrimination in outcome-specific PIT (i.e., net same versus net diMerent responding) in both ON and OFF conditions. Furthermore, this subject showed |z| < 2 across all other experimental stages. Based on these analyses, we conclude that the subject should be kept in all analyses. 

(9.2) In Figure 5, it seems that one male, in the ON situation, in the diNerent condition, has a quite higher level of responding - is this subject an outlier? If so, how does it aNect the statistical analysis after being removed? And who is this subject in the OFF condition?

The reviewer has identified two diMerent male rats infused with the eNpHR3.0 virus and has asked closer examination of their performance.

The first rat showed outlier-level responding on the diMerent action in the ON condition (|z| = 2.89) but normal responding for all other measures across LED conditions (|z| < 2). Additional analyses revealed |z| = 2.55 when examining choice discrimination magnitude in outcome-specific PIT during the ON condition but not during the OFF condition (|z| = 0.62). This subject exhibited |z| < 2 across all other experimental stages.

The second rat showed outlier-level responding on the same action in the OFF condition (|z| = 2.02) but normal responding for all other measures across LED conditions (|z| < 2). Additional analyses revealed |z| = 2.12 when examining choice discrimination magnitude in outcome-specific PIT during the OFF condition but not during the ON condition (|z| = 0.67). This subject also exhibited |z| < 2 across all other experimental stages.

We excluded these two subjects and conducted the same analyses as described in the original manuscript. Baseline responding did not diMer between groups (p = 0.14), allowing to look at the net eMect of the stimuli. Overall lever presses were greater in the eYFP rats (Group: F(1,16) = 6.08, p < 0.05; η² = 0.28) and were reduced by LED activation (LED: F(1,16) = 9.52, p < 0.01; η² = 0.44) and this reduction depended on the group considered (Group x LED: F(1,16) = 12.125, p < 0.001; η² = 0.43). Lever press rates were higher on the action earning the same outcome as the stimuli compared to the action earning the diMerent outcome (Lever: F(1,16)= 49.32; η² = 0.76; p < 0.001), regardless of group (Group x Lever: p = 0.14). There was a Lever by LED light condition interaction (Lever x LED: F(1,16)= 5.25; η² = 0.24; p < 0.05) but no an interaction between group, LED light condition, and Lever during the presentation of the predictive stimuli (p = 0.10). Given the significant Group x LED and Lever x LED interactions, additional analyses were conducted to determine the source of these interactions. In eYFP rats, LED activation had no eMect (LED: p = 0.70) and lever presses were greater on the same action (Lever: (F(1,9) = 23.94, p < 0.001; η² = 0.79) regardless of LED condition (LED x Lever: p = 0.72). By contrast, in eNpHR3.0 rats, lever presses were reduced by LED activation (LED: F(1,9) = 23.97, p < 0.001; η² = 0.73), were greater on the same action (Lever: F(1,9) = 16.920, p < 0.001; η² = 0.65) and the two factors interacted (LED x Lever: F(1,9) = 9.12, p < 0.01; η² = 0.50). These rats demonstrated outcome-specific PIT in the OFF condition (F(1,9) = 27.26, p < 0.001; η² = 0.75) but not in the ON condition (p = 0.08).

Overall, excluding these two rats altered the statistical analyses, but both the original and revised analyses yielded the same outcome: silencing the NAc-S D1-SPN to VP pathway disrupted PIT. More importantly, we do not believe there are suMicient grounds to exclude the two rats identified by the reviewer. These animals did not display outlier-level responding across training stages or during the choice test. Their potential classification as outliers would be based on responding during only one LED condition and not the other, with notably opposite patterns between the two rats despite belonging to the same experimental group. 

(10) I think it would be appreciable if in the cartoons from Figure 5.A and 6.A, the SPNs neurons were color-coded as in the results (test plots) and the supplementary figures (histological color-coding), such as D1- in blue & D2-SPNs in red.

Our current color-coding system uses blue for D1-SPNs transduced with eNpHR3.0 and red for D2-SPNs transduced with eNpHR3.0. The D1-SPNs and D2-SPNs shown in Figures 5A and 6A represent cells transduced with either eYFP (control) or eNpHR3.0 virus and therefore cannot be assigned the blue or red color, which is reserved for eNpHR3.0transduced cells specifically. The micrographs in the Supplemental Figures maintain consistency with the color-coding established in the main figures.

(11) As there are (relatively small) variations in the control performance in term of Net responding (from ~3 to ~7 responses per min), I wonder what would be the result of pooling eYFP groups from the two first experiments (Figures 3 & 4) and from the two last ones (Figures 5 & 6) - would the same statically results stand or vary (as eYFP vs D1-Cre vs A2a-Cre rats)? In particular for Figures 3 & 4, with and without the potential outlier, if it's indeed an outlier.

We considered the Reviewer’s recommendation but do not believe the requested analysis is appropriate. The Reviewer is requesting the pooling of data from subjects of distinct transgenic strains (D1-Cre and A2A-Cre rats) that underwent surgical and behavioral procedures at diMerent time points, sometimes months apart. Each experiment was designed with necessary controls to enable adequate statistical analyses for testing our specific hypotheses. 

(12) Presence of cameras in operant cages is mentioned in methods, but no data is presented regarding recordings, though authors mention that they allow for real-time observations of behavior. I suggest removing "to record" or adding a statement about the fact that no videos were recorded or used in the present study.

We have removed “to record” from the manuscript (page 18). 

(13) In all supplementary Figures, "F" is wrongly indicated as "E".

We thank the Reviewer for reporting these errors, which have been corrected. 

(14) While the authors acknowledge that the eNicacy of optogenetic inhibition of terminals is questionable, I think that more details are required to address this point in the discussion (existing literature?). Maybe, the combination of an anterograde tracer from SPNs to VP, to label VP neurons (to facilitate patching these neurons), and the Credependent inhibitory opsin in the NAc Shell, with optogenetic illumination at the level of the VP, along with electrophysiological recordings of VP neurons, could help address this question but may, reasonably, seem challenging technically.

Our manuscript does not state that optogenetic inhibition of terminals is questionable. It acknowledges that we do not provide any evidence about the eMicacy of the approach. Regardless, we have provided additional details and suggestions to address this lack of evidence (page 13). 

(15) A nice addition could be an illustration of the proposed model (from line 374), but it may be unnecessary.

We have carefully considered the reviewer's recommendation. The proposed model is detailed in three published articles, including one that is freely accessible, which we have cited when presenting the model in our manuscript (page 14). This reference should provide interested readers with easy access to a comprehensive illustration of the model.

Reviewer 2 (Recommendations for the Author):

As noted in my public comments, this is a truly excellent and compelling study. I have only a few minor comments.

(1) I could not find the coordinates/parameters for the dorsal striatal AAV injections for that component of the tract tracing experiment.

We apologize for this omission, which has now been corrected (page 16). 

(2) Please add the final group sizes to the figure captions.

We followed the Reviewer’s recommendation and added group sizes in the main figure captions. 

(3) The discussion of group exclusions (p 21 line 637) seems to accidentally omit (n = X) the number of NAc-S D1-SPNs-VP mice excluded.

We apologize for this omission, which has now been corrected (page 22). 

(4) There were some labeling issues in the supplementary figures (perhaps elsewhere, too). Specifically, panel E was listed twice (once for F) in captions.

We apologize for this error, which has now been corrected.  

(5) Inspection of the magazine entry data from PIT tests suggests that the optogenetic manipulations may have had some eNects on this behavior and would encourage the authors to probe further. There was a significant group diNerence for D1-SPN inhibition and a marginal group eNect for D2-SPNs. The fact that these eNects were in opposite directions is intriguing, although not easily interpreted based on the canonical D1/D2 model. Of course, the eNects are not specific to the light-on trials, but this could be due to carryover into light-oN trials. An analysis of trial-order eNects seems crucial for interpreting these eNects. One might also consider normalizing for pre-test baseline performance. Response rates during Pavlovian conditioning seem to suggest that D2eNpHR mice showed slightly higher conditioned responding during training, which contrasts with their low entry rates at test. I don't see any of this as problematic -- but more should be done to interpret these findings.

We thank the reviewer for raising this interesting point regarding magazine entry rates. Since these data are presented in the Supplemental Figures, we have added a section in the Supplemental Material file that elaborates on these findings. This section does not address trial order eMects, as trial order was fully counterbalanced in our experiments and the relevant statistical analyses would lack adequate power. Baseline normalization was not conducted because the reviewer's suggestion was based on their assumption that eNpHR3.0 rats in the D2-SPNs experiment showed slightly higher magazine entries during Pavlovian training. However, this was not the case. In fact, like the eNpHR3.0 rats in the D1-SPNs experiment, they tended to display lower magazine entries during training. The added section therefore focuses on the potential role of response competition during outcome-specific PIT tests. Although we concluded that response competition cannot explain our findings, we believe it may complicate interpretation of magazine entry behavior. Thus, we recommend that future studies examine the role of NAc-S SPNs using purely Pavlovian tasks. It is worth nothing that we have recently completed experiments (unpublished) examining NAc-S D1- and D2-SPN silencing during stimulus presentation in a Pavlovian task identical to the one used here. Silencing of either SPN population had no eMect on magazine entry behavior.

Reviewer 3 (Recommendations for the Author):

Broad comments:

Throughout the manuscript, the authors draw parallels between the eNect established via pharmacological manipulations and those shown here with optogenetic manipulation. I understand using the pharmacological data to launch this investigation, but these two procedures address very diNerent physiological questions. In the case of a pharmacological manipulation, the targets are receptors, wherever they are expressed, and in the case of D2 receptors, this means altering function in both pre-synaptically expressed autoreceptors and post-synaptically expressed D2 MSN receptors. In the case of an optogenetic approach, the target is a specific cell population with a high degree of temporal control. So I would just caution against comparing results from these types of studies too closely.

Related to this point is the consideration of the physiological relevance of the manipulation. Under normal conditions, dopamine acts at D1-like receptors to increase the probability of cell firing via Ga signaling. In contrast, dopamine binding of D2-like receptors decreases the cell's firing probability (signaling via Gi/o). Thus, shunting D1MSN activation provides a clear impression of the role of these cells and, putatively, the role of dopamine acting on these cells. However, inhibiting D2-MSNs more closely mimics these cells' response to dopamine (though optogenetic manipulations are likely far more impactful than Gi signaling). All this is to say that when we consider the results presented here in Experiment 2, it might suggest that during PIT testing, normal performance may require a halting of DA release onto D2-MSNs. This is highly speculative, of course, just a thought worth considering.

We agree with the comments made by the Reviewer, and the original manuscript included statements acknowledging that pharmacological approaches are limited in the capacity to inform about the function of NAc-S SPNs (pages 4 and 9). As noted by the Reviewer, these limitations are especially salient when considering NAc-S D2-SPNs. Based on the Reviewer’s comment, we have modified our discussion to further underscore these limitations (page 12). Finally, we agree with the suggestion that PIT may require a halting of DA release onto D2-SPNs. This is consistent with the model presented, whereby D2-SPNs function is required to trigger enkephalin release (page 13).     

Section-Specific Comments and Questions:

Results:

Anterograde tracing and ex vivo cell recordings in D1 Cre and A2a Cre rats: Why are there no statistics reported for the e-phys data in this section? Was this merely a qualitative demonstration? I realize that the A2a-Cre condition only shows 3 recordings, so I appreciate the limitations in analyzing the data presented.

The reviewer is correct that we initially intended to provide a qualitative demonstration. However, we have now included statistical analyses for the ex vivo recordings. It is important to note that there were at least 5 recordings per condition, though overlapping data points may give the impression of fewer recordings in certain conditions. We have provided the exact number of recordings in both the main text (page 5) and figure legend. 

What does trial by trial analysis look like, because in addition to the eNects of extinction, do you know if the responsiveness of the opsin to light stimulation is altered after repeated exposures, or whether the cells themselves become compromised in any way with repeated light-inhibition, particularly given the relatively long 2m duration of the trial.

The Reviewer raises an interesting point, and we provide complete trial-by-trial data for each experiment below. As identified by the Reviewer, there is some evidence for extinction, although it remained modest. Importantly, the data suggest that light stimulation did not aMect the physiology of the targeted cells. In eNpHR3.0 rats, performance across OFF trials remained stable (both for Same and DiMerent) even though they were preceded by ON trials, indicating no carryover eMects from optical stimulation.

Author response image 2.

The statistics for the choice test are not reported for eNpHR-D1-Cre rats, but do show a weakening of the instrumental devaluation eNect "Group x Lever x LED: F1,18 = 10.04, p < 0.01, = 0.36". The post hoc comparisons showed that all groups showed devaluation, but it is evident that there is a weakening of this eNect when the LED was on (η² = 0.41) vs oN (η² = 0.78), so I think the authors should soften the claim that NAcS-D1s are not involved in value-based decision-making. (Also, there is a typo in the legend in Figure S1, where the caption for panel "F" is listed as "E".) I also think that this could be potentially interesting in light of the fact that with circuit manipulation, this same weakening of the instrumental devaluation eNect was not observed. To me, this suggests that D1-NAcS that project to a diNerent region (not VP) contribute to value-based decision making.

This comment overlaps with one made in the Public Review, for which we have already provided a response. Given its importance, we have added a section addressing this point in the supplemental discussion of the Supplementary Material file, which aligns with the location of the relevant data. The caption labelling error has been corrected.

Materials and Methods:

Subjects:

Were these heterozygous or homozygous rats? If hetero, what rats were used for crossbreeding (sex, strain, and vendor)? Was genotyping done by the lab or outsourced to commercial services? If genotyping was done within the lab, please provide a brief description of the protocol used. How was food restriction established and maintained (i.e., how many days to bring weights down, and was maintenance achieved by rationing or by limiting ad lib access to food for some period in the day)?

The information requested by the Reviewer have been added to the subjects section (pages 15-16).  

Were rats pair/group housed after implantation of optic fibers?

We have clarified that rats were group houses throughout (see subjects section; pages 15-16). 

Behavioral Procedures:

How long did each 0.2ml sucrose infusion take? For pellets, for each US delivery, was it a single pellet or two in quick succession?

We have modified the method section to indicate that the sucrose was delivered across 2 seconds and that a single pellet was provided (page 17). 

The CS to ITI duration ratio is quite low. Is there a reason such a short ratio was used in training?

These parameters are those used in all our previous experiments on outcome-specific PIT. There is no specific reason for using such a ratio, except that it shortens the length of the training session. 

Relative to the end of training, when were the optical implantation surgeries conducted, and how much recovery time was given before initiating reminder training and testing?

Fibre-optic implantation was conducted 3-4 days after training and another 3-4 days were given for recovery. This has been clarified in the Materials and methods section (pages 15-16).

I think a diagram or schematic showing the timeline for surgeries, training, and testing would be helpful to the audience.

We opted for a text-based experimental timeline rather than a diagram due to slight temporal variations across experiments (page 15).

On trials, when the LED was on, was light delivered continuously or pulsed? Do these opto-receptors 'bleach' within such a long window?

We apologize for the lack of clarity; the light was delivered continuously. We have modified the manuscript (pages 6 and 19) and figure legend accordingly. The postmortem analysis did not provide evidence for photobleaching (Supplemental Figures) and as noted above, the behavioural results do not indicate any negative physiological impact on cell function.  

Immunofluorescence: The blocking solution used during IHC is described as "NHS"; is this normal horse serum?

The Reviewer is correct; NHS stands for normal horse serum. This has been added (page 21). 

Microscopy and imaging:

For the description of rats excluded due to placement or viral spread problems, an n=X is listed for the NAc S D1 SPNs --> VP silencing group. Is this a typo, or was that meant to read as n=0? Also, was there a major sex diNerence in the attrition rate? If so, I think reporting the sex of the lost subjects might be beneficial to the scientific community, as it might reflect a need for better guidance on sex-specific coordinates for targeting small nuclei.

We apologize for the error regarding the number of excluded animals. This error has been corrected (page 23). There were no major sex diMerences in the attrition rate. The manuscript has been updated to provide information about the sex of excluded animals (page 23). 

References

Cao, J., Willett, J. A., Dorris, D. M., & Meitzen, J. (2018). Sex DiMerences in Medium Spiny Neuron Excitability and Glutamatergic Synaptic Input: Heterogeneity Across Striatal Regions and Evidence for Estradiol-Dependent Sexual DiMerentiation. Front Endocrinol (Lausanne), 9, 173. https://doi.org/10.3389/fendo.2018.00173

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Laurent, V., Bertran-Gonzalez, J., Chieng, B. C., & Balleine, B. W. (2014). δ-Opioid and Dopaminergic Processes in Accumbens Shell Modulate the Cholinergic Control of Predictive Learning and Choice. J Neurosci, 34(4), 1358-1369. https://doi.org/10.1523/JNEUROSCI.4592-13.2014

Laurent, V., Leung, B., Maidment, N., & Balleine, B. W. (2012). μ- and δ-opioid-related processes in the accumbens core and shell diMerentially mediate the influence of reward-guided and stimulus-guided decisions on choice. J Neurosci, 32(5), 1875-1883. https://doi.org/10.1523/JNEUROSCI.4688-11.2012

Matamales, M., McGovern, A. E., Mi, J. D., Mazzone, S. B., Balleine, B. W., & BertranGonzalez, J. (2020). Local D2- to D1-neuron transmodulation updates goal-directed learning in the striatum. Science, 367(6477), 549-555. https://doi.org/10.1126/science.aaz5751

Parkes, S. L., Bradfield, L. A., & Balleine, B. W. (2015). Interaction of insular cortex and ventral striatum mediates the eMect of incentive memory on choice between goaldirected actions. J Neurosci, 35(16), 6464-6471. https://doi.org/10.1523/JNEUROSCI.4153-14.2015

Pettibone, J. R., Yu, J. Y., Derman, R. C., Faust, T. W., Hughes, E. D., Filipiak, W. E., Saunders, T. L., Ferrario, C. R., & Berke, J. D. (2019). Knock-In Rat Lines with Cre Recombinase at the Dopamine D1 and Adenosine 2a Receptor Loci. eNeuro, 6(5). https://doi.org/10.1523/ENEURO.0163-19.2019

Willett, J. A., Will, T., Hauser, C. A., Dorris, D. M., Cao, J., & Meitzen, J. (2016). No Evidence for Sex DiMerences in the Electrophysiological Properties and Excitatory Synaptic Input onto Nucleus Accumbens Shell Medium Spiny Neurons. eNeuro, 3(1), ENEURO.0147-15.2016. https://doi.org/10.1523/ENEURO.0147-15.2016

Author response:

Reviewer #1 (Public review):

In the current article, Octavia Soegyono and colleagues study "The influence of nucleus accumbens shell D1 and D2 neurons on outcome-specific Pavlovian instrumental transfer", building on extensive findings from the same lab. While there is a consensus about the specific involvement of the Shell part of the Nucleus Accumbens (NAc) in specific stimulus-based actions in choice settings (and not in General Pavlovian instrumental transfer - gPIT, as opposed to the Core part of the NAc), mechanisms at the cellular and circuitry levels remain to be explored. In the present work, using sophisticated methods (rat Cre-transgenic lines from both sexes, optogenetics, and the well-established behavioral paradigm outcome-specific PIT-sPIT), Octavia Soegyono and colleagues decipher the differential contribution of dopamine receptors D1 and D2 expressing spiny projection neurons (SPNs).

After validating the viral strategy and the specificity of the targeting (immunochemistry and electrophysiology), the authors demonstrate that while both NAc Shell D1- and D2-SPNs participate in mediating sPIT, NAc Shell D1-SPNs projections to the Ventral Pallidum (VP, previously demonstrated as crucial for sPIT), but not D2-SPNs, mediates sPIT. They also show that these effects were specific to stimulus-based actions, as value-based choices were left intact in all manipulations.

This is a well-designed study, and the results are well supported by the experimental evidence. The paper is extremely pleasant to read and adds to the current literature.

We thank the Reviewer for their positive assessment.

Reviewer #2 (Public review):

Summary:

This manuscript by Soegyono et al. describes a series of experiments designed to probe the involvement of dopamine D1 and D2 neurons within the nucleus accumbens shell in outcome-specific Pavlovian-instrumental transfer (osPIT), a well-controlled assay of cue-guided action selection based on congruent outcome associations. They used an optogenetic approach to phasically silence NAc shell D1 (D1-Cre mice) or D2 (A2a-Cre mice) neurons during a subset of osPIT trials. Both manipulations disrupted cue-guided action selection but had no effects on negative control measures/tasks (concomitant approach behavior, separate valued guided choice task), nor were any osPIT impairments found in reporter-only control groups. Separate experiments revealed that selective inhibition of NAc shell D1 but not D2 inputs to ventral pallidum was required for osPIT expression, thereby advancing understanding of the basal ganglia circuitry underpinning this important aspect of decision making.

Strengths:

The combinatorial viral and optogenetic approaches used here were convincingly validated through anatomical tract-tracing and ex vivo electrophysiology. The behavioral assays are sophisticated and well-controlled to parse cue and value-guided action selection. The inclusion of reporter-only control groups is rigorous and rules out nonspecific effects of the light manipulation. The findings are novel and address a critical question in the literature. Prior work using less decisive methods had implicated NAc shell D1 neurons in osPIT but suggested that D2 neurons may not be involved. The optogenetic manipulations used in the current study provide a more direct test of their involvement and convincingly demonstrate that both populations play an important role. Prior work had also implicated NAc shell connections to ventral pallidum in osPIT, but the current study reveals the selective involvement of D1 but not D2 neurons in this circuit. The authors do a good job of discussing their findings, including their nuanced interpretation that NAc shell D2 neurons may contribute to osPIT through their local regulation of NAc shell microcircuitry.

We thank the Reviewer for their positive assessment.

Weaknesses:

The current study exclusively used an optogenetic approach to probe the function of D1 and D2 NAc shell neurons. Providing a complementary assessment with chemogenetics or other appropriate methods would strengthen conclusions, particularly the novel demonstration of D2 NAc shell involvement. Likewise, the null result of optically inhibiting D2 inputs to the ventral pallidum leaves open the possibility that a more complete or sustained disruption of this pathway may have impaired osPIT.

We acknowledge the reviewer's valuable suggestion that demonstrating NAc-S D1- and D2-SPN engagement in outcome-specific PIT through another technique would strengthen our optogenetic findings. Several approaches could provide this validation. Chemogenetic manipulation, as the reviewer suggested, represents one compelling option. Alternatively, immunohistochemical assessment of phosphorylated histone H3 at serine 10 (P-H3) offers another promising avenue, given its established utility in reporting striatal SPN plasticity in the dorsal striatum (Matamales et al., 2020). We hope to complete such an assessment in future work since it would address the limitations of previous work that relied solely on ERK1/2 phosphorylation measures in NAc-S SPNs (Laurent et al., 2014).

Regarding the null result from optical silencing of D2 terminals in the ventral pallidum, we agree with the reviewer's assessment. While we acknowledge this limitation in the current manuscript (see discussion), we aim to address this gap in future studies to provide a more complete mechanistic understanding of the circuit.

Reviewer #3 (Public review):

Summary:

The authors present data demonstrating that optogenetic inhibition of either D1- or D2-MSNs in the NAc Shell attenuates expression of sensory-specific PIT while largely sparing value-based decision on an instrumental task. They also provide evidence that SS-PIT depends on D1-MSN projections from the NAc-Shell to the VP, whereas projections from D2-MSNs to the VP do not contribute to SS-PIT.

Strengths:

This is clearly written. The evidence largely supports the authors' interpretations, and these effects are somewhat novel, so they help advance our understanding of PIT and NAc-Shell function.

We thank the Reviewer for their positive assessment.

Weaknesses:

I think the interpretation of some of the effects (specifically the claim that D1-MSNs do not contribute to value-based decision making) is not fully supported by the data presented.

We appreciate the reviewer's comment regarding the marginal attenuation of value-based choice observed following NAc-S D1-SPN silencing. While this manipulation did produce a slight reduction in choice performance, the behavior remained largely intact. We are hesitant to interpret this marginal effect as evidence for a direct role of NAc-S D1-SPNs in value-based decision-making, particularly given the substantial literature demonstrating that NAc-S manipulations typically preserve such choice behavior (Corbit & Balleine, 2011; Corbit et al., 2001; Laurent et al., 2012). Notably, previous work has shown that NAc-S D1 receptor blockade impairs outcome-specific PIT while leaving value-based choice unaffected (Laurent et al., 2014). We favor an alternative explanation for our observed marginal reduction. As documented in Supplemental Figure 1, viral transduction extended slightly into the nucleus accumbens core (NAc-C), a region established as critical for value-based decision-making (Corbit & Balleine, 2011; Corbit et al., 2001; Laurent et al., 2012). The marginal impairment may therefore reflect inadvertent silencing of a small NAc-C D1-SPN population rather than a functional contribution from NAc-S D1-SPNs. Future studies specifically targeting larger NAc-C D1-SPN populations would help clarify this possibility and provide definitive resolution of this question.

Author response:

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

Reviewer #1 (Public review):

Summary:

The authors used high-density probe recordings in the medial prefrontal cortex (PFC) and hippocampus during a rodent spatial memory task to examine functional sub-populations of PFC neurons that are modulated vs. unmodulated by hippocampal sharp-wave ripples (SWRs), an important physiological biomarker that is thought to have a role in mediating information transfer across hippocampal-cortical networks for memory processes. SWRs are associated with the reactivation of representations of previous experiences, and associated reactivation in hippocampal and cortical regions has been proposed to have a role in memory formation, retrieval, planning, and memory-guided behavior. This study focuses on awake SWRs that are prevalent during immobility periods during pauses in behavior. Previous studies have reported strong modulation of a subset of prefrontal neurons during hippocampal SWRs, with some studies reporting prefrontal reactivation during SWRs that have a role in spatial memory processes. The study seeks to extend these findings by examining the activity of SWR-modulated vs. unmodulated neurons across PFC sub-regions, and whether there is a functional distinction between these two kinds of neuronal populations with respect to representing spatial information and supporting memory-guided decision-making.

Strengths:

The major strength of the study is the use of Neuropixels 1.0 probes to monitor activity throughout the dorsal-ventral extent of the rodent medial prefrontal cortex, permitting an investigation of functional distinction in neuronal populations across PFC sub-regions. They are able to show that SWR-unmodulated neurons, in addition to having stronger spatial tuning than SWR-modulated neurons as previously reported, also show stronger directional selectivity and theta-cycle skipping properties.

Weaknesses:

(1) While the study is able to extend previous findings that SWR-modulated PFC neurons have significantly lower spatial tuning that SWR-unmodulated neurons, the evidence presented does not support the main conclusion of the paper that only the unmodulated neurons are involved in spatial tuning and signaling upcoming choice, implying that SWR-modulated neurons are not involved in predicting upcoming choice, as stated in the abstract. This conclusion makes a categorical distinction between two neuronal populations, that SWR-modulated neurons are involved and SWR-unmodulated are not involved in predicting upcoming choice, which requires evidence that clearly shows this absolute distinction. However, in the analyses showing non-local population decoding in PFC for predicting upcoming choice, the results show that SWR-unmodulated neurons have higher firing rates than SWR-modulated neurons, which is not a categorical distinction. Higher firing rates do not imply that only SWR-unmodulated neurons are contributing to the non-local decoding. They may contribute more than SWR-modulated neurons, but there are no follow-up analyses to assess the contribution of the two sub-populations to non-local decoding.

We agree with the reviewer that this is indeed not a categorical distinction, and do not wish to claim that the SWR-modulated neurons have absolutely no role in non-local decoding and signaling upcoming choice. We have adjusted this in the title, abstract and text to clarify this for the reader. Furthermore, we have performed additional analyses to elucidate the role of SWR-modulated neurons in non-local decoding by creating separate decoding models for SWR-modulated and unmodulated PFC neurons respectively. These analyses show that the SWR-unmodulated neurons are indeed encoding representations of the upcoming choice more often than the alternative choice, whereas the SWR-modulated neurons do not reliably differentiate the upcoming and alternative choices in non-local decoding at the choice point (see new Fig 4d).

(2) Further, the results show that during non-local representations of the hippocampus of the upcoming options, SWR-excited PFC neurons were more active during hippocampal representations of the upcoming choice, and SWR-inhibited PFC neurons were less active during hippocampal representations of the alternative choice. This clearly suggests that SWR-modulated neurons are involved in signaling upcoming choice, at least during hippocampal non-local representations, which contradicts the main conclusion of the paper.

This does not contradict the main conclusion of the paper, but in fact strengthens the hypothesis we are putting forward: that the SWR-modulated neurons are more linked to the hippocampal non-local representations, whereas the SWR-unmodulated neurons seem to have their own encoding of upcoming choice which is not linked to the signatures in the hippocampus (almost no time overlap with hippocampal representations, no phase locking to hippocampal theta, no time locking to hippocampal SWRs, no increased firing during hippocampal representations of upcoming choice).

(3) Similarly, one of the analyses shows that PFC nonlocal representations show no preference for hippocampal SWRs or hippocampal theta phase. However, the examples shown for non-local representations clearly show that these decodes occur prior to the start of the trajectory, or during running on the central zone or start arm. The time period of immobility prior to the start arm running will have a higher prevalence of SWRs and that during running will have a higher prevalence of theta oscillations and theta sequences, so non-local decoded representations have to sub-divided according to these known local-field potential phenomena for this analysis, which is not followed.

These analyses are in fact separated based on proximity to SWRs (only segments that occurred within 2 seconds of SWR onset were included, see Methods) and theta periods respectively (selected based on a running speed of more than 5 cm/s and the absence of SWRs in the hippocampus, see Methods). We have clarified this in the main text.

(4) The primary phenomenon that the manuscript relies on is the modulation of PFC neurons by hippocampal SWRs, so it is necessary to perform the PFC population decoding analyses during SWRs (or examine non-local decoding that occurs specifically during SWRs), as reported in previous studies of PFC reactivation during SWRs, to see if there is any distinction between modulated and unmodulated neurons in this reactivation. Even in the case of independent PFC reactivation as reported by one study, this PFC reactivation was still reported to occur during hippocampal SWRs, therefore decoding during SWRs has to be examined. Similarly, the phenomenon of theta cycle skipping is related to theta sequence representations, so decoding during PFC and hippocampal theta sequences has to be examined before coming to any conclusions.

The histograms shown in Figure 5a (see updated Fig 5a where we look at the closest SWR in time and compare the occurrence with shuffled data) show that there is no increased prevalence of decoding upcoming and alternative choices in the PFC during hippocampal SWRs. The lack of overlap of non-local decoding between the hippocampus and PFC further shows that these non-local representations occur at different timepoints in the PFC and hippocampus (see updated Fig 4e where we added a statistical test to show the likeliness of the overlap between the decoded segments in the PFC and hippocampus). Based on the reviewer's suggestion, we have additionally decoded the information in the PFC during hippocampal SWRs exclusively, and found that the direction on the maze could not be predicted based on the decoding of SWR time points in the PFC. See figure below. Similarly, we can see from the histograms in Figure 5c that there is no phase locking to the hippocampal theta phase for non-local representations in the PFC, and in contrast there is phase locking of the hippocampal encoding of upcoming choice to the rising phase of the theta cycle (Fig 6c), further highlighting the separation between these two regions in the non-local decoding.

Reviewer #2 (Public review):

Summary:

This work by den Bakker and Kloosterman contributes to the vast body of research exploring the dynamics governing the communication between the hippocampus (HPC) and the medial prefrontal cortex (mPFC) during spatial learning and navigation. Previous research showed that population activity of mPFC neurons is replayed during HPC sharp-wave ripple events (SWRs), which may therefore correspond to privileged windows for the transfer of learned navigation information from the HPC, where initial learning occurs, to the mPFC, which is thought to store this information long term. Indeed, it was also previously shown that the activity of mPFC neurons contains task-related information that can inform about the location of an animal in a maze, which can predict the animals' navigational choices. Here, the authors aim to show that the mPFC neurons that are modulated by HPC activity (SWRs and theta rhythms) are distinct from those "encoding" spatial information. This result could suggest that the integration of spatial information originating from the HPC within the mPFC may require the cooperation of separate sets of neurons.

This observation may be useful to further extend our understanding of the dynamics regulating the exchange of information between the HPC and mPFC during learning. However, my understanding is that this finding is mainly based upon a negative result, which cannot be statistically proven by the failure to reject the null hypothesis. Moreover, in my reading, the rest of the paper mainly replicates phenomena that have already been described, with the original reports not correctly cited. My opinion is that the novel elements should be precisely identified and discussed, while the current phrasing in the manuscript, in most cases, leads readers to think that these results are new. Detailed comments are provided below.

Major concerns:

(1) The main claim of the manuscript is that the neurons involved in predicting upcoming choices are not the neurons modulated by the HPC. This is based upon the evidence provided in Figure 5, which is a negative result that the authors employ to claim that predictive non-local representations in the mPFC are not linked to hippocampal SWRs and theta phase. However, it is important to remember that in a statistical test, the failure to reject the null hypothesis does not prove that the null hypothesis is true. Since this claim is so central in this work, the authors should use appropriate statistics to demonstrate that the null hypothesis is true. This can be accomplished by showing that there is no effect above some size that is so small that it would make the effect meaningless (see https://doi.org/10.1177/070674370304801108).

We would like to highlight a few important points here. (1) We indeed do not intend to claim that the SWR-modulated neurons are not at all involved in predicting upcoming choice, just that the SWR-unmodulated neurons may play a larger role. We have rephrased the title and abstract to make this clearer. (2) The hypothesis that we put forward is based not only on a negative effect, but on the findings that: the SWR-unmodulated neurons show higher spatial tuning (Fig 3b), more directional selectivity (Fig 3d), more frequent encoding of the upcoming choice at the choice point (new analysis, added in Fig 4d), and higher spike rates during the representations of the upcoming choice (Fig 5b). This is further highlighted by the fact that the representations of upcoming choice in the PFC are not time locked to SWRs (whereas the hippocampal representations of upcoming choice are;  see Fig 5a and Fig 6a), and not time-locked to hippocampal theta phase (whereas the hippocampal representations are; see Fig 5c and Fig 6c). Finally, the representations of upcoming and alternative choices in the PFC do not show a large overlap in time with the representations in the hippocampus (see updated Fig 4e were we added a statistical test to show the likelihood of the overlap of decoded timepoints). All these results together lead us to hypothesize that SWR-modulation is not the driving factor behind non-local decoding in the PFC. (3) Based on the reviewers suggestion, we have added a statistical test to compare the phase-locking based of the non-local decoding to hippocampal SWRs and theta phase to shuffled posterior probabilities. Instead of looking at all SWRs in a -2 to 2 second window, we have now only selected the closest SWR in time within that window, and did the statistical comparison in the bin of 0-20 ms from SWR onset. With this new analysis we are looking more directly at the time-locking of the decoded segments to SWR onset (see updated Fig 5a and 6a).

(2) The main claim of the work is also based on Figure 3, where the authors show that SWRs-unmodulated mPFC neurons have higher spatial tuning, and higher directional selectivity scores, and a higher percentage of these neurons show theta skipping. This is used to support the claim that SWRs-unmodulated cells encode spatial information. However, it must be noted that in this kind of task, it is not possible to disentangle space and specific task variables involving separate cognitive processes from processing spatial information such as decision-making, attention, motor control, etc., which always happen at specific locations of the maze. Therefore, the results shown in Figure 3 may relate to other specific processes rather than encoding of space and it cannot be unequivocally claimed that mPFC neurons "encode spatial information". This limitation is presented by Mashoori et al (2018), an article that appears to be a major inspiration for this work. Can the authors provide a control analysis/experiment that supports their claim? Otherwise, this claim should be tempered. Also, the authors say that Jadhav et al. (2016) showed that mPFC neurons unmodulated by SWRs are less tuned to space. How do they reconcile it with their results?

The reviewer is right to assert caution when talking about claims such as spatial tuning where other factors may also be involved. Although we agree that there may be some other factors influencing what we are seeing as spatial tuning, it is very important to note that the behavioral task is executed on a symmetrical 4-armed maze, where two of the arms are always used for the start of the trajectory, and the other two arms (North and South) function as the goal (reward) arms. Therefore, if the PFC is encoding cognitive processes such as task phases related to decision-making and reward, we would not be able to differentiate between the two start arms and the two goal arms, as these represent the same task phases. Note also that the North and South arm are illuminated in a pseudo-random order between trials and during cue-based rule learning this is a direct indication of where the reward will be found. Even in this phase of the task, the PFC encodes where the animal will turn on a trial-to-trial basis (meaning the North and South arm are still differentiated correctly on each trial even though the illumination and associated reward are changing).

Secondly, importantly, the reviewer mentions that we claimed that Jadhav et al. (2016) showed that mPFC neurons unmodulated by SWRs are less tuned to space, but this is incorrect. Jadhav et al. (2016) showed that SWR-unmodulated neurons had lower spatial coverage, meaning that they are more spatially selective (congruent with our results). We have rephrased this in the text to be clearer.

(3) My reading is that the rest of the paper mainly consists of replications or incremental observations of already known phenomena with some not necessarily surprising new observations:

(a) Figure 2 shows that a subset of mPFC neurons is modulated by HPC SWRs and theta (already known), that vmPFC neurons are more strongly modulated by SWRs (not surprising given anatomy), and that theta phase preference is different between vmPFC and dmPFC (not surprising given the fact that theta is a travelling wave).

The finding that vmPFC neurons are more strongly modulated by SWRs than dmPFC indeed matches what we know from anatomy, but that does not make it a trivial finding. A lot remains unknown about the mPFC subregions and their interactions with the hippocampus, and not every finding will be directly linked to the anatomy. Therefore, in our view this is a significant finding which has not been studied before due to the technical complexity of large-scale recordings along the dorsal-ventral axis of the mPFC.

Similarly, theta being a traveling wave (which in itself is still under debate), does not mean we should assume that the dorsal and ventral mPFC should follow this signature and be modulated by different phases of the theta cycle. Again, in our view this is not at all trivial, but an important finding which brings us closer to understanding the intricate interactions between the hippocampus and PFC in spatial learning and decision-making.

(b) Figure 4 shows that non-local representations in mPFC are predictive of the animal's choice. This is mostly an increment to the work of Mashoori et al (2018). My understanding is that in addition to what had already been shown by Mashoori et al here it is shown how the upcoming choice can be predicted. The author may want to emphasize this novel aspect.

In our view our manuscript focuses on a completely different aspect of learning and memory than the paper the reviewer is referring to (Mashoori et al. 2018). Importantly, the Mashoori et al. paper looked at choice evaluation at reward sites and shows that disappointing reinforcements are associated with reactivations in the ACC of the unselected target. This points to the role of the ACC in error detection and evaluation. Although this is an interesting result, it is in essence unrelated to what we are focusing on here, which is decision making and prediction of upcoming choices. The fact that the turning direction of the animal can be predicted on a trial-to-trial basis, and even precedes the behavioral change over the course of learning, sheds light on the role of the PFC in these important predictive cognitive processes (as opposed to post-choice reflective processes).

(c) Figure 6 shows that prospective activity in the HPC is linked to SWRs and theta oscillations. This has been described in various forms since at least the works of Johnson and Redish in 2007, Pastalkova et al 2008, and Dragoi and Tonegawa (2011 and 2013), as well as in earlier literature on splitter cells. These foundational papers on this topic are not even cited in the current manuscript.

We have added these citations to the introduction (line 37).

Although some previous work is cited, the current narrative of the results section may lead the reader to think that these results are new, which I think is unfair. Previous evidence of the same phenomena should be cited all along the results and what is new and/or different from previous results should be clearly stated and discussed. Pure replications of previous works may actually just be supplementary figures. It is not fair that the titles of paragraphs and main figures correspond to notions that are well established in the literature (e.g., Figure 2, 2nd paragraph of results, etc.).

We have changed the title of paragraph 2 and Figure 2 to highlight more clearly the novel result (the difference between the dorsal and ventral mPFC), and have improved clarity of the text throughout to highlight the novelty of our results better.

(d) My opinion is that, overall, the paper gives the impression of being somewhat rushed and lacking attention to detail. Many figure panels are difficult to understand due to incomplete legends and visualizations with tiny, indistinguishable details. Moreover, some previous works are not correctly cited. I tried to make a list of everything I spotted below.

We have addressed all the comments in the Recommendations for Authors.

Reviewer #1 (Recommendations for the authors):

(1) Expanding on the points above, one of the strengths of the study is expanding the previous result that SWR-unmodulated neurons are more spatially selective (Jadhav et al., 2016), across prefrontal sub-regions, and showing that these neurons are more directionally selective and show more theta cycle skipping. Theta cycle skipping is related to theta sequence representations and previous studies have established PFC theta sequences in parallel to hippocampal theta sequences (Tang et al., 2021; Hasz and Redish, 2020; Wang et al., 2024), and the theta cycle skipping result suggests that SWR-unmodulated neurons should show stronger participation than SWR-modulated neurons in PFC theta sequences that decode to upcoming or alternative location, which can be tested in this high-density PFC physiology data. This is still unlikely to make a categorical distinction that only SWR-unmodulated neurons participate in theta sequence decoding, but will be useful to examine.

We thank the reviewer for their suggestion and have now included results based on separate decoding models that only use SWR-modulated or SWR-unmodulated mPFC neurons. From this analysis we see that indeed SWR-unmodulated neurons are not the only group contributing to theta sequence decoding, but they do distinguish more strongly between the upcoming and alternative arms at the choice point (see new Fig 4d).

(2) Non-local decoding in 50ms windows on a theta timescale is a valid analysis, but ignoring potential variability in the internal state during running vs. immobility, and as indicated by LFPs by the presence of SWRs or theta oscillations, is incorrect especially when conclusions are being made about decoding during SWRs and theta oscillation phase, and in light of previous evidence that these are distinct states during behavior. There are multiple papers on PFC theta sequences (Tang et al., 2021; Hasz and Redish, 2020; Wang et al., 2024), and on PFC reactivation during SWRs (Shin et al., 2019; Kaefer et al., 2020; Jarovi et al., 2023), and this dataset of high-density prefrontal recordings using Neuropixels 1.0 provides an opportunity to investigate these phenomena in detail. Here, it should be noted that although Kaefer et al. reported independent prefrontal reactivation from hippocampal reactivation, these PFC reactivation events still occurred during hippocampal SWRs in their data, and were linked to memory performance.

From our data we see that the time segments that represent upcoming or alternative choice in the prefrontal cortex are in fact not time-locked to hippocampal SWRs (updated Fig 5a where we look only at the closest SWR in time and compare this to shuffled data). In addition, these segments do not overlap much with the decoded segments in the hippocampus (see updated Fig 4e where we added a shuffling procedure to assess the likelihood of the overlap with hippocampal decoded segments). Importantly, we are not ignoring the variability during running and immobility, as theta segments were selected based on a running speed of more than 5 cm/s and the absence of SWRs in the hippocampus (see Methods), ensuring that the theta and SWR analyses were done on the two different behavioral states respectively. We have  clarified this in the main text.

(3) The majority of rodent studies make the distinction between ACC, PrL, and IL, although as the authors noted, there are arguments that rodent mPFC is a continuum (Howland et al., 2022), or even that rodent mPFC is a unitary cingulate cortical region (van Heukelum et al., 2020). The authors choose to present the results as dorsal (ACC + dorsal PrL) vs. ventral mPFC (ventral PrL + IL), however, in my opinion, it will be more useful to the field to see results separately for ACC, PrL, and IL, given the vast literature on connectivity and functional differences in these regions.

We appreciate the reviewer’s suggestion. Initially, we did perform all analyses separately for the ACC, PLC and ILC subregions. However, we observed that the differences between subregions (strength of SWR-modulation and the phase locking to theta) varied uniformly along the dorsal-ventral axis, i.e., the PLC showed a profile of SWR-modulation and theta phase locking that fell in between that of the ACC and the ILC. This is also highlighted in paragraph 3 of the introduction (lines 52-56). For that reason, and for the sake of reducing the number of variables, increasing statistical power, and improving readability, we focused on the dorsal-ventral distinction instead, as this is where the main differences were seen.

(4) I suggest that the authors refrain from making categorical distinctions as in their title and abstract, such as "neurons that are involved in predicting upcoming choice are not the neurons that are modulated by hippocampal sharp-wave ripples" when the evidence presented can only support gradation of participation of the two neuronal sub-populations, not an absolute distinction. The division of SWR-modulated and SWR-unmodulated neurons itself is determined by the statistic chosen to divide the neurons into one or two sub-classes and will vary with the statistical threshold employed. Further, previous studies have suggested that SWR-excited and SWR-inhibited neurons comprise distinct functional sub-populations based on their activity properties (Jadhav et al., 2016; Tang et al., 2017), but it is not clear to what degree is SWR-modulated neurons a distinct and singular functional sub-population. In the absence of connectivity information and cross-correlation measures within and across sub-populations, it is prudent to be conservative about this interpretation of SWR-unmodulated neurons.

We agree with the reviewer that the distinction is not categorical and have changed the wording in the title and abstract. We also do not intend to claim that the SWR-modulated neurons are a distinct and singular functional sub-population, and for that reason the firing rates from the SWR-excited and SWR-inhibited groups are reported separately throughout the paper.

Reviewer #2 (Recommendations for the authors):

Minor detailed remarks:

(1) The authors should provide a statistical test, perhaps against shuffled data, for Figures 5a,c and 6a,c.

We thank the reviewer for their suggestion and have added statistical tests in Figures 5a, 5c, 6a and 6c.

(2) The behavioral task is explained only in the legend of Figure 1c, and the explanation is quite vague. In this type of article format, readers need to have a clear understanding of the task without having to refer to the methods section. A clear understanding of the task is crucial for interpreting all subsequent analyses. In my opinion, the word 'trial' in the figure is misleading, as these are sessions composed of many trials.

We have added a more thorough description of the behavioral task, both in the main text and the Figure legend.

(3) Figure 1d, legend of markers missing.

We have added a legend for the markers.

(4) When there are multiple bars and a single p-value is presented, it is unclear which group comparisons the p-value pertains to. For instance, Figures 2c-f and 3b, d, f (right parts), and 5b...

For all p-values we have added lines to the figures that indicate the groups that were compared and have added descriptions of the statistical test to the figure legends to indicate what each p-value represents.

(5) In Figure 3c, the legend does not explain what the colored lines represent, and the lines themselves are very small and almost indistinguishable.

We have changed the colored lines to quadrants on the maze to clarify what each direction represents.

(6) Figure 4a is too small, and the elements are so tiny that it is impossible to distinguish them and their respective colors. The term 'segment' has not been unequivocally explained in the text. All the different elements of the panel should be explicitly explained in the legend to make it easily understandable. What do the pictograms of the maze on the left represent? What does the dashed vertical line indicate?

We have added the definition of a segment in the text (lines 283-286) and have improved the clarity and readability of Figure 4a.

(7) In Figure 5, what do the red dots on the right part relate to? The legend should explicitly explain what is shown in the left and right parts, respectively. What comparisons do the p-values relate to?

We have adjusted the legend to explain the left and right parts of the figure and we have added the statistical test that was used to get to the p-value (in addition to the text which already explained this).

(8) Panels b of Figures 5 and 6 should have the same y-axis scale for comparison. The position of the p-values should also be consistent. With the current arrangement in Figure 6, it is unclear what the p-values relate to.

We have adjusted the y-scale to be the same for Figures 5 and 6, and we have added a description of the statistical test to the legend.

(9) Multiple studies have previously shown that mPFC activity contains spatial information (e.g., refs 24-27). It is important that, throughout the paper, the authors frame their results in relation to previous findings, highlighting what is novel in this work.

We thank the reviewer for this valuable suggestion. In the revised manuscript, we have indicated more clearly which results replicate previous findings and highlighted novel results.

(10) Please note that Peyrache et al. (2009) do not show trajectory replay, nor do they decode location. I am not familiar with all the cited literature, but this makes me think that the authors may want to double-check their citations to ensure they assign the correct claims to each past work.

We have adjusted the reference to the work to exclude the word ‘trajectory’ and doublechecked our other citations.

(11) The authors perform theta-skipping analysis, first described by Kay et al., but do not cite the original paper until the discussion.

Thank you pointing out this oversight. We have now included this citation earlier in the paper (line 231).

(12) Additionally, some parts of the text are difficult to grasp, and there are English vocabulary and syntax errors. I am happy to provide comments on the next version of the text, but please include page and line numbers in the PDF. The authors may also consider using AI to correct English mistakes and improve the fluency and readability of their text.

We have carefully gone through the text to correct any errors.  We have now also included page and line numbers and we will be happy to address any specific issues the reviewer may spot in the revised manuscript.

Author response:

The following is the authors’ response to the original reviews

Public Reviews: 

Reviewer #1 (Public review): 

This study presents evidence that remote memory in the APP/PS1 mouse model of Alzheimer's disease (AD) is associated with PV interneuron hyperexcitability and increased inhibition of cortical engram cells. Its strength lies in the fact that it explores a neglected aspect of memory research - remote memory impairments related to AD (for which the primary research focus is usually on recent memory impairments) -which has received minimal attention to date. While the findings are intriguing, the weakness of the paper hovers around purely correlational types of evidence and superficial data analyses, which require substantial revisions as outlined below. 

We thank the reviewer for their feedback, and we appreciate the recognition of the study’s novelty in addressing remote memory impairments in AD. We acknowledge the reviewer’s concerns and have implemented revisions to strengthen the manuscript.

Major concerns: 

(1) In light of previous work, including that by the authors themselves, the data in Figure 1 should be implemented by measurements of recent memory recall in order to assess whether remote memories are exclusively impaired or whether remote memory recall merely represents a continuation of recent memory impairments.

We agree with the reviewer that is an important point. In line with their suggestion in minor comment 1, we now omitted the statement on recent memory in the results (previously on lines 109-111 and 117). Nonetheless, previous independent experiments from our group have repeatedly shown recent memory deficits in APP/PS1 mice at 12 weeks of age, including a recent article published in 2023. We refer the reviewer to figure 2c in Végh et al. (2014) and figure 2i in Kater et al. (2023). We have added a reference of the latter paper to our discussion section (line 458-459). Therefore, we are confident that the recent memory deficit at 12 weeks of age is a stable phenotype in our APP/PS1 mice.

With these data in mind, we argue that the remote memory recall impairment is not a continuation of recent memory impairments. Recent memory deficits emerge already at 12 weeks of age, and when remote memory is assessed at 16 weeks (4 weeks after training at 12 weeks of age), APP/PS1 mice are still capable of forming and retrieving a remote memory. This suggests that remote memory retrieval can occur even when recent memory is compromised, arguing against the idea that the remote memory deficit observed at 20 weeks is a continuation of earlier recent memory impairments. We have clarified this point in the revised manuscript by adding the following sentence to the discussion section (line 462-465): 

‘This suggests that a remote memory can be formed even when recent memory expression is already compromised, indicating that the remote memory deficit in 20-week-old APP/PS1 mice is not a continuation of earlier recent memory impairments.’

(2) Figure 2 shows electrophysiological properties of PV cells in the mPFC that correlate with the behavior shown in Figure 1. However, the mice used in Figure 2 are different than the mice used in Figure 1. Thus, the data are correlative at best, and the authors need to confirm that behavioral impairments in the APP/PS1 mice crossed to PV-Cre (and SST-Cre mice) used in Figure 2 are similar to those of the APP/PS1 mice used in Figure 1. Without that, no conclusions between behavioral impairments and electrophysiological as well as engram reactivation properties can be made, and the central claims of the paper cannot be upheld. 

We thank the reviewer for raising this concern. Indeed, the remote memory impairment and PV hyperexcitability are correlative data, and therefore we do not make causal claims based on these data. However, please note that most of our key findings, including behavioural impairments, characterization of the engram ensemble and reactivation thereof, as well as inhibitory input measurements, were acquired using the same mouse line (APP/PS1), strengthening the coherence of our conclusions. Also, our electrophysiological findings in APP/PS1 (enhanced sIPSC frequency) and APP/PS1-PV-Cre-tdTomato (enhanced PV cell excitability) mice align well. Direct comparisons between the transgenic mouse lines APP/PS1 and APP/PS1 Parv-Cre were performed in our previous studies, confirming that these lines are similar in terms of behaviour and pathology. Specifically, we demonstrated that APP/PS1 mice display spatial memory impairments at 16 weeks of age, Fig 4a-d, consistent with the deficits observed in APP/PS1 Parv-Cre mice at 16 weeks of age, Fig 5a-c (Hijazi et al., 2020a). Additionally, Hijazi et al. (2020a) showed that soluble and insoluble Aβ levels do not differ between APP/PS1 Parv-Cre and APP/PS1 mice (sFig. 1), indicating comparable levels of pathology between these lines. While we do not have a similar characterization of the APP/PS1 SST-Cre line, we should mention that we also did not observe excitability differences in SST cells. We now acknowledge the limitation in the revised discussion section (line 480-487), and stress that our electrophysiology and behavioural findings are correlative in nature:

‘Although the excitability measurements were performed in APP/PS1-PV-Cre-tdTomato mice, and not in the APP/PS1 parental line, we previously found that these transgenic mouse lines exhibit comparable amyloid pathology (both soluble and insoluble amyloid beta levels) as well as similar spatial memory deficits (Hijazi et al., 2020a; Kater et al., 2023). Thus, our observations indicate that the APP/PS1 PV-Cre-tdTomato and APP/PS1 lines are similar in terms of pathology and behaviour. Nonetheless, further work is needed to identify a causal link between PV cell hyperexcitability and remote memory impairment.’ 

(3) The reactivation data starting in Figure 3 should be analysed in much more depth: 

a) The authors restrict their analysis to intra-animal comparisons, but additional ones should be performed, such as inter-animal (WT vs APP/PS1) as well as inter-age (12-16w vs 16-20w). In doing so, reactivation data should be normalized to chance levels per animal, to account for differences in labelling efficiency - this is standard in the field (see original Tonegawa papers and for a reference). This could highlight differences in total reactivation that are already apparent, such as for instance in WT vs APP/PS1 at 20w (Figure 3o) and highlight a decrease in reactivation in AD mice at this age, contrary to what is stated in lines 213-214. 

We would like to thank the reviewer for the valuable input on the reactivation data in Figure 3. 

We agree with the reviewer and now depict the data as normalized to chance levels (Figure 3). The original figures are now supplemental (sFig. 5). The reactivation data normalized to chance are similar to the original results, i.e. no difference was observed in the reactivation of the mPFC engram ensemble between genotypes. The reviewer may have overlooked that we did perform inter-animal (WT vs. APP/PS1) comparisons, however these were not significantly different. We have made this clearer in the main text, lines 277, 288-289, 294-295 and 303-304. Moreover, the reviewer recommended including inter-age group comparisons, which have now been added to the supplemental figures (sFig. 6). No genotype-dependent differences were observed. While a main effect of age group did emerge, indicating that there is a potential increased overlap between Fos+ and mCherry+ in animals aged 16-20 weeks, we caution against overinterpreting this finding. These experimental groups were processed in separate cohorts, with viral injection and 4TM-induced tagging performed at different moments in time, which may have contributed to the observed differences in overlap. We have addressed this point in the revised discussion (line 612-617):

‘Furthermore, we also observed an increase in the amount overlap between Fos+ and mCherry+ engram cells when comparing the 12-16w and 16-20w age groups. This finding should be interpreted with caution, as the experimental groups were processed in separate cohorts, with viral injections and 4TM-induced tagging performed at different moments in time. This may have contributed to the observed differences between ages.’

b) Comparing the proportion of mcherry+ cells in PV- and PV+ is problematic, considering that the PV- population is not "pure" like the PV+, but rather likely to represent a mix of different pyramidal neurons (probably from several layers), other inhibitory neurons like SST and maybe even glial cells. Considering this, the statement on line 218 is misleading in saying that PVs are overrepresented. If anything, the same populations should be compared across ages or groups.  

We thank the reviewer for their insightful comment and agree that the PV- population of cells is likely more heterogenous than the PV+ population. However, we would like to clarify that all quantified cells were selected based on Nissl immunoreactivity, and to exclude non-neuronal cells, stringent thresholding was applied in the script that was used to identify Nissl+ cells. The threshold information has now been added to the methods section (line 758-760). Thus, although heterogenous, the analysed PV- population reflects a neuronal subset. In response to the reviewer’s suggestion, we have now included overlap measurements relative to chance levels (Figure 3). These analyses did not reveal differences with the original analyses, i.e., there are no genotype specific differences. We have also incorporated the suggested inter-age group comparisons (sFig. 6) and found no differences between age groups. In light of the raised concerns, we have removed the statement that PV cells were overrepresented in the engram ensemble.

c) A similar concern applies to the mcherry- population in Figure 4, which could represent different types of neurons that were never active, compared to the relatively homogeneous engram mcherry+ population. This could be elegantly fixed by restricting the comparison to mCherry+Fos+ vs mCherry+Fos- ensembles and could indicate engram reactivation-specific differences in perisomatic inhibition by PV cells. 

The comparison the reviewer suggests, comparing mCherry+Fos+ to mCherry+Fos- is indeed conceptually interesting and could provide more insight into engram reactivation and PV input. However, there are practical limitations to performing this analysis, as neurons in close proximity need to be compared in a pairwise manner to account for local variability in staining intensity. As shown in Figure 3c+k and Figure 4a+b, d+e, PV immunostaining intensity varies to a certain extend within a given image. While pairwise comparisons of neighbouring neurons were feasible when analysing mCherry+ and mCherry- cells, they are unfortunately not feasible for the mCherry+Fos+ vs. mCherry+Fos- comparison. The occurrence of spatially adjacent mCherry+Fos+ and mCherry+Fos- neurons is too sparse for a pairwise comparison. This analysis would therefore result in substantial under-sampling and limit the reliability of the analysis. Nonetheless, we agree with the reviewer that the mCherry- population may be more heterogenous than the mCherry+ population, despite the fact that PV+ neurons and that non-neuronal cells were excluded from both populations in the analyses. We therefore added a statement to the discussion to acknowledge this limitation (line 536-539): 

‘Although PV+ cells were not included in this analysis and we excluded non-neuronal cells based on the area of the Nissl stain, the mCherry- population was potentially more heterogenous than the mCherry+ population, which may have contributed to the differences we observed.’

(4) At several instances, there are some doubts about the statistical measures having been employed: 

a) In Figure 4f, it is unclear why a repeated measurement ANOVA was used as opposed to a regular ANOVA. 

b) In Supplementary Figure 2b, a Mann-Whitney test was used, supposedly because the data were not normally distributed. However, when looking at the individual data points, the data does seem to be normally distributed. Thus, the authors need to provide the test details as to how they measured the normalcy of distribution. 

a) Based on the pairwise comparison of neighbouring neurons within animals, the data in Figure 4f was analysed with a repeated measure ANOVA. 

b) We thank the author for their comment on Supplementary Figure 2b. The data is indeed normally distributed, and we have analysed it using a D’Agostino & Pearson test. We have corrected this in the supplemental figure. 

Minor concerns: 

(1) Line 117: The authors cite a recent memory impairment here, as shown by another paper. However, given the notorious difficulty in replicating behavioral findings, in particular in APP/PS1 mice (number of backcrossings, housing conditions, etc., might differ between laboratories), such a statement cannot be made. The authors should either show in their own hands that recent memory is indeed affected at 12 weeks of age, or they should omit this statement. 

We thank the reviewer for this thoughtful comment. As noted in our response to major concern (1), we have addressed this concern by providing additional information and clarification in the discussion (line 462-465) regarding the possibility that remote memory impairments are a continuation of recent memory impairments. As mentioned in our response, we have added a reference to a more recent study from our lab (Kater et al. (2023). These findings are consistent with the earlier report from our lab (Végh et al. (2014), underscoring the reproducibility of this phenotype across independent cohorts and time. Notably, the experiments in the 2023 and present study were performed using the same housing and experimental conditions. Nevertheless, in light of the reviewer’s suggestion, and to avoid overstatement or speculation, we have now omitted the sentence referring to recent memory impairments at 12 weeks of age from the results section.

(2) Pertaining to Figure 3, low-resolution images of the mPFC should be provided to assess the spread of injection and the overall degree of double-positive cells.  

We agree with the reviewer and have added images of the mPFC as a supplemental figure (sFig. 3) that show the spread of the injection. Unfortunately, it is not possible to visualize the overall degree of double-positive cells at a lower magnification (or low-resolution). Representative examples of colocalization are presented in Figure 3.

Reviewer #2 (Public review): 

This study presents a comprehensive investigation of remote memory deficits in the APP/PS1 mouse model of Alzheimer's disease. The authors convincingly show that these deficits emerge progressively and are paralleled by selective hyperexcitability of PV interneurons in the mPFC. Using viral-TRAP labeling and patch-clamp electrophysiology, they demonstrate that inhibitory input onto labeled engram cells is selectively increased in APP/PS1 mice, despite unaltered engram size or reactivation. These findings support the idea that alterations in inhibitory microcircuits may contribute to cognitive decline in AD. 

However, several aspects of the study merit further clarification. Most critically, the central paradox, i.e., increased inhibitory input without an apparent change in engram reactivation, remains unresolved. The authors propose possible mechanisms involving altered synchrony or impaired output of engram cells, but these hypotheses require further empirical support. Additionally, the study employs multiple crossed transgenic lines without reporting the progression of amyloid pathology in the mPFC, which is important for interpreting the relationship between circuit dysfunction and disease stage. Finally, the potential contribution of broader network dysfunction, such as spontaneous epileptiform activity reported in APP/PS1 mice, is also not addressed. 

We thank the reviewer for their evaluation and appreciate the positive assessment of our study’s contributing to understanding remote memory deficits and the dysfunction of inhibitory microcircuits in AD. We also acknowledge the relevant points raised and have revised the manuscript to clarify our interpretations. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

(1) Line 68: What are "APP23xPS45" mice? This is most likely a typo.

This line is a previously reported double transgenic amyloid beta mouse model that was obtained by crossing APP23 (overexpressing human amyloid precursor protein with the Swedish double mutation at position 670/671) with PS45 (carrying a transgene for mutant Presenilin 1, G384A mutation) (Busche et al., 2008; Grienberger et al., 2012). 

(2) Line 148: The authors should also briefly describe in the main text that APP/PS1 x SST-Cre mice were generated and used here.  

We thank the reviewer for their comment and have added their suggestion to the main text (line 166-168):

‘To do this, APP/PS1 mice were crossed with SST-Cre mice to generate APP/PS1 SST-Cre mice. Following microinjection of AAV-hSyn::DIO-mCherry into the mPFC, recordings were obtained from SST neurons.’

(3) The discussion should be condensed because of redundancies on several occasions. For example, memory allocation is discussed starting on line 371, then again on line 392. This should be combined. Likewise, how the correlative nature of the findings about PV interneurons could be further functionally addressed is discussed on lines 413 and 454, and should be condensed into one paragraph. 

We thank the reviewer for this suggestion and have revised the discussion to remove the redundancies as proposed.  

Reviewer #2 (Recommendations for the authors): 

To strengthen the manuscript, the following points should be addressed: 

(1) Quantify amyloid pathology: It is essential to assess amyloid-β levels (soluble and insoluble) in the mPFC of APP/PS1-PV-Cre-tdTomato mice at the studied ages. This would help determine whether the observed circuitlevel changes track with disease progression as seen in canonical APP/PS1 models. 

We thank the reviewer for this valuable suggestion and agree that assessing Aβ levels in the mPFC is important to determine whether the observed circuit level alterations in APP/PS1 mice coincide with the progression of amyloid pathology. Therefore, we assessed the amyloid plaque load in the mPFC of APP/PS1 mice at 16 and 20 weeks of age (new supplemental figure sFig. 1) and observed no difference in plaque load between these two time points. This suggests that the increased excitability in the mPFC cannot be attributed to differences in plaque load (insoluble amyloid beta).

In line with this, we previously studied both soluble and insoluble Aβ levels in the CA1 and reported that there are no differences between 12 and 16 weeks of age (Kater et al., 2023), while PV cell hyperexcitability is present at 16 weeks of age (Hijazi et al., 2020a). From 24 weeks onwards, the level of amyloid beta increases. Similarly, Végh et al. (2014) showed using immunoblotting that monomeric and low molecular weight oligomeric forms of soluble Aβ are already present as early as 6 weeks of age and become more prominent at 24 weeks of age. Although the soluble Aβ measurements were performed in the hippocampus, we think these findings can be extrapolated to cortical regions, as the APP and PS1 mutations in APP/PS1 mice are driven by a prion promotor, which should induce consistent expression across brain regions. Data from other research groups support this hypothesis (Kim et al., 2015; Zhang et al., 2011). Thus, large regional differences in soluble Aβ are not expected. The temporal progression suggests that increasing levels of soluble amyloid beta might contribute to the emergence of PV cell hyperexcitability. We have added this point to the manuscript (line 585-591):

‘Since amyloid beta plaque load in the mPFC remains comparable between 16- and 20-week-old APP/PS1 mice, the observed increased excitability is unlikely the result of changes in insoluble amyloid beta levels. Previous data from our lab show that soluble amyloid beta is already present as early as 6 weeks of age and becomes more prominent at 24 weeks of age (Kater et al., 2023; Végh et al., 2014). The progressive increase in soluble amyloid beta levels may contribute to the emergence of PV cell hyperexcitability.’

Finally, we previously compared soluble and insoluble amyloid beta levels in APP/PS1 and APP/PS1 Parv Cre mice and show that these are similar (Hijazi et al., 2020a). While our current study shows the progression of amyloid beta accumulation in APP/PS1 mice, these mice also exhibit altered microcircuitry (enhanced sIPSC frequency on engram cells) at 20 weeks of age, the same age at which we observed PV cell hyperexcitability in APP/PS1 Parv Cre tdTomato mice. This further supports the generalizability of our findings across genotypes, between APP/PS1 and APP/PS1 Parv Cre tdTomato mice. 

(2) Examine later disease stages: Since the current effects are modest, assessing memory performance, PV cell excitability, and engram inhibition at more advanced stages could clarify whether these alterations become more pronounced with disease progression. 

We thank the reviewer for this thoughtful suggestion. Investigating advanced disease stages could indeed provide valuable insights into whether the observed alterations in memory performance, PV cell hyperexcitability and engram inhibition become more pronounced over time. Our previous work has shown that changes in pyramidal cell excitability emerge at a later stage than in PV cells, supporting the idea of progressive circuit dysfunction (Hijazi et al., 2020a). However, at these more advanced stages, additional pathological processes, such as an increased gliosis (Janota, Brites, Lemere, & Brito, 2015; Kater et al., 2023) and synaptic loss (Alonso-Nanclares, MerinoSerrais, Gonzalez, & DeFelipe, 2013; Bittner et al., 2012), will likely contribute to both electrophysiological and behavioural measurements. Furthermore, we would like to point out that the current changes observed in memory performance, PV hyperexcitability and increased inhibitory input on engram cells at 16-20 weeks of age are not modest, but already quite substantial. Our focus on these early time points in APP/PS1 mice were intentional, as it helps us understand the initial changes in Alzheimer’s disease at a circuit level and to identify therapeutic targets early intervention. What happens at later stages is certainly of interest, but beyond the scope of this study and should therefore be addressed in future studies. We have incorporated a discussion related to this point into the revised manuscript (line 602-606):

‘Moreover, it is relevant to investigate whether changes in PV and PYR cell excitability, as well as input onto engram cells in the mPFC, become more pronounced at later disease stages. Nonetheless, by focussing on early disease timepoints in the present study, we aimed to understand the initial circuit-level changes in AD and identify targets for early therapeutic intervention.’

(3) Address network hyperexcitability: Spontaneous epileptiform activity has been reported in APP/PS1 mice from 4 months of age (Reyes-Marin & Nuñez, 2017). Including EEG data or discussing this point in relation to your findings would help contextualize the observed inhibitory remodeling within broader network dysfunction. 

We thank the reviewer for this valuable input and for highlighting the study by Reyes-Marin and Nuñez (2017). In line with this, we recently reported longitudinal local field potential (LFP) recordings in freely behaving APP/PS1 Parv-Cre mice and wild type control animals between the ages of 3 to 12 months (van Heusden et al., 2023). Weekly recordings were performed in the home cage under awake mobile conditions. These data showed no indications of epileptiform activity during wakefulness, consistent with previous findings that epileptic discharges in APP/PS1 mice predominantly occur during sleep (Gureviciene et al., 2019). Recordings were obtained from the prefrontal cortex (PFC), parietal cortex and the hippocampus. In contrast, the study by Reyes-Marin and Nuñez (2017) recorded from the somatosensory cortex in anesthetized animals. Here, during spontaneous recordings, no differences were observed in delta, theta or alpha frequency bands between APP/PS1 and WT mice. Interestingly, we observed an early increase in absolute power, particularly in the hippocampus and parietal cortex from 12 to 24 weeks of age in APP/PS1 mice. In the PFC we found a shift in relative power from lower to higher frequencies and a reduction in theta power. Connectivity analyses revealed a progressive, age-dependent decline in theta/alpha coherence between the PFC and both the parietal cortex and hippocampus. Given the well-established role of PV interneurons network synchrony and coordinating theta and gamma oscillations critical for cognitive function (Sohal, Zhang, Yizhar, & Deisseroth, 2009; Xia et al., 2017), these findings support the idea of early circuit dysfunction in APP/PS1 mice. Our findings, i.e. hyperexcitability of PV cells, align with these LFP based networklevel observations. These data suggest an early shift in the E/I balance, contributing to altered oscillatory dynamics and impaired inter-regional connectivity, possibly leading to alterations in memory. However, whether the observed PV hyperexcitability in our study directly contributes to alterations in power and synchrony remains to be elucidated. Furthermore, it would be interesting to determine the individual contribution of PV cell hyperexcitability in the hippocampus versus the mPFC to network changes and concurrent memory deficits. We have added a statement on network hyperexcitability to the discussion (line 561-565). 

‘Interestingly, we recently found a progressive disruption of oscillatory network synchrony between the mPFC and hippocampus in APP/PS1 Parv-Cre mice (van Heusden et al., 2023). However, whether the observed PV cell hyperexcitability directly contributes to changes in inter-regional synchrony, and whether this leads to alterations at a network level, i.e. increased inhibitory input on engram cells, and consequently to memory deficits, remains to be elucidated in future studies.’ 

(4) Mechanisms responsible for PV hyperexcitability: Related to the previous point, a discussion of the possible underlying mechanisms, e.g., direct effects of amyloid-β, inflammatory processes, or compensatory mechanisms, would strengthen the discussion. 

We agree with the reviewer that this will strengthen the discussion. We have now added a comprehensive discussion in the revised manuscript to address potential mechanisms responsible for PV cell hyperexcitability (line 579-594).:

‘Prior studies have shown that neurons in the vicinity of amyloid beta plaques show increased excitability (Busche et al., 2008). We demonstrated that PV neurons in the CA1 are hyperexcitable and that treatment with a BACE1 inhibitors, i.e. reducing amyloid beta levels, rescues PV excitability (Hijazi et al., 2020a). In line with this, we also reported that addition of amyloid beta to hippocampal slices increases PV excitability, without altering pyramidal cell excitability (Hijazi et al., 2020a). Finally, applying amyloid beta to an induced mouse model of PV hyperexcitability further impairs PV function (Hijazi et al., 2020b). Since amyloid beta plaque load in the mPFC remains comparable between 16- and 20-week-old APP/PS1 mice, the observed increased excitability is unlikely the result of changes in insoluble amyloid beta levels. Previous data from our lab show that soluble amyloid beta is already present as early as 6 weeks of age and becomes more prominent at 24 weeks of age (Kater et al., 2023; Végh et al., 2014). The progressive increase in soluble amyloid beta levels may contribute to the emergence of PV cell hyperexcitability. We hypothesize that the hyperexcitability induced by amyloid beta may result from disrupted ion channel function, as PV neuron dysfunction can result from altered potassium (Olah et al., 2022) and sodium channel activity (Verret et al., 2012).’

(5) Excitatory-inhibitory balance: While the main focus is on increased inhibition onto engram cells, the reported increase in sEPSC frequency (Figure 5g) across genotypes suggests the presence of excitatory remodelling as well. A brief discussion of how this may interact with increased inhibition would be valuable.  

We thank the reviewer for this comment regarding the interaction between excitatory and inhibitory remodelling. We have now incorporated this discussion point into the revised manuscript (line 528-534):

‘Interestingly, both WT and APP/PS1 mice showed an increase in sEPSC frequency onto engram cells, suggesting that increased excitatory input is a consequence of memory retrieval and not affected by genotype. However, only in APP/PS1 mice, the augmented excitatory input coincided with an elevation of inhibitory input onto engram cells. The resulting imbalance between excitation and inhibition could therefore potentially disrupt the precise control of engram reactivation and contribute to the observed remote memory impairment.’

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Author response:

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

Reviewer #1 (Public review):

In this manuscript, Chang et al. investigated the cell type-specific role of the integrin activator Shv in activity-dependent synaptic remodeling. Using the Drosophila larval neuromuscular junction as a model, they show that glial-secreted Shv modulates synaptic plasticity by maintaining the extracellular balance of neuronal Shv proteins and regulating ambient extracellular glutamate concentrations, which in turn affects postsynaptic glutamate receptor abundance. Furthermore, they report that genetic perturbation of glial morphogenesis phenocopies the defects observed with the loss of glial Shv. Altogether, their findings propose a role for glia in activity-induced synaptic remodeling through Shv secretion. While the conclusions are intriguing, several issues related to experimental design and data interpretation merit further discussion.

We appreciate the insightful and constructive comments. We have added new data and modified the text to address your concerns.  In doing so, the manuscript has been substantially strengthened.  Please see our detailed point-by-point response below. 

Reviewer #2 (Public review):

In this paper Chang et al follow up on their lab's previous findings about the secreted protein Shv and its role in activity-induced synaptic remodeling at the fly NMJ. Previously they reported that shv mutants have impaired synaptic plasticity. Normally a high stimulation paradigm should increase bouton size and GluR expression at synapses but this does not happen in shv mutants. The phenotypes relating to activity dependent plasticity were completely recapitulated when Shv was knocked down only in neurons and could be completely rescued by incubation in exogenously applied Shv protein. The authors also showed that Shv activation of integrin signaling on both the pre- and post- synapse was the molecular mechanism underlying its function. Here they extend their study to consider the role of Shv derived from glia in modulating synaptic features at baseline and remodeling conditions. This study is important to understand if and how glia contribute to these processes. Using cell-type specific knockdown of Shv only in glia causes abnormally high baseline GluR expression and prevents activity-dependent increases in bouton size or GluR expression post-stimulation. This does not appear to be a developmental defect as the authors show that knocking down Shv in glia after basic development has the same effects as lifelong knockdown, so Shv is acting in real time. Restoring Shv in ONLY glia in mutant animals is sufficient to completely rescue the plasticity phenotypes and baseline GluR expression, but glial-Shv does not appear to activate integrin signaling which was shown to be the mechanism for neuronally derived Shv to control plasticity. This led the authors to hypothesize that glial Shv works by controlling the levels of neuronal Shv and extracellular glutamate. They provide evidence that in the absence of glial Shv, synaptic levels of Shv go up overall, presumably indicating that neurons secrete more Shv. In this context which could then work via integrin signaling as described to control plasticity. They use a glutamate sensor and observe decreased signal (extracellular glutamate) from the sensor in glial Shv KD animals, however, this background has extremely high GluR levels at the synapse which may account for some or all of the decreases in sensor signal in this background. Additional controls to test if increased GluR density alone affects sensor readouts and/or independently modulating GluR levels in the glial KD background would help strengthen this data. In fact, glialspecific shv KD animals have baseline levels of GluR that are potentially high enough to have hit a ceiling of expression or detection that accounts for the inability for these levels to modulate any higher after strong stimulation and such a ceiling effect should be considered when interpreting the data and conclusions of this paper. Several outstanding questions remain-why can't glial derived Shv activate integrin pathways but exogenously applied recombinant Shv protein can? The effects of neuronal specific rescue of shv in a shv mutant are not provided vis-à-vis GluR levels and bouton size to compare to the glial only rescue. Inclusion of this data might provide more insight to outstanding questions of how and why the source of Shv seems to matter for some aspects of the phenotypes but not others despite the fact that exogenous Shv can rescue and in some experimental paradigms but not others.

We appreciate your insightful comments. We have added new data and modified the text to address your concerns.  In doing so, the manuscript has been substantially strengthened.  Please also see the enclosed point-by-point response.

To address the question of whether altered GluR density alone affects sensor readouts, we expressed GluR using a mhc promoter-driven GluRIIA fusion line, which increases total GluRIIA expression in muscle independently of the Gal4/UAS system. As shown in Figure 6 – figure supplement 1, mhc-GluRIIA animals exhibited elevated levels of not only GluRIIA but also the obligatory GluRIIC subunit. Despite this increase in GluR expression, we did not observe any change in extracellular glutamate levels, as measured by live imaging using the neuronal iGluSnFR sensor (updated Figure 6A). These results suggest that elevated GluR density alone does not alter iGluSnFR sensors dynamics and further support our conclusions.

In regard to the question about ceiling effect, we do not think that the lack of GluR enhancement in repo>shv-RNAi is due to a saturated postsynaptic state. This is based on results in Figure 6, which shows that GluR levels can increase up to fourfold upon stimulation in the presence of glutamate, whereas repo>shv-RNAi results in only a ~2-fold increase in baseline GluR concentration. These results suggest that the synapse retains the capacity for further upregulation. 

To address the question of why exogenously applied Shv activates integrin while glial derived Shv does not, we tested whether glia and neurons could differentially modify Shv. Based on Western blot analyses of adult heads and larval brains showing that Shv is present as a single band (Fig. 1A and Figure 2 – figure supplement 1B), the functional differences in neuronal or glial Shv is not likely due to the presence of different isoforms. Consistent with this, FlyBase also suggests that shv encodes a single isoform. However, while we did not detect obvious posttranslational modifications when Shv protein was expressed in neurons or glia (Figure 5 – figure supplement 1A), we cannot exclude the possibility that different cell types process Shv differently through post-transcriptional or post-translational mechanisms. Notably, shv is predicted to undergo A-to-I RNA editing, including an editing site in the coding region, which will result in a single amino acid change (St Laurent et al., 2013). Given that ADAR, the editing enzyme, is enriched in neurons and absent from glia (Jepson et al., 2011), such cell-specific editing could contribute to functional differences. It will be interesting to investigate this in the future. We have now included this in the Discussion section.

Additionally, we have now included new data on neuronal Shv rescue of shv¹ mutants as suggested in the updated Figure 4. Consistent with previous findings that neuronal Shv rescues integrin signaling and electrophysiological phenotypes (Lee et al., 2017), we found that it also restores bouton size, GluR levels, and activity-induced synaptic remodeling. These results support the functional contribution of neuronal Shv. 

Reviewer #3 (Public review):

Summary:

The manuscript by Chang and colleagues provides compelling evidence that glia-derived Shriveled (Shv) modulates activity-dependent synaptic plasticity at the Drosophila neuromuscular junction (NMJ). This mechanism differs from the previously reported function of neuronally released Shv, which activates integrin signaling. They further show that this requirement of Shv is acute and that glial Shv supports synaptic plasticity by modulating neuronal Shv release and the ambient glutamate levels. However, there are a number of conceptual and technical issues that need to be addressed.

We appreciate the insightful and constructive comments. We have added new data and modified the text to address your concerns.  In doing so, the manuscript has been substantially strengthened.  Please see our detailed point-by-point response below.

Major comments:

(1) From the images provided for Fig 2B +RU486, the bouton size appears to be bigger in shv RNAi + stimulation, especially judging from the outline of GluR clusters.

Thank you for pointing this out. We have selected another image to better represent the data.

(2) The shv result needs to be replicated with a separate RNAi.

We have used another independent RNAi line targeting shv to confirm our findings (BDSC 37507). This shv-RNAi³⁷⁵⁰⁷ line also showed the same phenotype, including increased GluR levels and impaired activity-induced synaptic remodeling line (new Figure 2 – figure supplement 1A).

(3) The phenotype of shv mutant resembles that of neuronal shv RNAi - no increased GluR baseline. Any insights why that is the case?

This is an interesting question. We speculate that neuronal Shv normally has a dominant role in maintaining GluR levels during development, mainly through its ability to activate integrin signaling. Consistent with this, we have shown that mutations in integrin leads to a drastic reduction in GluR levels at the NMJ (Lee et al., 2017). While we have shown that neuronal knockdown of shv elevates Shv from glia (Fig. 5E), glial Shv cannot activate integrin signaling (Fig. 5B, 5C). Additionally, high levels of glial Shv will elevate ambient glutamate concentrations (Figure 6A), which will likely reduce GluR abundance and impair synaptic remodeling (Augustin et al.  2007, Chen et al., 2009, and Figure 6B). Therefore, neuronal knockdown of Shv resulted in the same phenotype as shv¹ mutant. 

(4) In Fig 3B, SPG shv RNAi has elevated GluR baseline, while PG shv RNAi has a lower baseline. In both cases, there is no activity induced GluR increase. What could explain the different phenotypes?

SPG is the middle glial cell layer in the fly peripheral nervous system and may also influence the PG layer through signaling mechanisms (Lavery et al., 2007), therefore having a stronger effect. We have now mentioned this in the text. 

(5) In Fig 4C, the rescue of PTP is only partial. Does that suggest neuronal shv is also needed to fully rescue the deficit of PTP in shv mutants?

This is indeed a possibility. We have shown that neuronal and glial Shv each contribute to activity-induced synaptic remodeling through different mechanisms. It will be interesting test this in the future.

(6) The observation in Fig 5D is interesting. While there is a reduction in Shv release from glia after stimulation, it is unclear what the mechanism could be. Is there a change in glial shv transcription, translation or the releasing machinery? It will be helpful to look at the full shv pool vs the released ones. 

Thank you for the suggestion. To address this, we monitored the levels of intracellular Shv using a permeabilized preparation (we found that the addition of detergent to permeabilize the sample strips away extracellular Shv). Combined with the extracellular staining results, we can get an idea about the total amount of Shv. As shown in the updated Figure 5D, intracellular Shv levels (permeabilized) remained unchanged following stimulation, indicating that there is no intracellular accumulation and that the observed decrease in extracellular Shv is unlikely due to impaired release machinery.

(7) In Fig 5E, what will happen after stimulation? Will the elevated glial Shv after neuronal shv RNAi be retained in the glia? 

Thank you for the interesting question. We agree that examining Shv distribution following neuronal activity would be highly informative. While we plan to perform time-lapse experiments in future studies to address this, we feel that such analyses are beyond the scope of the current manuscript.

(8) It would be interesting to see if the localization of shv differs based on if it is released by neuron or glia, which might be able to explain the difference in GluR baseline. For example, by using glia-Gal4>UAS-shv-HA and neuronal-QF>QUAS-shv-FLAG. It seems important to determine if they mix together after release? It is unclear if the two shv pools are processed differently.

We agree that investigating whether neuronal and glial shv pools colocalize or are differentially processed is an important future direction. We hope to examine how each pool responds to stimulation in the shv¹ mutant background using LexA and Gal4 systems in the future

(9) Alternatively, do neurons and glia express and release different Shv isoforms, which would bind different receptors?

Thank you for the questions. We have now addressed this in the discussion and also enclosed below:

Based on Western blot analyses of adult heads and larval brains showing that Shv is present as a single band (Fig. 1A and Figure 2 – figure supplement 1B), the functional differences in neuronal or glial Shv is not likely due to the presence of different isoforms. Consistent with this, FlyBase also suggests that shv encodes a single isoform (Ozturk-Colak et al., 2024). However, while we did not detect obvious post-translational modifications when Shv protein was expressed in neurons or glia (Figure 5 – figure supplement 1A), we cannot exclude the possibility that different cell types process Shv differently through posttranscriptional or post-translational mechanisms. Notably, shv is predicted to undergo A-to-I RNA editing, including an editing site in the coding region, which could result in a single amino acid change (St Laurent et al., 2013). Given that ADAR, the editing enzyme, is enriched in neurons and absent from glia (Jepson et al., 2011), such cell-specific editing could contribute to functional differences. It will be interesting to investigate this in the future.

(10) It is claimed that Sup Fig 2 shows no observable change in gross glial morphology, further bolstering support that glial Shv does not activate integrin. This seems quite an overinterpretation. There is only one image for each condition without quantification. It is hard to judge if glia, which is labeled by GFP (presumably by UAS-eGFP?), is altered or not.

Thank you for raising this concern. To strengthen our claim, we now include additional images (Figure 5, figure supplement 2). No obvious change in overall glial morphology was observed, with glia continuing to wrap the segmental nerves and extend processes that closely associate with proximal synaptic boutons (Figure 5, figure supplement 2). These observations suggest that glial  Shv is not essential for maintaining normal glial structure or survival, and is consistent with the idea that glial Shv does not activate integrin, as integrin signaling is required to maintain the integrity of peripheral glial layers. 

(11) The hypothesis that glutamate regulates GluR level as a homeostatic mechanism makes sense. What is the explanation of the increased bouton size in the control after glutamate application in Fig 6?

We speculate that it could be due to a retrograde signaling mechanism activated by elevated extracellular glutamate, allowing neurons to modulate bouton morphology in response to synaptic demand. It will be interesting to investigate this possibility in the future.  

(12) What could be a mechanism that prevents elevated glial released Shv to activate integrin signaling after neuronal shv RNAi, as seen in Fig 5E?

One potential mechanism is post-translational or post-transcriptional processing of Shv. Although our Western blots did not reveal differences in the molecular weight of glial vs. neuronal Shv, we cannot exclude the possibility that modifications not readily detectable by this method are responsible. Additionally, as mentioned in the Discussion section, post-transcriptional processing such as A-to-I RNA editing could introduce changes in the Shv protein, potentially altering its ability to interact with or activate integrin. 

(13) Any speculation on how the released Shv pool is sensed?

The same RNA editing modification mentioned earlier or post-translational modifications in Shv may also influence how it is sensed by target cells. 

Reviewer #1 (Recommendations for the authors):

Issues Regarding Cell Type-Specific Secretion and the Role of Shv:

Extracellular Secretion of Shv:

(1) The data in Figure 1 suggest that Shv is not secreted under resting conditions, challenging the proposed extracellular role of Shv. It remains unclear whether Shv secretion can be confirmed using Shv-eGFP (knock-in) following high K+ stimulation.

We apologize for not being clear. In Figure 1, Shv signals we’ve shown are from permeabilized preparation, which preferentially labels intracellular Shv. We do observe secreted Shv-eGFP following stimulation (Figure 5E), consistent with our hypothesis. However, endogenous extracellular Shv-eGFP signal is very weak, and was therefore detected using the GFP antibody and amplified with a  fluorescent secondary antibody. We have now also included additional controls in Figure 5E to demonstrate the specificity of the staining.

(2) In Figure 5D, total Shv staining should be included to evaluate potential presynaptic accumulation of intracellular Shv, which may lead to extracellular secretion upon stimulation. Additionally, the representative images of glial rescue do not seem to align with the quantification data; more extracellular Shv signals were observed after stimulation.

Thank you for the comments. We monitored the levels of intracellular Shv using a permeabilized preparation (detergent treatment stripped away extracellular Shv signal). When combined with non-permeabilized extracellular staining, this approach provides insights into total Shv levels. We found no intracellular accumulation of Shv and the intracellular levels remained unchanged following stimulation (updated Figure 5D), suggesting that reduced extracellular Shv is not likely due to impaired release. Additionally, we have selected another image for glial rescue by avoiding the trachea region, which better represent the quantification data.

(3) In Figure 5E, "extracellular" Shv staining in repo>shv-RNAi samples appears localized within synaptic boutons. This raises concerns about the staining protocol potentially labeling intracellular proteins. Control experiments using presynaptic cytosolic markers are needed to confirm staining specificity.

Thank you for the thoughtful suggestion. To validate that our staining protocol is selective for extracellular proteins, we also stained for cysteine string protein (CSP), an intracellular synaptic vesicle protein predominantly located in the presynaptic terminals (Zinsmaier et al., 1990; Umbach et al., 1994), under the same conditions. CSP was detected only in the permeabilized condition (updated Figure 5E), suggesting that the non-permeabilizing protocol is selective for extracellular proteins. 

(4) The study does not clarify why Shv knockdown in either perineurial glia or subperineurial glia abolishes stimulus-dependent synaptic remodeling. Does Shv secretion occur from PG, SPG, or both toward the synaptic bouton?

Thank you for raising this point. SPG is the middle glial cell layer in the fly peripheral nervous system and may also influence the PG layer through signaling mechanisms (Lavery et al., 2007). Consistent with this, we observed a stronger effect on GluR levels when SPG was disrupted compared to PG. It will be interesting to distinguish whether Shv is released by PG or SPG in the future.

(5) The possibility of an inter-glial role for Shv via integrin signaling in regulating glial morphogenesis is underexplored. The rough morphological characterization in Supplemental Figure 2 requires more detailed quantification and the use of sub-glial typespecific GAL4 drivers.

We now include additional images (Figure 5, figure supplement 2) to examine the overall glial morphology. There was no obvious change in gross glial morphology, with glia continuing to wrap the segmental nerves and extend processes that closely associate with proximal synaptic boutons when shv is knocked down in glia (Figure 5, figure supplement 2). These observations suggest that glial  Shv is not essential for maintaining normal glial structure or survival, and is consistent with the idea that glial Shv does not activate integrin, as integrin signaling is required to maintain the integrity of peripheral glial layers (Xie and Auld, 2011; Hunter et al., 2020).

(6) While repo>shv rescues stimulus-dependent bouton size and GluR increases in the shv mutant (Figure 5), the interaction between neuronal and glial Shv remains unclear. Does neuronal Shv influence the expression or distribution of glial Shv?

We agree that investigating whether neuronal and glial shv pools influence each other’s expression or distribution is an important future direction. We hope to investigate this in more detail in the future using LexA-LexOp and GAL4/UAS dual expression systems.

Issues Regarding the Regulation of GluR and Perisynaptic Glutamate by Glial Shv:

(7) The methodology for iGluSnFR measurement (Figure 6A) is inadequately described. If anti-HRP staining was used to normalize signals, it suggests the experiment may have involved fixed tissue. However, iGluSnFR typically measures glutamate levels in live cells, raising concerns about the validity of this approach in fixed samples.

We apologize for not being clear about the method used to measure iGluSnFR. The original figure was generated from imaging iGluSnFR signals immediately following fixation. To address the reviewer’s concern and validate these results, we have now performed live imaging experiments using a water dipping objective to measure iGluSnFR intensity in unfixed preparations (new Figure 6A). To label synaptic boutons, we co-expressed mtdTomato using the neuronal driver, nSybGAL4. The results from the live imaging experiments confirmed our original observations that glial Shv required to control ambient extracellular glutamate levels (see updated Fig. 6A and text). Additionally, to ascertain that the decrease in iGluSnFR signal reflects a decrease in ambient extracellular glutamate levels rather than glutamate depletion caused by high levels of GluR, we upregulated GluR levels using mhc-GluRIIA, which drives GluRIIA expression in muscles (Petersen et al., 1997). We found mhc-GluRIIA animals exhibited elevated levels of not only GluRIIA but also the obligatory GluRIIC subunit. However, iGluSnFR signals at the synapse remained unchanged (Figure 6A), suggesting that elevated GluR density alone does not reduce signals. Taken together, these results suggest that glial Shv plays a critical role in controlling ambient extracellular glutamate levels. 

(8) As shown in Figure 2, repo>shv-RNAi increases GluR levels before high K+ stimulation, potentially saturating postsynaptic GluR expression and precluding further increases upon stimulation.

Our data in Figure 6 show that GluR levels can increase up to four-fold upon stimulation in the presence of glutamate, whereas repo>shv-RNAi results in only a ~2-fold increase in baseline GluR concentration. These results suggest that the synapse retains the capacity for further upregulation. Thus, we do not think that the lack of GluR enhancement in repo>shv-RNAi is due to a saturated postsynaptic state, but rather reflects a requirement for glial Shv in activity-dependent modulation.

(9) Despite glial shv knockdown lowering extracellular glutamate levels, GluR levels unexpectedly increase (Figure 6B). This contradicts the known requirement for high ambient glutamate concentrations to promote GluR clustering and membrane expression (Chen et al., 2009). Furthermore, adding 2 mM glutamate reverses these increases, suggesting additional complexity in the regulation of Shv synaptic remodeling.

Thank you for the comment and the opportunity to clarify this point. While it may seem counterintuitive at first glance, our observations are in line with previous reports that showed low ambient glutamate levels significantly elevated GluR intensity at the Drosophila NMJ (Chen et al., 2009), but such increase can be reversed by glutamate supplementation (Augustin et al., 2007; Chen et al., 2009). We have revised the text to more clearly reflect this connection.

(10) If glial Shv promotes GluR expression, why does the increased extracellular Shv from neuronal shv knockdown (elav>shv-RNAi, Figure 5E) fail to elicit stimulus-dependent GluR elevation?

We speculate that this is because glial Shv does not activate integrin signaling (Figure 5B, C), and elevated glial Shv increases ambient glutamate concentration (Figure 6A), thereby reducing GluR expression (Augustin et al., 2007; Chen et al., 2009). This is indeed what we observed when shv is knocked down in neurons. 

Additional Issues:

(11) The type of bouton used for quantification (e.g., Ib or Is boutons) is not specified, which is critical for interpreting the results.

We apologize for not being clear. We analyzed type Ib boutons as done previously (Lee et al., 2017 and Chang et al., 2024), and have now included this information in the Methods section.  

(12) The extent of Shv protein depletion in the repo-GeneSwitch system needs validation to confirm the efficacy of the knockdown.

Thank you for the suggestion. We confirmed the efficiency of acute shv knockdown by the repo-GeneSwitch system by performing Western blot analysis of dissected larval brains (Figure 2 – figure supplement 1B). Acute glial knockdown using the repo-GeneSwitch driver resulted in a 30% reduction in Shv levels, similar to the decrease observed with the repo-GAL4 driver, suggesting that the GeneSwitch driver is functional. Furthermore, knockdown of shv by the ubiquitous tubulin-GAL4 driver completely eliminated Shv protein, indicating that the RNAi construct is effective.  

Reviewer #2 (Recommendations for the authors):

(1) General comment on statistics/data presentation: The authors employ an unusual method of using both one-way ANOVA and multiple t-test stats for the same data. Would a 2-way ANOVA be the more appropriate solution to this problem (to analyze across genotype and stimulation condition)? Also a chart in the supplementals showing all comparisons rather than just the fraction explicitly reported in the graphs would be helpful (it is not clear if no indication on significance indicates no difference or just not reported between some of the baseline levels, especially since everything is presented as ratios and in some cases this could help with data interpretation of which baseline levels are different and how they compare to other baselines and other post-stim levels). Further, there are no sample sizes given for any experiment, nor are any values of means, SD, etc ever explicitly given.

We appreciate the thoughtful suggestion. While a two-way ANOVA could be used to examine interaction effects between genotype and stimulation condition, our analysis was designed to address a specific biological question: whether each genotype, independent of baseline levels, is capable of undergoing activitydependent synaptic remodeling. To this end, we used t-tests to directly compare unstimulated vs. stimulated conditions within each genotype, allowing us to determine whether stimulation produces a significant effect in an all-or-none manner. In parallel, we applied one-way ANOVA with post hoc tests to analyze differences among baseline (unstimulated) conditions across genotypes. This approach is justified by the fact that stimulation was applied acutely and separately, and therefore the baseline values should not be influenced by the stimulated condition. Because we were not aiming to compare the extent of synaptic remodeling between genotypes, we did not use a two-way ANOVA to analyze interaction effects across all conditions.

In response to the reviewer’s suggestion, we have now added the sample number in the graphs. Additionally, in the Methods section, we include information that each sample represents biological repeats, and that data are presented as fold-change relative to unstimulated controls from the same experimental batch. This normalization is necessary, as absolute GluR intensities can vary depending on microscope settings and staining conditions.

(2) To clarify distinct roles of Shv coming from neurons vs glia it would help if the authors could include more data on the rescue of shv mutants with UAS-Shv in neurons alone. This data is never shown in the manuscript and data on what effect this rescue has on the pertinent phenotypes in this paper (bouton size and GluR staining) is not reported in the referred to 2017 paper. What this does and does not do for these phenotypes has important implications for how to interpret the glia-only rescue findings.

Thank you for the suggestion. We have now included new data on neuronal Shv rescue in shv¹ mutants as suggested (updated Figure 4A). Consistent with previous findings that neuronal Shv rescues integrin signaling and electrophysiological phenotypes (Lee et al., 2017), we found that it also restores bouton size, GluR levels, and activity-induced synaptic remodeling. These results support the functional contribution of neuronal Shv. 

(3) Figure 1C: Where are the images in the periphery taken? The morphology of the glia is odd in that "blobs" of glial membrane seemingly unattached to anything else are floating about? Perhaps these are a thin stack projection and so the connection to the main glia "stalks" are just cut off? Could a specific individual synapse be shown? Also consider HRP shown on its own so that where the actual boutons are could be more clear. It seems like both the Tomato and HRP channels are really overexposed making visualizing the morphology quite confusing. Also why not use the antibody against Shv to directly visualize expression which is more direct than a knock-in tagged version?

Figure 1C shows a single optical slice of the NMJ at muscle segment 2, selected to clearly highlight Shv-eGFP localization at a branch in close contact with the glial membrane. The glial stalk is not visible in this image because it lies in a different focal plane from the branch of interest. We have now specified this information in the figure legend. In the original figure, the HRP signal (405 channel) was oversaturated, which interfered with visual clarity. In the updated Figure 1C, we reduced the intensity of overexposed channels to better reveal the weak ShveGFP signal and fine glial processes. While we have generated an antibody against Shv, the amount is extremely limited, and hence the Shv-eGFP fusion serves as a valuable tool for visualizing subcellular localization.

(4) Do glutamate levels really rise in glia Shv KD? Although iGluSnFR signal changes could it be the high level of GluR at the synapse acting as sponges to sequester glutamate so that it can't stimulate the sensor as well? One way to test this would be to overexpress or KD GluRs in muscle in wildtype (or in the repo>Shv RNAi background) to see if that alone can modulate iGluSnfR signals?

Thank you for suggesting this important control. To address the question of whether high level GluR density alone could influence neuronal iGluSnFR sensor readouts, we expressed GluR using a mhc promoter-driven GluRIIA fusion line, which increases total GluRIIA expression in muscle independently of the Gal4/UAS system. As shown in Figure 6 – figure supplement 1, mhc-GluRIIA animals exhibited elevated levels of not only GluRIIA but also the obligatory GluRIIC subunit. Despite this increase in GluR expression, we did not observe any change in extracellular glutamate levels, as measured by live imaging using the neuronal iGluSnFR sensor (updated Figure 6A). These results suggest that elevated GluR density alone does not alter iGluSnFR sensors  dynamics and further support our conclusions.

(5) The authors have some Shv constructs that can't be secreted or can't bind to integrins. Performing cell type specific rescues with these constructs might also help distinguish how source matters for each proposed sub-function of Shv though this may be outside the scope of this study. 

Thank you for noticing the Shv constructs we have. We hope to further test subfunctions of Shv in the future.

(6) At one point the authors discuss experiments that measure how much Shv is released by glia during neuronal stimulation. Then state that "These data indicate that glial Shv does not directly inhibit integrin signaling." But how this experiment relates to integrin signaling is not explained and unclear.

We apologize for the confusion. We have now updated the text to better explain our logic: “This activity-induced decrease in glial Shv levels, along with reduced integrin activation (Fig. 5B), suggest that glial Shv does not act by directly inhibiting integrin signaling.”

Reviewer #3 (Recommendations for the authors):

Minor comments

(1) Readers are left wondering what causes the increased baseline of GluR after glial shv RNAi at Fig 1, which is addressed much later. It would be helpful to preemptively mention this.

Thank you for the suggestion. To maintain a logical flow, we chose to first present the phenotypic data in Figures 1 and 2 and then return to the mechanistic explanation once we introduced ambient glutamate measurements. 

(2) Be consistent with eGFP vs EGFP.

Thank you, we have corrected the inconsistencies.  

(3) Scale bar for Fig 1B is missing in the low-magnification panel.

Thank you for pointing out. We’ve put in the scale bar for Figure 1B.   

(4) Fig 1C, it would be helpful to elaborate on the anatomy. For example, what NMJ/abdominal segment is this? Why only some axons are surrounded by glia?

Figure 1C presents a single optical slice of the NMJ at muscle segment 2, chosen to highlight Shv-eGFP localization at a branch closely juxtaposed to the glial membrane. The glial stalk is not shown in this image because it resides in a different focal plane than the branch being visualized. We have now included this information in the figure legend.

(5) For Fig 3B, while it is stated that "we observed normal synaptic remodeling using alrmGAL4," the effect size is smaller. There seems to be a decrease in the amount of synaptic remodeling occurring?

Thank you for pointing this out. Our primary goal was to determine whether each genotype, regardless of baseline GluR levels, is capable of undergoing activitydependent synaptic remodeling in response to stimulation. For this reason, we focused on detecting the presence or absence of remodeling rather than comparing the extent of remodeling across genotypes. While a smaller effect on activity-induced bouton size was observed with alrm-GAL4, the change was still statistically significant, indicating that remodeling does occur in this genotype. Currently, we do not have a clear biological interpretation for differences in the magnitude of remodeling, and therefore chose not to emphasize cross-genotype comparisons.

Author response:

Reviewer #1 (Public review):

Major Concerns:

(1) Lack of Direct Evidence for RadD-NKp46 Interaction

The central claim that RadD interacts with NKp46 is not formally demonstrated. A direct binding assay (e.g., Biacore, ELISA, or pull-down with purified proteins) is essential to support this assertion. The absence of this fundamental experiment weakens the mechanistic conclusions of the study.

The reviewer is correct. Direct assays are currently quite impossible because RadD is huge protein and it will take years to purify it. Instead, we used immunoprecipitation assays using NKp46-Ig (Author response images 1 and 2). Fusobacteria were lysed using RIPA buffer, and the lysates were centrifuged twice to separate the supernatant from the pellet (which contains the bacterial membranes). The resulting lysates were incubated overnight with 2.5 µg of purified NKp46 and protein G-beads. After thorough washing, the bound proteins were placed in sample buffer and heated at 95 °C for 8 minutes. The eluates were run on a 10% acrylamide gel and visualized by Coomassie blue staining. As can be seen the NKp46-Ig was able to precipitate protein band around 350Kd in both F. polymorphum ATCC10953 (Author response image 1) and in F. nucleatum ATCC23726 (Author response image 2).

Author response image 1. NKp46 immunoprecipitation with Fusobacterium polymorphum (ATCC 10953) lysates. The resulting lysates of supernatant and pellet of Fusobacterium were immunoprecipitated (IP) with 2.5 μg of control fusion protein (RBD-Ig) or with NKp46-Ig. A 2.5 μg of purified fusion proteins were also run on gel.

Author response image 2. NKp46 immunoprecipitation with Fusobacterium nucleatum (ATCC 23726) lysates. The resulting lysates of supernatant and pellet of Fusobacterium were immunoprecipitated (IP) with 2.5 μg of Control fusion protein (RBD-Ig) or with NKp46-Ig. 2.5 μg of purified fusion proteins were also run on gel.

(2) Figure 2: Binding Specificity and Bacterial Strains

A CEACAM1-Ig control should be included in all binding experiments to distinguish between specific and non-specific Ig interactions. There is differential Ig binding between strains ATCC 23726 and 10953. The authors should quantify RadD expression in each strain to determine if the difference in binding is due to variation in RadD levels.

No significant difference in mCEACAM-1-Ig binding was observed across multiple independent experiments. Author response image 3 shows a representative histogram showing mCEACAM-1-Ig binding to F. nucleatum ATCC 23726 and F. polymorphum ATCC 10953. Comparable binding levels were detected in both bacterial species (upper histogram). Similarly, NKp46-Ig and Ncr1-Ig fusion proteins exhibited comparable binding patterns (lower histogram). It is currently not possible to quantify RadD expression directly, as no anti-RadD antibody is available.

Author response image 3. CEACAM-1 Ig binding to Fusobacterium ATCC 23726 and ATCC 10953. Upper histograms show staining with secondary antibody alone (gray) compared to CEACAM-1 Ig (black line). Lower histograms show binding of NKp46 and Ncr1 fusion proteins to the two Fusobacterium strains. Gray represent secondary antibody controls.

(3) Figure 3: Flow Cytometry Inconsistencies and Missing Controls

What do the FITC-negative, Ig-negative events represent? The authors should clarify whether these are background signals, bacterial aggregates, or debris.

We now present the gating strategy used in these experiments (Author response image 4). Fusion negative Ig samples were the bacterial samples stained only with the secondary antibody APC (anti-human AF647). The TITC-negative represent unlabeled bacteria.

Author response image 4. Gating strategy for FITC-labeled Fusobacterium stained with fusion proteins. Bacteria were first gated as shown in the left panel. The gated population was then further analyzed in the right plot: the lower-left quadrant represents bacterial debris, the upper-left quadrant corresponds to FITC-stained bacteria only, and the upper-right quadrant shows bacteria double-positive for FITC and APC, indicating binding of the fusion proteins.

Panel B, CEACAM1-Ig binding appears markedly increased compared to WT bacteria. The reason for this enhancement should be discussed-does it reflect upregulation of the bacterial ligand or an artifact of overexpression? Fluorescence compensation should be carefully reviewed for the NKp46/NCR1-Ig binding assays to ensure that the signals are not due to spectral overlap or nonspecific binding. Importantly, binding experiments using the FadI/RadD double knockout strain are missing and should be included. This control is essential.

We don’t know why expression of CEACAM1-Ig binding is increased. Indeed, it will be nice to have the FadI/RadD double knockout strain which we currently don’t have.

In Panel E, the basis for calculating fold-change in MFI is unclear. Please indicate the reference condition to which the change is normalized.

The mean fluorescence intensity (MFI) fold change was calculated by dividing the MFI obtained from staining with the fusion proteins by the MFI of the corresponding secondary antibody control (bacteria incubated without fusion proteins).

(4) Figure 4: Binding Inhibition and Receptor Sensitivity

Panel A lacks representative FACS plots and is currently difficult to interpret.

Fusobacteria binding to CEACAM-1, NKp46, and NCR1 fusion proteins was tested in the presence of 5 and 10 mM L-arginine (Author response image 5). L-arginine inhibited the binding of NKp46-Ig and NCR1-Ig, whereas no effect was observed on CEACAM-1-Ig binding.

Author response image 5. Fusobacterium binding inhibition by L-Arginine. The figure shows the binding of CEACAM1-Ig (left panel), NKp46-Ig (middle panel), and Ncr1-Ig (right panel) in the presence of 0 mM (black), 5 mM (red), and 10 mM (blue) L-arginine.

Differences in the sensitivity of human vs. mouse NKp46 to arginine inhibition should be discussed, given species differences in receptor-ligand interactions.

Ncr1, the murine orthologue of human NKp46, shares approximately 58% sequence identity with its human counterpart (1). The observed differences in arginine-mediated inhibition of bacterial binding between mouse and human NKp46 might stem from structural differences or distinct posttranslational modifications, such as glycosylation. Indeed, prediction algorithms combined with high-performance liquid chromatography analysis revealed that Ncr1 possesses two putative novel O-glycosylation sites, of which only one is conserved in humans (2).

References

(1) Biassoni R., Pessino A., Bottino C., Pende D., Moretta L., Moretta A. The murine homologue of the human NKp46, a triggering receptor involved in the induction of natural cytotoxicity. Eur J Immunol. 1999 Mar; 29(3).

(2) Glasner A., Roth Z., Varvak A., Miletic A., Isaacson B., Bar-On Y., Jonjić S., Khalaila I., Mandelboim O. Identification of putative novel O-glycosylations in the NK killer receptor Ncr1 essential for its activity. Cell Discov. 2015 Dec 22; 1:15036.

What are the inhibition results using F. nucleatum strains deficient in FadI?

The inhibition pattern observed in the F. nucleatum ΔFadI mutant was comparable to that of the wild-type strain (Author response image 6). When cultured under identical conditions and exposed to increasing concentrations of arginine (0, 5, and 10 mM), the F. nucleatum ΔFadI strain also demonstrated a dose-dependent reduction in binding to NKp46 and Ncr1.

Author response image 6. Arginine inhibition of NKp46-Ig and Ncr1-Ig binding in F. nucleatum ΔFadI. Histograms show NKp46-Ig (A, C) and Ncr1-Ig (B, D) binding to F. nucleatum ATCC10953 ΔFadI (A and B) and to F. nucleatum ATCC23726 ΔFadI (A and B) following exposure to 5 mM and 10 mM L-Arginine. Panels (E) and (F) display the mean fluorescence intensity (MFI) quantification corresponding to (A and B) and (C and D), respectively.

In Panel B, CEACAM1-Ig and RadD-deficient bacteria must be included as negative controls for binding specificity upon anti-NKp46 blocking.

We appreciate the request to include CEACAM1-Ig and RadD-deficient bacteria as negative controls for specificity under anti-NKp46 blocking. We don’t not think it is necessary since the 02 antibody is specific for NKp46, we used other anti0NKp46 antibodies that did not block the interaction and an irrelevant antibofy, we showed that arginine produced a dose-dependent reduction in NKp46/Ncr1 binding, consistent with an arginine-inhibitable RadD interaction already shown in our manuscript (Fig. 4A). The ΔRadD strains we used already demonstrate loss of NKp46/Ncr1 binding and loss of NK-boosting activity (Figs. 3, 5). Collectively, these data establish that NKp46/Ncr1 recognition of a high-molecular-weight ligand consistent with RadD is specific and functionally relevant.

Figure 5: Functional NK Activation and Tumor Killing

In Panels B and C, the key control condition (NK cells + anti-NKp46, without bacteria) is missing. This is needed to evaluate if NKp46 recognition is involved in tumor killing. The authors should explicitly test whether pre-incubation of NK cells with bacteria enhances their anti-tumor activity.

No significant difference in NK cell cytotoxicity was observed between untreated NK cells and NK cells incubated with anti-NKp46 antibody in the absence of bacteria. Therefore, the NK + anti-NKp46 (O2) group was included as an additional control alongside the other experimental conditions shown in Figures 5b and 5c, and is presented in Author response image 7 below.

Author response image 7. NK cytotoxicity against breast cancer cell lines. NK cell cytotoxicity against T47D (left) and MCF7 (right) breast cancer cell lines. This experiment follows the format of Figure 5b and 5c, with the addition of the NK cells + O2 antibody group. No significant differences were observed when values were normalized to NK cells alone.

Could bacteria induce stress signals in tumor cells that sensitize them to NK killing? This distinction is critical.

It remains unclear whether the bacteria induce stress-related signals in tumor cells that render them more susceptible to NK cell–mediated cytotoxicity.

(6) Figure 5D: Mechanism of Peripheral Activation

It is suggested that contact between bacteria and NK cells in the periphery leads to their activation. Can the authors confirm whether this pre-activation leads to enhanced killing of tumor targets, or if bacteria-tumor co-localization is required? The literature indicates that F. nucleatum localizes intracellularly within tumor cells. If so, how is RadD accessible to NKp46 on infiltrating NK cells?

We do not expect that pre-activation of NK cells with bacteria would enhance their tumor-killing capacity. In fact, when NK cells were co-incubated with bacteria, we occasionally observed NK cell death. Although F. nucleatum can reside intracellularly, bacterial entry requires prior adhesion to tumor cells. At this stage—before internalization—the bacteria are accessible for recognition and binding by NK cells.

(8) Figure 5E and In Vivo Relevance

Surprisingly, F. nucleatum infection is associated with increased tumor burden. Does this reflect an immunosuppressive effect? Are NK cells inhibited or exhausted in infected mice (TGIT, SIGLEC7...)? If NK cell activation leads to reduced tumor control in the infected context, the role of RadD-induced activation needs further explanation. RadD-deficient bacteria, which do not activate NK cells, result in even poorer tumor control. This paradox needs to be addressed: how can NK activation impair tumor control while its absence also reduces tumor control?

Siglec-7 lacks a direct orthologue in mice, and neither mouse TIGIT nor CEACAM1 bind F. nucleatum. The increased tumor burden observed in infected mice may therefore result from bacterial interference with immune cell infiltration and accumulation within the tumor microenvironment (Parhi, L., Alon-Maimon, T., Sol, A. et al. Breast cancer colonization by Fusobacterium nucleatum accelerates tumor growth and metastatic progression. Nat Commun 11, 3259 (2020)). Consequently, the NK cells that do reach the tumor site can recognize and kill F. nucleatum–bearing tumor cells through RadD–NKp46 interactions. In the absence of RadD, this recognition is impaired, leading to reduced NK-mediated cytotoxicity and increased tumor growth.

(9) NKp46-Deficient Mice: Inconsistencies

In Ncr1⁻/⁻ mice, infection with WT or RadD-deficient F. nucleatum has no impact on tumor burden. This suggests that NKp46 is dispensable in this context and casts doubt on the physiological relevance of the proposed mechanism. This contradiction should be discussed more thoroughly.

Ncr1 is also directly involved in mediating NK cell–dependent killing of tumor cells, even in the absence of bacterial infection. Therefore, in Ncr1-deficient mice, F. nucleatum has no additional effect on tumor progression (Glasner, A., Ghadially, H., Gur, C., Stanietsky, N., Tsukerman, P., Enk, J., Mandelboim, O. Recognition and prevention of tumor metastasis by the NK receptor NKp46/NCR1. J Immunol. 2012).

Reviewer #2 (Public review):

Weaknesses:

(1) A previous study by this group (PMID: 38952680) demonstrated that RadD of F. nucleatum binds to NK cells via Siglec-7, thereby diminishing their cytotoxic potential. They further proposed that the RadD-Siglec-7 interaction could act as an immune evasion mechanism exploited by tumor cells. In contrast, the present study reports that RadD of F. nucleatum can also bind to the activating receptor NKp46 on NK cells, thereby enhancing their cytotoxic function.

Siglec-7 lacks a direct orthologue in mice, and neither mouse TIGIT nor CEACAM1 bind F. nucleatum. In contrast, NKp46 and its murine homologue, Ncr1, both recognize and bind the bacterium.

While F. nucleatum-mediated tumor progression has been documented in breast and colon cancers, the current study proposes an NK-activating role for F. nucleatum in HNSC. However, it remains unclear whether tumor-infiltrating NK cells in HNSC exhibit differential expression of NKp46 compared to Siglec-7. Furthermore, heterogeneity within the NK cell compartment, particularly in the relative abundance of NKp46⁺ versus Siglec-7⁺ subsets, may differ substantially among breast, colon, and HNSC tumors. Such differences could have been readily investigated using publicly available single-cell datasets. A deeper understanding of this subset heterogeneity in NK cells would better explain why F. nucleatum is passively associated with a favorable prognosis in HNSC but correlates with poor outcomes in breast and colon cancers.

Currently, there are no publicly available single-cell datasets suitable for characterizing NK cell heterogeneity in the context of F. nucleatum infection—particularly regarding the expression of Siglec-7, NKp46, or CEACAM1 and their potential association with poor clinical outcomes in breast, head and neck squamous cell carcinoma (HNSC), or colorectal cancer (CRC). Furthermore, no RNA-seq datasets are available for breast cancer cases specifically associated with F. nucleatum infection and poor prognosis. Therefore, we analyzed bulk RNA expression datasets for Siglec-7 and CEACAM1 and evaluated their associations with HNSC and CRC using the same patient databases utilized in our manuscript (Author response image 8). No significant differences in Siglec-7 expression were detected between HNSC and CRC samples (Author response image 8A). Although CEACAM1 mRNA levels did not differ between F. nucleatum–positive and –negative cases within either cancer type, its overall expression was higher in CRC compared to HNSC (Author response image 8B).

Author response image 8. Siglec7 and Ceacam1 expression and the prognostic effect of F. nucleatum in a tumor-type-specific manner. Comparison of Siglec7 (A) and Ceacam1 (B) expression across HNSC and CRC tumors. Log₂ expression levels of NKp46 mRNA were compared across HNSC and CRC cohorts, stratified by F. nucleatum positive and negative. Results were analyzed by one-way ANOVA with Bonferroni post hoc correction.

(2) The in vivo tumor data (Figure 5D-F) appear to contradict the authors' claims. Specifically, Figure 5E suggests that WT mice engrafted with AT3 breast tumors and inoculated with WT F. nucleatum exhibited an even greater tumor burden compared to mice not inoculated with F. nucleatum, indicating a tumor-promoting effect. This finding conflicts with the interpretation presented in both the results and discussion sections.

Siglec-7 lacks a direct orthologue in mice, and neither mouse TIGIT nor CEACAM1 bind F. nucleatum. The increased tumor burden observed in infected mice may therefore result from bacterial interference with immune cell infiltration and accumulation within the tumor microenvironment (Parhi, L., Alon-Maimon, T., Sol, A. et al. Breast cancer colonization by Fusobacterium nucleatum accelerates tumor growth and metastatic progression. Nat Commun 11, 3259 (2020)). Consequently, the NK cells that do reach the tumor site can recognize and kill F. nucleatum–bearing tumor cells through RadD–NKp46 interactions. In the absence of RadD, this recognition is impaired, leading to reduced NK-mediated cytotoxicity and increased tumor growth.

(3) Although the authors acknowledge that F. nucleatum may have tumor context-specific roles in regulating NK cell responses, it is unclear why they chose a breast cancer model in which F. nucleatum has been reported to promote tumor growth. A more appropriate choice would have been the well-established preclinical oral cancer model, such as the 4-nitroquinoline 1-oxide (4NQO)-induced oral cancer model in C57BL/6 mice, which would more directly relate to HNSC biology.

The tumor model we employed is, to date, the only model in which F. nucleatum has been shown to exert a measurable effect, which is why we selected it for our study (Parhi, L., Alon-Maimon, T., Sol, A. et al. Breast cancer colonization by Fusobacterium nucleatum accelerates tumor growth and metastatic progression. Nat Commun. 2020; 11: 3259). We have not tested the 4-nitroquinoline-1-oxide (4NQO)–induced oral cancer model, and we are uncertain whether its use would be ethically justified.

(4) Since RadD of F. nucleatum can bind to both Siglec-7 and NKp46 on NK cells, exerting opposing functional effects, the expression profiles of both receptors on intratumoral NK cells should be evaluated. This would clarify the balance between activating and inhibitory signals in the tumor microenvironment and provide a more mechanistic explanation for the observed tumor context-dependent outcomes.

This question was answered in Author response image 8 above.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

This is an interesting study on the role of FGF signaling in the induction of primitive streak-like cells (PS-LC) in human 2D-gastruloids. The authors use a previously characterized standard culture that generates a ring of PSLCs (TBXT+) and correlate this with pERK staining. A requirement for FGF signaling in TBXT induction is demonstrated via pharmacological inhibition of MEK and FGFR activity. A second set of culture conditions (with no exogenous FGFs) suggests that endogenous FGFs are required for pERK and TBXT induction. The authors then characterize, via scRNA-seq, various components of the FGF pathway (genes for ligands, receptors, ERK regulators, and HSPG regulation). They go on to characterize the pFGFR1, receptor isoforms, and polarized localization of this receptor. Finally, they perform FGF4 inhibition and use a cell line with a limited FGF17 inactivation (heterozygous null) and show that loss of these FGFs reduces PS-LC and derivative cell types. 

Strengths: 

(1) As the authors point out, the role of FGF signaling in gastrulation is less well understood than other signaling pathways. Hence this is a valuable contribution to that field. 

(2) The FGF4 and FGF17 loss-of-function experiments in Figure 5 are very intriguing. This is especially so given the intriguing observation that these FGFs appear to be dominating in this model of human gastrulation, in contrast to what FGFs dominate in mice, chicks, and frogs. 

(3) In general this paper is valuable as a further development of the Human gastruloid system and the role of FGF signaling in the induction of PS-CLs. The wide net that the authors cast in characterizing the FGF ligand gene, receptor isoforms, and downstream components provides a foundation for future work. As the authors write near the beginning of the Discussion "Many questions remain." 

We thank the reviewer for these positive comments.

Weaknesses: 

(1) FGFs are cell survival factors in various aspects of development. The authors fail to address cell death due to loss of FGF signaling in their experiments. For example, in Figure 1E (which requires statistical analysis) and 1G (the bottom FGFRi row), there appears to be a significant amount of cell loss. Is this due to cell death? The authors should address the question of whether the role of FGF/ERK signaling is to keep the cells alive. 

Indeed, FGF also strongly affects cell survival and it is an interesting question to what extent this depends on ERK. Our manuscript focuses instead on the role of FGF/ERK signaling in cell fate patterning. As mentioned in our discussion, figure 1de show that doxycycline induced pERK leads to more TBXT+ cells than the control without restoring cell number, suggesting the role of FGF in controlling cell number is independent of the requirement for FGF/ERK in PS-LC differrentiation. To further support this, we have added data showing low doses of MEKi are sufficient to inhibit differentiation without affecting cell number (Supp. Fig. 1i).

To address the reviewers question regarding the cause of cell loss, we now stained for BrdU and cleaved Cas3 to assess proliferation and apoptosis in the presence and absence of MEK and FGFR inhibition (new Supp. Fig.

1ef). This shows that the effect of these inhibitors on cell number is primarily due to a reduction in proliferation. We have also included statistical analysis in Fig.1e. 

(2) Regarding the sparse cells in 1G, is there a reduction in cell number only with FGFRi and not MEKi? Is this reproducible? Gattiglio et al (Development, 2023, PMID: 37530863) present data supporting a "community effect" in the FGF-induced mesoderm differentiation of mouse embryonic stem cells. Could a community effect be at play in this human system (especially given the images in the bottom row of 1G)? If the authors don't address this experimentally they should at least address the ideas in Gattoglio et al. 

Indeed, FGFRi reproducibly affects cell number more than MEKi, in line with the fact that pathways other than MAPK/ERK downstream of FGF (e.g. PI3K) play important roles in cell survival and growth. However, we think the lack of differentiation in MEKi and FGFRi in Fig.1g cannot be attributed to a loss of cells combined with a community effect. This is because without FGFRi or MEKi cells efficiently differentiate to primitive streak at much lower densities than those originally shown, consistent with the data we discuss in response to (1) arguing against a primarily indirect effect of FGF on PS-LC differentiation through cell density. In the context of directed differentiation (rather than 2D gastruloids), we have now shown in a controlled manner that the effect of MEKi and FGFRi does not depend on a community effect by repeating the experiment in Fig.1g while adjusting cell seeding densities to obtain similar final cell densities in all three conditions (new Fig.1g, new Supp Fig.1g). Furthermore we have included new data showing extremely sparse cells without MEKi or FGFRi still differentiate without problems (new Supp Fig 1h). We have also include Gattoglio et al in our revised discussion.

(3) Do the FGF4 and FGF17 LOF experiments in Figure 5 affect cell numbers like FGFRi in Figure 1? 

We did not observe major changes in cell number in the FGF4 and FGF17 loss of function experiments. This is in line with our observation that low levels of ERK signaling are sufficient to maintain proliferation (new Supp. Fig. 1i), and the fact that low levels of ERK signaling are maintained in the absence of FGF4 and FGF17 (Fig.5), likely by FGF2 (Fig. 2). In contrast, FGFRi treatment in Fig.1 leads to a nearly complete loss of FGF signaling (ERK and other pathways) that has a dramatic effect on cell number.

Why examine PS-LC induction only in FGF17 heterozygous cells and not homozygous FGF17 nulls? 

We were unable to obtain homozygous FGF17 nulls, it is not clear if there is a reason for this. In the absence of homozygous nulls, we have now further corroborated our findings with additional knockdown data (described in response to other comments below).

(4) The idea that FGF8 plays a dominant role during gastrulation of other species but not humans is so intriguing it warrants deeper testing. The authors dismiss FGF8 because its mRNA "...levels always remained low." (line 363) as well as the data published in Zhai et al (PMID: 36517595) and Tyser et al (PMID: 34789876). But there are cases in mouse development where a gene was expressed at levels so low, that it might be dismissed, and yet LOF experiments revealed it played a role or even was required in a developmental process. The authors should consider FGF8 inhibition or inactivation to explore its potential role, despite its low levels of expression. 

We thank the reviewer for this suggestion. We have now analyzed the role of FGF8 using FISH to visualize its expression and siRNA to understand its function (Fig.5d,f,h; Supp.Fig.5e,g,6e). We found that FGF8 expression is higher earlier in differentiation, preceding most expression of TBXT. Our scRNA-seq only analyzed samples at 42h so did not capture this. Furthermore, FGF8 expression localized inside the PS-like ring rather than coinciding with it like FGF4. Surprisingly, FGF8 knockdown led to an increase in primitive streak-like differentiation, suggesting it may counteract FGF4. The results are shown in the revised Fig. 5 and Supplemental Fig. 5. While this certainly merits further investigation, understanding the role of FGF8 in more detail is beyond the scope of the current work. 

(5) Redundancy is a common feature in FGF genetics. What is the effect of inhibiting FGF4 in FGF17 LOF cells? 

Further siRNA and shRNA experiments showed that FGF17 knockdown had a much smaller effect than FGF4 knockdown on expression of primitive streak markers (Fig.5i, Supp.Fig.6f-i) but that FGF17 knockdown did lead to a complete loss of the mesoderm marker TBX6 (Fig.5j, Supp.Fig.6j). A double knockdown of FGF4+FGF17 looked similar to FGF4 alone (Supp.Fig.6k). Thus, we now think the more likely scenario is that FGF17 is downstream of FGF4-dependent PS-differentiation and although this may have a positive feedback effect whereby this FGF17 can then enhance further PS-differentiation, which we previously interpreted as partial redundancy, the primary role of FGF17 may be later, in mesoderm differentiation.

(6) I suggest stating that the authors take more caution in describing FGF gradients. For example, in one Results heading they write "Endogenous FGF4 and FGF17 gradients underly the ERK activity pattern.", implying an FGF protein gradient. However, they only present data for FGF mRNA , not protein. This issue would be clarified if they used proper nomenclature for gene, mRNA (italics), and protein (no italics) throughout the paper. 

Thank you for the suggestion. We have edited the paper to more clearly distinguish protein and mRNA. We do think our data provide substantial indirect evidence for a protein gradient which is what the results heading is meant to convey. Receptor activation is high where ERK activity is high (Fig.3), and receptor activation is limited by ligands, since creating a scratch to let exogenous FGF reach the basal side of cells in the center leads to receptor activation (Fig.4). This strongly suggests ERK activity reflects an FGF protein gradient. 

Reviewer #2 (Public review): 

Summary: 

The role of FGFs in embryonic development and stem cell differentiation has remained unclear due to its complexity. In this study, the authors utilized a 2D human stem cell-based gastrulation model to investigate the functions of FGFs. They discovered that FGF-dependent ERK activity is closely linked to the emergence of primitive streak cells. Importantly, this 2D model effectively illustrates the spatial distribution of key signaling effectors and receptors by correlating these markers with cell fate markers, such as T and ISL1. Through inhibition and loss-of-function studies, they further corroborated the needs of FGF ligands. Their data shows that FGFR1 is the primary receptor, and FGF2/4/17 are the key ligands for primitive streak development, which aligns with observations in primate embryos. Additional experiments revealed that the reduction of FGF4 and FGF17 decreases ERK activity. 

Strengths: 

This study provides comprehensive data and improves our understanding of the role of FGF signaling in primate

primitive streak formation. The authors provide new insights related to the spatial localization of the key components of FGF signaling and attempt to reveal the temporal dynamics of the signal propagation and cell fate decision, which has been challenging. 

Weaknesses: 

Given the solid data, the work only partially clarifies the complex picture of FGF signaling, so details remain somewhat elusive. The findings lack a strong punchline, which may limit their broader impact. 

We thank this reviewer for their valuable feedback and compliment on the solidity of our data. The punchline of our work is that FGF4 and FGF17-dependent ERK signaling plays a key role in differentiation of human PS-like cells and mesoderm, and that these are different FGFs than those thought to drive mouse gastrulation. A second key point is that like BMP and TGFβ signaling, FGF signaling is restricted to the basolateral sides of pluripotent stem cell colonies due to polarized receptor expression, which is crucial for understanding the response to exogenous ligands added to the cell medium. Indeed, many facets of FGF signaling remain to be investigated in the future, such as how FGF regulates and is regulated by other signals, which we will dedicate a different manuscript to. 

Reviewer #3 (Public review): 

Jo and colleagues set out to investigate the origins and functions of localized FGF/ERK signaling for the differentiation and spatial patterning of primitive streak fates of human embryonic stem cells in a well-established micropattern system. They demonstrate that endogenous FGF signaling is required for ERK activation in a ringdomain in the micropatterns, and that this localized signaling is directly required for differentiation and spatial patterning of specific cell types. Through high-resolution microscopy and transwell assays, they show that cells receive FGF signals through basally localized receptors. Finally, the authors find that there is a requirement for exogenous FGF2 to initiate primitive streak-like differentiation, but endogenous FGFs, especially FGF4 and FGF17, fully take over at later stages. 

Even though some of the authors' findings - such as the localized expression of FGF ligands during gastrulation and the importance of FGF/ERK signaling for cell differentiation in the primitive streak - have been reported in model organisms before, this is one of the first studies to investigate the role of FGF signaling during primitive streak-like differentiation of human cells. In doing so, the paper reports a number of interesting and valuable observations, namely the basal localization of FGF receptors which mirrors that of BMP and Nodal receptors, as well as the existence of a positive feedback loop centered on FGF signaling that drives primitive-streak differentiation. The authors also perform a comparison of the role of different FGFs across species and try to assign specific functions to individual FGFs. In the absence of clean genetic loss-of-function cell lines, this part of the work remains less strong. 

We thank the reviewer for emphasizing the value of our findings in a human model for gastrulation. We agree more loss-of-function experiments would provide further insight into the role of different FGFs. While we did not manage to create knockout cell lines, we have now performed both siRNA and shRNA knock-down of all FGF4, and FGF17 in two different hPSC lines, performed siRNA knockdown of FGF8, and also made a FGF4+FGF17 shRNA double knockdown cell lines to more completely test the functions of the individual FGFs (Fig.5, Supp.Fig.5,6). Our data suggest FGF17 may be downstream of FGF4 and primarily required for mesoderm differentiation while FGF8 appears to counteract FGF4. In doing this we have added a large amount of new data to the manuscript and we have removed the heterozygous knockout data in the first version of the manuscript which we felt added little to the new data. Further experiments are still needed to solidify our interpretation but those are beyond the scope of the current work.   

Reviewer #1 (Recommendations for the authors): 

(1) FGF2 is added to culture experiments (e.g. Figure 4), but the commercial source is not mentioned in Methods. For example, it could be added to "Supplementary Table 1: Cell signaling reagents." 

We apologize for this oversight and have now added the information to Supplementary Table 1.

(2) Line 117-118: "For example, by controlling the expression of Wnt or Nodal which are both required for PS-like differentiation". It is clear what the authors mean, but this is not a complete sentence. 

We edited this for clarity, it now reads: “First, is FGF/ERK signaling required directly for PS-like differentiation, or does it act indirectly? These possibilities are not mutually exclusive. For example, FGF/ERK could be required directly but also act indirectly by controlling Wnt or Nodal expression, as both Wnt and Nodal signaling are required for PS-like differentiation.”

(3) Line 246 "...found its spatial pattern to strongly resembles that of pERK..." either remove "to" or change "resembles" to "resemble" 

Thank you for catching this. We removed “to”.

(4) Lines 391- 393 seem to be missing a word in the last phrase: "...with FGF17 more important continued differentiation to mesoderm and endoderm." Maybe "during" after the word "important"? 

Thank you for catching this, indeed the word “during” was missing and we have now added it.

(5) Please define acronyms in Figure 3D (PS-LC was defined previously, but not others). 

We apologize for the oversight, we have now defined the acronyms.

(6) The three blue lines in Figure 5B (right) are hard to discern (and I'm not colorblind). I suggest also using a variety of dotted lines in a subset of these FGFs. 

Thanks you for the suggestion. We have now given all the FGFs colors that are more clearly distinct and made the TBXT and TBX6 lines dashed.  

Reviewer #2 (Recommendations for the authors): 

(1) The reviewer acknowledges that FGF signaling is complex, particularly when dynamics and its correlation with cell fates are considered. To improve the clarity of the findings, the authors are encouraged to provide an additional schematic figure that clearly delineates the main findings of this study.  

Thank you for the suggestion. We have now added a summary figure (Fig.6) to our discussion, which we hope helps present our findings more clearly.

(2) The data suggest that FGF signaling may function differently in mice compared to primates, and their stem cell model aligns more closely with the latter. While the authors discuss this in the contents only based on sequencing data, it would be valuable to conduct some experiments with mouse embryos to validate the key differences. 

It is unclear to us which experiments the reviewer has in mind. There is ample data on FGF expression in the mouse literature, as are many knockout phenotypes. Furthermore, verifying loss of function phenotypes (e.g. FGF17 knockout) in mouse is beyond our expertise.

(3) Heparan sulfate proteoglycan (HSPG) is mentioned as an important component of FGF signaling; however, the only data related to HSPG is single-cell sequencing results. The authors should consider performing immunostaining or other assays to validate HSPG expression and spatial distribution, similar to the approach they used for other signaling components. 

Our scratch experiments in Fig. 4 strongly argue against HSPGs as being responsible for the spatial pattern of FGF receptor activation: after a scratch across the colony the response is strong all along the scratch as expected if presence of FGF (an FGF gradient) controls the level of activity. If HSPGs were limiting, FGF flowing in from the media show not be able to uniformly activate receptors around the scratch.

In addtion, we have now included an immunostain for HS in a newly added Supp. Fig. 4 which does not explain the observed pattern of ERK signaling.

(4) In the scratch experiment, particularly high PERK expression is observed at the edge of the scratch. The authors should provide an explanation for why this expression is significantly higher compared to the edges of the colony. Additionally, it would be interesting to investigate the fate of the cells with super high PERK expression.  

We have now determined that adaptive response to FGF is the reason that the response around the scratch is initially much higher than in the ERK activity ring that overlaps with the primitive streak-like cells. We have added figures showing that although the intial response to FGF exposure after scratching is very high, the response around the scratch adapts to levels similar in those in the ERK ring over the course of 6 hours (Fig.4ij). 

(5) For some of the key experiments, multiple cell lines should be used to ensure that the findings are reproducible and applicable across different human stem cell lines.

We have now checked FISH stainings and knockdown phenotypes for different FGFs in two different cell lines: ESI17 (hESC, XX) and PGP1 (hiPSC, XY). These results are shown in Supplementary Figures 6. We found all results to be consistent.

(6) Where applicable, the meaning of error bars needs to be more clearly presented, including details on the number of independent experiments or samples used. 

Thank you for pointing this out. Where error bar definitions were missing we have now added them to the figure captions.

Reviewer #3 (Recommendations for the authors): 

(1) The authors only analyze the ppERK ring in micropatterns of a single size. What was the motivation for the choice of this size? Can the authors how the ppERK ring is expected to depend on colony size? 

Much smaller patterns lose the interior pluripotent regions while much larger patters have a much larger pluripotent region, which requires larger tilings to image without providing additional insight. The colony sizedependence of cell fate patterning was described in the paper that established the 2D gastruloids model (Warmflash Nat Methods 2014) and we later showed this due to a fixed length scale of the BMP and Nodal signaling gradients from the colony edge (Jo et al Elife 2022). We have now included data showing that the ERK patterns behaves similarly, with a fixed length scale of the pattern implying that in smaller colonies the ERK ring becomes a disc and the entire center of the colony has high ERK signaling (Supp Fig 1a).

(2) The scRNAseq is somewhat confusing - why do the two datasets not overlap in the PHATE representation? This is unexpected, because the two samples have been treated similarly, and the authors have integrated their data to iron out possible batch effects. This discrepancy should be discussed. The authors should also specify from which reference exactly the first dataset comes from.  

The two datasets do overlap nicely, the same fates are well mixed in the same place and the gene expresison profiles for the integrated data (e.g., Fig.2e) look smooth, so we believe the integration is good, but different cell fates are represented to different degrees. In particular, sample 2 shows much more mesoderm differentiation making the mesoderm branch mostly orange. Occassionally samples differentiate faster or slower than average which we see here, and these samples were collected far apart in time. We do not believe this affects our conclusions, if anything, we think performing the analysis on two samples that differ this much should make the conclusions more robust.  

(3) If find it intriguing that exogenous FGF2 is important early on for primitive streak-like differentiation, although the authors show that it does not reach the center of the colony. The authors may want to discuss this conundrum. Does the FGF2 effect propagate from the outside to the inside, or does it act at an early stage when the cells have not yet formed a tight epithelium on the micropattern? 

The cells in the experiment in Fig. 5a were given 24h to epithelialize, so we we do believe it acts from the edge. We believe this may be due to FGF2 modulating the early BMP response on the edge and are working on a manuscript that further explores this pathway crosstalk.

(4) The authors' statement that FGF4 and FGF17 have partially redundant functions is not very strong, mainly because the study lacks a full FGF17 loss-of-function cell line. If the authors wanted to improve on this point, they could knock down FGF4 in the FGF17 heterozygous line, or produce a homozygous FGF17 KO line. If there are specific reasons why FGF17 homozygous lines cannot be produced, this could be interesting to discuss, too. Finally, I noticed that the methods list experiments with an FGF17 siRNA, but these are not shown in the manuscript. 

We agree our evidence was previously not as strong as it could be. While there is no reason we know of why homozygous knockout lines cannot be produced, we failed to produce on. To strengthen our evidence we have therefore included substantial new knockdown data.  We have now performed both siRNA and shRNA knockdown of all FGF4, and FGF17 in two different hPSC lines, performed siRNA knockdown of FGF8, and also made a FGF4+FGF17 shRNA double knockdown cell lines to more completely test the functions of the individual FGFs (Fig.5, Supp.Fig.5,6). These experiments showed that FGF17 knockdown had a much smaller effect than FGF4 knockdown on expression of primitive streak markers (Fig.5i, Supp.Fig.6f-i) but that FGF17 knockdown did lead to a complete loss of the mesoderm marker TBX6 (Fig.5j, Supp.Fig.6j). A double knockdown of FGF4+FGF17 looked similar to FGF4 alone (Supp.Fig.6k). Thus, we now think the more likely scenario is that FGF17 is downstream of FGF4-dependent PS-differentiation and although this may have a positive feedback effect whereby this FGF17 can then enhance further PS-differentiation, which we previously interpreted as partial redundancy, the primary role of FGF17 may be later, in mesoderm differentiation. Furthermore, our new data suggests FGF8 may counteract FGF4 and limit PS-like differentiation. 

Minor 

(5) Line 63: Reference(s) appear to be missing. 

This whole paragraph summarizes the results of the references given on line 55, we have now repeated the relevant references where the reviewer indicated.

(6) Supplementary Figure 1a,b does not show ppERK, unlike stated in lines 102 - 104. 

Indeed, the data described in lines 102-104 is shown in Fig.1a and we have removed the original Supplementary Figure 1ab since it did not provide relevant information.

(7) Line 201: It is not clear whether this is a new sequencing dataset, or if existing datasets have been reanalyzed. 

We agree our description was unclear. We have edited the text, which now explicitly states that our analysis is based on one dataset we collected previously and a replicate that was newly collected and deposited on GEO for this manuscript.

(8) Figure 2f; Supplementary Figure 2b, c: The colors need to be explained in scale bars. How has this data been normalized to allow for comparison between very different sample types? 

We have now added color bars indicating the scale for each of these figure panels. As the caption stated, the interspecies comparison was normalized within each species, so the highest FGF level for any FGF at any time within each species is normalized to one. We are thus comparing between species the relative expression of different FGFs within each species. Indeed there is no good way to compare absolute expression between species. For extra clarity we have expanded our description of the interspecies comparison analysis and normalization in the methods section.

(9) Line 232: Where is the expression of SEF shown? 

It is shown in Fig. 2i, under the official gene name IL17RD.

(10) Supplementary Figure 4 seems to be missing. 

Thank you for pointing this out. We have now added a supplementary Fig.4.

(11) Line 437: Citation needed. 

We have included citations now.

(12) Line 439: A similar feedback loop has been proposed to operate during mesoderm differentiation in mouse ESC (pmid: 37530863 ). The authors may consider citing this work. 

Thank you for the suggestion, we have now included this work in the discussion. The feedback loop proposed in that work involves FGF8, while we were trying to explain why FGF4 and not FGF8 appears to be conserved across species by invoking an FGF4 feedback loop. Thus, it becomes even harder to explain differences in FGF4 and FGF8 expression between human and mouse gastrulation.

(13) Supplementary Figure 6 is not described in the main text. 

We have removed the original Supplementary Figure 6 and corresponding heterozygous knockout data in the main figure which we felt added little to the extensive knockdown data we now present. We did create a new Supplementary Figure 6 showing additional knockdown data which is described in the main tekst.

(14) Submission of sequencing data to GEO needs to be updated. 

We have now made the GEO data public.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

All experiments are convincing, clearly visualized and quantified. 

The strength of the paper is that it clearly indicates that there are temporal controlled feedback systems which is important for endothelial collective cell behavior. 

A limitation of the study is that the inhibitory studies in vivo may include off-target effects as well. Future endeavors, including specific knockout models, optogenetics and/or transgenic zebrafish lines that visualize endothelial cell properties (proliferation and migration) will be informative to track individual endothelial cell responses upon feedback signals.

We agree with the reviewer and are currently conducting experiments with optogenetic tools, knockout models, and transgenic zebrafish lines to dissect the feedback loop dynamics at the cellular scale.    

Reviewer #2 (Public review):

Major strengths: The combination of in vitro and in vivo assessment provides evidence for timing in physiologically relevant contexts, and rigorous quantification of outputs is provided. The idea of defining temporal aspects of the system is quite interesting. New RNA profiling supports the model. 

Weaknesses: Actinomycin D blocks most transcription so exposure for hours likely leads to secondary and tertiary effects and perhaps effects on viability.

We agree with the reviewer that “off-target” effects are a limitation of the pharmacologic approach. We have also previously shown that long-term treatment with actinomycin D reduces ECFC survival (Mason et al., 2019). 

Reviewer #3 (Public review):

Strengths: The authors conduct ASPM assay to find the time scale of feedback when ECFCs attach to three different matrics. They observe the common time scale of feedback. Thus, under very specific conditions they use, the reproducibility is validated by their ASPM assay. The feedback loop mediated by inhibition of gene expression by Actinomycin D is similar to that obtained from YAP/TAZ-depleted cells, suggesting the mechanotranduction might be involved in the feedback loop. The time scale representing infection point might be interesting when considering the continuous motility in cultured endothelial cells, although it might not account for the migration of endothelial cells that is controlled by a wide variety of extracellular cues. In vivo, stiffness of extracellular matrix is merely one of the cues. 

Weaknesses: ASPM assay is based on attachment-dependent phenomenon. The time scale including the inflection point determined by ASPM experiments using cultured cells and the mechanotransduction-based theory do not seem to fit in vivo ISV elongation. Although it is challenging to find the conserved theory of continuous cell motility of endothelial cells, the data is preliminary and does not support the authors' claim. There is no evidence that mechanotransduction solely determines the feedback loop during elongation of ISVs. The points to be addressed are listed in recommendations for the authors.

The ASPM assay enabled us to define temporal dynamics of YAP/TAZ mechanotransduction. We then used those insights to design ISV washout experiments that tested if the characteristic time scales were conserved in vivo. However, we agree with the limitations identified by the reviewer. Cells behave and respond to mechanical cues differently in 2D vs 3D environments, and the microenvironment in vivo is much more complex. Future work with optogenetic tools will be useful to dissect the temporal kinetics in vivo during ISV elongation.

Author response:

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

Reviewer #3 (Public review): 

Summary: 

The manuscript explores behavioral responses of C. elegans to hydrogen sulfide, which is known to exert remarkable effects on animal physiology in a range of contexts. The possibility of genetic and precise neuronal dissection of responses to H2S motivates the study of responses in C. elegans. The revised manuscript does not seem to have significantly addressed what was lacking in the initial version. 

The authors have added further characterization of possible ASJ sensing of H2S by calcium imaging but ASJ does not appear to be directly involved. Genetic and parallel analysis of O2 and CO2 responsive pathways do not reveal further insights regarding potential mechanisms underlying H2S sensing. Gene expression analysis extends prior work. Finally, the authors have examined how H2S-evoked locomotory behavioral responses are affected in mutants with altered stress and detoxification response to H2S, most notably hif-1 and egl-9. These data, while examining locomotion, are more suggestive that observed effects on animal locomotion are secondary to altered organismal toxicity as opposed to specific behavioral responedse 

Overall, the manuscript provides a wide range of intriguing observations, but mechanistic insight or a synthesis of disparate data is lacking. 

We thank the reviewer for the valuable feedback. We agree that while our investigation provides broad coverage, it does not fully resolve the mechanisms of H₂S perception. As both reviewers noted, the avoidance response to high levels of H₂S is most likely driven by its toxicity, particularly at the level of mitochondria, rather than by direct perception of H₂S. We also favor this model and have revised the results and discussion to highlight this interpretation, while acknowledging that other mechanisms cannot be excluded (main changes lines 387-402 and 535-547).

Building on this view, our observations point toward mitochondrial ROS transients as the trigger for H₂S avoidance. First, toxic levels of H₂S are known to promote ROS production (1). Second, similar to acute H₂S, brief exposure to rotenone, an ETC complex I inhibitor that rapidly generates mitochondrial ROS, triggers locomotory responses (Figure 7E) (Lines 393-396). Third, regardless of duration, rotenone exposure inhibits H₂S-evoked avoidance (Figure 7E) (Lines 389-391), likely by preventing or dampening H₂S-evoked mitochondrial ROS bursts when ETC function is impaired and ROS is already high. Notably, animals subjected to prolonged rotenone exposure, ETC mutants, and quintuple sod mutants, each experiencing chronically high ROS levels, fail to respond to H₂S and display reduced locomotory activity, presumably due to ROS toxicity and/or activation of stress-adaptive mechanisms (Figure 7).

Consistent with the activation of stress-responsive pathways, H₂S exposure alters expression of genes controlled by SKN-1 and HIF-1 signaling. Both pathways are ROS-sensitive and promote adaptation to chronic ROS production (2-4). Their activation, as in egl-9, render these animals insensitive to H₂S-evoked ROS transients (Figure 5B) (Lines 303-305). Conversely, mutants defective in these adaptive pathways, such as hif-1, still show initial locomotory responses to H₂S, but rapidly lose activity during prolonged H₂S exposure (Figure 5D) (Lines 318-319). These observations suggest that HIF-1 pathway is dispensable for initiating the response to H₂S evoked ROS transients, but essential for protecting against ROS toxicity.

In this context, the neural circuit we examined, such as ASJ neurons, is not directly involved in H₂S perception (Line 165-169 and 448-457). Instead, it likely modulates a circuit that is responsive to ROS toxicity. This circuit is also influenced by ambient O₂ levels, the state of O₂ sensing circuit, and nutrient status, in a manner reminiscent of the CO₂ responses (5, 6).

Reviewer #4 (Public review): 

Summary: 

The authors establish a behavioral paradigm for avoidance of H2S and conduct a large candidate screen to identify genetic requirements. They follow up by genetically dissecting a large number of implicated pathways - insulin, TGF-beta, oxygen/HIF-1, and mitochondrial ROS, which have varied effects on H2S avoidance. They additionally assay whole-animal gene expression changes induced by varying concentrations and durations of H2S exposure. 

Strengths: 

The implicated pathways are tested extensively through mutants of multiple pathway molecules. The authors address previous reviewer concerns by directly testing the ability of ASJ to respond to H2S via calcium imaging. This allows the authors to revise their previous conclusion and determine that ASJ does not directly respond to H2S and likely does not initiate the behavioral response. 

We thank the reviewer for the supportive comments.

Weaknesses: 

Despite the authors focus on acute perception of H2S, I don't think the experiments tell us much about perception. I think they indicate pathways that modulate the behavior when disrupted, especially because most manipulations used broadly affect physiology on long timescales. For instance, genetic manipulation of ASJ signaling, oxygen sensing, HIF-1 signaling, mitochondrial function, as well as starvation are all expected to constitutively alter animal physiology, which could indirectly modulate responses to H2S. The authors rule out effects on general locomotion in some cases, but other physiological changes could relatively specifically modulate the H2S response without being involved in its perception. 

I am actually not convinced that H2S is directly perceived by the C. elegans nervous system at all. As far as I can tell, the avoidance behavior could be a response to H2S-induced tissue damage rather than the gas itself. 

We thank the reviewer for the valuable insights, and fully agree that the H₂S may not be directly perceived by C. elegans. Please see detailed responses below.

Reviewer #4 (Recommendations for the authors): 

The clarity of the paper is improved in this version. My main issue has to do with "perception" of H2S. At times the authors suggest that hydrogen sulfide should be perceived by a neural circuit ("we did not specifically identify the neural circuit mediating H2S signaling"), while at other times they discuss the possibility that it is not directly perceived neuronally ("Supporting the idea that acute mitochondrial ROS generation initiates avoidance of high H2S levels,"). The authors should clearly state their model for H2S perception. Do they think there is a receptor and sensory neuron for H2S (not identified in this paper)? If not, what does it mean for there to be a neural circuit mediating the response? To me, it looks more like what is being "perceived" by a neural circuit is ROS-induced toxicity, not H2S itself. 

To drill down on direct modulation of acute perception, are any of the pathway manipulations used in this paper performed on the timescale of perception? Rotenone for 10 mins is close to that timescale, and in fact it increases speed independently of H2S, consistent with ROSinduced toxicity, not H2S being the signal that induces the behavior. Optogenetic activation of RMG could also be on the acute timescale. Can the authors clarify for how long blue light was on the worms before the start of the assay? Or was it turned on at the same time as video acquisition commenced? This could be evidence that RMG acutely modulates this behavioral response. 

I feel that the ASJ calcium imaging data should be in the main figure given its importance in revising the original model. 

We thank the reviewer for the valuable advice.

As suggested, ASJ calcium imaging data are displayed in the main figure (Figure 2I) (Line 167).

As both reviewers noted, our initial presentation was not sufficiently clear regarding the mechanism underlying H₂S avoidance. We agree with the reviewer that H₂S avoidance is unlikely mediated by direct perception via a H₂S-specific receptor, but likely arises from acute mitochondrial dysfunction and ROS generation. 

ROS

In line with the reviewer’s perspective, our observations point toward mitochondrial ROS transients as the trigger for H₂S avoidance. First, toxic levels of H₂S are known to promote ROS production (1). Second, similar to acute H₂S, brief exposure to rotenone, an ETC complex I inhibitor that rapidly generates mitochondrial ROS, triggers locomotory responses (Figure 7E) (Lines 393-396). Third, regardless of duration, rotenone exposure inhibits H₂S-evoked avoidance (Figure 7E) (Lines 389-391), likely by preventing or dampening H₂S-evoked mitochondrial ROS bursts when ETC function is impaired and ROS is already high. Notably, animals subjected to prolonged rotenone exposure, ETC mutants, and quintuple sod mutants, each experiencing chronically high ROS levels, fail to respond to H₂S and display reduced locomotory activity, presumably due to ROS toxicity and/or activation of stress-adaptive mechanisms (Figure 7). We revised the Results and Discussion to present the model more consistently (main changes lines 387-402 and 535-547).

Consistent with the activation of stress-responsive pathways, H₂S exposure alters expression of genes controlled by SKN-1 and HIF-1 signaling. Both pathways are ROS-sensitive and promote adaptation to chronic ROS production (2-4). Their activation, as in egl-9, render these animals insensitive to H₂S-evoked ROS transients (Figure 5B) (Lines 303-305). Conversely, mutants defective in these adaptive pathways, such as hif-1, still show initial locomotory responses to H₂S, but rapidly lose activity during prolonged H₂S exposure (Figure 5D) (Lines 318-319). These observations suggest that HIF-1 pathway is dispensable for initiating the response to H₂ Sevoked ROS transients, but essential for protecting against ROS toxicity.

ASJ neurons

ASJ neurons and DAF-11 signaling are required for H₂S-evoked behavioral responses. However, ASJ does not exhibit an H₂S-evoked calcium transient. It suggests that ASJ neurons do not directly detect H₂S (Line 165-169 and 448-457), but likely modulate the circuit responsive to ROS toxicity. This circuit can also be modulated by ambient O₂ levels, the state of O₂ sensing circuit, and nutrient status, in a manner reminiscent of the CO₂ responses (5, 6). 

O₂ sensing circuit

Consistent with the reviewer’s view, we favor the model that H₂S avoidance is likely induced by ROS transients. We believe that the state of O₂ sensing circuit, similar to ASJ neurons, modulates the neural circuit that is responsive to H₂S-evoked ROS toxicity. This circuit is inhibited as long as O₂ sensing circuit is active. In the RMG optogenetic experiment, channelrhodopsin was photo-stimulated as soon as the assay was initiated at 7% O₂ (Methods Lines 633-634 and Figure legend Lines 1177-1178), therefore RMG remained active throughout the assay including at 7% O₂. Our interpretation is that RMG activation inhibits this ROSresponsive circuit and H₂S avoidance. However, these observations do not resolve if H₂S is acutely and directly perceived. The modulation of H₂S response by O₂ circuit was discussed between Lines 437-447.

References

(1) J. Jia et al., SQR mediates therapeutic effects of H(2)S by targeting mitochondrial electron transport to induce mitochondrial uncoupling. Sci Adv 6, eaaz5752 (2020).

(2) S. J. Lee, A. B. Hwang, C. Kenyon, Inhibition of Respiration Extends C. elegans Life Span via Reactive Oxygen Species that Increase HIF-1 Activity. Current Biology 20, 2131-2136 (2010).

(3) C. Lennicke, H. M. Cocheme, Redox metabolism: ROS as specific molecular regulators of cell signaling and function. Mol Cell 81, 3691-3707 (2021).

(4) D. A. Patten, M. Germain, M. A. Kelly, R. S. Slack, Reactive oxygen species: stuck in the middle of neurodegeneration. J Alzheimers Dis 20 Suppl 2, S357-367 (2010).

(5) A. J. Bretscher, K. E. Busch, M. de Bono, A carbon dioxide avoidance behavior is integrated with responses to ambient oxygen and food in Caenorhabditis elegans. Proc Natl Acad Sci U S A 105, 8044-8049 (2008).

(6) E. A. Hallem, P. W. Sternberg, Acute carbon dioxide avoidance in Caenorhabditis elegans. Proc Natl Acad Sci U S A 105, 8038-8043 (2008).

Author response:

Reviewer #1 (Public review):

Summary:

Okazaki et al. showed flickering stimuli to patients with unilateral spatial neglect (USN) and measured EEG responses. They compared this with another patient group (post-stroke, but no USN) and healthy controls. The author's rationale was to entrain intrinsic brain rhythms using the flicker of different frequencies (3-30 Hz). Effects found unique to the 9-Hz stimulation condition differentiate USN patients from the other groups, leading them to conclude that USN can be characterized by increased hemispheric alpha asymmetry, driven by a relatively increased response in the intact hemisphere.

Strengths:

This study is principled empirical work that benefits from access to special patient groups of considerable size (about 60 stroke patients in total, and 20 USN). The authors use state-of-the-art established methods to (1) deliver and (2) quantify the responses to the flicker stimulation in the EEG recordings. In addition, they use phase-coupling measures to investigate cross-frequency coupling (here: alpha-gamma) and a measure of directed connectivity between brain areas, transfer entropy. The results are supported by means of simulations using a coupled-oscillators model.

Weaknesses:

In my eyes, the major conceptual weakness of the study is that the authors make the a priori assumption that the flicker stimulation entrains intrinsic brain rhythms, especially alpha (9 Hz). To date, there is no direct (and only equivocal indirect) evidence that alpha rhythms can be entrained with periodic visual stimulation. In the present study, the assumption of alpha entrainment permeates some analytical decisions - where it would be possible to separate stimulus-driven from intrinsic rhythms more strongly than is currently the case, potentially yielding deeper insights into the oscillopathy of USN - and, ultimately, the interpretation of the results. Another potential issue to consider here is the analysis of gamma rhythms in EEG data, absent a control of miniature eye movements, a known problem (Yuval-Greenberg et al., 2008, https://doi.org/10.1016/j.neuron.2008.03.027) that may be exacerbated here, given that USN patients could show different auxiliary gaze behaviour.

Reviewer #1 expressed concern that alpha entrainment is assumed a priori; however, our interpretation is based on the empirical observation of frequency-specific (9 Hz) hemispheric asymmetry, not on a prior assumption. This 9 Hz specificity is difficult to explain by a simple summation of stimulus-evoked responses and is more appropriately interpreted as a resonance phenomenon in the alpha band, which is close to the intrinsic resonance frequency of the visual system [1, 2]. In the revision, we will strengthen the conceptual distinction between stimulus-driven and intrinsic components and clarify that entrainment is a conclusion supported by our data and modeling.

Gamma contamination by eye movements is a valid theoretical concern. However, it is unlikely that saccadic spike potentials explain our α-γ coupling findings, due to several factors including timing constraints and spectral properties. In the revision, we will add explicit discussion of this limitation while explaining why our coupling patterns are more consistent with physiological neural coupling than with artifacts.

Reviewer #2 (Public review):

This study investigates how altered neural oscillations may contribute to unilateral spatial neglect (USN) following right-hemisphere stroke. By combining steady-state visual evoked potentials (SSVEPs), phase-amplitude coupling (PAC), transfer entropy (TE), and computational modeling, the authors aim to show that USN arises from disrupted hemispheric synchronization dynamics rather than simply from lesion extent. The integration of empirical EEG data with a mechanistic model is a major strength and offers a valuable new perspective on how frequency-specific neural dynamics relate to clinical symptoms.

The work has several notable strengths. The combination of experimental and modeling approaches is innovative and powerful, and the findings provide a coherent mechanistic framework linking abnormal neural entrainment to attentional deficits. The study also provides concrete evidence to support the potential for frequency-specific neuromodulatory interventions, which could have translational relevance At the same time, there are areas where the evidence could be clarified or contextualized further. The manuscript would benefit from more detailed characterization of lesions, since differences in lesion topography (white vs. gray matter, occipital vs. parietal areas) could greatly improve our understanding of the physiopathology causing unilateral spatial neglect and the altered neural oscillations reported. Methodological choices, such as focusing analyses on occipital electrodes rather than parietal sites, and the potential influence of volume conduction in transfer entropy analyses, also need clearer justification/elaboration. In addition, while the authors report several neural metrics, it is not always clear why SSVEP power was chosen as the primary correlate of clinical severity over other measures. More broadly, the manuscript would be strengthened by clearer definitions of dependent variables and reporting of software and toolboxes used.

Overall, the study makes a significant contribution by demonstrating that USN can be conceptualized as a disorder of disrupted oscillatory dynamics. With some clarifications and expansions, the paper will provide readers with a clearer understanding of both the strengths and the limitations of the evidence, and it will stand as a valuable reference for future work on oscillatory mechanisms in stroke and attention.

We agree that further lesion characterization would be generally useful. However, as shown in Supplementary Figure 1, lesions in our USN cohort involved both cortical and subcortical regions, and cortical damage often extended into adjacent white matter. Therefore, a strict gray-versus-white-matter classification was not feasible. This anatomical diversity suggests that the frequency-specific hemispheric asymmetry observed here cannot be fully explained by lesion location or size alone, but rather may reflect altered network dynamics following right-hemisphere damage. We will clarify this point in the revised Discussion.

Regarding transfer entropy (TE) and volume conduction, TE is theoretically insensitive to zero-lag correlations and quantifies temporally directed information transfer. Furthermore, we used amplitude envelopes rather than raw oscillations as input, which should greatly reduce the risk of spurious causal estimation due to sinusoidal autocorrelation structure. Moreover, if such spurious connectivity due to autocorrelation had occurred, it would have been expected to appear equally in both feedforward and feedback directions. Therefore, the feedforward-limited (visual→frontal) asymmetry observed in our study cannot be explained by volume conduction or autocorrelation effects. We will maintain this position clearly in the revision.

Regarding other methodological points: we focused on occipital electrodes (O1/O2) because visual stimuli primarily drive the visual system (we also analyzed parietal sites but found no significant hemispheric differences; Figure 4). We chose SSVEP power for clinical correlation because it was the primary phenomenon distinguishing USN from non-USN patients. In the revision, we will clarify these points and include software and toolbox information.

We believe these revisions will substantially strengthen the manuscript and clarify the conceptual and methodological contributions of our study.

References

(1) Rosanova, M., Casali, A., Bellina, V., Resta, F., Mariotti, M., and Massimini, M. (2009). Natural frequencies of human corticothalamic circuits. J Neurosci 29, 7679-7685.

(2) Okazaki, Y.O., Nakagawa, Y., Mizuno, Y., Hanakawa, T., and Kitajo, K. (2021). Frequency- and Area-Specific Phase Entrainment of Intrinsic Cortical Oscillations by Repetitive Transcranial Magnetic Stimulation. Front Hum Neurosci 15, 608947.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

Summary:

The manuscript characterizes a functional peptidergic system in the echinoderm Apostichopus japonicus that is related to the widely conserved family of calcitonin/diuretic hormone 31 (CT/DH31) peptides in bilaterian animals. In vitro analysis of receptor-ligand interactions, using multiple receptor activation assays, identifies three cognate receptors for two CT-like peptides in the sea cucumber, which stimulate cAMP, calcium, and ERK signaling. Only one of these receptors clusters within the family of calcitonin and calcitonin-like receptors (CTR/CLR) in bilaterian animals, whereas two other receptors cluster with invertebrate pigment dispersing factor receptors (PDFRs). In addition, this study sheds light on the expression and in vivo functions of CT-like peptides in A. japonicus, by quantitative real-time PCR, immunohistochemistry, pharmacological experiments on body wall muscle and intestine preparations, and peptide injection and RNAi knockdown experiments. This reveals a conserved function of CT-like peptides as muscle relaxants and growth regulators in A. japonicus.

Strengths:

This work combines both in vitro and in vivo functional assays to identify a CT-like peptidergic system in an economically relevant echinoderm species, the sea cucumber A. japonicus. A major strength of the study is that it identifies three G protein-coupled receptors for AjCT-like peptides, one related to the CTR/CLR family and two related to the PDFR family. A similar finding was previously reported for the CT-related peptide DH31 in Drosophila melanogaster that activates both CT-type and PDF-type receptors. Here, the authors expand this observation to a deuterostomian animal, which suggests that receptor promiscuity is a more general feature of the CT/DH31 peptide family and that CT/DH31-like peptides may activate both CT-type and PDF-type receptors in other animals as well.

Besides the identification of receptor-ligand pairs, the downstream signaling pathways of AjCT receptors have been characterized, revealing broad and in some cases receptor-specific effects on cAMP, calcium, and ERK signaling.

Functional characterization of the CT-related peptide system in heterologous cells is complemented with ex vivo and in vivo experiments. First, peptide injection and RNAi knockdown experiments establish transcriptional regulation of all three identified receptors in response to changing AjCT peptide levels. Second, ex vivo experiments reveal a conserved role for the two CT-like peptides as muscle relaxants, which have differential effects on body wall muscle and intestine preparations. Finally, peptide injection and knockdown experiments uncover a growth-promoting role for one CT-like peptide (AjCT2). Injection of AjCT2 at high concentration, or long-term knockdown of the AjCT precursor, affects diverse growth-related parameters including weight gain rate, specific growth rate, and transcript levels of growth-regulating transcription factors. The authors also reveal a growth-promoting function for the PDFR-like receptor AjPDFR2, suggesting that this receptor mediates the effects of AjCT2 on growth.

Weaknesses:

The authors present a more detailed phylogenetic analysis in the revised version, including a larger number of species. But some clusters in the analysis are not well supported because they have only low bootstrap values. This makes it difficult to interpret the clustering in some parts of the tree.

Thank you for the reviewer’s comments. In response, we have produced a new phylogenetic analysis using the maximum likelihood method. This was done by Nayeli Escudero Castelán and Kite Jones in the Elphick group at QMUL and therefore they have been added as co-authors of this paper. The new phylogenetic tree (Figure 2, line 206) includes broad taxonomic sampling of CT-type receptors and PDF-type receptors. CRH-type receptors, which are also members of the secretin-type GPCR sub-family, have been included as an outgroup to root the tree. In the previous version the much more distantly related vasopressin/oxytocin-type receptors, which are rhodopsin-type GPCRs, were included as an outgroup. Furthermore, VIP-type receptors were also included in the previous tree but these have been omitted from the new tree because VIP receptor orthologs only occur in vertebrates and therefore they are not representative of a bilaterian GPCR family. The new tree shows high bootstrap support for key clades, notably achieving a bootstrap value of 100 for a clade comprising both deuterostomian and protostomian PDF receptors. This provides important evidence that the A. japonicus PDF-type receptors characterised in this study (AjPDFR1, AjPDFR2) are co-orthologs of the PDF-type receptor that has been characterised previously in Drosophila. Similarly, there is strong bootstrap support (100) for a clade comprising CT/DH31-type receptors and, importantly, the CT-type receptor characterised in this study (AjCTR) is positioned in a branch of this clade that comprises deuterostomian CT-type receptors (with bootstrap support of 100). Details of methods employed to produce the new receptor tree are included in lines 727-739. The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

Expression of CT-like peptides was investigated both at transcript and protein level, but insight into the expression of the three peptide receptors is limited. This makes it difficult to understand the mechanism underlying the (different) functions of the two CT-like peptides in vivo. The authors identify differences in signal transduction cascades activated by each peptide, which might underpin distinct functions, but these differences were established only in heterologous cells.

We appreciate the reviewer's insightful comments. Regarding expression of CT-like peptide receptors, we have quantitatively analyzed the mRNA expression levels of the three receptors in key tissues using qRT-PCR (Figure 6, line 319) and receptor expression exhibits significant tissue-specific differences. Combined with the heterologous expression assays and In vivo functional validation, we believe our findings have provided clear mechanistic insights into the functional divergence of the two CT-like peptides. Investigation of the expression of the three receptor proteins in A. japonicus would require generation of specific antibodies, which was beyond the scope of this study. Furthermore, immunohistochemical visualization of neuropeptide receptor expression in other invertebrates has not been reported widely, which likely reflects technical difficulties in generation of antibodies that can be used to specifically detect receptor proteins that are typically expressed a low level in comparison to the neuropeptides that act as their ligands. 

We acknowledge that investigating signal transduction cascades in heterologous cells (rather than native A. japonicus cells) is a limitation. However, as a non-model organism, A. japonicus currently lacks established cell lines for such research. Therefore, using heterologous cells was the most feasible approach to examine the differential signaling cascades activated by the peptides through the three receptors. Importantly, our in vivo experiments demonstrated that long-term knockdown of either the AjCT precursor or AjPDFR2 resulted in similar and significant growth defects. The phenotypic consistency strongly suggests that AjCT2 and AjPDFR2 function within the same signaling pathway, with AjPDFR2 serving as the key receptor functionally activated by AjCT2.

The authors show overlapping phenotypes for a long-term knockdown of the AjCT precursor and the AjPDFR2 receptor, suggesting that the growth-regulating functions of AjCT2 are mediated by this receptor pathway. However, it remains unclear whether this mechanism underpins the growth-regulating function of AjCT2, until further in vivo evidence for this ligand-receptor interaction is presented. For example, the authors could investigate whether knockdown of AjPDFR2 attenuates the effects of AjCT2 peptide injection. In addition, a functional PDF system in this species remains uncharacterized, and a potential role of PDF-like peptides in growth regulation has not yet been investigated in A. japonicus. Therefore, it also remains unclear whether the ability of CT-like peptides to activate PDFRs is an evolutionary ancient property of this peptide family or whether this is an example of convergent evolution in some protostomian (Drosophila) and deuterostomian (sea cucumber) species.

Thank you for the reviewer’s insightful comments and constructive questions. We acknowledge the request for more direct evidence to demonstrate how AjCT2 functions in vivo through AjPDFR2. However, long-term knockdown of the AjCT precursor and AjPDFR2 both resulted in identical and significant growth defect phenotypes. The high phenotypic consistency, combined with the activation effect of AjCT2 on AjPDFR2 in heterologous cells, strongly suggests that they function within the same signaling pathway, with AjPDFR2 serving as the key receptor functionally activated by AjCT2. While exogenous peptide injection combined with receptor knockdown is a classic method for verifying receptor activation, phenotypic overlap itself is widely accepted in genetic research as robust evidence for pathway association (Shafer and Taghert, 2009; Van Sinay et al., 2017). A. japonicus is a non-model organism with a 3-month aestivation period in summer followed shortly by winter hibernation. During these periods, we are unable to conduct in vivo experiments. Any single experimental suggestion from reviewers could potentially require one more year of research and we have already conducted an additional year of research, in response to reviewer feedback, since submitting the original manuscript. We hope therefore that these challenges associated with working with aquatic invertebrate non-model organisms is recognized by the reviewers.

We fully agree that the functional PDF/PDFR system in A. japonicus and its potential role in growth regulation remain uncharacterized. Currently, the precursors of the PDF-type neuropeptide in echinoderms remain unidentified, which precludes clear pharmacological characterization of the two receptors. While further exploration of echinoderm PDF-type neuropeptides is still needed, our phylogenetic analysis-conducted using the maximum likelihood method with optimized parameters and rigorous sequence curation-demonstrates that the deuterostomian PDFRs (including AjPDFR1 and AjPDFR2) are positioned in a clade with the well-characterized protostomian PDFR clades with extremely high bootstrap support (value=100). Therefore, these two receptors in A. japonicus clearly belong to the PDF receptor family and our findings clearly indicate that the ability of CT-like peptides to activate PDFRs is either an evolutionarily ancient and conserved property or has arisen independently in different lineages. Details of methods employed to produce the new receptor tree are included in line 727-739. The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

Shafer, O. T., & Taghert, P. H. (2009). RNA-interference knockdown of Drosophila pigment dispersing factor in neuronal subsets: the anatomical basis of a neuropeptide's circadian functions. PloS one, 4(12), e8298. doi: 10.1371/journal.pone.0008298.

Van Sinay, E., Mirabeau, O., Depuydt, G., Van Hiel, M. B., Peymen, K., Watteyne, J., Zels, S., Schoofs, L., & Beets, I. (2017). Evolutionarily conserved TRH neuropeptide pathway regulates growth in Caenorhabditis elegans. Proceedings of the National Academy of Sciences of the United States of America, 114(20), E4065–E4074. doi: 10.1073/pnas.1617392114.

Reviewer #2 (Public review):

Summary:

The authors show that A. japonicus calcitonins (AjCT1 and AjCT2) activate not only the calcitonin/calcitonin-like receptor, but they also activate the two "PDF receptors", ex vivo. They also explore secondary messenger pathways that are recruited following receptor activation. They determine the source of CT1 and CT2 using qPCR and in situ hybridization and finally test the effects of these peptides on tissue contractions, feeding and growth. This study provides solid evidence that CT1 and CT2 act as ligands for calcitonin receptors; however, evidence supporting cross-talk between CT peptides and "PDF receptors" is weak.

Strengths:

This is the first study to report pharmacological characterization of CT receptors in an echinoderm. Multiple lines of evidence in cell culture (receptor internalization and secondary messenger pathways) support this conclusion.

Weaknesses:

The authors claim that A. japonicus CTs activate "PDF" receptors and suggest that this cross-talk is evolutionary ancient since similar phenomenon also exists in the fly Drosophila melanogaster. These conclusions are not fully supported. The authors perform phylogenetic analysis to show that the two "PDF" receptors form an independent clade. The bootstrap support is quite low in a lot of instances, especially for the deuterostomian and protostomian PDFR clades which is below 30. With such low support, it is unclear if the clade comprising deuterostomian "PDFR" is in fact PDFRs and not another receptor type whose endogenous ligand (besides CT) remains to be discovered.

Thank you for the reviewer’s comments. In response, we have produced a new phylogenetic analysis using the maximum likelihood method. This was done by Nayeli Escudero Castelán and Kite Jones in the Elphick group at QMUL and therefore they have been added as co-authors of this paper. The new phylogenetic tree (Figure 2, line 206) includes broad taxonomic sampling of CT-type receptors and PDF-type receptors. CRH-type receptors, which are also members of the secretin-type GPCR sub-family, have been included as an outgroup to root the tree. In the previous version the much more distantly related vasopressin/oxytocin-type receptors, which are rhodopsin-type GPCRs, were included as an outgroup. Furthermore, VIP-type receptors were also included in the previous tree but these have been omitted from the new tree because VIP receptor orthologs only occur in vertebrates and therefore they are not representative of a bilaterian GPCR family. The new tree shows high bootstrap support for key clades, notably achieving a bootstrap value of 100 for a clade comprising both deuterostomian and protostomian PDF receptors. This provides important evidence that the A. japonicus PDF-type receptors characterized in this study (AjPDFR1, AjPDFR2) are co-orthologs of the PDF-type receptor that has been characterized previously in Drosophila. Similarly, there is strong bootstrap support (100) for a clade comprising CT/DH31-type receptors and, importantly, the CT-type receptor characterized in this study (AjCTR) is positioned in a branch of this clade that comprises deuterostomian CT-type receptors (with bootstrap support of 100). Details of methods employed to produce the new receptor tree are included in lines 727-739. The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

Reviewer #2 (Recommendations for the authors):

Figure 1C: The bootstrap support is quite low in a lot of instances, especially for the deuterostomian and protostomian PDFR clades which is below 30. With such support, I would be hesitant to label the blue clade as deuterostomian PDFR for two reasons: 1) no members of this clade have been shown to be activated by a PDF-like substance and 2) the current study shows that these receptors are activated by CT-type peptides. Therefore, the phylogenetic analyses do not support the conclusions of this paper. What is the basis for calling these receptors PDFR and not CTR in light of weak phylogenetic support?

Thank you for the reviewer’s comments. In response, we have produced a new phylogenetic analysis using the maximum likelihood method. This was done by Nayeli Escudero Castelán and Kite Jones in the Elphick group at QMUL and therefore they have been added as co-authors of this paper. The new phylogenetic tree (Figure 2, line 206) includes broad taxonomic sampling of CT-type receptors and PDF-type receptors. CRH-type receptors, which are also members of the secretin-type GPCR sub-family, have been included as an outgroup to root the tree. In the previous version the much more distantly related vasopressin/oxytocin-type receptors, which are rhodopsin-type GPCRs, were included as an outgroup. Furthermore, VIP-type receptors were also included in the previous tree but these have been omitted from the new tree because VIP receptor orthologs only occur in vertebrates and therefore they are not representative of a bilaterian GPCR family. The new tree shows high bootstrap support for key clades, notably achieving a bootstrap value of 100 for a clade comprising both deuterostomian and protostomian PDF receptors. This provides important evidence that the A. japonicus PDF-type receptors characterized in this study (AjPDFR1, AjPDFR2) are co-orthologs of the PDF-type receptor that has been characterized previously in Drosophila. Similarly, there is strong bootstrap support (100) for a clade comprising CT/DH31-type receptors and, importantly, the CT-type receptor characterized in this study (AjCTR) is positioned in a branch of this clade that comprises deuterostomian CT-type receptors (with bootstrap support of 100). Details of methods employed to produce the new receptor tree are included in lines 727-739 The new phylogenetic tree is shown below and has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183).

We agree with the reviewer that no members of the PDF-type receptor clade in deuterostomes have yet been shown to be activated by a PDF-like substance. That is because the precursors of the PDF-type neuropeptides in echinoderms remain unidentified so far, which precludes clear pharmacological characterization of these receptors within the deuterostomian PDFR clade. However, the new phylogenetic tree now provides strong support (bootstrap value = 100) for the clade comprising deuterostomian and protostomian PDFRs, confirming the classification of AjPDFR1 and AjPDFR2 as PDF-type receptors. 

References:

Bauknecht P, Jékely G. Large-Scale Combinatorial Deorphanization of Platynereis Neuropeptide GPCRs. Cell reports, 2015, 12(4), 684–693. doi:  10.1016/j.celrep.2015.06.052.

Beets I, Zels S, Vandewyer E, Demeulemeester J, et al. System-wide mapping of peptide-GPCR interactions in C. elegans. Cell reports, 2023, 42(9), 113058. doi: 10.1016/j.celrep.2023.113058.

Cardoso J C, Mc Shane J C, Li Z, et al. Revisiting the evolution of Family B1 GPCRs and ligands: Insights from mollusca. Molecular and cellular endocrinology, 2024, 586, 112192. doi: 10.1016/j.mce.2024.112192.

Gorn A H, Lin H Y, Yamin M, et al. Cloning, characterization, and expression of a human calcitonin receptor from an ovarian carcinoma cell line. The Journal of clinical investigation, 1992, 90(5), 1726–1735. doi: 10.1172/JCI116046.

Huang T, Su J, Wang X, et al. Functional Analysis and Tissue-Specific Expression of Calcitonin and CGRP with RAMP-Modulated Receptors CTR and CLR in Chickens. Animals: an open access journal from MDPI, 2024, 14(7), 1058. doi: 10.3390/ani14071058.

Johnson E C, Shafer O T, Trigg J S, et al. A novel diuretic hormone receptor in Drosophila: evidence for conservation of CGRP signaling. Journal of Experimental Biology, 2005, 208(7): 1239-1246. doi: 10.1242/jeb.01529.

McLatchie L M, Fraser N J, Main M J, et al. RAMPs regulate the transport and ligand specificity of the calcitonin-receptor-like receptor. Nature, 1998, 393(6683): 333-339. doi: 10.1038/30666.

Schwartz J, Réalis-Doyelle E, Dubos M P, et al. Characterization of an evolutionarily conserved calcitonin signaling system in a lophotrochozoan, the Pacific oyster (Crassostrea gigas). Journal of Experimental Biology, 2019, 222(13): jeb201319. doi: 10.1242/jeb.201319.

Sekiguchi T, Kuwasako K, Ogasawara M, et al. Evidence for conservation of the calcitonin superfamily and activity-regulating mechanisms in the basal chordate Branchiostoma floridae: insights into the molecular and functional evolution in chordates. Journal of Biological Chemistry, 2016, 291(5): 2345-2356. doi: 10.1074/jbc.M115.664003.

The new results following AjCT and AjPDFR2 knockdown are a welcome addition. While this additional evidence supports the claim that AjCT could mediate its effects via AjPDFR2, this evidence does not show that AjCT acts as an endogenous ligand for PDFR in vivo. In combination with the weak phylogenetic analyses, I would recommend the authors to key down their claims that they have functionally characterized a PDFR (in the title and text).

Thank you for your insightful comments and we do understand the reviewer’s concern. 

Regarding “the weak phylogenetic analyses”, as highlighted above, we have produced a new phylogenetic tree (Fig 2, line 206) that provides strong bootstrap support for the clade comprising deuterostome and protostome PDF-type receptors. For this reason, it is our opinion that inclusion of “pigment-dispersing factor-type receptors” in the title of the paper is appropriate. The details of phylogenetic analysis method were added in line 727-739, and the updated phylogenetic tree has been incorporated into the revised manuscript (Figure 2, line 206). The description of new phylogenetic tree has also been modified accordingly in the revised manuscript (line 169-183). Besides, long-term knockdown of the AjCT precursor and AjPDFR2 both resulted in identical and significant growth defect phenotypes. And the observation of phenotypic overlap is widely accepted in genetic research as strong evidence for pathway association (Shafer and Taghert, 2009; Van Sinay et al., 2017). This high degree of phenotypic consistency, coupled with our in vitro finding that AjCT2 specifically activates AjPDFR2, strongly supports the conclusion that AjCT2 and AjPDFR2 function within the same signaling pathway in vivo, with AjPDFR2 serving as the key receptor functionally activated by AjCT2.

References:

Shafer, O. T., & Taghert, P. H. (2009). RNA-interference knockdown of Drosophila pigment dispersing factor in neuronal subsets: the anatomical basis of a neuropeptide's circadian functions. PloS one, 4(12), e8298. doi: 10.1371/journal.pone.0008298.

Van Sinay, E., Mirabeau, O., Depuydt, G., Van Hiel, M. B., Peymen, K., Watteyne, J., Zels, S., Schoofs, L., & Beets, I. (2017). Evolutionarily conserved TRH neuropeptide pathway regulates growth in Caenorhabditis elegans. Proceedings of the National Academy of Sciences of the United States of America, 114(20), E4065–E4074. doi: 10.1073/pnas.1617392114.

Since there is no formal logic defining the use of "type" vs "like" vs "related", I would encourage the authors to use one term (of their choice) to avoid unnecessary confusion. Or another possibility is that these relationships are defined at some point in the manuscript so that it becomes clear to the reader.

Thank you for the reviewer’s comments. The “CT-related peptides” has defined in the Introduction (line 54-58). As per your suggestion, we have now defined both “CT-type peptides” and “CT-like peptides” in the Introduction (line 76-79). “CT-type peptides” are characterized by an N-terminal disulphide bridge, whereas “CT-like peptides” (diuretic hormone 31 (DH31)-type peptides) lack this feature. Additionally, in accordance with the definitions, we have corrected these three descriptions in the revised manuscript (line 80, 83, 88 for “CT-type peptides”) to ensure consistent and accurate usage of these terms.

"To provide in vivo evidence supporting CT-mediated activation of "PDF" receptors, we conducted the following experiments: Firstly, we confirmed that AjPDFR1 and AjPDFR2were the functional receptors of AjCT1and AjCT2 (Figure 2, 3 and 4). Secondly, injection of AjCT2 and siAjCTP1/2-1 in vivo induced corresponding changes in AjPDFR1and AjPDFR2expression levels in the intestine (Figure 8C, 9A, 9B and 9C)."

None of these experiments provide direct evidence that CT activates PDFR in vivo. The functional studies are indeed a welcome addition but they cannot discriminate between correlation and causation.

Thank you for the reviewer’s insightful comments. We agree that the functional studies do not constitute direct proof that CT’s activation of PDFR in vivo. However, we observed identical and significant growth defect phenotypes following long-term knockdown of the AjCT precursor and the AjPDFR2. This high degree of phenotypic congruence, combined with the established in vitro activation of AjPDFR2 by AjCT2, provides strong support for the conclusion that AjCT2 acts as the key endogenous ligand activating the AjPDFR2 signaling pathway in vivo. Importantly, such phenotypic overlap has been widely accepted in genetic research as strong evidence for functional pathway association (Shafer and Taghert, 2009; Van Sinay et al., 2017).

References:

Shafer, O. T., & Taghert, P. H. (2009). RNA-interference knockdown of Drosophila pigment dispersing factor in neuronal subsets: the anatomical basis of a neuropeptide's circadian functions. PloS one, 4(12), e8298. doi: 10.1371/journal.pone.0008298.

Van Sinay, E., Mirabeau, O., Depuydt, G., Van Hiel, M. B., Peymen, K., Watteyne, J., Zels, S., Schoofs, L., & Beets, I. (2017). Evolutionarily conserved TRH neuropeptide pathway regulates growth in Caenorhabditis elegans. Proceedings of the National Academy of Sciences of the United States of America, 114(20), E4065–E4074. doi: 10.1073/pnas.1617392114.

Author response:

Reviewer #1 (Public review):

Summary:

This preprint from Shaowei Zhao and colleagues presents results that suggest tumorous germline stem cells (GSCs) in the Drosophila ovary mimic the ovarian stem cell niche and inhibit the differentiation of neighboring non-mutant GSC-like cells. The authors use FRT-mediated clonal analysis driven by a germline-specific gene (nos-Gal4, UASp-flp) to induce GSC-like cells mutant for bam or bam's cofactor bgcn. Bam-mutant or bgcn-mutant germ cells produce tumors in the stem cell compartment (the germarium) of the ovary (Figure 1). These tumors contain non-mutant cells - termed SGC for single-germ cells. 75% of SGCs do not exhibit signs of differentiation (as assessed by bamP-GFP) (Figure 2). The authors demonstrate that block in differentiation in SGC is a result of suppression of bam expression (Figure 2). They present data suggesting that in 73% of SGCs, BMP signaling is low (assessed by dad-lacZ) (Figure 3) and proliferation is less in SGCs vs GSCs. They present genetic evidence that mutations in BMP pathway receptors and transcription factors suppress some of the non-autonomous effects exhibited by SGCs within bam-mutant tumors (Figure 4). They show data that bam-mutant cells secrete Dpp, but this data is not compelling (see below) (Figure 5). They provide genetic data that loss of BMP ligands (dpp and gbb) suppresses the appearance of SGCs in bam-mutant tumors (Figure 6). Taken together, their data support a model in which bam-mutant GSC-like cells produce BMPs that act on nonmutant cells (i.e., SGCs) to prevent their differentiation, similar to what is seen in the ovarian stem cell niche. 

Strengths:

(1) Use of an excellent and established model for tumorous cells in a stem cell microenvironment.

(2) Powerful genetics allow them to test various factors in the tumorous vs nontumorous cells.

(3) Appropriate use of quantification and statistics.

We greatly appreciate these comments.

Weaknesses:

(1) What is the frequency of SGCs in nos>flp; bam-mutant tumors? For example, are they seen in every germarium, or in some germaria, etc, or in a few germaria?

This is a great question. Because the SGC phenotype depends on the presence of germline tumor clones, our quantification was restricted to germaria that contained them.These quantification data ("SGCs and/or germline cysts per germarium with germline clones") will be presented in the revised Figure 1.

(2) Does the breakdown in clonality vary when they induce hs-flp clones in adults as opposed to in larvae/pupae?

Our initial attempts to induce ovarian hs-flp germline clones by heat-shocking adult flies were unsuccessful, with very few clones being observed. Therefore, we shifted our approach to an earlier developmental stage. Successful induction was achieved by subjecting late-L3/early-pupal animals to a twice-daily heatshock at 37°C for 6 consecutive days (2 hours per session with a 6-hour interval, see Lines 325-329) (Zhao et al., 2018).

(3) Approximately 20-25% of SGCs are bam+, dad-LacZ+. Firstly, how do the authors explain this? Secondly, of the 70-75% of SGCs that have no/low BMP signaling, the authors should perform additional characterization using markers that are expressed in GSCs (i.e., Sex lethal and nanos).

These 20-25% of SGCs are bamP-GFP⁺ dad-lacZ-, not bam⁺ dad-lacZ⁺ (see Figure 2C and 3D). They would be cystoblast-like cells that may have initiated a differentiation program toward forming germline cysts (see Lines 109-117). The 70-75% of SGCs that have low BMP signaling exhibit GSC-like properties, including: 1) dot-like spectrosomes; 2) dad-lacZ positivity; 3) absence of bamP-GFP expression. While additional markers would be beneficial, we think that this combination of properties is sufficient to classify these cells as GSC-like. 

(4) All experiments except Figure 1I (where a single germarium with no quantification) were performed with nos-Gal4, UASp-flp. Have the authors performed any of the phenotypic characterizations (i.e., figures other than Figure 1) with hs-flp?

Yes, we initially identified the SGC phenotype through hs-flp-mediated mosaic analysis of bam or bgcn mutant in ovaries. However, as noted in our response to Weakness (2), this approach was very labor-intensive. Therefore, we switched to using the more convenient nos::flp system for subsequent experiments. To our observation, there was no difference in the SGC phenotype between these two approaches, confirming that the nos::flp system is a valid and more practical alternative for its study. 

(5) Does the number of SGCs change with the age of the female? The experiments were all performed in 14-day-old adult females. What happens when they look at a young female (like 2-day-old). I assume that the nos>flp is working in larval and pupal stages, and so the phenotype should be present in young females. Why did the authors choose this later age? For example, is the phenotype more robust in older females? Or do you see more SGCs at later time points?

These are very good questions. Such time-course analysis data will be provided in revised Figure 1. The SGC phenotype depends on the presence of bam or bgcn mutant germline clones. Germaria from 14-day-old flies contained bigger and more such clones than those from younger flies. This age-dependent increase in clone size and frequency significantly enhanced the efficiency of our quantification (see Lines 129-131). 

(6) Can the authors distinguish one copy of GFP versus 2 copies of GFP in germ cells of the ovary? This is not possible in the Drosophila testis. I ask because this could impact the clonal analyses diagrammed in Figure 4A and 4G and in 6A and B. Additionally, in most of the figures, the GFP is saturated, so it is not possible to discern one vs two copies of GFP.

We greatly appreciate this comment. It was also difficult for us to distinguish 1 and 2 copies of GFP in the Drosophila ovary. In Figure 4A-F, to resolve this problem, we used a triplecolor system, in which red germ cells (RFP^+/+ GFP^-/-) are bam mutant, yellow germ cells (RFP^+/- GFP^+/-) are wild-type, and green germ cells (RFP^-/- GFP^+/+) are punt or med mutant. In Figure 4G-J, we quantified the SGC phenotype only in black germ cells (GFP^-/-), which are wild-type (control) or mad mutant.  In Figure 6, we quantified the SGC phenotype only in green germ cells (both GFP^+/+ and GFP^+/-), all of which are wild-type.

(7) More evidence is needed to support the claim of elevated Dpp levels in bam or bgcn mutant tumors. The current results with the dpp-lacZ enhancer trap in Figure 5A, B are not convincing. First, why is the dpp-lacZ so much brighter in the mosaic analysis (A) than in the no-clone analysis (B)? It is expected that the level of dpplacZ in cap cells should be invariant between ovaries, and yet LacZ is very faint in Figure 5B. I think that if the settings in A matched those in B, the apparent expression of dpp-lacZ in the tumor would be much lower and likely not statistically significant. Second, they should use RNA in situ hybridization with a sensitive technique like hybridization chain reactions (HCR) - an approach that has worked well in numerous Drosophila tissues, including the ovary.

We appreciate this critical comment. The settings of immunofluorescent staining and confocal parameters in Figure 5A were the same as those in 5B. To our observation, the level of dpp-lacZ in cap cells was variable across germaria, even within the same ovary, as quantified in Figure 5C. We will provide RNA in situ hybridization data to further strengthen the conclusion that bam or bgcn mutant germline tumors secret BMP ligands.  

(8) In Figure 6, the authors report results obtained with the bamBG allele. Do they obtain similar data with another bam allele (i.e., bamdelta86)?

No. Given that bam^BG was functionally indistinguishable from bam^Δ86 in inducing the SGC phenotype (compare Figure 6F, I with Figure 6-figure supplement 3C), we believe that repeating these experiments with bam^Δ86 would be redundant and would not alter the key conclusion of our study. Thanks for the understanding!

Reviewer #2 (Public review):

While the study by Zhang et al. provides valuable insights into how germline tumors can non-autonomously suppress the differentiation of neighboring wild-type germline stem cells (GSCs), several conceptual and technical issues limit the strength of the conclusions.

Major points:

(1) Naming of SGCs is confusing. In line 68, the authors state that "many wild-type germ cells located outside the niche retained a GSC-like single-germ-cell (SGC) morphology." However, bam or bgcn mutant GSCs are also referred to as "SGCs," which creates confusion when reading the text and interpreting the figures. The authors should clarify the terminology used to distinguish between wild-type SGCs and tumor (bam/bgcn mutant) SGCs, and apply consistent naming throughout the manuscript and figure legends.

We apologize for any confusion. In our manuscript, the term "SGC" is reserved specifically for wild-type germ cells that maintain a GSC-like morphology outside the niche. bam or bgcn mutant germ cells are referred to as GSC-like tumor cells (Lines 87-88), not SGCs.

(a) The same confusion appears in Figure 2. It is unclear whether the analyzed SGCs are wild-type or bam mutant cells. If the SGCs analyzed are Bam mutants, then the lack of Bam expression and failure to differentiate would be expected and not informative. However, if the SGCs are wild-type GSCs located outside the niche, then the observation would suggest that Bam expression is silenced in these wildtype cells, which is a significant finding. The authors should clarify the genotype of the SGCs analyzed in Figure 2C, as this information is not currently provided.

The SGCs analyzed in Figure 2A-C are wild-type, GSC-like cells located outside the niche. They were generated using the same genetic strategy depicted in Figures 1C and 1E (with the schematic in Figure 1B). The complete genotypes for all experiments are available in Source data 1. 

(b) In Figures 4B and 4E, the analysis of SGC composition is confusing. In the control germaria (bam mutant mosaic), the authors label GFP⁺ SGCs as "wild-type," which makes interpretation unclear. Note, this is completely different from their earlier definition shown in line 68.

The strategy to generate SGCs in Figure 4B-F (with the schematic in Figure 4A) is completely different from that in Figure 1C-F, H, and I (with the schematic in Figure 1B). In Figure 4B-F, we needed to distinguish punt^-/- (or med^-/-) with punt^+/- (or med^+/-) germ cells. As noted in our response to Reviewer #1’s Weakness (6), it was difficult for us to distinguish 1 and 2 copies of GFP in the Drosophila ovary. Therefore, we chose to use the triple-color system to distinguish these germ cells in Figure 4B-F (see genotypes in Source data 1). 

(c) Additionally, bam⁺/⁻ GSCs (the first bar in Figure 4E) should appear GFP⁺ and Red⁺ (i.e., yellow). It would be helpful if the authors could indicate these bam⁺/⁻ germ cells directly in the image and clarify the corresponding color representation in the main text. In Figure 2A, although a color code is shown, the legend does not explain it clearly, nor does it specify the identity of bam⁺/⁻ cells alone. Figure 4F has the same issue, and in this graph, the color does not match Figure 4A.

The color-to-genotype relationships for the schematics in Figures 2A and 4E are provided in Figures 1B and 4A, respectively. Due to the high density of germ cells, it is impractical to label each genotype directly in the images. In contrast to Figure 4E, the colors in Figure 4F do not represent genotypes; instead, blue denotes the percentage of SGCs, and red denotes the percentage of germline cysts, as indicated below the bar chart. 

(2) The frequencies of bam or bgcn mutant mosaic germaria carrying [wild-type] SGCs or wild-type germ cell cysts with branched fusomes, as well as the average number of wild-type SGCs per germarium and the number of days after heat shock for the representative images, are not provided when Figure 1 is first introduced. Since this is the first time the authors describe these phenotypes, including these details is essential. Without this information, it is difficult for readers to follow and evaluate the presented observations.

Thanks for this constructive suggestion. We will include such quantification data in the revised manuscript.

(3) Without the information mentioned in point 2, it causes problems when reading through the section regarding [wild-type] SGCs induced by impairment of differentiation or dedifferentiation. In lines 90-97, the authors use the presence of midbodies between cystocytes as a criterion to determine whether the wild-type GSCs surrounded by tumor GSCs arise through dedifferentiation. However, the cited study (Mathieu et al., 2022) reports that midbodies can be detected between two germ cells within a cyst carrying a branched fusome upon USP8 loss.

Unlike wild-type cystocytes, which undergo incomplete cytokinesis and lack midbodies, those with USP8 loss undergo complete cell division, with the presence of midbodies (white arrow, Figure 1F’ from Mathieu et al., 2022) as a marker of the late cytokinesis stage (Mathieu et al., 2022). 

(a) Are wild-type germ cell cysts with branched fusomes present in the bam mutant mosaic germaria? What is the proportion of germaria containing wild-type SGCs versus those containing wild-type germ cell cysts with branched fusomes?

(b) If all bam mutant mosaic germaria carry only wild-type GSCs outside the niche and no germaria contain wild-type germ cell cysts with branched fusomes, then examining midbodies as an indicator of dedifferentiation may not be appropriate.

We greatly appreciate this critical comment. bam mutant mosaic germaria indeed contained wild-type germline cysts, as evidenced by an SGC frequency of ~70%, rather than 100% (see Figures 2H, 4F, 4J, 6F, 6I, and Figure 6-figure supplement 3C). Since the SGC phenotype depends on the presence of bam or bgcn mutant germline tumors, we quantified it as “the percentage of SGCs relative to the total number of SGCs and germline cysts that are surrounded by germline tumors” (see Lines 124-129). Quantifying the SGC phenotype as "the percentage of germaria with SGCs" would be imprecise. This is because the presence and number of SGCs were highly variable among germaria with bam mutant germline clones, and a small number of germaria entirely lacked these clones. We will provide the data of "SGCs and/or germline cysts per germarium with germline clones" in revised Figure 1.

(c) If, however, some germaria do contain wild-type germ cell cysts with branched fusomes, the authors should provide representative images and quantify their proportion.

Such representative germaria are shown in Figure 2G, 3B, 3C, 6D, 6E, and 6H. The percentage of germline cysts can be calculated by “100% - SGC%”.

(d) In line 95, although the authors state that 50 germ cell cysts were analyzed for the presence of midbodies, it would be more informative to specify how many germaria these cysts were derived from and how many biological replicates were examined.

As noted in our response to points a) and b) above, the germ cells surrounded by germline tumors, rather than germarial numbers, are more precise for analyzing the phenotype. For this experiment, we examined >50 such germline cysts via confocal microscopy. As the analysis was performed on a defined cellular population, this sample size should be sufficient to support our conclusion. 

(4) Note that both bam mutant GSCs and wild-type SGCs can undergo division to generate midbodies (double cells), as shown in Figure 4H. Therefore, the current description of the midbody analysis is confusing. The authors should clarify which cell types were examined and explain how midbodies were interpreted in distinguishing between cell division and differentiation.

We assayed for the presence of midbodies or not specifically within the germline cysts surrounded by bam mutant tumors, not within the tumors themselves (Lines 94-95). As detailed in Lines 88-97, the absence of midbodies was used as a key criterion to exclude the possibility of dedifferentiation.  

(5) The data in Figure 5 showing Dpp expression in bam mutant tumorous GSCs are not convincing. The Dpp-lacZ signal appears broadly distributed throughout the germarium, including in escort cells. To support the claim more clearly, the authors should present corresponding images for Figures 5D and 5E, in which dpp expression was knocked down in the germ cells of bam or bgcn mutant mosaic germaria. Showing these images would help clarify the localization and specificity of Dpp-lacZ expression relative to the tumorous GSCs.

We greatly appreciate this comment. RNA in situ hybridization data will be provided to further strengthen the conclusion that bam or bgcn mutant germline tumors secret BMP ligands.

(6) While Figure 6 provides genetic evidence that bam mutant tumorous GSCs produce Dpp to inhibit the differentiation of wild-type SGCs, it should be noted that these analyses were performed in a dpp⁺/⁻ background. To strengthen the conclusion, the authors should include appropriate controls showing [dpp⁺/⁻; bam⁺/⁻] SGCs and [dpp⁺/⁻; bam⁺/⁻] germ cell cysts without heat shock (as referenced in Figures 6F and 6I).

Schematic cartoons in Figure 6A and 6B demonstrate that these analyses were performed in a dpp^+/- background. Figure 6-figure supplement 1 indicates that dpp^+/- or gbb^+/- does not affect GSC maintenance, germ cell differentiation, and female fly fertility. Figure 6C is the control for 6D and 6E, and 6G is the control for 6H, with quantification in 6F and 6I.  We used nos::flp, not the heat shock method, to induce germline clones in these experiments (see genotypes in Source data 1).

(7) Previous studies have reported that bam mutant germ cells cause blunted escort cell protrusions (e.g., Kirilly et al., Development, 2011), which are known to contribute to germ cell differentiation (e.g., Chen et al., Frontiers in Cell and Developmental Biology, 2022). The authors should include these findings in the Discussion to provide a broader context and to acknowledge how alterations in escort cell morphology may further influence differentiation defects in their model.

Thanks for teaching us! Such discussion will be included in the revised manuscript.

(8) Since fusome morphology is an important readout of SGCs vs differentiation. All the clonal analysis should have fusome staining.

SGC is readily distinguishable from multi-cellular germline cyst based on morphology. In some clonal analysis experiments, fusome staining was not feasible due to technical limitations such as channel saturation or antibody incompatibility. Thanks for the understanding! 

(9) Figure arrangement. It is somewhat difficult to identify the figure panels cited in the text due to the current panel arrangement.

The figure panels were arranged to optimize space while ensuring that related panels are grouped in close proximity for logical comparison. We would be happy to consider any specific suggestions for an alternative layout that could improve clarity. Thanks!

(10) The number of biological replicates and germaria analyzed should be clearly stated somewhere in the manuscript-ideally in the Methods section or figure legends. Providing this information is essential for assessing data reliability and reproducibility.

Thanks for this constructive suggestion. Such information will be included in figure legends in the revised manuscript.

Reviewer #3 (Public review):

Summary:

Zhang et al. investigated how germline tumors influence the development of neighboring wild-type (WT) germline stem cells (GSC) in the Drosophila ovary. They report that germline tumors inhibit the differentiation of neighboring WT GSCs by arresting them in an undifferentiated state, resulting from reduced expression of the differentiation-promoting factor Bam. They find that these tumor cells produce low levels of the niche-associated signaling molecules Dpp and Gbb, which suppress bam expression and consequently inhibit the differentiation of neighboring WT GSCs non-cell-autonomously. Based on these findings, the authors propose that germline tumors mimic the niche to suppress the differentiation of the neighboring stem cells.

Strengths:

This study addresses an important biological question concerning the interaction between germline tumor cells and WT germline stem cells in the Drosophila ovary. If the findings are substantiated, they could provide valuable insights applicable to other stem cell systems.

We greatly appreciate these comments.

Weaknesses:

Previous work from Xie's lab demonstrated that bam and bgcn mutant GSCs can outcompete WT GSCs for niche occupancy. Furthermore, a large body of literature has established that the interactions between escort cells (ECs) and GSC daughters are essential for proper and timely germline differentiation (the differentiation niche). Disruption of these interactions leads to arrest of germline cell differentiation in a status with weak BMP signaling activation and low bam expression, a phenotype virtually identical to what is reported here. Thus, it remains unclear whether the observed phenotype reflects "direct inhibition by tumor cells" or "arrested differentiation due to the loss of the differentiation niche". Because most data were collected at a very late stage (more than 10 days after clonal induction), when tumor cells already dominate the germarium, this question cannot be solved. To distinguish between these two possibilities, the authors could conduct a time-course analysis to examine the onset of the WT GSC-like singlegerm-cell (SGC) phenotype and determine whether early-stage tumor clones with a few tumor cells can suppress the differentiation of neighboring WT GSCs with only a few tumor cells present. If tumor cells indeed produce Dpp and Gbb (as proposed here) to inhibit the differentiation of neighboring germline cells, a small cluster or probably even a single tumor cell generated at an early stage might prevent the differentiation of their neighboring germ cells.

Thanks for this critical comment. Such time-course analysis data will be provided in revised Figure 1.

The key evidence supporting the claim that tumor cells produce Gpp and Gbb comes from Figures 5 and 6, which suggest that tumor-derived dpp and gbb are required for this inhibition. However, interpretation of these data requires caution. In Figure 5, the authors use dpp-lacZ to support the claim that dpp is upregulated in tumor cells (Figure 5A and 5B). However, the background expression in somatic cells (ECs and pre-follicular cells) differs noticeably between these panels. In Figure 5A, dpp-lacZ expression in somatic cells in 5A is clearly higher than in 5B, and the expression level in tumor cells appears comparable to that in somatic cells (dpplacZ single channel). Similarly, in Figure 5B, dpp-lacZ expression in germline cells is also comparable to that in somatic cells. Providing clear evidence of upregulated dpp and gbb expression in tumor cells (for example, through single-molecular RNA in situ) would be essential.

We greatly appreciate this critical comment. In our data, the expression of dpp-lacZ in cap cells was variable across germaria, even within the same ovary, as quantified in Figure 5C. The images in Figures 5A and 5B were selected as representative examples of positive signaling. To directly address the reviewer's point and strengthen our conclusion, we will perform RNA in situ hybridization data in the revised manuscript to visualize the expression of BMP ligands within the bam or bgcn mutant germline tumor cells.

Most tumor data present in this study were collected from the bam[86] null allele, whereas the data in Figure 6 were derived from a weaker bam[BG] allele. This bam[BG] allele is not molecularly defined and shows some genetic interaction with dpp mutants. As shown in Figure 6E, removal of dpp from homozygous bam[BG] mutant leads to germline differentiation (evidenced by a branched fusome connecting several cystocytes, located at the right side of the white arrowhead). In Figure 6D, fusome is likely present in some GFP-negative bam[BG]/bam[BG] cells. To strengthen their claim that the tumor produces Dpp and Gbb to inhibit WT germline cell differentiation, the authors should repeat these experiments using the bam[86] null allele.

Although a structure resembling a "branched fusome" is visible in Figure 6E (right of the white arrowhead), it is an artifact resulting from the cytoplasm of GFP-positive follicle cells, which also stain for α-Spectrin, projecting between germ cells of different clones (see the merged image). In both our previous (Zhang et al., 2023) and current studies, bam^BG was functionally indistinguishable from bam^Δ86 in its ability to block GSC differentiation and induce the SGC phenotype (compare Figure 6F, I with Figure 6-figure supplement 3C). Given this, we believe that repeating the extensive experiments in Figure 6 with the bam^Δ86 allele would be scientifically redundant and would not change the key conclusion of our study. We thank the reviewer for their consideration.

It is well established that the stem niche provides multiple functional supports for maintaining resident stem cells, including physical anchorage and signaling regulation. In Drosophila, several signaling molecules produced by the niche have been identified, each with a distinct function - some promoting stemness, while others regulate differentiation. Expression of Dpp and Gbb alone does not substantiate the claim that these tumor cells have acquired the niche-like property. To support their assertion that these tumors mimic the niche, the authors should provide additional evidence showing that these tumor cells also express other niche-associated markers. Alternatively, they could revise the manuscript title to more accurately reflect their findings.

Dpp and Gbb are the key niche signals from cap cells for maintaining GSC stemness. Our work demonstrates that germline tumors can specifically mimic this signaling function, not the full suite of cap cell properties, to create a non-cell-autonomous differentiation block. The current title “Tumors mimic the niche to inhibit neighboring stem cell differentiation” reflects this precise concept: a partial, functional mimicry of the niche's most relevant activity in this context. We feel it is an appropriate and compelling summary of our main conclusion.

In the Method section, the authors need to provide details on how dpp-lacZ expression levels were quantified and normalized.

Thanks for this suggestion. Such information will be included in the revised manuscript.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

The authors report the structure of the human CTF18-RFC complex bound to PCNA. Similar structures (and more) have been reported by the O'Donnell and Li labs. This study should add to our understanding of CTF18-RFC in DNA replication and clamp loaders in general. However, there are numerous major issues that I recommend the authors fix. 

Strengths: 

The structures reported are strong and useful for comparison with other clamp loader structures that have been reported lately. 

Weaknesses: 

The structures don't show how CTF18-RFC opens or loads PCNA. There are recent structures from other groups that do examine these steps in more detail, although this does not really dampen this reviewer's enthusiasm. It does mean that the authors should spend their time investigating aspects of CTF18-RFC function that were overlooked or not explored in detail in the competing papers. The paper poorly describes the interactions of CTF18-RFC with PCNA and the ATPase active sites, which are the main interest points. The nomenclature choices made by the authors make the manuscript very difficult to read. 

Reviewer #2 (Public review): 

Summary 

Briola and co-authors have performed a structural analysis of the human CTF18 clamp loader bound to PCNA. The authors purified the complexes and formed a complex in solution. They used cryo-EM to determine the structure to high resolution. The complex assumed an auto-inhibited conformation, where DNA binding is blocked, which is of regulatory importance and suggests that additional factors could be required to support PCNA loading on DNA. The authors carefully analysed the structure and compared it to RFC and related structures. 

Strength & Weakness 

Their overall analysis is of high quality, and they identified, among other things, a human-specific beta-hairpin in Ctf18 that flexibly tethers Ctf18 to Rfc2-5. Indeed, deletion of the beta-hairpin resulted in reduced complex stability and a reduction in a primer extension assay with Pol ε. This is potentially very interesting, although some more work is needed on the quantification. Moreover, the authors argue that the Ctf18 ATP-binding domain assumes a more flexible organisation, but their visual representation could be improved. 

The data are discussed accurately and relevantly, which provides an important framework for rationalising the results. 

All in all, this is a high-quality manuscript that identifies a key intermediate in CTF18dependent clamp loading. 

Reviewer #3 (Public review): 

Summary: 

CTF18-RFC is an alternative eukaryotic PCNA sliding clamp loader that is thought to specialize in loading PCNA on the leading strand. Eukaryotic clamp loaders (RFC complexes) have an interchangeable large subunit that is responsible for their specialized functions. The authors show that the CTF18 large subunit has several features responsible for its weaker PCNA loading activity and that the resulting weakened stability of the complex is compensated by a novel beta hairpin backside hook. The authors show this hook is required for the optimal stability and activity of the complex. 

Relevance: 

The structural findings are important for understanding RFC enzymology and novel ways that the widespread class of AAA ATPases can be adapted to specialized functions. A better understanding of CTF18-RFC function will also provide clarity into aspects of DNA replication, cohesion establishment, and the DNA damage response. 

Strengths: 

The cryo-EM structures are of high quality enabling accurate modelling of the complex and providing a strong basis for analyzing differences and similarities with other RFC complexes. 

Weaknesses: 

The manuscript would have benefitted from more detailed biochemical analysis to tease apart the differences with the canonical RFC complex. 

I'm not aware of using Mg depletion to trap active states of AAA ATPases. Perhaps the authors could provide a reference to successful examples of this and explain why they chose not to use the more standard practice in the field of using ATP analogues to increase the lifespan of reaction intermediates. 

Overall appraisal: 

Overall the work presented here is solid and important. The data is sufficient to support the stated conclusions and so I do not suggest any additional experiments. 

Reviewer #1 (Recommendations for the authors): 

We thank the reviewer for their positive comments and for their thorough review. All raised points have been addressed below.

Major points 

(1) The nomenclature used in the paper is very confusing and sometimes incorrect. The authors refer to CTF18 protein as "Ctf18", and the entire CTF18-RFC complex as "CTF18". This results in massive confusion because it is hard to ascertain whether the authors are discussing the individual subunits or the entire complex. Because these are human proteins, each protein name should be fully capitalized (i.e. CTF18, RFC4 etc). The full complex should be referred to more clearly with the designation CTF18-RFC or CTF18-RLC (RFC-like complex). Also, because the yeast and human clamp loader complexes use the same nomenclature for different subunits, it would be best for the authors to use the "A, B, C, D, E subunit" nomenclature that has been standard in the field for the past 20 years. Finally, the authors try to distinguish PCNA subunits by labeling them "PCNA2" or "PCNA1" (see Page 8 lines 180,181 for an example). This is confusing because the names of the RFC subunits have similar formats (RFC2, RFC3, RFC4, etc). In the case of RFC this denotes unique genes, whereas PCNA is a homotrimer. Could the authors think of another way to denote the different subunits, such as super/subscript? PCNA-I, PCNA-II, PCNA-III? 

We thank the reviewer for pointing out the confusing nomenclature. Following the referee suggestion, we now refer to the CTF18 full complex as “CTF18-RFC”. We prefer keeping the nomenclature used for CTFC18 subunits as RFC2, RFC3 etc., as recently used in Yuan et al, Science, 2024. However, we followed the referee’s suggestion for PCNA subunits, now referred to as PCNA-I, PCNA-II and PCNA-III.

(2) I believe that the authors are over-interpreting their data in Figure 1. The claim that "less sharp definition" of the map corresponding to the AAA+ domain of Ctf18 supports a relatively high mobility of this subunit is largely unsubstantiated. There are several reasons why one could get varying resolution in a cryo-EM reconstruction, such as compositional heterogeneity, preferred orientation artifacts, or how the complex interacts with the air-water interface. If other data were presented that showed this subunit is flexible, this evidence would support that data but cannot alone as justification for subunit mobility. Along these lines, how was the buried surface area (2300 vs 1400 A2) calculated? Is this the total surface area or only the buried surface area involving the AAA+ domains? It is surprising that these numbers are so different considering that the subunits and complexes look so similar (Figures 1c and 2b). 

We respectfully disagree with the suggestion that our interpretation of local flexibility in the AAA+ domain of Ctf18 is overreaching. Several lines of evidence support this interpretation. First, compositional heterogeneity is unlikely, as the A′ domain of Ctf18 is well-resolved and forms stable interactions with RFC3, indicating that Ctf18 is consistently incorporated into the complex. Second, preferred orientation artifacts are excluded, as the particle distribution shows excellent angular coverage (Fig. S9a). Third, we now include a 3D variability analysis (3DVA; Supplementary Video 1), which reveals local conformational heterogeneity centered around the AAA+ domain of Ctf18, consistent with intrinsic flexibility.

Regarding the buried surface area values, the reported numbers refer specifically to the interfaces between the AAA+ domain of Ctf18 and RFC2, and are derived from buried surface area calculations performed with PISA. The smaller interface (~1400 Ų) compared to RFC1–RFC2 (~2300 Ų) reflects low sequence identity (~26%) and divergent structural features, including the absence of conserved elements such as the canonical PIP-box in Ctf18. We have clarified and expanded this explanation in the revised manuscript (Page 7).

(3) The authors very briefly discuss interactions with PCNA and how the CTF18-RFC complex differs from the RFC complex. This is amongst the most interesting results from their work, but also not well-developed. Moreover, Figure 3D describing these interactions is extremely unclear. I feel like this observation had potential to be interesting, but is largely ignored by the authors. 

We thank the referee for pointing this out. We have expanded the section describing the interactions of CTF18-RFC and PCNA (Page 9 in the new manuscript), and made a new panel figure with further details (Fig. 3D).  

(4) The authors make the observation that key ATP-binding residues in RFC4 are displaced and incompatible with nucleotide binding in their CTF18-RFC structure compared to the hRFC structure. This should be a main-text figure showing these displacements and how it is incompatible with ATP binding. Again, this is likely an interesting finding that is largely glossed over by the authors. 

We now discuss this feature in detail (Pag 11 in the new manuscript), and added two figure insets (Fig. 4c) describing the incompatibility of RFC4 with nucleotide binding.

(5) The authors claim that the work of another group (citation 50) "validate(s) our predictions regarding the significant similarities between CTF18-RFC and canonical RFC in loading PCNA onto a ss/dsDNA junction." However, as far as this reviewer can tell the work in citation 50 was posted online before the first draft of this manuscript appeared on biorxiv, so it is dubious to claim that these were "predictions." 

We agree with the referee about this claim. We have now revised the text as follows:

“While our work was being finalized, several cryo-EM structures of human CTF18-RFC bound to PCNA and primer/template DNA were reported by another group (He et al, PNAS, 2024). These findings are consistent with the distinct features of CTF18-RFC observed in our structures and independently support the notion of significant mechanistic similarity between CTF18-RFC and canonical RFC in loading PCNA onto a ss/dsDNA junction”.

(6) The authors use a primer extension assay to test the effects of truncating the Nterminal beta hairpin of CTF18. However, this assay is only a proxy for loading efficiency and the observed effects of the mutation are rather subtle. The authors could test their hypothesis more clearly if they performed an ATPase assay or even better a clamp loading assay. 

We thank the referee for this valuable suggestion. In response, we have performed clamp loading assays comparing the activities of human RFC, wild-type CTF18-RFC, and the β-hairpin–truncated CTF18-RFC mutant. The results, now presented in Fig. 6 and Table 1 of the revised manuscript, clearly show that truncation of the N-terminal βhairpin results in a slower rate of PCNA loading. We propose that this reduced loading rate likely contributes to the diminished Pol ε–mediated DNA synthesis observed in the primer extension assays.

Minor points 

(1) Page 3 line 53 the introduction suggests that ATP hydrolysis prompts clamp closure. While this may be the case, to my knowledge all recent structural work shows that closure can occur without ATP hydrolysis. It may be better to rephrase it to highlight that under normal loading conditions, ATP hydrolysis occurs before clamp closure. 

The text now reads (Page 3): 

“DNA binding prompts the closure of the clamp and hydrolysis of ATP induces the concurrent disassembly of the closed clamp loader from the sliding clamp-DNA complex, completing the cycle necessary for the engagement of the replicative polymerases to start DNA synthesis.”

(2) Page 3 line 60, I do not see how the employment of alternative loaders highlights the specificity of the loading mechanism - would it not be possible for multiple loaders to have promiscuous clamp loading? 

We thank the referee for this comment. The text now reads (Page 3):

“However, eukaryotes also employ alternative loaders (20), including CTF18-RFC (6, 21-24), which likely use a conserved loading mechanism but are functionally specialized through specific protein interactions and context-dependent roles in DNA replication.”

(3) Page 4 line 75 could you please cite a study that shows Ctf8 and Dcc1 bind to the Ctf18 C-terminus and that a long linker is predicted to be flexible? 

Two references have been added (Stokes et al, NAR, 2020 and Grabarczyk et al, Structure, 2018)

(4) Figure 2A has the N-terminal region of Ctf18 as bound to RFC3 but should likely be labeled as bound to RFC5. This caused significant confusion while trying to parse this figure. Further, the inclusion of "X" as a sequence - does this refer to a sequence that was not buildable in the cryo-EM map? I would be surprised that density immediately after the conserved DEXX box motif is unbuildable. If this is the case, it should be clearly stated in the figure legend that "X" denotes an unbuildable sequence. For the conserved beta-hairpin in the sequence, could the authors superimpose the AlphaFold prediction onto their structure? It would be more informative than just looking at the sequence. 

We apologize for this confusion. The error in Figure 2A has been corrected. The figure caption now explicitely says that “X” refers to amino acid residues in the sequence which were not modelled. A superposition of the cryo-EM model of the N-terminal Beta hairpin in human Ctf18 and AlphaFold predictions for this feature in drosophila and yeast Ctf18 is now presented in Figure 2A.

(5) Page 8 line 168, the use of the term "RFC5" here feels improper, since the "C" subunit is not RFC5 in all lower eukaryotes (see comment above about nomenclature). For instance, in S cerevisiae, the C subunit is RFC3. I would expect this interaction to be maintained in all C subunits, not all RFC5 subunits. 

The text now reads (Page 8):

“Therefore, lower eukaryotes may use a similar b-hairpin motif to bind the corresponding subunit of the RFC-module complex (RFC5 in human, Rfc3 in S. cerevisiae), emphasizing its importance.”  

(6) Page 10 line 228, the authors claim that hydrolysis is dispensable at the Ctf18/RFC2 interface based on evidence from RFC1/RFC2 interface, by analogy that this is the "A/B" interface in both loaders. However, the wording makes it sound as if the cited data were collected while studying Ctf18 loaders. The authors should clarify this point. 

The text has been modified as follows (Pag 11): 

“Prior research has indicated that hydrolysis at the large subunit/RFC2 interface is not essential for clamp loading by various loaders (48-51), while the others are critical for the clamp-loading activity of eukaryotic RFCs. “

(7) Page 11 line 243/244 the authors introduce the separation pin. Could they clarify whether Ctf18 contains any aromatic residues in this structural motif that would suggest it serves the same functional purpose? Also, the authors highlight this is similar to yeast RFC, which makes it sound like this is not conserved in human RFC, but the structural motif is also conserved in human RFC. 

We thank the reviewer for this helpful comment. We have clarified in the revised text (Page 12) that the separation pin is conserved not only in yeast RFC but also in human RFC, and now note that human Ctf18 also harbors aromatic residues at the corresponding positions. This observation is supported by the new panel in Figure 4e.

Minutia 

(1) Page 2 line 37 please remove the word "and" before PCNA. 

This has been corrected.

(2) Please define AAA+ and update the language to clarify that not all pentameric AAA+ ATPases are clamp loaders. 

AAA+ has been now defined (Page 3).

(3) Page 4 line 86 Given the relatively weak interaction of Pol ε. 

This has been corrected.

(4) Page 8 line 204 the authors likely mean "leucine" and not "lysine". 

We thank the reviewer for catching this. The error has been corrected.

(5) Page 14 line 300, the authors claim that CTF18 utilizes three subunits but then list four. 

We have corrected this.

Reviewer #2 (Recommendations for the authors): 

We thank the reviewer for their positive comments and valuable suggestions. The points raised by the referee have been addressed below.

Major point: 

(1) Please quantify Figure 6 and S9 from 3 independent repeats and determine the standard deviation to show the variability of the Ctf18 beta hairpin deletion.  The authors suggest that a suboptimal Ctf18 complex interaction with PCNA impacts the stability of the complex, but do not test this hypothesis. Could the suboptimal PIP motif in Ctf18 be changed to an improved motif and the impact tested in the primer extension assay? Although not essential, it would be a nice way to explore the mechanism. 

We thank the reviewer for the suggestion. However, we note that Figure 6b (now 7b) already presents the quantification of the primer extension assay from three independent replicates, with error bars showing standard deviations, and includes the calculated rate of product accumulation. These data clearly indicate a 42% reduction in primer synthesis rate upon deletion of the Ctf18 β-hairpin.

We agree that we do not provide direct evidence of impaired complex stability upon deletion of the Ctf18 β-hairpin. However, the 2D classification of the cryo-EM dataset (Figure S9) shows a marked reduction in the number of particles corresponding to intact CTF18-RFC–PCNA complexes in the β-hairpin deletion sample, with the majority of particles corresponding to free PCNA. This contrasts with the wild-type dataset, where complex particles are predominant. These findings indirectly suggest that deletion of the β-hairpin compromises the stability or assembly of the clamp-loader–clamp complex.

We thank the reviewer for the valuable suggestion to mutate the weak PIP-box of Ctf18. While an interesting direction, we instead sought to directly test the mechanism by performing quantitative clamp loading assays. These assays revealed a significant reduction in the rate of PCNA loading by the CTF18^Δ165–194-RFCmutant (Figure 6), supporting the conclusion that the β-hairpin contributes to productive PCNA loading. This loading delay likely underlies the reduced rate of primer extension observed in the Pol ε assay (Figure 7), consistent with impaired formation of processive polymerase– clamp complexes.

(2) I did not see the method describing how the 2D classes were quantified to evaluate the impact of the Ctf18 beta hairpin deletion on complex formation. Please add the relevant information. 

The relevant information has been added to the Method section:

“For quantification of complex stability, the number of particles contributing to each 2D class was extracted from the classification metadata (Datasets 1 and 3). All classes showing isolated PCNA rings were summed and compared to the total number of particles in classes representing intact CTF18-RFC–PCNA complexes. This analysis was performed for both wild-type and β-hairpin deletion mutant datasets. Notably, no 2D classes corresponding to free PCNA were observed in the wild-type dataset, whereas in the mutant dataset, a substantial fraction of particles corresponded to isolated PCNA, suggesting reduced stability of the mutant complex.”

Minor point: 

(1) Page 2, line 25. Detail what type of mobility is referred to. Do you mean flexibility in the EM-map? 

We have clarified this. The text now reads:

“The unique RFC1 (Ctf18) large subunit of CTF18-RFC, which based on the cryo-EM map shows high relative flexibility, is anchored to PCNA through an atypical low-affinity PIP box”

(2) Page 4, line 82. Please introduce CMGE, or at least state what the abbreviation stands for. 

This has been addressed.

(3) Page 4, line 89. Specify that the architecture of the HUMAN CTF18-RFC module is not known, as the yeast one has been published. 

At the time our study was initiated, the architecture of the human CTF18-RFC module was unknown. A structure of the human complex was published by another group during the final stages of our work and is now properly acknowledged in the Discussion.

(4) Page 6. Is it possible to illustrate why the autoinhibited state cannot bind to DNA? A visual representation would be nice. 

We thank the reviewer for this suggestion. Figure 4b in the original manuscript already illustrates why the autoinhibited, overtwisted conformation of the CTF18-RFC pentamer cannot accommodate DNA. In this state, the inner chamber of the loader is sterically occluded, precluding the binding of duplex DNA.

Reviewer #3 (Recommendations for the authors): 

We thank Reviewer #3 for their constructive feedback and positive overall assessment of our work.

We also thank the reviewer for their remarks on the use of Mg depletion to halt hydrolysis. Magnesium is an essential cofactor for ATP hydrolysis, and its depletion is expected to effectively prevent catalysis by destabilizing the transition state, possibly more completely than the use of slowly hydrolysable analogues such as ATPγS. We have recently employed Mg^²+ depletion to successfully trap a pre-hydrolytic intermediate in a replicative AAA+ helicase engaged in DNA unwinding (Shahid et al., Nature, 2025). This precedent supports the rationale for our choice, and the reference has now been included in the revised manuscript.

I think the authors deposited the FSC curve for the +Mg structure in the -Mg structure PDB/EMDB entry according to the validation report. 

We thank the reviewer for their careful inspection of the deposition materials. The discrepancy in the deposited FSC curve has now been corrected, and the appropriate FSC curves have been assigned to the correct PDB/EMDB entries.

Author response:

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

Reviewer #1 (Public review): 

This paper measures the positioning and diffusivity of RNaseE-mEos3.2 proteins in E. coli as a function of rifampicin treatment, compares RNaseE to other E. coli proteins, and measures the effect of changes in domain composition on this localization and motion. The straightforward study is thoroughly presented, including very good descriptions of the imaging parameters and the image analysis/modeling involved, which is good because the key impact of the work lies in presenting this clear methodology for determining the position and mobility of a series of proteins in living bacteria cells. 

Thank you for the nice summary and positive feedback on the descriptions and methodology. 

My key notes and concerns are listed below; the most important concerns are indicated with asterisks. 

(1) The very start of the abstract mentions that the domain composition of RNase E varies among species, which leads the reader to believe that the modifications made to E. coli RNase E would be to swap in the domains from other species, but the experiment is actually to swap in domains from other E. coli proteins. The impact of this work would be increased by examining, for instance, RNase E domains from B. subtilis and C. crescentus as mentioned in the introduction. 

Thank you for the suggestions. We agree that the sentence may convey an unintended expectation. Our original intention was to note the presence and absence of certain domains of RNase E (e.g. membrane-binding motif and CTD) vary across species, rather than the actual sequence variations. To avoid any misinterpretation, we decided to remove the sentence from the abstract. Using the domains of B. subtilis and C. crescentus RNase E in E. coli is a very interesting suggestion, but we will leave that for a future study. 

(2) Furthermore, the introduction ends by suggesting that this work will modulate the localization, diffusion, and activity of RNase E for "various applications", but no applications are discussed in the discussion or conclusion. The impact of this work would be increased by actually indicating potential reasons why one would want to modulate the activity of RNase E. 

Thank you for this suggestion. For example, an E. coli strain expressing membranebound RNase E without CTD can help stabilize mRNAs and enhance protein expression. In fact, this idea was used in a commercial BL21 cell line (Invitrogen’s One Shot BL21 Star), to increase the yield of protein expression. We also think that environmentally modulated MB% of RNase E can be useful for controlling the mRNA half-lives and protein expression levels in different conditions. We discussed these ideas at the end of the Discussion.

(3) Lines 114 - 115: "The xNorm histogram of RNase E shows two peaks corresponding to each side edge of the membrane": "side edge" is not a helpful term. I suggest instead: "...corresponding to the membrane at each side of the cell" 

Thank you. We made the suggested change.

(4) A key concern of this reviewer is that, since membrane-bound proteins diffuse more slowly than cytoplasmic proteins, some significant undercounting of the % of cytoplasmic proteins is expected due to decreased detectability of the faster-moving proteins. This would not be a problem for the LacZ imaging where essentially all proteins are cytoplasmic, but would significantly affect the reported MB% for the intermediate protein constructs. How is this undercounting considered and taken into account? One could, for instance, compare LacZ vs. LacY (or RNase E) copy numbers detected in fixed cells to those detected in living cells to estimate it.  

Thank you for raising this point and suggesting a possible way to address this. We compared the number of tracks for mEos3.2-fused proteins in live vs fixed cells and tested the undercounting effect of cytoplasmic molecules. We compared WT RNase E molecules in live and fixed cells and found that there are about 50% lower molecules detected in the fixed cells, which agrees with the expectation that fluorescent proteins lose their signal upon fixation. Similarly, cytoplasmic RNase E (RNase E ΔMTS) copy number was also ~50% less in the fixed cells compared to live cells. If cytoplasmic molecules were undercounted compared membrane-bound molecules in live cells, fixation would reduce the copy number less than 50%. The comparable ratio of 50% indicates that the undercounting issue is not significant. This control analysis is provided in Figure S1B-C, and we made corresponding textual change in the result section as below:

For this analysis, we first confirmed that proteins localized on the membrane and in the cytoplasm are detected with equal probability, despite differences in their mobilities (Fig. S1B-C). 

(5) The rifampicin treatment study is not presented well. Firstly, it is found that LacY diffuses more rapidly upon rifampicin treatment. This change is attributed to changes in crowding at the membrane due to mRNA. Several other things change in cells after adding rif, including ATP levels, and these factors should be considered. More importantly, since the change in the diffusivity of RNaseE is similar to the change in diffusivity of LacY, then it seems that most of the change in RNaseE diffusion is NOT due to RNaseE-mRNAribosome binding, but rather due to whatever crowding/viscosity effects are experienced by LacY (along these lines: the error reported for D is SEM, but really should be a confidence interval, as in Figure 1, to give the reader a better sense of how different (or similar) 1.47 and 1.25 are). 

We agree with the reviewer that upon rifampicin treatment, RNase E’s D increases to a similar extent as that of LacY. Hence, the increase likely arises from a factor common to both proteins. We have added the reviewer’s suggested interpretation as a possible explanation in the manuscript as below. 

The similar fold change in D_RNE and D_LacY upon rif treatment suggests that the change in RNE diffusion may largely be attributed to physical changes in the intracellular environment (such as reduced viscosity or macromolecular crowding[41,42]), rather than a loss of RNA-RNE interactions.

As requested by the reviewer, we have provided confidence intervals for our D values in Table S8. Because these intervals are very narrow, we chose to present the SEM as the error metric for D and have also reported the corresponding errors for the fold-change values whenever we describe the fold differences between D values. 

(6) Lines 185-189: it is surprising to me that the CTD mutants both have the same change in D (5.5x and 5.3x) relative to their full-length counterparts since D for the membranebound WT protein should be much less sensitive to protein size than D for the cytoplasmic MTS mutant. Can the authors comment? 

Perhaps the reviewer understood that these differences are the ratios between +/-CTD (e.g. WT RNE vs ΔCTD). However, the differences we mentioned were from membrane-bound vs cytoplasmic versions of RNase E with comparable sizes (e.g. WT RNase E vs RNase E ΔMTS). We modified text and added a summary sentence at the end of the paragraph to clarify the point.

We found that D_ΔMTS is ~5.5 times that of D_RNE (Fig. 3B). [...] Together, these results suggest that the membrane binding reduces RNE mobility by a factor of 5.

That being said, we also realized a similar fold difference between +/-CTD. Specifically, WT RNE vs RNE ΔCTD (both membrane-bound) show a ~4.1-fold difference and RNE ΔMTS vs RNE ΔMTS ΔCTD (both cytoplasmic) show ~3.9-fold difference. We do not currently do not have a clear explanation for this pattern. Given that these two pairs have a similar change in mass, we speculate that the relationship between D and molecular mass may be comparable for membrane-bound and free-floating RNE variants. 

(7) Lines 190-194. Again, the confidence intervals and experimental uncertainties should be considered before drawing biological conclusions. It would seem that there is "no significant change" in the rhlB and pnp mutants, and I would avoid saying "especially for ∆pnp" when the same conclusion is true for both (one shouldn't say 1.04 is "very minute" and 1.08 is just kind of small - they are pretty much the same within experiments like this). 

Thank you for raising this point, which we fully agree with. That being said, we decided to remove results related to the degradosome proteins to improve the flow of the paper. We are preparing another paper related to the RNA degradosome complex formation. 

(8) Lines 221-223 " This is remarkable because their molecular masses (and thus size) are expected to be larger than that of MTS" should be reconsidered: diffusion in a membrane does not follow the Einstein law (indeed lines 223-225 agree with me and disagree with lines 221-223). (Also the discussion paragraph starting at line 375). Rather, it is generally limited by the interactions with the transmembrane segments with the membrane. So Figure 3D does not contain the right data for a comparison, and what is surprising to me is that MTS doesn't diffuse considerably faster than LacY2. 

We agree with the reviewer’s point that diffusion in a membrane does not follow the Stokes-Einstein law. That is why we introduced Saffman’s model. However, even in this model, proteins of larger size (or mass) should be slower than smaller size (a reason why we presented Figure 3D, now 4D). In other words, both Einstein and Saffman models predict that larger particles diffuse slower, although the exact scaling relationship differs between two models. Here, we assume that mass is related to the size. Contrary to Saffman’s model for membrane proteins, LacY2 diffuses faster than MTS despite of large size. Using MD simulations, we showed that this discrepancy can be explained by different interaction energies as the reviewer mentioned. This analysis further demonstrates that the size is not the only factor to consider protein diffusion in the membrane. We edited the paragraph to clarify the expectations and our interpretations.

According to the Stokes-Einstein relation for diffusion in simple fluids[49] and the Saffman-Delbruck diffusion model for membrane proteins, D decreases as particle size increases, albeit with different scaling behaviors. […] Thus, if size (or mass) were the primary determinant of diffusion, LacY2 and LacY6 would diffuse more slowly than the smaller MTS. The observed discrepancy instead implies that D may be governed by how each motif interacts with the membrane. For example, the way that TM domains are anchored to the membrane may facilitate faster lateral diffusion with surrounding lipids. 

(9) The logical connection between the membrane-association discussion (which seems to ignore associations with other proteins in the cell) and the preceding +/- rifampicin discussion (which seeks to attribute very small changes to mRNA association) is confusing.

Thank you for raising this point. We re-arranged the second result section to present diffusion due to membrane binding first before rifampicin. Furthermore, we stated our hypothesis and expectations in the beginning of the results section. This addition will legitimate our logic flow.

(10) Separately, the manuscript should be read through again for grammar and usage. For instance, the title should be: "Single-molecule imaging reveals the *roles* of *the* membrane-binding motif and *the* C-terminal domain of RNase E in its localization and diffusion in Escherichia coli". Also, some writing is unwieldy, for instance, "RNase E's D" would be easier to read if written as D_{RNaseE}. (underscore = subscript), and there is a lot of repetition in the sentence structures. 

Thank you for catching grammar mistakes. We went through extensive proofreading to avoid these mistakes and also used simple notation suggested by the reviewer, such as D_RNE, to make it easier to read. Thank you again for your suggestions.

Reviewer #2 (Public review): 

Summary: 

Troyer and colleagues have studied the in vivo localisation and mobility of the E.coli RNaseE (a protein key for mRNA degradation in all bacteria) as well as the impact of two key protein segments (MTS and CTD) on RNase E cellular localisation and mobility. Such sequences are important to study since there is significant sequence diversity within bacteria, as well as a lack of clarity about their functional effects. Using single-molecule tracking in living bacteria, the authors confirmed that >90% of RNaseE localised on the membrane, and measured its diffusion coefficient. Via a series of mutants, they also showed that MTS leads to stronger membrane association and slower diffusion compared to a transmembrane motif (despite the latter being more embedded in the membrane), and that the CTD weakens membrane binding. The study also rationalised how the interplay of MTS and CTD modulate mRNA metabolism (and hence gene expression) in different cellular contexts. 

Strengths: 

The study uses powerful single-molecule tracking in living cells along with solid quantitative analysis, and provides direct measurements for the mobility and localisation of E.coli RNaseE, adding to information from complementary studies and other bacteria. The exploration of different membrane-binding motifs (both MTS and CTD) has novelty and provides insight on how sequence and membrane interactions can control function of protein-associated membranes and complexes. The methods and membrane-protein standards used contribute to the toolbox for molecular analysis in live bacteria. 

Thank you for the nice summary of our work and positive comments about the paper’s strengths.

Weaknesses: 

The Results sections can be structured better to present the main hypotheses to be tested. For example, since it is well known that RNase E is membrane-localised (via its MTS), one expects its mobility to be mainly controlled by the interaction with the membrane (rather than with other molecules, such as polysomes and the degradosome). The results indeed support this expectation - however, the manuscript in its current form does not lay down the dominant hypothesis early on (see second Results chapter), and instead considers the rifampicin-addition results as "surprising"; it will be best to outline the most likely hypotheses, and then discuss the results in that light. 

Thank you for this comment. We addressed this point by stating our main hypothesis from the beginning of the results section. We also agree with the reviewer that the membrane binding effect should be discussed first; hence, we re-arranged the result section. In the revised manuscript, we discuss the effect of membrane binding on diffusion first, followed by rif effects.

Similarly, the authors should first discuss the different modes of interaction for a peripheral anchor vs a transmembrane anchor, outline the state of knowledge and possibilities, and then discuss their result; in its current version, the ms considers the LacY2 and LacY6 faster diffusion compared to MTS "remarkable", but considering the very different mode of interaction, there is no clear expectation prior to the experiment. In the same section, it would be good to see how the MD simulations capture the motion of LacY6 and LacY12, since this will provide a set of results consistent with the experimental set. 

Thank you for pointing this out. In fact, there is little discussion in the literature about the different modes of interaction for a peripheral anchor vs a transmembrane anchor. To our knowledge, our work (experiments and MD simulations) is the first that directly compared the two to reveal that the peripheral anchor has higher interaction energy than the transmembrane anchor. We added a sentence “Despite the prevalence of peripheral membrane proteins, how they interact with the membrane and how this differs from TM proteins remain poorly understood”. Furthermore, we added the MD simulation result of LacY6 and LacY12 in Figure 4E-F.

The work will benefit from further exploration of the membrane-RNase E interactions; e.g., the effect of membrane composition is explored by just using two different growth media (which on its own is not a well-controlled setting), and no attempts to change the MTS itself were made. The manuscript will benefit from considering experiments that explore the diversity of RNaseE interactions in different species; for example, the authors may want to consider the possibility of using the membrane-localisation signals of functional homologs of RNaseE in different bacteria (e.g., B. subtilis). It would be good to look at the effect of CTD deletions in a similar context (i.e., in addition to the MTS substitution by LacY2 and LacY6). 

Thank you very much for this suggestion. During revision, we engineered point mutations in MTS and analyzed critical hydrophobic residues for membrane binding. We characterized MB% in both +/-CTD variants (Fig. 2 and Fig. S6) and their effect on lacZ mRNA degradation (Fig. 6). We will leave the use of membrane motif of B. subtilis RNase E for future study. 

The manuscript will benefit from further discussion of the unstructured nature of the CTD, especially since the RNase CTD is well known to form condensates in Caulobacter crescentus; it is unclear how the authors excluded any roles for RNaseE phase separation in the mobility of RNaseE in E.coli cells. 

Yes, we agree with the reviewer that the intrinsically disordered nature of the CTD might contribute to condensate formation. We explored this possibility using both epifluorescence microscopy (with a YFP fusion) and single-molecule imaging with cluster analysis (using an mEos3.2 fusion). Please see Figure S8. We did observe some weak de-clustering of RNase E upon CTD deletion. In the current study, we are unable to quantify the extent to which clustering contributes to the slow diffusion of RNase E. However, we speculate that the clustering may be linked to the low MB% of certain RNE mutants containing CTD, and we discussed this possibility in the Discussion.

[…] further supporting that the CTD decreases membrane association across RNE variants. We speculate that this effect may be related to the CTD’s role in promoting phase-separated ribonucleoprotein condensates, as observed in Caulobacter crescentus[19]. In E. coli, we also observed a modest increase in the clustering tendency of RNE compared to ΔCTD (Fig. S8). 

Some statements in the Discussion require support with example calculations or toning down substantially. Specifically, it is not clear how the authors conclude that RNaseE interacts with its substrate for a short time (and what this time may actually be); further, the speculation about the MTS "not being an efficient membrane-binding motif for diffusion" lacks adequate support as it stands. 

Thank you for these points. To elaborate our point on transient interaction between RNase E and RNA, we added a sentence “Specifically, if RNE interacts with mRNAs for ~20 ms or less, the slow-diffusing state would last shorter than the frame interval and remain undetected in our experiment.” Also, we added this sentence in the discussion.

One possible explanation is that RNA-bound RNE (and RNase Y) is short-lived compared to our frame interval (~20 ms), unlike other RNA-binding proteins related to transcription and translation, interacting with RNA for ~1 min for elongation [48].

Plus, we clarified the wording used in the second sentence that the reviewer pointed out as follows,

Lastly, the slow diffusion of the MTS in comparison to LacY2 and LacY6 suggests that MTS is less favorable for rapid lateral motion in the membrane. 

Reviewer #3 (Public review): 

Summary: 

The manuscript by Troyer et al quantitatively measured the membrane localization and diffusion of RNase E, an essential ribonuclease for mRNA turnover as well as tRNA and rRNA processing in bacteria cells. Using single-molecule tracking in live E. coli cells, the authors investigated the impact of membrane targeting sequence (MTS) and the Cterminal domain (CTD) on the membrane localization and diffusion of RNase E under various perturbations. Finally, the authors tried to correlate the membrane localization of RNase E to its function on co- and post-transcriptional mRNA decay using lacZ mRNA as a model. 

The major findings of the manuscripts include: 

(1) WT RNase E is mostly membrane localized via MTS, confirming previous results. The diffusion of RNase E is increased upon removal of MTS or CTD, and more significantly increased upon removal of both regions. 

(2) By tagging RNase E MTS and different lengths of LacY transmembrane domain (LacY2, LacY6, or LacY12) to mEos3.2, the results demonstrate that short LacY transmembrane sequence (LacY2 and LacY6) can increase the diffusion of mEos3.2 on the membrane compared to MTS, further supported by the molecular dynamics simulation. A similar trend was roughly observed in RNase E mutants with MTS switched to LacY transmembrane domains. 

(3) The removal of RNase E MTS significantly increases the co-transcriptional degradation of lacZ mRNA, but has minimal effect on the post-transcriptional degradation of lacZ mRNA. Removal of CTD of RNase E overall decreases the mRNA decay rates, suggesting the synergistic effect of CTD on RNase E activity. 

Strengths: 

(1) The manuscript is clearly written with very detailed method descriptions and analysis parameters. 

(2) The conclusions are mostly supported by the data and analysis. 

(3) Some of the main conclusions are interesting and important for understanding the cellular behavior and function of RNase E. 

Thank you for your thorough summary of our work and positive comments.

Weaknesses: 

(1) Some of the observations show inconsistent or context-dependent trends that make it hard to generalize certain conclusions. Those points are worth discussion at least. Examples include: 

(a) The authors conclude that MTS segment exhibits reduced MB% when succinate is used as a carbon source compared to glycerol, whereas LacY2 segment maintains 100% membrane localization, suggesting that MTS can lose membrane affinity in the former growth condition (Ln 341-342). However, the opposite case was observed for the WT RNase E and RNase E-LacY2-CTD, in which RNase E-LacY2-CTD showed reduced MB% in the succinate-containing M9 media compared to the WT RNase E (Ln 264-267). This opposite trend was not discussed. In the absence of CTD, would the media-dependent membrane localization be similar to the membrane localization sequence or to the fulllength RNase E? 

This is a great point. Thank you for pointing out the discrepancy in data. We think the weak membrane interaction of RNaseE-lacY2-CTD likely stems from the structure instability in the presence of the CTD. Our data shows that an RNase E variant with a cytoplasmic population under a normal growth condition exhibits a greater cytoplasmic fraction in a poor growth media. In contrast, RNaseE-MTS and RNaseE-LacY2 lacking the CTD both showed 100% MB% under both normal and poor growth conditions. These results are presented in Figure S6 and further discussed in the Discussion section.

The loss of MB% in LacY2-based RNE was observed only in the presence of the CTD (Fig. S6D), suggesting that the CTD negatively affects membrane binding of RNE, possibly by altering protein conformation. In fact, all ΔCTD RNE mutants we tested exhibited higher MB% than their CTD-containing counterparts (Fig. S6A-B). 

(b) When using mEos3.2 reporter only, LacY2 and LacY6 both increase the diffusion of mEos3.2 compared to MTS. However, when inserting the LacY transmembrane sequence into RNase E or RNase E without CTD, only the LacY2 increases the diffusion of RNase E. This should also be discussed. 

Thank you for raising this point. As the reviewer pointed out, as the membrane motifs, both LacY2 and LacY6 diffuse faster than the MTS, but when they are fused to RNE, only LacY2-based RNE diffuses faster than MTS-based RNE. We speculate that it is possibly due to a structural reason—having four (large) LacY6 in a tetrameric arrangement may cancel out the original fast-diffusing property of LacY6. We added this idea in the result section:

This result may be due to the high TM load (24 helices) created by four LacY6 anchors in the RNE tetramer. Although all constructs are tetrameric, the 24-helix load (LacY6), compared with 8 (LacY2) and 4 (MTS), likely enlarges the membrane-embedded footprint and increases drag, thereby changing the mobility advantages assessed as standalone membrane anchors.

(2) The authors interpret that in some cases the increase in the diffusion coefficient is related to the increase in the cytoplasm localization portion, such as for the LacY2 inserted RNase E with CTD, which is rational. However, the authors can directly measure the diffusion coefficient of the membrane and cytoplasm portion of RNase E by classifying the trajectories based on their localizations first, rather than just the ensemble calculation. 

Thank you for this suggestion. Currently, because of the 2D projection effect from imaging, we cannot clearly distinguish which individual tracks are from the cytoplasm or from the inner membrane based on the localization. Therefore, we are unable to assign individual tracks as membrane-bound or cytoplasmic. However, we can demonstrate that the xNorm data can be separated into two different spatial populations based on the diffusion coefficient. D. That is we can plot xNorm of slow tracks vs xNorm of fast tracks. This analysis showed that the slow tracks have LacY-like xNorm profiles while the fast tracks have LacZ-like xNorm profiles, also quantitatively supporting our MB% fitting results. We have added this analysis to Figure S2.

(3) The error bars of the diffusion coefficient and MB% are all SEM from bootstrapping, which are very small. I am wondering how much of the difference is simply due to a batch effect. Were the data mixed from multiple biological replicates? The number of biological replicates should also be reported. 

Thank you for raising this point. In the original manuscript, we reported the number of tracks analyzed and noted that all data was from at least three separate biological replicates (measurements were repeated at least three different days). Furthermore, in the revised manuscript, we have provided the number of cells imaged in Table S6. 

(4) Some figures lack p-values, such as Figures 4 and 5C-D. Also, adding p-values directly to the bar graphs will make it easier to read. 

Thank you for checking these details. We added p values in the graphs showing k_d1 and k_d2 (Table S7).

Reviewer #2 (Recommendations for the authors): 

Minor and technical points: 

(1) Clarity and flow will be improved if each section first highlights the objective for the experiments that are described (e.g., line 240). 

Thank you for the suggestion. We addressed this point by editing the beginning of each subsection in the Results. 

(2) Line 272 (and elsewhere)."1.33-times faster is wrong". The authors mean 33% faster (from 0.075 to 1, see Figure 4G), and not 133% faster. Needs fixing. 

Thanks for pointing this out. We changed this as well as other incidences where we talk about the fold difference. For example, this particular incidence was changed to:

Indeed, in the absence of the CTD, we found that the D of LacY2-based RNE was 1.33 ± 0.01 times as fast as the MTS-based RNE. 

(3) The authors need to consider the fitting of two species on their D population. e.g., how will a 93% - 7% split between diffusive species would have looked for the distribution in S4B? Note also the L1 profile in Fig S4C - while it is not hugely different from Figure S4B, the analysis gives a 41% amplitude for the fast-diffusing species. The 2-species analysis can also be used on some of the samples with much higher cytoplasmic components. Further, tracks that are in the more central region can be analysed to see whether the fast-diffusing species increase in amplitude. 

Thank you for this comment. The D histograms of L1 and RNase E show a dominant peak at around 0.015, but L1 has a residual population in the shoulder (note the difference between L1’s experimental data and D1 fit, a yellow line in now Figure S3B). This residual shoulder population is absent in the D histogram of RNase E. We also performed two-species analysis as suggested by the reviewer and provided the result in Figure S3C. The analysis shows that the two-population fit (black line) is very close to one one-population fit (yellow line). While we agree with the reviewer that subpopulation analysis is helpful for other proteins that show <90% MB% (>10% significant cytoplasmic population). we found it useful to divide xNorm histogram into two populations based on the diffusivity (rather than doing two-population fit to the D histogram, which does not have spatial information). This analysis, shown in Figure S2, supports our MB% fit results.

(4) The authors suggest that the sequestration of RNaseE to the membrane limits its interaction with cytoplasmic mRNAs, and may increase mRNA lifetime. While this is true and supported by the authors' preprint (Ref15), it will also be good to consider (and discuss) that highly-transcribed regions are in the nucleoid periphery (and thus close to the membrane) and that ribosomes/polysomes are likewise predominantly peripheral (coregulation of transcription/translation) and membrane proximal. 

This is an interesting point, which we appreciate very much. The lacZ gene, when induced, is shown to move to the nucleoid periphery (Yang et al. 2019, Nat Comm). Also, in our preprint (Ref 15), we engineered to have lacZ closer to the membrane, by translationally fusing it to lacY. However, the degradation rate of lacZ mRNA was not enhanced by the proximity to the membrane (for both k<Sub>d1</sub> and k_d2). For lacZ mRNA, we mainly see the change in k_d1 when RNE localization changes. We think it is due to the slow diffusion of the nascent mRNA (attached to the chromosome) and the slow diffusion of membrane-bound RNE, such that regardless of the location of the nascent mRNA, the degradation by the membrane-bound RNE is inefficient. Only when RNE is free diffusing in the cytoplasm, it seems to increase k_d1 (the decay of nascent mRNAs).

Reviewer #3 (Recommendations for the authors):

(1) It will increase the clarity of the manuscript if the authors can provide better nomenclatures for different constructs, such as for different membrane targeting sequences fused to mEos3.2, full-length RNase E, or CDT truncated RNaseE. 

Thank you for this suggestion. We agree that many constructions were discussed, and their naming can be confusing. To help with clarity, we have abbreviated RNase E as RNE throughout the text where appropriate. 

(2) Line 342, Figure S7D should be cited instead of S6D. 

Thank you for finding this error. We made a proper change in the revised manuscript.

Author response:

Reviewer #1 (Public review):

Summary:

The authors describe the results of a single study designed to investigate the extent to which horizontal orientation energy plays a key role in supporting view-invariant face recognition. The authors collected behavioral data from adult observers who were asked to complete an old/new face matching task by learning broad-spectrum faces (not orientation filtered) during a familiarization phase and subsequently trying to label filtered faces as previously seen or novel at test. This data revealed a clear bias favoring the use of horizontal orientation energy across viewpoint changes in the target images. The authors then compared different ideal observer models (cross-correlations between target and probe stimuli) to examine how this profile might be reflected in the image-level appearance of their filtered images. This revealed that a model looking for the best matching face within a viewpoint differed substantially from human data, exhibiting a vertical orientation bias for extreme profiles. However, a model forced to match targets to probes at different viewing angles exhibited a consistent horizontal bias in much the same manner as human observers.

Strengths:

I think the question is an important one: The horizontal orientation bias is a great example of a low-level image property being linked to high-level recognition outcomes, and understanding the nature of that connection is important. I found the old/new task to be a straightforward task that was implemented ably and that has the benefit of being simple for participants to carry out and simple to analyze. I particularly appreciated that the authors chose to describe human data via a lower-dimensional model (their Gaussian fits to individual data) for further analysis. This was a nice way to express the nature of the tuning function, favoring horizontal orientation bias in a way that makes key parameters explicit. Broadly speaking, I also thought that the model comparison they include between the view-selective and view-tolerant models was a great next step. This analysis has the potential to reveal some good insights into how this bias emerges and ask finegrained questions about the parameters in their model fits to the behavioral data.

We thank the reviewer for their positive appraisal of the importance of our research question as well as of the soundness of our approach to it.

Weaknesses:

I will start with what I think is the biggest difficulty I had with the paper. Much as I liked the model comparison analysis, I also don't quite know what to make of the view-tolerant model. As I understand the authors' description, the key feature of this model is that it does not get to compare the target and probe at the same yaw angle, but must instead pick a best match from candidates that are at different yaws. While it is interesting to see that this leads to a very different orientation profile, it also isn't obvious to me why such a comparison would be reflective of what the visual system is probably doing. I can see that the view-specific model is more or less assuming something like an exemplar representation of each face: You have the opportunity to compare a new image to a whole library of viewpoints, and presumably it isn't hard to start with some kind of first pass that identifies the best matching view first before trying to identify/match the individual in question. What I don't get about the view-tolerant model is that it seems almost like an anti-exemplar model: You specifically lack the best viewpoint in the library but have to make do with the other options. Again, this is sort of interesting and the very different behavior of the model is neat to discuss, but it doesn't seem easy to align with any theoretical perspective on face recognition. My thinking here is that it might be useful to consider an additional alternate model that doesn't specifically exclude the best-matching viewpoint, but perhaps condenses appearance across views into something like a prototype. I could even see an argument for something like the yaw-averages presented earlier in the manuscript as the basis for such a model, but this might be too much of a stretch. Overall, what I'd like to see is some kind of alternate model that incorporates the existence of the best-match viewpoint somehow, but without the explicit exemplar structure of the view-specific model.

The view-tolerant model was designed so that identity needed to be abstracted away from variations in yaw to support face recognition. We believe this model aligns with the notion of tolerant recognition.

The tolerance of identity recognition is presumably empowered by the internal representation of the natural statistics of identity, i.e. the stable traits and (idiosyncratic) variability of a face, which builds up through the varied encounters with a given face (Burton, Jenkins et al. 2005, Burton, Jenkins and Schweinberger 2011, Jenkins and Burton 2011, Jenkins, White et al. 2011, Burton, Kramer et al. 2016, Menon, Kemp and White 2018).

The average of various images of a face provides its appearance distribution (i.e., variability) and central tendency (i.e., stable properties; Figure 1) and could be used as a reasonable proxy of its natural statistical properties (Burton, Jenkins et al. 2005). We thus believe that the alternate model proposed by the reviewer is relevant to existing theories of face identity recognition and agree that our current model observers do not fully capture this aspect. It is thus an excellent idea to examine the orientation tuning profile of a model observer that compares a specific view of a face to the average encompassing all views of a face identity. Since the horizontal range is proposed to carry the view-stable cues to identity, we expect that such a ‘viewpoint-average’ model observer will perform best with horizontally filtered faces and that its orientation tuning profile will significantly predict human performance across views. We expect the viewpointtolerant and viewpoint-average observers will behave similarly as they manifest the stability of the horizontal identity cues across variations in viewpoint.

Besides this larger issue, I would also like to see some more details about the nature of the crosscorrelation that is the basis for this model comparison. I mostly think I get what is happening, but I think the authors could expand more on the nature of their noise model to make more explicit what is happening before these cross-correlations are taken. I infer that there is a noise-addition step to get them off the ceiling, but I felt that I had to read between the lines a bit to determine this.

The view-selective model responded correctly whenever successfully matching a given face identity at a specific viewpoint to itself. Since there was an exact match in each trial, resulting in uninformative ceiling performance, we decreased the signal-to-noise ratio (SNR) of the target and probe images to .125 (face RMS contrast: .01; noise RMS contrast: .08). In every trial, target and probe faces were each combined with 10 different random noise patterns. SNR was adjusted so that the overall performance of the view-selective model was in the range of human performance. We will describe these important aspects in the methods and add a supplemental with the graphic illustration of the d’ distributions of each model and human observers.

Another thing that I think is worth considering and commenting on is the stimuli themselves and the extent to which this may limit the outcomes of their behavioral task. The use of the 3D laserscanned faces has some obvious advantages, but also (I think) removes the possibility for pigmentation to contribute to recognition, removes the contribution of varying illumination and expression to appearance variability, and perhaps presents observers with more homogeneous faces than one typically has to worry about. I don't think these negate the current results, but I'd like the authors to expand on their discussion of these factors, particularly pigmentation. Naively, surface color and texture seem like they could offer diagnostic cues to identity that don't rely so critically on horizontal orientations, so removing these may mean that horizontal bias is particularly evident when face shape is the critical cue for recognition.

We indeed got rid of surface color by converting images to gray scales. While we acknowledge that the conversion to grayscales may have removed one potential source of surface information, it is unlikely that our stimuli fully eliminated the contribution of surface pigmentation in our study. Pigmentation refers to all surface reflectance property (Russell, Sinha et al. 2006) and hue (color) is only one surface cue among others. The grayscaled 3D laser scanned faces used here still contained natural variations in crucial surface cues such as skin albedo (i.e., how light or dark the surface appears) and texture (i.e., spatial variation in how light is reflected). Both color and grayscale stimuli (2D face pictures or 3D laser scanned faces like ours) have actually been used to disentangle the role of shape and surface cues to identity recognition (e.g., Troje and Bulthoff 1996, Vuong, Peissig et al. 2005, Russell, Sinha et al. 2006, Russell, Biederman et al. 2007, Jiang, Dricot et al. 2009).

More fundamentally, we demonstrated that the diagnosticity of the horizontal range of face information is not restricted to the transmission of shape cues. Our recent work has indeed shown that the processing of both face shape and surface most critically relies on horizontal information (Dumont, Roux-Sibilon and Goffaux 2024).

Reviewer #2 (Public review):

This study investigates the visual information that is used for the recognition of faces. This is an important question in vision research and is critical for social interactions more generally. The authors ask whether our ability to recognise faces, across different viewpoints, varies as a function of the orientation information available in the image. Consistent with previous findings from this group and others, they find that horizontally filtered faces were recognised better than vertically filtered faces. Next, they probe the mechanism underlying this pattern of data by designing two model observers. The first was optimised for faces at a specific viewpoint (viewselective). The second was generalised across viewpoints (view-tolerant). In contrast to the human data, the view-specific model shows that the information that is useful for identity judgements varies according to viewpoint. For example, frontal face identities are again optimally discriminated with horizontal orientation information, but profiles are optimally discriminated with more vertical orientation information. These findings show human face recognition is biased toward horizontal orientation information, even though this may be suboptimal for the recognition of profile views of the face.

One issue in the design of this study was the lowering of the signal-to-noise ratio in the viewselective observer. This decision was taken to avoid ceiling effects. However, it is not clear how this affects the similarity with the human observers.

The view-selective model responded correctly whenever successfully matching a given face identity at a specific viewpoint to itself. Since there was an exact match in each trial, resulting in uninformative ceiling performance, we decreased the signal-to-noise ratio (SNR) of the target and probe images to .125 (face RMS contrast: .01; noise RMS contrast: .08). In every trial, target and probe faces were each combined with 10 different random noise patterns. SNR was adjusted so that the overall performance of the view-selective model was in the range of human performance. We will describe these important aspects in the methods and add a supplemental with the graphic illustration of the d’ distributions of each model and human observers.

Another issue is the decision to normalise image energy across orientations and viewpoints. I can see the logic in wanting to control for these effects, but this does reflect natural variation in image properties. So, again, I wonder what the results would look like without this step.

Energy of natural images is disproportionately distributed across orientations (e.g., Hansen, Essock et al. 2003). Images of faces cropped from their background as used here contain most of their energy in the horizontal range (Keil 2009, Goffaux and Greenwood 2016, Goffaux 2019). If not normalized after orientation filtering, such uneven distribution of energy would boost recognition performance in the horizontal range across views. Normalization was performed across our experimental conditions merely to avoid energy from explaining the influence of viewpoint on the orientation tuning profile.

We are not aware of any systematic natural variations of energy across face views. To address this, we measured face average energy (i.e., RMS contrast) in the original stimulus set, i.e., before the application of any image processing or manipulation. Background pixels were excluded from these image analyses. Across yaws, we found energy to range between .11 and .14 on a 0 to 1 grayscale. This is moderate compared to the range of energy variations we measured across identities (from .08 to .18). This suggests that variations in energy across viewpoints are moderate compared to variations related to identity. It is unclear whether these observations are specific to our stimulus set or whether they are generalizable to faces we encounter in everyday life. They, however, indicate that RMS contrast did not substantially vary across views in the present study and suggest that RMS normalization is unlikely to have affected the influence of viewpoint on recognition performance.

Nonetheless, we acknowledge the importance of this issue regarding the trade-off between experimental control and stimulus naturalness, and we will refer to it explicitly in the methods section.

Despite the bias toward horizontal orientations in human observers, there were some differences in the orientation preference at each viewpoint. For example, frontal faces were biased to horizontal (90 degrees), but other viewpoints had biases that were slightly off horizontal (e.g., right profile: 80 degrees, left profile: 100 degrees). This does seem to show that differences in statistical information at different viewpoints (more horizontal information for frontal and more vertical information for profile) do influence human perception. It would be good to reflect on this nuance in the data.

Indeed, human performance data indicates that while identity recognition remains tuned to horizontal information, horizontal tuning shows some variation across viewpoints. We primarily focused on the first aspect because of its direct relevance to our research objective, but also discussed the second aspect: with yaw rotation, certain non-horizontal morphological features such as the jaw line or nose bridge, etc. may increasingly contribute to identity recognition, whereas at frontal or near frontal views, features are mostly horizontally-oriented (e.g., Keil 2008, Keil 2009). We will relate this part of the discussion more explicitly to the observation of the fluctuation of the peak location as a function of yaw.

Author response:

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

Reviewer 1:

The authors frequently refer to their predictions and theory as being causal, both in the manuscript and in their response to reviewers. However, causal inference requires careful experimental design, not just statistical prediction. For example, the claim that "algorithmic differences between those with BPD and matched healthy controls" are "causal" in my opinion is not warranted by the data, as the study does not employ experimental manipulations or interventions which might predictably affect parameter values. Even if model parameters can be seen as valid proxies to latent mechanisms, this does not automatically mean that such mechanisms cause the clinical distinction between BPD and CON, they could plausibly also refer to the effects of therapy or medication. I recommend that such causal language, also implicit to expressions like "parameter influences on explicit intentional attributions", is toned down throughout the manuscript.

Thankyou for this chance to be clearer in the language. Our models and paradigm introduce a from of temporal causality, given that latent parameter distributions are directly influenced by latent parameter estimates at a previous point in time (self-uncertainty and other uncertainty directly governs social contagion). Nevertheless, we appreciate the reviewers perspective and have now toned down the language to reflect this.

Abstract:

‘Our model makes clear predictions about the mechanisms of social information generalisation concerning both joint and individual reward.’

Discussion:

‘We can simulate this by modelling a framework that incorporates priors based on both self and a strong memory impression of a notional other (Figure S3).’

‘We note a strength of this work is the use of model comparison to understand algorithmic differences between those with BPD and matched healthy controls.’

Although the authors have now much clearer outlined the stuy's aims, there still is a lack of clarity with respect to the authors' specific hypotheses. I understand that their primary predictions about disruptions to self-other generalisation processes underlying BPD are embedded in the four main models that are tested, but it is still unclear what specific hypotheses the authors had about group differences with respect to the tested models. I recommend the authors specify this in the introduction rather than refering to prior work where the same hypotheses may have been mentioned.

Thankyou for this further critique which has enabled us to more cleary refine our introduction. We have now edited our introduction to be more direct about our hypotheses, that these hypotheses are instantiated into formal models, and what our predictions were. We have also included a small section on how previous predictions from other computational assessments of BPD link to our exploratory work, and highlighted this throughout the manuscript.

‘This paper seeks to address this gap by testing explicitly how disruptions in self-other generalization processes may underpin interpersonal disruptions observed in BPD. Specifically, our hypotheses were: (i) healthy controls will demonstrate evidence for both self-insertion and social contagion, integrating self and other information during interpersonal learning; and (ii) individuals with BPD will exhibit diminished self-other integration, reflected in stronger evidence for observations that assume distinct self-other representations.

We tested these hypotheses by designing a dynamic, sequential, three-phase Social Value Orientation (Murphy & Ackerman, 2014) paradigm—the Intentions Game—that would provide behavioural signatures assessing whether BPD differed from healthy controls in these generalization processes (Figure 1A). We coupled this paradigm with a lattice of models (M1-M4) that distinguish between self-insertion and social contagion (Figure 1B), and performed model comparison:

M1. Both self-to-other (self-insertion) and other-to-self (social contagion) occur before and after learning M2. Self-to-other transfer only occurs M3. Other-to-self transfer only occurs M4. Neither transfer process, suggesting distinct self-other representations

We additionally ran exploratory analysis of parameter differences and model predictions between groups following from prior work demonstrating changes in prosociality (Hula et al., 2018), social concern (Henco et al., 2020), belief stability (Story et al., 2024a), and belief updating (Story, 2024b) in BPD to understand whether discrepancies in self-other generalisation influences observational learning. By clearly articulating our hypotheses, we aim to clarify the theoretical contribution of our findings to existing literature on social learning, BPD, and computational psychiatry.’

Caveats should also be added about the exploratory nature of the many parameter group comparisons. If there are any predictions about group differences that can be made based on prior literature, the authors should make such links clear.

Thank you for this. We have now included caveats in the text to highlight the exploratory nature of these group comparisons, and added direct links to relevant literature where able:

Introduction

‘We additionally ran exploratory analysis of parameter differences and model predictions between groups following from prior work demonstrating changes in prosociality (Hula et al., 2018), social concern (Henco et al., 2020), belief stability (Story et al., 2024a), and belief updating (Story, 2024b) in BPD to understand whether discrepancies in self-other generalisation influences observational learning. By clearly articulating our hypotheses, we aim to clarify the theoretical contribution of our findings to existing literature on social learning, BPD, and computational psychiatry.’

Model Comparison

‘We found that CON participants were best fit at the group level by M1 (Frequency = 0.59, Exceedance Probability = 0.98), whereas BPD participants were best fit by M4 (Frequency = 0.54, Exceedance Probability = 0.86; Figure 2A). This suggests CON participants are best fit by a model that fully integrates self and other when learning, whereas those with BPD are best explained as holding disintegrated and separate representations of self and other that do not transfer information back and forth.

We first explore parameters between separate fits (see Methods). Later, in order to assuage concerns about drawing inferences from different models, we examined the relationships between the relevant parameters when we forced all participants to be fit to each of the models (in a hierarchical manner, separated by group). In sum, our model comparison is supported by convergence in parameter values when comparisons are meaningful (see Supplementary Materials). We refer to both types of analysis below.’

Phase 2 analysis

‘Prior work predicts those with BPD should focus more intently on public social information, rather than private information that only concerns one party (Henco et al., 2020). In BPD participants, only new beliefs about the relative reward preferences – mutual outcomes for both player - of partners differed (see Fig 2E): new median priors were larger than median preferences in phase 1 (mean = -0.47; = -6.10, 95%HDI: -7.60, -4.60).’

‘Models of moral preference learning (Story et al., 2024) predicts that BPD vs non-BPD participants have more rigid beliefs about their partners. We found that BPD participants were equally flexible around their prior beliefs about a partner’s relative reward preferences (= -1.60, 95%HDI: -3.42, 0.23), and were less flexible around their beliefs about a partner’s absolute reward preferences (=-4.09, 95%HDI: -5.37, -2.80), versus CON (Figure 2B).’

Phase 3 analysis

‘Prior work predicts that human economic preferences are shaped by observation (Panizza, et al., 2021; Suzuki et al. 2016; Yu et al, 2021), although little-to-no work has examined whether contagion differs for relative vs. absolute preferences. Associative models predict that social contagion may be exaggerated in BPD (Ereira et al., 2018).… As a whole, humans are more susceptible to changing relative preferences more than selfish, absolute reward preferences, and this is disrupted in BPD.’

Psychometric and Intentional Attribution analysis

‘Childhood trauma, persecution, and poor mentalising in BPD are all predicted to disrupt one’s ability to change (Fonagy & Luyten, 2009).’

‘Prior work has also predicted that partner-participant preference disparity influences mental state attributions (Barnby et al., 2022; Panizza et al., 2021).’

I'm not sure I understand why the authors, after adding multiple comparison correction, now list two kinds of p-values. To me, this is misleading and precludes the point of multiple comparison corrections, I therefore recommend they report the FDR-adjusted p-values only. Likewise, if a corrected p-value is greater than 0.05 this should not be interpreted as a result.

We have now adjusted the exploratory results to include only the FDR corrected values in the text.

‘We assessed conditional psychometric associations with social contagion under the assumption of M3 for all participants. We conducted partial correlation analyses to estimate relationships conditional on all other associations and retained all that survived bootstrapping (5000 reps), permutation testing (5000 reps), and subsequent FDR correction. When not controlled for group status, RGPTSB and CTQ scores were both moderately associated with MZQ scores (RGPTSB r = 0.41, 95%CI: 0.23, 0.60, p[fdr]=0.043; CTQ r = 0.354 95%CI: 0.13, 0.56, p[fdr]=0.02). This was not affected by group correction. CTQ scores were moderately and negatively associated with shifts in individualistic reward preferences (; r = -0.25, 95%CI: -0.46, -0.04, p[fdr]=0.03). This was not affected by group correction. MZQ scores were in turn moderately and negatively associated with shifts in prosocial-competitive preferences () between phase 1 and 3 (r = -0.26, 95%CI: -0.46, -0.06, p[fdr]=0.03). This was diminished when controlled for group status (r = 0.13, 95%CI: -0.34, 0.08, p[fdr]=0.20). Together this provides some evidence that self-reported trauma and self-reported mentalising influence social contagion (Fig S11). Social contagion under M3 was highly correlated with contagion under M1 demonstrating parsimony of outcomes across models (Fig S12).

Prior work has predicted that partner-participant preference disparity influences mental state attributions (Barnby et al., 2022; Panizza et al., 2021). We tested parameter influences on explicit intentional attributions in Phase 2 while controlling for group status. Attributions included the degree to which they believed their partner was motived by harmful intent (HI) and self-interest (SI). According with prior work (Barnby et al., 2022), greater disparity of absolute preferences before learning was associated on a trend level with reduced attributions of SI (<= -0.23, p[fdr]=0.08), and greater disparity of relative preferences before learning exaggerated attributions of HI = 0.21, p[fdr]=0.08), but did not survive correction (Figure S4B). This is likely due to partners being significantly less individualistic and prosocial on average compared to participants (= -5.50, 95%HDI: -7.60, -3.60; = 12, 95%HDI: 9.70, 14.00); partners are recognised as less selfish and more competitive.’

Can the authors please elaborate why the algorithm proposed to be employed by BPD is more 'entropic', especially given both their self-priors and posteriors about partners' preferences tended to be more precise than the ones used by CON? As far as I understand, there's nothing in the data to suggest BPD predictions should be more uncertain. In fact, this leads me to wonder, similarly to what another reviewer has already suggested, whether BPD participants generate self-referential priors over others in the same way CON participants do, they are just less favourable (i.e., in relation to oneself, but always less prosocial) - I think there is currently no model that would incorporate this possibility? It should at least be possible to explore this by checking if there is any statistical relationship between the estimated θ_ppt^m and 〖p(θ〗_par |D^0).

Thank you for this opportunity to be clearer in our wording. We belief the reviewer is referring to this line in the discussion: ‘In either case, the algorithm underlying the computational goal for BPD participants is far higher in entropy and emphasises a less stable or reliable process of inference.’

We note in the revised Figure 2 panel E and in the results that those with BPD under M4 show insertion along absolute reward (they still expect diminished selfishness in others), but neutral priors over relative reward (around 0, suggesting expectations of neither prosocial or competitive tendencies of others). Thus, θ_ppt^m (self preference) and θ_par^m (other preference) are tightly associated for absolute, but not relative reward.

In our wording, we meant that whether under model M4 or M1, those with BPD either show a neutral prior over relative reward (M4) or a prior with large variance over relative reward (M1), showing expectations of difference between themselves and their partner. In both cases, expectation about a partner’s absolute reward preferences is diminished vs. CON participants. We have strengthened our language in the discussion to clarify this:

‘In either case, the algorithm underlying the computational goal for BPD participants is far higher in uncertainty, whether through a neutral central tendency (M4) or large variance (M1) prior over relative reward in phase 2, and emphasises a less certain and reliable expectation about others.’

To note, social contagion under M3 was highly correlated with contagion under M1 (see Fig S11). This provides some preliminary evidence that trauma impacts beliefs about individualism directly, whereas trauma and persecutory beliefs impact beliefs about prosociality through impaired trait mentalising" - I don't understand what the authors mean by this, can they please elaborate and add some explanation to the main text?

We have now clarified this in the text:

‘Together this provides some evidence that self-reported trauma and self-reported mentalising influence social contagion (Fig S11). Social contagion under M3 was highly correlated with contagion under M1 demonstrating parsimony of outcomes across models (Fig S12).’

I noted that at least some of the newly added references have not been added to the bibliography (e.g., Hitchcock et al. 2022).

Thankyou for noticing this omission. We have now ensured all cited works are in the reference list.

Reviewer 2:

The paper is not based on specific empirical hypotheses formulated at the outset, but, rather, it uses an exploratory approach. Indeed, the task is not chosen in order to tackle specific empirical hypotheses. This, in my view, is a limitation since the introduction reads a bit vague and it is not always clear which gaps in the literature the paper aims to fill. As a further consequence, it is not always clear how the findings speak to previous theories on the topic.’

As I wrote in the public review, however, I believe that an important limitation of this work is that it was not based on testing specific empirical hypotheses formulated at the outset, and on selecting the experimental paradigm accordingly. This is a limitation because it is not always clear which gaps in the literature the paper aims to fill. As a consequence, although it has improved substantially compared to the previous version, the introduction remains a bit vague. As a further consequence, it is not always clear how the findings speak to previous theories on the topic. Still, despite this limitation, the paper has many strengths, and I believe it is now ready for publication

Thank you for this further critique. We appreciate your appraisal that the work has improved substantially and is ready for publication. We nevertheless have opted to clarify our introduction and aprior predictions throughout the manuscript (please see response to Reviewer 1).

Reviewer 3:

Although the authors note that their approach makes "clear and transparent a priori predictions," the paper could be improved by providing a clear and consolidated statement of these predictions so that the results could be interpreted vis-a-vis any a priori hypotheses.

In line with comments from both Reviewer 1 and 2, we have clarified our introduction to make it clear what our aprior predictions and hypotheses are about our core aims and exploratory analyses (see response to Reviewer 1).

The approach of using a partial correlation network with bootstrapping (and permutation) was interesting, but the logic of the analysis was not clearly stated. In particular, there are large group (Table 1: CON vs. BPD) differences in the measures introduced into this network. As a result, it is hard to understand whether any partial correlations are driven primarily by mean differences in severity (correlations tend to be inflated in extreme groups designs due to the absence of observation in middle of scales forming each bivariate distribution). I would have found these exploratory analyses more revealing if group membership was controlled for.

Thank you for this chance to be clearer in our methods. We have now written a more direct exposition of this exploratory method:

‘Exploratory Network Analysis

To understand the individual differences of trait attributes (MZQ, RGPTSB, CTQ) with other-to-self information transfer () across the entire sample we performed a network analysis (Borsboom, 2021). Network analysis allows for conditional associations between variables to be estimated; each association is controlled for by all other associations in the network. It also allows for visual inspection of the conditional relationships to get an intuition for how variables are interrelated as a whole (see Fig S11). We implemented network analysis with the bootNet package in r using the ‘estimateNetwork’ function with partial correlations (Epskamp, Borsboom & Fried, 2018). To assess the stability of the partial correlations we further implemented bootstrap resampling with 5000 repetitions using the ‘bootnet’ function. We then additionally shuffled the data and refitted the network 5000 times to determine a p_permuted value; this indicates the probability that a conditional relationship in the original network was within the null distribution of each conditional relationship. We then performed False Discovery Rate correction on the resulting p-values. We additionally controlled for group status for all variables in a supplementary analysis (Table S4).’

We have also further corrected for group status and reported these results as a supplementary table, and also within the main text alongside the main results. We have opted to relegate Figure 4 into a supplementary figure to make the text clearer.

‘We explored conditional psychometric associations with social contagion under the assumption of M3 for all participants (where everyone is able to be influenced by their partner). We conducted partial correlation analyses to estimate relationships conditional on all other associations and retained all that survived bootstrapping (5000 reps), permutation testing (5000 reps), and subsequent FDR correction. When not controlled for group status, RGPTSB and CTQ scores were both moderately associated with MZQ scores (RGPTSB r = 0.41, 95%CI: 0.23, 0.60, p[fdr]=0.043; CTQ r = 0.354 95%CI: 0.13, 0.56, p[fdr]=0.02). This was not affected by group correction. CTQ scores were moderately and negatively associated with shifts in individualistic reward preferences (; r = -0.25, 95%CI: -0.46, -0.04, p[fdr]=0.03). This was not affected by group correction. MZQ scores were in turn moderately and negatively associated with shifts in prosocial-competitive preferences () between phase 1 and 3 (r = -0.26, 95%CI: -0.46, -0.06, p[fdr]=0.03). This was diminished when controlled for group status (r = 0.13, 95%CI: -0.34, 0.08, p[fdr]=0.20). Together this provides some evidence that self-reported trauma and self-reported mentalising influence social contagion (Fig S11). Social contagion under M3 was highly correlated with contagion under M1 demonstrating parsimony of outcomes across models (Fig S12).’

Discussion first para: "effected -> affected"

Thanks for spotting this. We have now changed it.

Add "s" to "participant: "Notably, despite differing strategies, those with BPD achieved similar accuracy to CON participant."

We have now changed this.

Author response:

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

Reviewer #1 (Public review):

Summary:

Measurement of BOLD MR imaging has regularly found regions of the brain that show reliable suppression of BOLD responses during specific experimental testing conditions. These observations are to some degree unexplained, in comparison with more usual association between activation of the BOLD response and excitatory activation of the neurons (most tightly linked to synaptic activity) in the same brain location. This paper finds two patients whose brains were tested with both non-invasive functional MRI and with invasive insertion of electrodes, which allowed the direct recording of neuronal activity. The electrode insertions were made within the fusiform gyrus, which is known to process information about faces, in a clinical search for the sites of intractable epilepsy in each patient. The simple observation is that the electrode location in one patient showed activation of the BOLD response and activation of neuronal firing in response to face stimuli. This is the classical association. The other patient showed an informative and different pattern of responses. In this person, the electrode location showed a suppression of the BOLD response to face stimuli and, most interestingly, an associated suppression of neuronal activity at the electrode site.

Strengths:

Whilst these results are not by themselves definitive, they add an important piece of evidence to a long-standing discussion about the origins of the BOLD response. The observation of decreased neuronal activation associated with negative BOLD is interesting because, at various times, exactly the opposite association has been predicted. It has been previously argued that if synaptic mechanisms of neuronal inhibition are responsible for the suppression of neuronal firing, then it would be reasonable

Weaknesses:

The chief weakness of the paper is that the results may be unique in a slightly awkward way. The observation of positive BOLD and neuronal activation is made at one brain site in one patient, while the complementary observation of negative BOLD and neuronal suppression actually derives from the other patient. Showing both effects in both patients would make a much stronger paper.

We thank reviewer #1 for their positive evaluation of our paper. Obviously, we agree with the reviewer that the paper would be much stronger if BOTH effects – spike increase and decrease – would be found in BOTH patients in their corresponding fMRI regions (lateral and medial fusiform gyrus) (also in the same hemisphere). Nevertheless, we clearly acknowledge this limitation in the (revised) version of the manuscript (p.8: Material and Methods section).

Note that with respect to the fMRI data, our results are not surprising, as we indicate in the manuscript: BOLD increases to faces (relative to nonface objects) are typically found in the LatFG and BOLD decreases in the medialFG (in the revised version, we have added the reference to an early neuroimaging paper that describes this dissociation clearly:

Pelphrey, K. A., Mack, P. B., Song, A., Güzeldere, G., & McCarthy, G. Faces evoke spatially differentiated patterns of BOLD activation and deactivation. Neuroreport 14, 955–959 (2003).

This pattern of increase/decrease in fMRI can be appreciated in both patients on Figure 2, although one has to consider both the transverse and coronal slices to appreciate it.

Regarding electrophysiological data, in the current paper, one could think that P1 shows only increases to faces, and P2 would show only decreases (irrespective of the region). However, that is not the case since 11% of P1’s face-selective units are decreases (89% are increases) and 4% of P2’s face-selective units are increases. This has now been made clearer in the revised manuscript (p.5).

As the reviewer is certainly aware, the number and positions of the electrodes are based on strict clinical criteria, and we will probably never encounter a situation with two neighboring (macro-micro hybrid electrodes), one with microelectrodes ending up in the lateral MidFG, the other in the medial MidFG, in the same patient. If there is no clinical value for the patient, this cannot be done.

The only thing we can do is to strengthen these results in the future by collecting data on additional patients with an electrode either in the lateral or the medial FG, together with fMRI. But these are the only two patients we have been able to record so far with electrodes falling unambiguously in such contrasted regions and with large (and comparable) measures.

While we acknowledge that the results may be unique because of the use of 2 contrasted patients only (and this is why the paper is a short report), the data is compelling in these 2 cases, and we are confident that it will be replicated in larger cohorts in the future.

Finally, information regarding ethics approval has been provided in the paper.

Reviewer #2 (Public review):

Summary:

This is a short and straightforward paper describing BOLD fMRI and depth electrode measurements from two regions of the fusiform gyrus that show either higher or lower BOLD responses to faces vs. objects (which I will call face-positive and facenegative regions). In these regions, which were studied separately in two patients undergoing epilepsy surgery, spiking activity increased for faces relative to objects in the face-positive region and decreased for faces relative to objects in the face-negative region. Interestingly, about 30% of neurons in the face-negative region did not respond to objects and decreased their responses below baseline in response to faces (absolute suppression).

Strengths:

These patient data are valuable, with many recording sessions and neurons from human face-selective regions, and the methods used for comparing face and object responses in both fMRI and electrode recordings were robust and well-established. The finding of absolute suppression could clarify the nature of face selectivity in human fusiform gyrus since previous fMRI studies of the face-negative region could not distinguish whether face < object responses came from absolute suppression, or just relatively lower but still positive responses to faces vs. objects.

Weaknesses:

The authors claim that the results tell us about both 1) face-selectivity in the fusiform gyrus, and 2) the physiological basis of the BOLD signal. However, I would like to see more of the data that supports the first claim, and I am not sure the second claim is supported.

(1) The authors report that ~30% of neurons showed absolute suppression, but those data are not shown separately from the neurons that only show relative reductions. It is difficult to evaluate the absolute suppression claim from the short assertion in the text alone (lines 105-106), although this is a critical claim in the paper.

We thank reviewer #2 for their positive evaluation of our paper. We understand the reviewer’s point, and we partly agree. Where we respectfully disagree is that the finding of absolute suppression is critical for the claim of the paper: finding an identical contrast between the two regions in terms of RELATIVE increase/decrease of face-selective activity in fMRI and spiking activity is already novel and informative. Where we agree with the reviewer is that the absolute suppression could be more documented: it wasn’t, due to space constraints (brief report). We provide below an example of a neuron showing absolute suppression to faces (P2), as also requested in the recommendations to authors. In the frequency domain, there is only a face-selective response (1.2 Hz and harmonics) but no significant response at 6 Hz (common general visual response). In the time-domain, relative to face onset, the response drops below baseline level. It means that this neuron has baseline (non-periodic) spontaneous spiking activity that is actively suppressed when a face appears.

Author response image 1.

(2) I am not sure how much light the results shed on the physiological basis of the BOLD signal. The authors write that the results reveal "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain" (line 120). But I think to make this claim, you would need a region that exclusively had neurons showing absolute suppression, not a region with a mix of neurons, some showing absolute suppression and some showing relative suppression, as here. The responses of both groups of neurons contribute to the measured BOLD signal, so it seems impossible to tell from these data how absolute suppression per se drives the BOLD response.

It is a fact that we find both kinds of responses in the same region. We cannot tell with this technique if neurons showing relative vs. absolute suppression of responses are spatially segregated for instance (e.g., forming two separate sub-regions) or are intermingled. And we cannot tell from our data how absolute suppression per se drives the BOLD response. In our view, this does not diminish the interest and originality of the study, but the statement "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain” has been rephrased in the revised manuscript: "that BOLD decreases can be due to relative, or absolute (or a combination of both), spike suppression in the human brain”.

Reviewer #3 (Public review):

In this paper the authors conduct two experiments an fMRI experiment and intracranial recordings of neurons in two patients P1 and P2. In both experiments, they employ a SSVEP paradigm in which they show images at a fast rate (e.g. 6Hz) and then they show face images at a slower rate (e.g. 1.2Hz), where the rest of the images are a variety of object images. In the first patient, they record from neurons over a region in the mid fusiform gyrus that is face-selective and in the second patient, they record neurons from a region more medially that is not face selective (it responds more strongly to objects than faces). Results find similar selectivity between the electrophysiology data and the fMRI data in that the location which shows higher fMRI to faces also finds face-selective neurons and the location which finds preference to non faces also shows non face preferring neurons.

Strengths:

The data is important in that it shows that there is a relationship between category selectivity measured from electrophysiology data and category-selective from fMRI. The data is unique as it contains a lot of single and multiunit recordings (245 units) from the human fusiform gyrus - which the authors point out - is a humanoid specific gyrus.

Weaknesses:

My major concerns are two-fold:

(i) There is a paucity of data; Thus, more information (results and methods) is warranted; and in particular there is no comparison between the fMRI data and the SEEG data.

We thank reviewer #3 for their positive evaluation of our paper. If the reviewer means paucity of data presentation, we agree and we provide more presentation below, although the methods and results information appear as complete to us. The comparison between fMRI and SEEG is there, but can only be indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance). In addition, our manuscript aims at providing a short empirical contribution to further our understanding of the relationship between neural responses and BOLD signal, not to provide a model of neurovascular coupling.

(ii) One main claim of the paper is that there is evidence for suppressed responses to faces in the non-face selective region. That is, the reduction in activation to faces in the non-face selective region is interpreted as a suppression in the neural response and consequently the reduction in fMRI signal is interpreted as suppression. However, the SSVEP paradigm has no baseline (it alternates between faces and objects) and therefore it cannot distinguish between lower firing rate to faces vs suppression of response to faces.

We understand the concern of the reviewer, but we respectfully disagree that our paradigm cannot distinguish between lower firing rate to faces vs. suppression of response to faces. Indeed, since the stimuli are presented periodically (6 Hz), we can objectively distinguish stimulus-related activity from spontaneous neuronal firing. The baseline corresponds to spikes that are non-periodic, i.e., unrelated to the (common face and object) stimulation. For a subset of neurons, even this non-periodic baseline activity is suppressed, above and beyond the suppression of the 6 Hz response illustrated on Figure 2. We mention it in the manuscript, but we agree that we do not present illustrations of such decrease in the time-domain for SU, which we did not consider as being necessary initially (please see below for such presentation).

(1) Additional data: the paper has 2 figures: figure 1 which shows the experimental design and figure 2 which presents data, the latter shows one example neuron raster plot from each patient and group average neural data from each patient. In this reader's opinion this is insufficient data to support the conclusions of the paper. The paper will be more impactful if the researchers would report the data more comprehensively.

We answer to more specific requests for additional evidence below, but the reviewer should be aware that this is a short report, which reaches the word limit. In our view, the group average neural data should be sufficient to support the conclusions, and the example neurons are there for illustration. And while we cannot provide the raster plots for a large number of neurons, the anonymized data is made available at:

(a) There is no direct comparison between the fMRI data and the SEEG data, except for a comparison of the location of the electrodes relative to the statistical parametric map generated from a contrast (Fig 2a,d). It will be helpful to build a model linking between the neural responses to the voxel response in the same location - i.e., estimate from the electrophysiology data the fMRI data (e.g., Logothetis & Wandell, 2004).

As mentioned above the comparison between fMRI and SEEG is indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance) and would not allow to make such a model.

(b) More comprehensive analyses of the SSVEP neural data: It will be helpful to show the results of the frequency analyses of the SSVEP data for all neurons to show that there are significant visual responses and significant face responses. It will be also useful to compare and quantify the magnitude of the face responses compared to the visual responses.

The data has been analyzed comprehensively, but we would not be able to show all neurons with such significant visual responses and face-selective responses.

(c) The neuron shown in E shows cyclical responses tied to the onset of the stimuli, is this the visual response?

Correct, it’s the visual response at 6 Hz.

If so, why is there an increase in the firing rate of the neuron before the face stimulus is shown in time 0?

Because the stimulation is continuous. What is displayed at 0 is the onset of the face stimulus, with each face stimulus being preceded by 4 images of nonface objects.

The neuron's data seems different than the average response across neurons; This raises a concern about interpreting the average response across neurons in panel F which seems different than the single neuron responses

The reviewer is correct, and we apologize for the confusion. This is because the average data on panel F has been notch-filtered for the 6 Hz (and harmonic responses), as indicated in the methods (p.11): ‘a FFT notch filter (filter width = 0.05 Hz) was then applied on the 70 s single or multi-units time-series to remove the general visual response at 6 Hz and two additional harmonics (i.e., 12 and 18 Hz)’.

Here is the same data without the notch-filter (the 6Hz periodic response is clearly visible):

Author response image 2.

For sake of clarity, we prefer presenting the notch-filtered data in the paper, but the revised version makes it clear in the figure caption that the average data has been notch-filtered.

(d) Related to (c) it would be useful to show raster plots of all neurons and quantify if the neural responses within a region are homogeneous or heterogeneous. This would add data relating the single neuron response to the population responses measured from fMRI. See also Nir 2009.

We agree with the reviewer that this is interesting, but again we do not think that it is necessary for the point made in the present paper. Responses in these regions appear rather heterogenous, and we are currently working on a longer paper with additional SEEG data (other patients tested for shorter sessions) to define and quantify the face-selective neurons in the MidFusiform gyrus with this approach (without relating it to the fMRI contrast as reported here).

(e) When reporting group average data (e.g., Fig 2C,F) it is necessary to show standard deviation of the response across neurons.

We agree with the reviewer and have modified Figure 2 accordingly in the revised manuscript.

(f) Is it possible to estimate the latency of the neural responses to face and object images from the phase data? If so, this will add important information on the timing of neural responses in the human fusiform gyrus to face and object images.

The fast periodic paradigm to measure neural face-selectivity has been used in tens of studies since its original reports:

• in EEG: Rossion et al., 2015: https://doi.org/10.1167/15.1.18

• in SEEG: Jonas et al., 2016: https://doi.org/10.1073/pnas.1522033113

In this paradigm, the face-selective response spreads to several harmonics (1.2 Hz, 2.4 Hz, 3.6 Hz, etc.) (which are summed for quantifying the total face-selective amplitude). This is illustrated below by the averaged single units’ SNR spectra across all recording sessions for both participants.

Author response image 3.

There is no unique phase-value, each harmonic being associated with a phase-value, so that the timing cannot be unambiguously extracted from phase values. Instead, the onset latency is computed directly from the time-domain responses, which is more straightforward and reliable than using the phase. Note that the present paper is not about the specific time-courses of the different types of neurons, which would require a more comprehensive report, but which is not necessary to support the point made in the present paper about the SEEG-fMRI sign relationship.

(g) Related to (e) In total the authors recorded data from 245 units (some single units and some multiunits) and they found that both in the face and nonface selective most of the recoded neurons exhibited face -selectivity, which this reader found confusing: They write “ Among all visually responsive neurons, we found a very high proportion of face-selective neurons (p < 0.05) in both activated and deactivated MidFG regions (P1: 98.1%; N = 51/52; P2: 86.6%; N = 110/127)’. Is the face selectivity in P1 an increase in response to faces and P2 a reduction in response to faces or in both it’s an increase in response to faces

Face-selectivity is defined as a DIFFERENTIAL response to faces compared to objects, not necessarily a larger response to faces. So yes, face-selectivity in P1 is an increase in response to faces and P2 a reduction in response to faces.

Additional methods

(a) it is unclear if the SSVEP analyses of neural responses were done on the spikes or the raw electrical signal. If the former, how is the SSVEP frequency analysis done on discrete data like action potentials?

The FFT is applied directly on spike trains using Matlab’s discrete Fourier Transform function. This function is suitable to be applied to spike trains in the same way as to any sampled digital signal (here, the microwires signal was sampled at 30 kHz, see Methods).

In complementary analyses, we also attempted to apply the FFT on spike trains that had been temporally smoothed by convolving them with a 20ms square window (Le Cam et al., 2023, cited in the paper ). This did not change the outcome of the frequency analyses in the frequency range we are interested in. We have also added one sentence with information in the methods section about spike detection (p.10).

(b) it is unclear why the onset time was shifted by 33ms; one can measure the phase of the response relative to the cycle onset and use that to estimate the delay between the onset of a stimulus and the onset of the response. Adding phase information will be useful.

The onset time was shifted by 33ms because the stimuli are presented with a sinewave contrast modulation (i.e., at 0ms, the stimulus has 0% contrast). 100% contrast is reached at half a stimulation cycle, which is 83.33ms here, but a response is likely triggered before reaching 100% contrast. To estimate the delay between the start of the sinewave (0% contrast) and the triggering of a neural response, we tested 7 SEEG participants with the same images presented in FPVS sequences either as a sinewave contrast (black line) modulation or as a squarewave (i.e. abrupt) contrast modulation (red line). The 33ms value is based on these LFP data obtained in response to such sinewave stimulation and squarewave stimulation of the same paradigm. This delay corresponds to 4 screen refresh frames (120 Hz refresh rate = 8.33ms by frame) and 35% of the full contrast, as illustrated below (please see also Retter, T. L., & Rossion, B. (2016). Uncovering the neural magnitude and spatio-temporal dynamics of natural image categorization in a fast visual stream. Neuropsychologia, 91, 9–28).

Author response image 4.

(2) Interpretation of suppression:

The SSVEP paradigm alternates between 2 conditions: faces and objects and has no baseline; In other words, responses to faces are measured relative to the baseline response to objects so that any region that contains neurons that have a lower firing rate to faces than objects is bound to show a lower response in the SSVEP signal. Therefore, because the experiment does not have a true baseline (e.g. blank screen, with no visual stimulation) this experimental design cannot distinguish between lower firing rate to faces vs suppression of response to faces.

The strongest evidence put forward for suppression is the response of non-visual neurons that was also reduced when patients looked at faces, but since these are non-visual neurons, it is unclear how to interpret the responses to faces.

We understand this point, but how does the reviewer know that these are non-visual neurons? Because these neurons are located in the visual cortex, they are likely to be visual neurons that are not responsive to non-face objects. In any case, as the reviewer writes, we think it’s strong evidence for suppression.

We thank all three reviewers for their positive evaluation of our paper and their constructive comments.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

Zhang et al. addressed the question of whether advantageous and disadvantageous inequality aversion can be vicariously learned and generalized. Using an adapted version of the ultimatum game (UG), in three phases, participants first gave their own preference (baseline phase), then interacted with a "teacher" to learn their preference (learning phase), and finally were tested again on their own (transfer phase). The key measure is whether participants exhibited similar choice preferences (i.e., rejection rate and fairness rating) influenced by the learning phase, by contrasting their transfer phase and baseline phase. Through a series of statistical modeling and computational modeling, the authors reported that both advantageous and disadvantageous inequality aversion can indeed be learned (Study 1), and even be generalised (Study 2).

Strengths:

This study is very interesting, it directly adapted the lab's previous work on the observational learning effect on disadvantageous inequality aversion, to test both advantageous and disadvantageous inequality aversion in the current study. Social transmission of action, emotion, and attitude have started to be looked at recently, hence this research is timely. The use of computational modeling is mostly appropriate and motivated. Study 2, which examined the vicarious inequality aversion in conditions where feedback was never provided, is interesting and important to strengthen the reported effects. Both studies have proper justifications to determine the sample size.

Weaknesses:

Despite the strengths, a few conceptual aspects and analytical decisions have to be explained, justified, or clarified.

INTRODUCTION/CONCEPTUALIZATION

(1) Two terms seem to be interchangeable, which should not, in this work: vicarious/observational learning vs preference learning. For vicarious learning, individuals observe others' actions (and optionally also the corresponding consequence resulting directly from their own actions), whereas, for preference learning, individuals predict, or act on behalf of, the others' actions, and then receive feedback if that prediction is correct or not. For the current work, it seems that the experiment is more about preference learning and prediction, and less so about vicarious learning. The intro and set are heavily around vicarious learning, and later the use of vicarious learning and preference learning is rather mixed in the text. I think either tone down the focus on vicarious learning, or discuss how they are different. Some of the references here may be helpful: (Charpentier et al., Neuron, 2020; Olsson et al., Nature Reviews Neuroscience, 2020; Zhang & Glascher, Science Advances, 2020)

We are appreciative of the Reviewer for raising this question and providing the reference. In response to this comment we have elected to avoid, in most cases, use of the term ‘vicarious’ and instead focus the paper on learning of others’ preferences (without specific commitment to various/observational learning per se). These changes are reflected throughout all sections of the revised manuscript, and in the revised title. We believe this simplified terminology has improved the clarity of our contribution.

EXPERIMENTAL DESIGN

(2) For each offer type, the experiment "added a uniformly distributed noise in the range of (-10 ,10)". I wonder what this looks like? With only integers such as 25:75, or even with decimal points? More importantly, is it possible to have either 70:30 or 90:10 option, after adding the noise, to have generated an 80:20 split shown to the participants? If so, for the analyses later, when participants saw the 80:20 split, which condition did this trial belong to? 70:30 or 90:10? And is such noise added only to the learning phase, or also to the baseline/transfer phases? This requires some clarification.

We thank the Reviewer for pointing this out. The uniformly distributed noise was added to all three phases to make the proposers’ behavior more realistic. This added noise was rounded to integer numbers, constrained from -9 to 9, which means in both 70:30 and 90:10 offer types, an 80:20 split could not occur. We have made this feature of our design clear in the Method section Line 524 ~ 528:

“In all task phases, we added uniformly distributed noise to each trial’s offer (ranging from -9 to 9, inclusive, rounding to the nearest integer) such that the random amount added (or subtracted) from the Proposer’s share was subtracted (or added) to the Receiver’s share. We adopted this manipulation to make the proposers’ behavior appear more realistic. The orders of offers participants experienced were fully randomized within each experiment phase. ”

(3) For the offer conditions (90:10, 70:30, 50:50, 30:70, 10:90) - are they randomized? If so, how is it done? Is it randomized within each participant, and/or also across participants (such that each participant experienced different trial sequences)? This is important, as the order especially for the learning phase can largely impact the preference learning of the participants.

We agree with the Reviewer the order in which offers are experienced could be very important. The order of the conditions was randomized independently for each participant (i.e. each participant experienced different trial sequences). We made this point clear in the Methods part. Line 527 ~ 528:

“The orders of offers participants experienced were fully randomized within each experiment phase.”

STATISTICAL ANALYSIS & COMPUTATIONAL MODELING

(4) In Study 1 DI offer types (90:10, 70:30), the rejection rate for DI-AI averse looks consistently higher than that for DI averse (ie, the blue line is above the yellow line). Is this significant? If so, how come? Since this is a between-subject design, I would not anticipate such a result (especially for the baseline). Also, for the LME results (eg, Table S3), only interactions were reported but not the main results.

We thank the Reviewer for pointing out this feature of the results. Prompted by this comment, we compared the baseline rejection rates between two conditions for these two offer types, finding in Experiment 1 that rejection rates in the DI-AI-averse condition were significantly higher than in the DI-averse condition (DI-AI-averse vs. DI-averse; Offer 90:10, β = 0.13, p < 0.001, Offer 70:30, β = 0.09, p < 0.034). We agree with the Reviewer that there should, in principle, be no difference between the experiences of participants in these two conditions is identical in the Baseline phase. However, we did not observe these difference in baseline preferences in Experiment 2 (DI-AI-averse vs. DI-averse; Offer 90:10, β = 0.07, p < 0.100, Offer 70:30, β = 0.05, p < 0.193). On the basis of the inconsistency of this effect across studies we believe this is a spurious difference in preferences stemming from chance.

Regarding the LME results, the reason why only interaction terms are reported is due to the specification of the model and the rationale for testing.

Taking the model reported in Table S3 as an example—a logistic model which examines Baseline phase rejection rates as a function of offer level and condition—the between-subject conditions (DI-averse and DI-AI-averse) are represented by dummy-coded variables. Similarly, offer types were also dummy-coded, such that each of the five columns (90:10, 70:30, 50:50, 30:70, and 10:90) correspond corresponded to a particular offer type. This model specification yields ten interaction terms (i.e., fixed effects) of interest—for example, the “DI-averse × Offer 90:10” indicates baseline rejection rates for 90:10 offers in DI-averse condition. Thus, to compare rejection rates across specific offer types, we estimate and report linear contrasts between these resultant terms. We have clarified the nature of these reported tests in our revised Results—for example, line189-190: “linear contrasts; e.g. 90:10 vs 10:90, all Ps<0.001, see Table S3 for logistic regression coefficients for rejection rates).

Also in response to this comment that and a recommendation from Reviewer 2 (see below), we have revised our supplementary materials to make each model specification clearer as SI line 25:

“RejectionRate ~ 0 + (Disl + Advl):(Offer10 + Offer30 + Offer50 + Offer70 + Offer90) + (1|Subject)”

(5) I do not particularly find this analysis appealing: "we examined whether participants' changes in rejection rates between Transfer and Baseline, could be explained by the degree to which they vicariously learned, defined as the change in punishment rates between the first and last 5 trials of the Learning phase." Naturally, the participants' behavior in the first 5 trials in the learning phase will be similar to those in the baseline; and their behavior in the last 5 trials in the learning phase would echo those at the transfer phase. I think it would be stronger to link the preference learning results to the change between the baseline and transfer phase, eg, by looking at the difference between alpha (beta) at the end of the learning phase and the initial alpha (beta).

Thanks for pointing this out. Also, considering the comments from Reviewer 2 concerning the interpretation of this analysis, we have elected to remove this result from our revision.

(6) I wonder if data from the baseline and transfer phases can also be modeled, using a simple Fehr-Schimdt model. This way, the change in alpha/beta can also be examined between the baseline and transfer phase.

We agree with the Reviewer that a simplified F-S model could be used, in principle, to characterize Baseline and Transfer phase behavior, but it is our view that the rejection rates provide readers with the clearest (and simplest) picture of how participants are responding to inequity. Put another way, we believe that the added complexity of using (and explaining) a new model to characterize simple, steady-state choice behavior (within these phases) would not be justified or add appreciable insights about participants’ behavior.

(7) I quite liked Study 2 which tests the generalization effect, and I expected to see an adapted computational modeling to directly reflect this idea. Indeed, the authors wrote, "[...] given that this model [...] assumes the sort of generalization of preferences between offer types [...]". But where exactly did the preference learning model assume the generalization? In the methods, the modeling seems to be only about Study 1; did the authors advise their model to accommodate Study 2? The authors also ran simulation for the learning phase in Study 2 (Figure 6), and how did the preference update (if at all) for offers (90:10 and 10:90) where feedback was not given? Extending/Unpacking the computational modeling results for Study 2 will be very helpful for the paper.

We are appreciative of the Reviewer’s positive impression of Experiment 2. Upon reflection, we realize that our original submission was not clear about the modeling done in Experiment 2, and we should clarify here that we did also fit the Preference Inference model to this dataset. As in Experiment 1, this model assumes that the participants have a representation of the teacher’s preference as a Fehr-Schmidt form utility function and infer the Teacher’s Envy and Guilt parameters through learning. The model indicates that, on the basis of experience with the Teacher’s preferences on moderately unfair offers (i.e., offer 70:30 and offer 30:70), participants can successfully infer these guess of these two parameters, and in turn, compute Fehr-Schmidt utility to guide their decisions in the extreme unfair offers (i.e., offer 90:10 and offer 10:90).

In response to this comment, we have made this clearer in our Results (Line 377-382):

“Finally, following Experiment 1, we fit a series of computational models of Learning phase choice behavior, comparing the goodness-of-fit of the four best-fitting models from Experiment 1 (see Methods). As before, we found that the Preference Inference model provided the best fit of participants’ Learning Phase behavior (Figure S1a, Table S12). Given that this model is able to infer the Teacher’s underlying inequity-averse preferences (rather than learns offer-specific rejection preferences), it is unsurprising that this model best describes the generalization behavior observed in Experiment 2.”

and in our revised Methods (Line 551-553)

“We considered 6 computational models of Learning Phase choice behavior, which we fit to individual participants’ observed sequences of choices, in both Experiments 1 and 2, via Maximum Likelihood Estimation”

Reviewer #2 (Public review):

Summary:

This study investigates whether individuals can learn to adopt egalitarian norms that incur a personal monetary cost, such as rejecting offers that benefit them more than the giver (advantageous inequitable offers). While these behaviors are uncommon, two experiments demonstrate that individuals can learn to reject such offers through vicarious learning - by observing and acting in line with a "teacher" who follows these norms. The authors use computational modelling to argue that learners adopt these norms through a sophisticated process, inferring the latent structure of the teacher's preferences, akin to theory of mind.

Strengths:

This paper is well-written and tackles a critical topic relevant to social norms, morality, and justice. The findings, which show that individuals can adopt just and fair norms even at a personal cost, are promising. The study is well-situated in the literature, with clever experimental design and a computational approach that may offer insights into latent cognitive processes. Findings have potential implications for policymakers.

Weaknesses:

Note: in the text below, the "teacher" will refer to the agent from which a participant presumably receives feedback during the learning phase.

(1) Focus on Disadvantageous Inequity (DI): A significant portion of the paper focuses on responses to Disadvantageous Inequitable (DI) offers, which is confusing given the study's primary aim is to examine learning in response to Advantageous Inequitable (AI) offers. The inclusion of DI offers is not well-justified and distracts from the main focus. Furthermore, the experimental design seems, in principle, inadequate to test for the learning effects of DI offers. Because both teaching regimes considered were identical for DI offers the paradigm lacks a control condition to test for learning effects related to these offers. I can't see how an increase in rejection of DI offers (e.g., between baseline and generalization) can be interpreted as speaking to learning. There are various other potential reasons for an increase in rejection of DI offers even if individuals learn nothing from learning (e.g. if envy builds up during the experiment as one encounters more instances of disadvantageous fairness).

We are appreciative of the Reviewer’s insight here and for the opportunity to clarify our experimental logic. We included DI offers in order to 1) expose participants to the full spectrum of offer types, and avoid focusing participants exclusively upon AI offers, which might result in a demand characteristic and 2) to afford exploration of how learning dynamics might differ in DI context s—which was, to some extent, examined in our previous study (FeldmanHall, Otto, & Phelps, 2018)—versus AI contexts. Furthermore, as this work builds critically on our previous study, we reasoned that replicating these original findings (in the DI context) would be important for demonstrating the generality of the learning effects in the DI context across experimental settings. We now remark on this point in our revised Introduction Line 129 ~132:

“In addition, to mechanistically probe how punitive preferences are acquired in Adv-I and Dis-I contexts—in turn, assessing the replicability of our earlier study investigating punitive preference acquisition in the Dis context—we also characterize trial-by-trial acquisition of punitive behavior with computational models of choice.”

(2) Statistical Analysis: The analysis of the learning effects of AI offers is not fully convincing. The authors analyse changes in rejection rates within each learning condition rather than directly comparing the two. Finding a significant effect in one condition but not the other does not demonstrate that the learning regime is driving the effect. A direct comparison between conditions is necessary for establishing that there is a causal role for the learning regime.

We agree with the Reviewer and upon reflection, believe that direct comparisons between conditions would be helpful to support the claim that the different learning conditions are responsible for the observed learning effects. In brief, these specific tests buttress the idea that exposure to AI-averse preferences result in increases in AI punishment rates in the Transfer phase (over and above the rates observed for participants who were only exposed to DI-averse preferences).

Accordingly, our revision now reports statistics concerning the differences between conditions for AI offers in Experiment 1 (Line 198~ 207):

“Importantly, when comparing these changes between the two learning conditions, we observed significant differences in rejection rates for Adv-I offers: compared to exposure to a Teacher who rejected only Dis-I offers, participants exposed to a Teacher who rejected both Dis-I and Adv-I offers were more likely to reject Adv-I offers and rated these offers more unfair. This difference between conditions was evident in both 30:70 offers (Rejection rates: β(SE) = 0.10(0.04), p = 0.013; Fairness ratings: β(SE) = -0.86(0.17), p < 0.001) and 10:90 offers (Rejection rates: β(SE) = 0.15(0.04), p < 0.001, Fairness ratings: β(SE) = -1.04(0.17), p < 0.001). As a control, we also compared rejection rates and fairness rating changes between conditions in Dis-I offers (90:10 and 30:70) and Fair offers (i.e., 50:50) but observed no significant difference (all ps > 0.217), suggesting that observing an Adv-I-averse Teacher’s preferences did not influence participants’ behavior in response to Dis-I offers.”

Line 222 ~ 230:

“A mixed-effects logistic regression revealed a significant larger (positive) effect of trial number on rejection rates of Adv-I offers for the Adv-Dis-I-Averse condition compared to the Dis-I-Averse condition. This relative rejection rate increase was evident both in 30:70 offers (Table S7; β(SE) = -0.77(0.24), p < 0.001) and in 10:90 offers (β(SE) = -1.10(0.33), p < 0.001). In contrast, comparing Dis-I and Fairness offers when the Teacher showed the same tendency to reject, we found no significant difference between the two conditions (90:10 splits: β(SE)=-0.48(0.21),p=0.593;70:30 splits: β(SE)=-0.01(0.14),p=0.150; 50:50 splits: β(SE)=-0.00(0.21),p=0.086). In other words, participants by and large appeared to adjust their rejection choices in accordance with the Teacher’s feedback in an incremental fashion.”

And in Experiment 2 Line 333 ~ 345:

“Similar to what we observed in Experiment 1 (Figure 4a), Compared to the participants in the Dis-I-Averse Condition, participants in the Adv-I-Averse Condition increased their rates of rejection of extreme Adv-I offerers (i.e., 10:90) in the Transfer Phase, relative to the Baseline phase (β(SE) = -0.12(0.04), p < 0.004; Table S9), suggesting that participants’ learned (and adopted) Adv-I-averse preferences, generalized from one specific offer type (30:70) to an offer types for which they received no Teacher feedback (10:90). Examining extreme Dis-I offers where the Teacher exhibited identical preferences across the two learning conditions, we found no difference in the Changes of Rejection Rates from Baseline to Transfer phase between conditions (β(SE) = -0.05(0.04), p < 0.259). Mirroring the observed rejection rates (Figure 4b), relative to the Dis-I-Averse Condition, participants’ fairness ratings for extreme Adv-I offers increased more from the Baseline to Transfer phase in the Adv-Dis-I-Averse Condition than in the Dis-I-Averse condition (β(SE) = -0.97(0.18), p < 0.001), but, importantly, changes in fairness ratings for extreme Dis-I offers did not differ significantly between learning conditions (β(SE) = -0.06(0.18), p < 0.723)”

Line 361 ~ 368:

“Examining the time course of rejection rates in Adv-I-contexts during the Learning phase (Figure 5) revealed that participants learned over time to punish mildly unfair 30:70 offers, and these punishment preferences generalized to more extreme offers (10:90). Specifically, compared to the Dis-I-Averse Condition, in the Adv-Dis-I-Averse condition we observed a significant larger trend of increase in rejections rates for 10:90 (Adv-I) offers (Figure 5, β(SE) = -0.81(0.26), p < 0.002 mixed-effects logistic regression, see Table S10). Again, when comparing the rejection rate increase in the extremely Dis-I offers (90:10), we didn’t find significant difference between conditions (β(SE) = -0.25(0.19), p < 0.707).”

(3) Correlation Between Learning and Contagion Effects:

The authors argue that correlations between learning effects (changes in rejection rates during the learning phase) and contagion effects (changes between the generalization and baseline phases) support the idea that individuals who are better aligning their preferences with the teacher also give more consideration to the teacher's preferences later during generalization phase. This interpretation is not convincing. Such correlations could emerge even in the absence of learning, driven by temporal trends like increasing guilt or envy (or even by slow temporal fluctuations in these processes) on behalf of self or others. The reason is that the baseline phase is temporally closer to the beginning of the learning phase whereas the generalization phase is temporally closer to the end of the learning phase. Additionally, the interpretation of these effects seems flawed, as changes in rejection rates do not necessarily indicate closer alignment with the teacher's preferences. For example, if the teacher rejects an offer 75% of the time then a positive 5% learning effect may imply better matching the teacher if it reflects an increase in rejection rate from 65% to 70%, but it implies divergence from the teacher if it reflects an increase from 85% to 90%. For similar reasons, it is not clear that the contagion effects reflect how much a teacher's preferences are taken into account during generalization.

This comment is very similar to a previous comment made by Reviewer 1, who also called into question the interpretability of these correlations. In response to both of these comments we have elected to remove these analyses from our revision.

(4) Modeling Efforts: The modelling approach is underdeveloped. The identification of the "best model" lacks transparency, as no model-recovery results are provided, and fits for the losing models are not shown, leaving readers in the dark about where these models fail. Moreover, the reinforcement learning (RL) models used are overly simplistic, treating actions as independent when they are likely inversely related (for example, the feedback that the teacher would have rejected an offer provides feedback that rejection is "correct" but also that acceptance is "an error", and the later is not incorporated into the modelling). It is unclear if and to what extent this limits current RL formulations. There are also potentially important missing details about the models. Can the authors justify/explain the reasoning behind including these variants they consider? What are the initial Q-values? If these are not free parameters what are their values?

We are appreciative of the Reviewer for identifying these potentially unaddressed questions.

The RL models we consider in the present study are naïve models which, in our previous study (FeldmanHall, Otto, & Phelps, 2018), we found to capture important aspects of learning. While simplistic, we believed these models serve as a reasonable baseline for evaluating more complex models, such as the Preference Inference model. We have made this point more explicit in our revised Introduction, Line 129 ~ 132:

“In addition, to mechanistically probe how punitive preferences may be acquired in Adv-I and Dis-I contexts—in turn, assessing the replicability of our earlier study investigating punitive preference acquisition in the Dis-I context—we also characterize trial-by-trial acquisition of punitive behavior with computational models of choice.”

Again, following from our previous modeling of observational learning (FeldmanHall et al., 2018), we believe that the feedback the Teacher provides here is ideally suited to the RL formalism. In particular, when the teacher indicates that the participant’s choice is what they would have preferred, the model receives a reward of ‘1’ (e.g., the participant rejects and the Teacher indicates they would preferred rejection, resulting in a positive prediction error) otherwise, the model receives a reward of ‘0’ (e.g., the participant accepts and the Teacher indicates they would preferred rejection, resulting in a negative prediction error), indicating that the participant did not choose in accordance with the Teacher’s preferences. Through an error driven learning process, these models provide a naïve way of learning to act in accordance with the Teacher’s preferences.

Regarding the requested model details: When treating the initial values as free parameters (model 5), we set Q(reject, offertype) as free values in [0,1] and Q(accept,offertype) as 0.5. This setting can capture participants' initial tendency to reject or accept offers from this offer type. When the initial values are fixed, for all offer types we set Q(reject, offertype) = Q(accept,offertype) = 0.5. In practice, when the initial values are fixed, setting them to 0.5 or 0 doesn’t make much difference. We have clarified these points in our revised Methods, Line 275 ~ 576:

“We kept the initial values fixed in this model, that is Q₀(reject,offertype) =0.5, (offertype ∈ 90:10, 70:30, 50:50, 30:70, 10:90)”

And Line 582 ~ 584:

“Formally, this model treats Q₀(reject,offertype) =0.5, (offertype ∈ 90:10, 70:30, 50:50, 30:70, 10:90) as free parameters with values between 0 and 1.”

(5) Conceptual Leap in Modeling Interpretation: The distinction between simple RL models and preference-inference models seems to hinge on the ability to generalize learning from one offer to another. Whereas in the RL models learning occurs independently for each offer (hence to cross-offer generalization), preference inference allows for generalization between different offers. However, the paper does not explore RL models that allow generalization based on the similarity of features of the offers (e.g., payment for the receiver, payment for the offer-giver, who benefits more). Such models are more parsimonious and could explain the results without invoking a theory of mind or any modelling of the teacher. In such model versions, a learner learns a functional form that allows to predict the teacher's feedback based on said offer features (e.g., linear or quadratic form). Because feedback for an offer modulates the parameters of this function (feature weights) generalization occurs without necessarily evoking any sophisticated model of the other person. This leaves open the possibility that RL models could perform just as well or even show superiority over the preference learning model, casting doubt on the authors' conclusions. Of note: even the behaviourists knew that as Little Albert was taught to fear rats, this fear generalized to rabbits. This could occur simply because rabbits are somewhat similar to rats. But this doesn't mean little Alfred had a sophisticated model of animals he used to infer how they behave.

We are appreciative of the Reviewer for their suggestion of an alternative explanation for the observed generalization effects. Our understanding of the suggestion, put simply, put simply, is that an RL model could capture the observed generalization effects if the model were to learn and update a functional form of the Teacher’s rejection preferences using an RL-like algorithm. This idea is similar, conceptually to our account of preference learning whereby the learner has a representation of the teacher’s preferences. In our experiment the offer is in the range of [0-100], the crux of this idea is why the participants should take the functional form (either v-shaped or quadratic) with the minimum at 50. This is important because, at the beginning of the learning phase, the rejection rates are already v-shaped with 50 as its minimum. The participants do not need to adjust the minimum of this functional form. Thus, if we assume that the participants represent the teacher’s rejection rate as a v-shape function with a minimum at [50,50], then this very likely implies that the participants have a representation that the teacher has a preference for fairness. Above all, we agree that with suitable setup of the functional form, one could implement an RL model to capture the generalization effects, without presupposing an internal “model” of the teacher’s preferences.

However, there is another way of modeling the generalization effect by truly “model-free” similarity-based Reinforcement learning. In this approach, we do not assume any particular functional form of the teacher’s preferences, but rather, assumes that experience acquired in one offer type can be generalized to offers that are close (i.e., similar) to the original offer. Accordingly, we implement this idea using a simple RL model in which the action values for each offer type is updated by a learning rate that is scaled by the distance between that offer and the experienced offer (i.e., the offer that generated the prediction error). This learning rate is governed by a Gaussian distribution, similar to the case in the Gaussian process regression (cf. Chulz, Speekenbrink, & Krause, 2018). The initial value of the ‘Reject’ action, for each offer , is set to a free parameter between 0 and 1, and the initial value for the 'Accept’ action was set to 0.5. The results show that even though this model exhibits the trend of increasing rejection rates observed in the AI-DI punish condition, the initial preferences (i.e., starting point of learning) diverges markedly from the Learning phase behavior we observed in Experiment 1:

Author response image 1.

This demonstrated that the participant at least maintains a representation of the teacher’s preference at the beginning. That is, they have prior knowledge about the shape of this preference. We incorporated this property into the model, that is, we considered a new model that assumes v-shaped starting values for rejection with two parameters, alpha and beta, governing the slope of this v-shaped function (this starting value actually mimics the shape of the preference functions of the Fehr-Schmidt model). We found that this new model (which we term the “Model RL Sim Vstart”) provided a satisfactory qualitative fit of the Transfer phase learning curves in Experiment 1 (see below).

Author response image 2.

However, we didn’t adopt this model as the best model for the following reasons. First, this model yielded a larger AIC value (indicating worse quantitative fit) compared to our preference Inference model in both Experiments 1 and 2, likely owing to its increased complexity (5 free parameters versus 4 in the Preference Inference model). Accordingly, we believe that inclusion of this model in our revised submission would be more distracting than helpful on account of the added complexity of explaining and justifying these assumptions, and of course its comparatively poor goodness of fit (relative to the preference inference model).

(6) Limitations of the Preference-Inference Model: The preference-inference model struggles to capture key aspects of the data, such as the increase in rejection rates for 70:30 DI offers during the learning phase (e.g. Figure 3A, AI+DI blue group). This is puzzling.

Thinking about this I realized the model makes quite strong unintuitive predictions that are not examined. For example, if a subject begins the learning phase rejecting the 70:30 offer more than 50% of the time (meaning the starting guilt parameter is higher than 1.5), then overleaning the tendency to reject will decrease to below 50% (the guilt parameter will be pulled down below 1.5). This is despite the fact the teacher rejects 75% of the offers. In other words, as learning continues learners will diverge from the teacher. On the other hand, if a participant begins learning to tend to accept this offer (guilt < 1.5) then during learning they can increase their rejection rate but never above 50%. Thus one can never fully converge on the teacher. I think this relates to the model's failure in accounting for the pattern mentioned above. I wonder if individuals actually abide by these strict predictions. In any case, these issues raise questions about the validity of the model as a representation of how individuals learn to align with a teacher's preferences (given that the model doesn't really allow for such an alignment).

In response to this comment we explain our efforts to build a new model that might be able conceptually resolves the issue identified by the Reviewer.

The key intuition guiding the Preference inference model is a Bayesian account of learning which we aimed to further simplify. In this setting, a Bayesian learner maintains a representation of the teacher’s inequity aversion parameters and updates it according to the teacher’s (observed) behavior. Intuitively, the posterior distribution shifts to the likelihood of the teacher’s action. On this view, when the teacher rejects, for instance, an AI offer, the learner should assign a higher probability to larger values of the Guilt parameter, and in turn the learner should change their posterior estimate to better capture the teacher’s preferences.

In the current study, we simplified this idea, implementing this sort of learning using incremental “delta rule” updating (e.g. Equation 8 of the main text). Then the key question is to define the “teaching signal”. Assuming that the teacher rejects an offer 70:30, based on Bayesian reasoning, the teacher’s envy parameter (α) is more likely to exceed 1.5 (computed as 30/(50-30), per equation 7) than to be smaller than 1.5. Thus, 1.5, which is then used in equation 8 to update α, can be thought of as a teaching signal. We simply assumed that if the initial estimate is already greater than 1.5, which means the prior is consistent with the likelihood, no updating would occur. This assumption raises the question of how to set the learning rate range. In principle, an envy parameter that is larger than 1.5 should be the target of learning (i.e., the teaching signal), and thus our model definition allows the learning rate to be greater than 1, incorporating this possibility.

Our simplified preference inference model has already successfully captured some key aspects of the participants’ learning behavior. However, it may fail in the following case: assume that the participant has an initial estimate of 1.51 for the envy parameter (β). Let’s say this corresponds to a rejection rate of 60%. Thus, no matter how many times the teacher rejects the offer 70:30, the participant’s estimate of the envy parameter remains the same, but observing only one offer acceptance would decrease this estimate, and in turn, would decrease the model’s predicted rejection rate. We believe this is the anomalous behavior—in 70:30 offers—identified by the Reviewer which the model does not appear able to recreate participants’ in these offers.

This issue actually touches the core of our model specification, that is, the choosing of the teaching signal. As we chose 1.5 as the teaching signal—i.e. lower bound on whenever the teacher rejects or accepts an offer of 70:30, a very small deviation of 1.5 would fail one part of updating. One way to mitigate this problem would be to choose a lower bound for α greater than 1.5, such that when the Teacher rejects a 70:30 offer, we assign a number greater than 1.5 (by ‘hard-coding’ this into the model via modification of equation 7). One sensible candidate value could be the middle point between 1.5 and 10 (the maximum value of α per our model definition). Intuitively, the model of this setting could still pull up the value of α to 1.51 when the teacher rejects 70:30, thus alleviating (but not completely eliminating) the anomaly.

We fitted this modified Preference Inference model to the data from Experiment 1 (see Author response image 3 below) and found that even though this model has a smaller AIC (and thus better quantitative fit than the original Preference Inference model), it still doesn’t fully capture the participants’ behavior for 70:30 offers.

Author response image 3.

Accordingly, rather than revising our model to include an unprincipled ‘kludge’ to account for this minor anomaly in the model behavior, we have opted to report our original model in our revision as we still believe it parsimoniously captures our intuitions about preference learning and provides a better fit to the observed behavior than the other RL models considered in the present study.

Reviewer #1 (Recommendations for the authors):

(1) I do not particularly prefer the acronyms AI and DI for disadvantageous inequity and advantageous inequity. Although they have been used in the literature, not every single paper uses them. More importantly, AI these days has such a strong meaning of artificial intelligence, so when I was reading this, I'd need to very actively inhibit this interpretation. I believe for the readability for a wider readership of eLife, I would advise not to use AI/DI here, but rather use the full terms.

We thank the Reviewer for this suggestion. As the full spelling of the two terms are somewhat lengthy, and appear frequently in the figures, we have elected to change the abbreviations for disadvantageous inequity and advantageous inequity to Dis-I and Adv-I, respectively in the main text and the supplementary information. We still use AI/DI in the response letter to make the terminology consistent.

(2) Do "punishment rate" and "rejection rate" mean the same? If so, it would be helpful to stick with one single term, eg, rejection rate.

We thank the Reviewer for this suggestion. As these terms have the same meaning, we have opted to use the term “rejection rate” throughout the main text.

(3) For the linear mixed effect models, were other random effect structures also considered (eg, random slops of experimental conditions)? It might be worth considering a few model specifications and selecting the best one to explain the data.

Thanks for this comment. Following established best practices (Barr, Levy, Scheepers, & Tily, 2013) we have elected to use a maximal random effects structure, whereby all possible predictor variables in the fixed effects structure also appear in the random effects structure.

(4) For equation (4), the softmax temperature is denoted as tau, but later in the text, it is called gamma. Please make it consistent.

We are appreciative of the Reviewer’s attention to detail. We have corrected this error.

Reviewer #2 (Recommendations for the authors):

(1) Several Tables in SI are unclear. I wasn't clear if these report raw probabilities of coefficients of mixed models. For any mixed models, it would help to give the model specification (e.g., Walkins form) and explain how variables were coded.

We are appreciative of the Reviewer’s attention to detail. We have clarified, in the captions accompanying our supplemental regression tables, that these coefficients represent log-odds. Regretfully we are unaware of the “Walkins form” the Reviewer references (even after extensive searching of the scientific literature). However, in our new revision we do include lme4 model syntax in our supplemental information which we believe will be helpful for readers seeking replicate our model specification.

(2) In one of the models it was said that the guilt and envy parameters were bounded between 0-1 but this doesn't make sense and I think values outside this range were later reported.

We are again appreciative of the Reviewer’s attention to detail. This was an error we have corrected— the actual range is [0,10].

(3) It is unclear if the model parameters are recoverable.

In response to this comment our revision now reports a basic parameter recovery analysis for the winning Preference Inference model. This is reported in our revised Methods:

“Finally, to verify if the free parameters of the winning model (Preference Inference) are recoverable, we simulated 200 artificial subjects, based on the Learning Phase of Experiment 1, with free parameters randomly chosen (uniformly) from their defined ranges. We then employed the same model-fitting procedure as described above to estimate these parameter value, observing that parameters. We found that all parameters of the model can be recovered (see Figure S2).”

And scatter plots depicting these simulated (versus recovered) parameters are given in Figure S2 of our revised Supplementary Information:

(4) I was confused about what Figure S2 shows. The text says this is about correlating contagious effects for different offers but the captions speak about learning effects. This is an important aspect which is unclear.

We have removed this figure in response to both Reviewers’ comments about the limited insights that can be drawn on the basis of these correlations.

Author response:

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

Reviewer #1 (Public review):

Summary:

The aim of this paper is to develop a simple method to quantify fluctuations in the partitioning of cellular elements. In particular, they propose a flow-cytometry-based method coupled with a simple mathematical theory as an alternative to conventional imaging-based approaches.

Strengths:

The approach they develop is simple to understand and its use with flow-cytometry measurements is clearly explained. Understanding how the fluctuations in the cytoplasm partition vary for different kinds of cells is particularly interesting.

Weaknesses:

The theory only considers fluctuations due to cellular division events. This seems a large weakness because it is well known that fluctuations in cellular components are largely affected by various intrinsic and extrinsic sources of noise and only under particular conditions does partitioning noise become the dominant source of noise.

We thank the Reviewer for her/his evaluation of our manuscript. The point raised is indeed a crucial one. In a cell division cycle, there are at least three distinct sources of noise that affect component numbers [1] :

(1) Gene expression and degradation, which determine component numbers fluctuations during cell growth.

(2) Variability in cell division time, which depending on the underlying model may or may not be a function of protein level and gene expression.

(3) Noise in the partitioning/inheritance of components between mother and daughter cells.

Our approach specifically addresses the latter, with the goal of providing a quantitative measure of this noise source. For this reason, in the present work, we consider homogeneous cancer cell populations that could be considered to be stationary from a population point-of-view. By tracking the time evolution of the distribution of tagged components via live fluorescent markers, we aim at isolating partitioning noise effects. However, as noted by the Reviewer, other sources of noise are present, and depending on the considered system the relative contributions of the different sources may change. Thus, we agree that a quantification of the effect of the various noise sources on the accuracy of our measurements will improve the reliability of our method.

In this respect, assuming independence between noise sources, we reasoned that variability in cell cycle length would affect the timing of population emergence but not the intrinsic properties of those populations (e.g., Gaussian variance). To test this hypothesis, we conducted a preliminary set of simulations in which cell division times were drawn from an Erlang distribution (mean = 18 h, k=4k = 4k=4). The results, showing the behavior of the mean and variance of the component distributions across generations, are presented in Supplementary Information - Figure 1. Under the assumption of independence between different noise sources, no significant effects were observed even for high asymmetries of the partitioning distribution.

Next, we quantified the accuracy of our measurements in the presence of cross-talks between the various noise sources.Indeed, cells may adopt different growth and division strategies, which can be grouped into three categories based on what triggers division:

● Sizer-like cells divide upon reaching a certain size;

● Timer-like cells divide after a fixed time (corresponding to the previously treated case with independent noise);

● Adder-like cells divide once their volume has increased by a finite amount.

A detailed discussion of these strategies, including their mathematical formulation, can be found in [2]. Here we have assumed that cells follow a sizer-like model. In this way, we study a system in which cells with a higher number of components have shorter division times. Hence, older (newer) generations are emptied (populated) starting from higher values.

As can be observed, higher levels of division asymmetry increase the fluctuations of the system relative to the analytically expected behavior, particularly in later generations.

The result in Supplementary Information - Figure 3 demonstrates the robustness of our method, as the estimates remain within the pre-established experimental error margin. We have now discussed this aspect both in the main and in the Supplementary Information and thank the Reviewer for pointing it out.

(1) Soltani, Mohammad, et al. "Intercellular variability in protein levels from stochastic expression and noisy cell cycle processes." PLoS computational biology 12.8 (2016): e1004972.

(2) Mattia Miotto, Simone Scalise, Marco Leonetti, Giancarlo Ruocco, Giovanna Peruzzi, and Giorgio Gosti. A size-dependent division strategy accounts for leukemia cell size heterogeneity. Communications Physics, 7(1):248, 2024.

Reviewer #2 (Public review):

Summary:

The authors present a combined experimental and theoretical workflow to study partitioning noise arising during cell division. Such quantifications usually require time-lapse experiments, which are limited in throughput. To bypass these limitations, the authors propose to use flow-cytometry measurements instead and analyse them using a theoretical model of partitioning noise. The problem considered by the authors is relevant and the idea to use statistical models in combination with flow cytometry to boost statistical power is elegant. The authors demonstrate their approach using experimental flow cytometry measurements and validate their results using time-lapse microscopy. However, while I appreciate the overall goal and motivation of this work, I was not entirely convinced by the strength of this contribution. The approach focuses on a quite specific case, where the dynamics of the labelled component depend purely on partitioning. As such it seems incompatible with studying the partitioning noise of endogenous components that exhibit production/turnover. The description of the methods was partly hard to follow and should be improved. In addition, I have several technical comments, which I hope will be helpful to the authors.

We are grateful to the Reviewer for the comments. Indeed, both partitioning and production turnover noise are in general fundamental processes. At present the only way to consider them together are time-consuming and costly transfection/microscopy/tracking experiments. In this work, we aimed at developing a method to effectively pinpoint the first component, i.e. partitioning noise thus we opted to separate the two different noise sources.

Below, we provided a point-by-point response that we hope will clarify all raised concerns.

Comments:

(1) In the theoretical model, copy numbers are considered to be conserved across generations. As a consequence, concentrations will decrease over generations due to dilution. While this consideration seems plausible for the considered experimental system, it seems incompatible with components that exhibit production and turnover dynamics. I am therefore wondering about the applicability/scope of the presented approach and to what extent it can be used to study partitioning noise for endogenous components. As presented, the approach seems to be limited to a fairly small class of experiments/situations.

We see the Reviewer's point. Indeed, we are proposing a high-throughput and robust procedure to measure the partitioning/inheritance noise of cell components through flow cytometry time courses. By using live-cell staining of cellular compounds, we can track the effect of partitioning noise on fluorescence intensity distribution across successive generations. This specific procedure is purposely optimized to isolate partitioning noise from other sources and, as it is, can not track endogenous components or dyes that require fixation. While this certainly poses limits to the proposed approach, there are numerous contexts in which our methodology could be used to explore the role of asymmetric inheritance. Among others, (i) investigating how specific organelles are differentially partitioned and how this influences cellular behavior could provide deeper insights into fundamental biological processes: asymmetric segregation of organelles is a key factor in cell differentiation, aging, and stress response. During cell division, organelles such as mitochondria, the endoplasmic reticulum, lysosomes, peroxisomes, and centrosomes can be unequally distributed between daughter cells, leading to functional differences that influence their fate. For instance, Kajaitso et al. [1] proposed that asymmetric division of mitochondria in stem cells is associated with the retention of stemness traits in one daughter cell and differentiation in the other. As organisms age, stem cells accumulate damage, and to prevent exhaustion and compromised tissue function, cells may use asymmetric inheritance to segregate older or damaged subcellular components into one daughter cell. (ii) Asymmetric division has also been linked to therapeutic resistance in Cancer Stem Cells [2]. Although the functional consequences are not yet fully determined, the asymmetric inheritance of mitochondria is recognized as playing a pivotal role [3]. Another potential application of our methodology may be (iii) the inheritance of lysosomes, which, together with mitochondria, appears to play a crucial role in determining the fate of human blood stem cells [4]. Furthermore, similar to studies conducted on liquid tumors [5][6], our approach could be extended to investigate cell growth dynamics and the origins of cell size homeostasis in adherent cells [7][8][9]. The aforementioned cases of study can be readily addressed using our approach that in general is applicable whenever live-cell dyes can be used. We have added a discussion of the strengths and limitations of the method in the Discussion section of the revised version of the manuscript

(1) Katajisto, Pekka, et al. "Asymmetric apportioning of aged mitochondria between daughter cells is required for stemness." Science 348.6232 (2015): 340-343.

(2) Hitomi, Masahiro, et al. "Asymmetric cell division promotes therapeutic resistance in glioblastoma stem cells." JCI insight 6.3 (2021): e130510.

(3) García-Heredia, José Manuel, and Amancio Carnero. "Role of mitochondria in cancer stem cell resistance." Cells 9.7 (2020): 1693.

(4) Loeffler, Dirk, et al. "Asymmetric organelle inheritance predicts human blood stem cell fate." Blood, The Journal of the American Society of Hematology 139.13 (2022): 2011-2023.

(5) Miotto, Mattia, et al. "Determining cancer cells division strategy." arXiv preprint arXiv:2306.10905 (2023).

(6) Miotto, Mattia, et al. "A size-dependent division strategy accounts for leukemia cell size heterogeneity." Communications Physics 7.1 (2024): 248.

(7) Kussell, Edo, and Stanislas Leibler. "Phenotypic diversity, population growth, and information in fluctuating environments." Science 309.5743 (2005): 2075-2078.

(8) McGranahan, Nicholas, and Charles Swanton. "Clonal heterogeneity and tumor evolution: past, present, and the future." Cell 168.4 (2017): 613-628.

(9) De Martino, Andrea, Thomas Gueudré, and Mattia Miotto. "Exploration-exploitation tradeoffs dictate the optimal distributions of phenotypes for populations subject to fitness fluctuations." Physical Review E 99.1 (2019): 012417.

(2) Similar to the previous comment, I am wondering what would happen in situations where the generations could not be as clearly identified as in the presented experimental system (e.g., due to variability in cell-cycle length/stage). In this case, it seems to be challenging to identify generations using a Gaussian Mixture Model. Can the authors comment on how to deal with such situations? In the abstract, the authors motivate their work by arguing that detecting cell divisions from microscopy is difficult, but doesn't their flow cytometry-based approach have a similar problem?

The point raised is an important one, as it highlights the fundamental role of the gating strategy. The ability to identify the distribution of different generations using the Gaussian Mixture Model (GMM) strongly depends on the degree of overlap between distributions. The more the distributions overlap, the less capable we are of accurately separating them.

The extent of overlap is influenced by the coefficients of variation (CV) of both the partitioning distribution function and the initial component distribution. Specifically, the component distribution at time t results from the convolution of the component distribution itself at time t−1 and the partitioning distribution function. Therefore, starting with a narrow initial component distribution allows for better separation of the generation peaks. The balance between partitioning asymmetry and the width of the initial component distribution is thus crucial.

As shown in Supplementary Information - Figure 5, increasing the CV of either distribution reduces the ability to distinguish between different generations.

However, the variance of the initial distribution cannot be reduced arbitrarily. While selecting a narrow distribution facilitates a better reconstruction of the distributions, it simultaneously limits the number of cells available for the experiment. Therefore, for components exhibiting a high level of asymmetry, further narrowing of the initial distribution becomes experimentally impractical.

In such cases, an approach previously tested on liquid tumors [1] involves applying the Gaussian Mixture Model (GMM) in two dimensions by co-staining another cellular component with lower division asymmetry.

Regarding time-lapse fluorescence microscopy, the main challenge lies not in disentangling the interplay of different noise sources, but rather in obtaining sufficient statistical power from experimental data. While microscopy provides detailed insights into the division process and component partitioning, its low throughput limits large-scale statistical analyses. Current segmentation algorithms still perform poorly in crowded environments and with complex cell shapes, requiring a substantial portion of the image analysis pipeline to be performed manually, a process that is time-consuming and difficult to scale. In contrast, our cytometry-based approach bypasses this analysis bottleneck, as it enables a direct population-wide measurement of the system's evolution. We have added a detailed discussion of this argument in the Supplementary Material of the manuscript and added a clarification of the role of the gating strategy in the main text.

(1) Peruzzi, Giovanna, et al. "Asymmetric binomial statistics explains organelle partitioning variance in cancer cell proliferation." Communications Physics 4.1 (2021): 188.

(3) I could not find any formal definition of division asymmetry. Since this is the most important quantity of this paper, it should be defined clearly.

We thank the Reviewer for the note. With division asymmetry we refer to a quantity that reflects how similar two daughter cells are likely to be in terms of inherited components after a division process. We opted to measure it via the coefficient of variation (root squared variance divided by the mean) of the partitioning fraction distribution. We have amended this lack of definition in the reviewed version of the manuscript.

(4) The description of the model is unclear/imprecise in several parts. For instance, it seems to me that the index "i" does not really refer to a cell in the population, but rather a subpopulation of cells that has undergone a certain number of divisions. Furthermore, why is the argument of Equation 11 suddenly the fraction f as opposed to the component number? I strongly recommend carefully rewriting and streamlining the model description and clearly defining all quantities and how they relate to each other.

We have amending the text carefully to avoid double naming of variables and clarifying each computation passage. In equation 11 the variable f refers to the fluorescent intensity, but the notation will be changed to increase clarity.

(5) Similarly, I was not able to follow the logic of Section D. I recommend carefully rewriting this section to make the rationale, logic, and conclusions clear to the reader.

We have updated the manuscript clarifying the scope of section D and its results. In brief, Section A presents a general model to derive the variance of the partitioning distribution from flow cytometry time-course data without making any assumptions about the shape of the distribution itself. In Section D, our goal is to interpret the origin of asymmetry and propose a possible form for the partitioning distribution. Since the dyes used bind non-specifically to cytoplasmic amines, the tagged proteins are expected to be uniformly distributed throughout the cytoplasm and present in large numbers. Given these assumptions the least complex model for division follows the binomial distribution, with a parameter that measures the bias in the process. Therefore, we performed a similar computation to that in Section A, which allows us to estimate not only the variance but also the degree of biased asymmetry. Finally, we fitted the data to this new model and proposed an experimental interpretation of the results.

(6) Much theoretical work has been done recently to couple cell-cycle variability to intracellular dynamics. While the authors neglect the latter for simplicity, it would be important to further discuss these approaches and why their simplified model is suitable for their particular experiments.

We agree with the Reviewer, we have added a discussion on this topic in the Introduction and Discussion sections of the main text.

(7) In the discussion the authors note that the microscopy-based estimates may lead to an overestimation of the fluctuations due to limited statistics. I could not follow that reasoning. Due to the gating in the flow cytometry measurements, I could imagine that the resulting populations are more stringently selected as compared to microscopy. Could that also be an explanation? More generally, it would be interesting to see how robust the results are in terms of different gating diameters.

The Reviewer is right on the importance of the sorting procedure. As already discussed in a previous point, the gating strategy we employed plays a fundamental role: it reduces the overlap of fluorescence distributions as generations progress, enables the selection of an initial distribution distinct from the fluorescence background, allowing for longer tracking of proliferation, and synchronizes the initial population. The narrower the initial distribution, the more separated the peaks of different generations will be. However, this also results in a smaller number of cells available for the experiment, requiring a careful balance between precision and experimental feasibility. A similar procedure, although it would certainly limit the estimation error, would be impracticable In the case of microscopy. Indeed, the primary limitation and source of error is the number of recorded events. Our pipeline allowed us to track on the order of hundreds of division dynamics, but the analysis time scales non-linearly with the number of events. Significantly increasing the dataset would have been extremely time-consuming. Reducing the analysis to cells with similar fluorescence, although theoretically true, would have reduced the statistics to a level where the sampling error would drastically dominate the measure. Moreover, different experiments would have been hardly comparable, since different fluorescences could map in equally sized cells. In light of these factors, we expect higher CV for the microscopy measure than for flow cytometry’s ones. In the plots below, we show the behaviour of the mean and the standard deviation of N numbers sampled from a gaussian distribution N(0,1) as a function of the sampling number N. The higher is N the closer the sampled distribution will be to the true one. The region in the hundreds of samples is still very noisy, but to do much better we would have to reach the order of thousands. We have added a discussion on these aspects in the reviewed version of the manuscript, with a deeper description of the importance of the sorting procedure in the Supplementary Material. .

Author response image 1.

Standard deviation and mean value of a distribution of points sampled from a Gaussian distribution with mean 0 and standard deviation 1, versus the number of samples, N. Increasing N leads to a closer approximation of the expected values. In orange is highlighted the Microscopy Working Region (Microscopy WR) which corresponds to the number of samples we are able to reach with microscopy experiments. In yellow the region we would have to reach to lower the estimating error, which is although very expensive in terms of analysis time.

(7) It would be helpful to show flow cytometry plots including the identified subpopulations for all cell lines, currently, they are shown only for HCT116 cells. More generally, very little raw data is shown.

We have provided the requested plots for the other cell lines together with additional raw data coming from simulations in the Supplementary Material.

(8) The title of the manuscript could be tailored more to the considered problem. At the moment it is very generic.

We see the Reviewer point. The proposed title aims at conveying the wide applicability of the presented approach, which ultimately allows for the assessment of the levels of fluctuations in the levels of the cellular components at division. This in turn reflects the asymmetricity in the division.

Reviewer #1 (Recommendations for the authors):

(1) I am quite concerned about the fact that the theory only considers fluctuations due to cellular division events since intrinsic and extrinsic noise sources are often dominant. I suggest that the authors simulate a full model of cell growth and division (that accounts for fluctuations in gene expression, cell-cycle dynamics, and cell division to generate a controlled synthetic dataset and then use this as input to their method to understand how robust are their results to the influence of noise sources other than partitioning.

We thank the reviewer for the suggestions and following his advice we performed two sets of simulations in which we took into account the effect of the other noise sources. A detailed description of the results and the methods has been added to the Supplementary Material, while the topic has also been assessed in the main text. A cell proliferation cycle is affected by different sources of variability: (i) production and degradation processes of molecules; (ii) variability in length of the cell cycle; (iii) partitioning noise, which identifies asymmetric inheritance of components between the two daughter cells. However, the experimental approach and the model have been formulated to specifically address the effects of partitioning noise. Indeed, since we are dealing with components tagged via live fluorescent markers, production of new fluorophores is impossible and can therefore be discarded. Instead, the degradation process is a global effect that influences the behavior of the mean of the distribution in a time-dependent manner. However, by looking at the experimental data in Figure 1 of the main text, no significant depletion of fluorescence is observed, or at least it is hidden by the experimental fluctuations of the measure. Instead, a more careful evaluation has to be done for what concerns fluctuation in cell cycle length. We conducted two sets of simulations. In the first, we assumed the independence between fluctuations in cell cycle length and partitioning noise.

Cell’s division time was extracted from an Erlang distribution (mean = 18 , k = 4) and the results, showing the behavior of the mean and variance of the component distributions across generations, are presented in Supplementary Information - Figure 1. Under the assumption of independence between different noise sources, no significant effects were observed even for high asymmetries of the partitioning distribution. The second set of simulations considered a situation in which the cell’s components and division time are coupled. We assumed a sizer-like division strategy for which bigger cells have a shorter division time and the results of the simulations are shown in Supplementary Information - Figure 2.

As can be observed, higher levels of division asymmetry increase the fluctuations of the system relative to the analytically expected behavior, particularly in later generations.

The result in Supplementary Information - Figure 3 demonstrates the robustness of our method, as the estimates remain within the pre-established experimental error margin. However, a detailed description of this topic has been provided in the Supplementary Information and into the main text.

(2) I find the use of the Cauchy distribution somewhat odd since this does not have a finite mean or a variance and I suspect it is unlikely this mimics a naturally measurable distribution in their experiments. This should either be justified biologically or else replaced by a more realistic distribution.

Following the reviewer’s suggestion, we have changed the distribution to Gaussian one.

(3) There is a large body of literature on gene expression models that incorporate a large amount of detail including cell-cycle dynamics and cell division which are relevant to their discussion but not referenced. I suggest they read the following and see how to incorporate at least some of them in their discussion:

Frequency domain analysis of fluctuations of mRNA and protein copy numbers within a cell lineage: theory and experimental validation., Physical Review X, 11.2 (2021): 021032.

Exact solution of stochastic gene expression models with bursting, cell cycle and replication dynamics., Physical Review E, 101.3 (2020): 032403.

Coupling gene expression dynamics to cell size dynamics and cell cycle events: Exact and approximate solutions of the extended telegraph model., Iscience, 26.1 (2023).

Models of protein production along the cell cycle: An investigation of possible sources of noise., Plos one, 15.1 (2020): e0226016.

Sources, propagation and consequences of stochasticity in cellular growth., Nature communications, 9(1), 4528

Intrinsic and extrinsic noise of gene expression in lineage trees., Scientific Reports, 9.1 (2019): 474.

We thank the Reviewer for the provided articles. We enlarged both introduction and discussion commenting on them, also in response to the second Reviewer comments.

Reviewer #2 (Recommendations for the authors):

(1) Even when it is used only during simulation for the sake of illustration, the Cauchy distribution is a somewhat unfortunate choice as its moments do not exist and hence, the authors' approach would not apply. I would recommend using another distribution instead.

Following the Reviewer’s suggestion we have changed the distribution to Gaussian ones.

(2) "cells population" should be "cell population".

We have amended this mistake in the text.

Author Response

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

Reviewer #1:

Concerns Public Review:

1)The framing of 'infinite possible types of conflict' feels like a strawman. While they might be true across stimuli (which may motivate a feature-based account of control), the authors explore the interpolation between two stimuli. Instead, this work provides confirmatory evidence that task difficulty is represented parametrically (e.g., consistent with literatures like n-back, multiple object tracking, and random dot motion). This parametric encoding is standard in feature-based attention, and it's not clear what the cognitive map framing is contributing.

Suggestion:

1) 'infinite combinations'. I'm frankly confused by the authors response. I don't feel like the framing has changed very much, besides a few minor replacements. Previous work in MSIT (e.g., by the author Zhongzheng Fu) has looked at whether conflict levels are represented similarly across conflict types using multivariate analyses. In the paper mentioned by Ritz & Shenhav (2023), the authors looked at whether conflict levels are represented similarly across conflict types using multivariate analyses. It's not clear what this paper contributes theoretically beyond the connections to cognitive maps, which feel like an interpretative framework rather than a testable hypothesis (i.e., these previous paper could have framed their work as cognitive maps).

Response: We acknowledge the limitations inherent in our experimental design, which prevents us from conducting a strict test of the cognitive space view. In our previous revision, we took steps to soften our conclusions and emphasize these limitations. However, we still believe that our study offers valuable and novel insights into the cognitive space, and the tests we conducted are not merely strawman arguments.

Specifically, our study aimed to investigate the fundamental principles of the cognitive space view, as we stated in our manuscript that “the representations of different abstract information are organized continuously and the representational geometry in the cognitive space is determined by the similarity among the represented information (Bellmund et al., 2018)”. While previous research has applied multivariate analyses to understand cognitive control representation, no prior studies had directedly tested the two key hypotheses associated with cognitive space: (1) that cognitive control representation across conflict types is continuous, and (2) that the similarity among representations of different conflict types is determined by their external similarity.

Our study makes a unique contribute by directly testing these properties through a parametric manipulation of different conflict types. This approach differs significantly from previous studies in two ways. First, our parametric manipulation involves more than two levels of conflict similarity, enabling us to directly test the two critical hypotheses mentioned above. Unlike studies such as Fu et al. (2022) and other that have treated different conflict types categorically, we introduced a gradient change in conflict similarity. This differentiation allowed us to employ representational similarity analysis (RSA) over the conflict similarity, which goes beyond mere decoding as utilized in prior work (see more explanation below for the difference between Fu et al., 2022 and our study [1]).

Second, our parametric manipulation of conflict types differs from previous studies that have manipulated task difficulty, and the modulation of multivariate pattern similarity observed in our study could not be attributed by task difficulty. Previous research, including the Ritz & Shenhav (2023) (see below explanation[2]), has primarily shown that task difficulty modulates univoxel brain activation. A recent work by Wen & Egner (2023) reported a gradual change in the multivariate pattern of brain activations across a wide range of frontoparietal areas, supporting the reviewer’s idea that “task difficulty is represented parametrically”. However, we do not believe that our results reflect the task difficulty representation. For instance, in our study, the spatial Stroop-only and Simon-only conditions exhibited similar levels of difficulty, as indicated by their relatively comparable congruency effects (Fig. S1). Despite this similarity in difficulty, we found that the representational similarity between these two conditions was the lowest (see revised Fig. S4, the most off-diagonal value). This observation aligns more closely with our hypothesis that these two conditions are most dissimilar in terms of their conflict types.

[1] Fu et al. (2022) offers important insights into the geometry of cognitive space for conflict processing. They demonstrated that Simon and flanker conflicts could be distinguished by a decoder that leverages the representational geometry within a multidimensional space. However, their model of cognitive space primarily relies on categorical definitions of conflict types (i.e., Simon versus flanker), rather than exploring a parametric manipulation of these conflict types. The categorical manipulations make it difficult to quantify conceptual similarity between conflict types and hence limit the ability to test whether neural representations of conflict capture conceptual similarity. To the best of our knowledge, no previous studies have manipulated the conflict types parametrically. This gap highlights a broader challenge within cognitive science: effectively manipulating and measuring similarity levels for conflicts, as well as other high-level cognitive processes, which are inherently abstract. We therefore believe our parametric manipulation of conflict types, despite its inevitable limitations, is an important contribution to the literature.

We have incorporated the above statements into our revised manuscript: Methodological implications. Previous studies with mixed conflicts have applied mainly categorical manipulations of conflict types, such as the multi-source interference task (Fu et al., 2022) and color Stroop-Simon task (Liu et al., 2010). The categorical manipulations make it difficult to quantify conceptual similarity between conflict types and hence limit the ability to test whether neural representations of conflict capture conceptual similarity. To the best of our knowledge, no previous studies have manipulated the conflict types parametrically. This gap highlights a broader challenge within cognitive science: effectively manipulating and measuring similarity levels for conflicts, as well as other high-level cognitive processes, which are inherently abstract. The use of an experimental paradigm that permits parametric manipulation of conflict similarity provides a way to systematically investigate the organization of cognitive control, as well as its influence on adaptive behaviors.

[2] The work by Ritz & Shenhav (2023) indeed applied multivariate analyses, but they did not test the representational similarity across different levels of task difficulty in a similar way as our investigation into different levels of conflict types, neither did they manipulated conflict types as our study. They first estimated univariate brain activations that were parametrically scaled by task difficulty (e.g., target coherence), yielding one map of parameter estimates (i.e., encoding subspace) for each of the target coherence and distractor congruence. The multivoxel patterns from the above maps were correlated to test whether the target coherence and distractor congruence share the similar neural encoding. It is noteworthy that the encoding of task difficulty in their study is estimated at the univariate level, like the univariate parametric modulation analysis in our study. The representational similarity across target coherence and distractor congruence was the second-order test and did not reflect the similarity across different difficulty levels. Though, we have found another study (Wen & Egner, 2023) that has directly tested the representational similarity across different levels of task difficulty, and they observed a higher representational similarity between conditions with similar difficulty levels within a wide range of brain regions.

Reference:

Wen, T., & Egner, T. (2023). Context-independent scaling of neural responses to task difficulty in the multiple-demand network. Cerebral Cortex, 33(10), 6013-6027. https://doi.org/10.1093/cercor/bhac479

Fu, Z., Beam, D., Chung, J. M., Reed, C. M., Mamelak, A. N., Adolphs, R., & Rutishauser, U. (2022). The geometry of domain-general performance monitoring in the human medial frontal cortex. Science (New York, N.Y.), 376(6593), eabm9922. https://doi.org/10.1126/science.abm9922

Ritz, H., & Shenhav, A. (2023). Orthogonal neural encoding of targets and distractors supports multivariate cognitive control. https://doi.org/10.1101/2022.12.01.518771 Another issue is suggesting mixtures between two types of conflict may be many independent sources of conflict. Again, this feels like the strawman. There's a difference between infinite combinations of stimuli on the one hand, and levels of feature on the other hand. The issue of infinite stimuli is why people have proposed feature-based accounts, which are often parametric, eg color, size, orientation, spatial frequency. Mixing two forms of conflict is interesting, but the task limitations (i.e., highly correlated features) prevent an analysis of whether these are truly mixed (or eg reflect variations on just one of the conflict types). Without being able to compare a mixture between types vs levels of only one type, it's not clear what you can draw from these results re: how these are combined (and not clear how it reconciles the debate between general and specific).

Response: As the reviewer pointed out, a feature (or a parameterization) is an efficient way to encode potentially infinite stimuli. This is the same idea as our hypothesis: different conflict types are represented in a cognitive space akin to concrete features such as a color spectrum. This concept can be illustrated in the figure below.

Author response image 1.

We would like to clarify that in our study we have manipulated five levels of conflict types, but they all originated from two fundamental sources: vertically spatial Stroop and horizontally Simon conflicts. We agree that the mixture of these two sources does not inherently generate additional conflict sources. However, this mixture does influence the similarity among different conflict conditions, which provides essential variability that is crucial for testing the core hypotheses (i.e., continuity and similarity modulation, see the response above) of the cognitive space view. This clarification is crucial as the reviewer’s impression might have been influenced by our introduction, where we repeatedly emphasized multiple sources of conflicts. Our aim in the introduction was to outline a broader conceptual framework, which might not directly reflect the specific design of our current study. Recognizing the possibility of misinterpretation, we have adjusted our introduction and discussion to place less emphasis on the variety of possible conflict sources. For example, we have removed the expression “The large variety of conflict sources implies that there may be innumerable number of conflict conditions” from the introduction. As we have addressed in the previous response, the observed conflict similarity effect could not be attributed to merely task difficulty. Similarly, the mixture of spatial Stroop and Simon conflicts should not be attributed to one conflict source only; doing so would oversimplify it to an issue of task difficulty, as it would imply that our manipulation of conflict types merely represented varying levels of a single conflict, akin to manipulating task difficulty when everything else being equal. Importantly, the mixed conditions differ from variations along a single conflict source in that they also incorporate components of the other conflict source, thereby introducing difference beyond that would be found within variances of a single conflict source. There are a few additional evidence challenging the single dimension assumption. In our previous revisions, we compared model fittings between the Cognitive-Space model and the Stroop-/Simon-only models, and results showed that the CognitiveSpace model (BIC = 5377093) outperformed the Stroop-Only (BIC = 5377122) and Simon-Only (BIC = 5377096) models. This suggests that mixed conflicts might not be solely reflective of either Stroop or Simon sources, although we did not include these results due to concerns raised by reviewers about the validity of such comparisons, given the high anticorrelation between the two dimensions. Furthermore, Fu et al. (2022) demonstrated that the mixture of Simon and Flanker conflicts (the sf condition) is represented as the vector sum of the Flanker and Simon dimensions within their space model, indicating a compositional nature. Similarly, our mixed conditions are combinations of Stroop and Simon conflicts, and it is plausible that these mixtures represent a fusion of both Stroop and Simon components, rather than just one. Thus, we disagree that the mixture of conflicts is a strawman. In response to this concern, we have included a statement in our limitation section: “Another limitation is that in our design, the spatial Stroop and Simon effects are highly anticorrelated. This constraint may make the five conflict types represented in a unidimensional space (e.g., a circle) embedded in a 2D space. This limitation also means we cannot conclusively rule out the possibility of a real unidimensional space driven solely by spatial Stroop or Simon conflicts. However, this appears unlikely, as it would imply that our manipulation of conflict types merely represented varying levels of a single conflict, akin to manipulating task difficulty when everything else being equal. If task difficulty were the primary variable, we would expect to see greater representational similarity between task conditions of similar difficulty, such as the Stroop and Simon conditions, which demonstrates comparable congruency effects (see Fig. S1). Contrary to this, our findings reveal that the Stroop-only and Simon-only conditions exhibit the lowest representational similarity (Fig. S4). Furthermore, Fu et al. (2022) has shown that the representation of mixtures of Simon and Flanker conflicts was compositional, rather than reflecting single dimension, which also applies to our cases.”

My recommendation would be to dramatically rewrite to reduce the framing of this providing critical evidence in favor of cognitive maps, and being more overt about the limitations of this task. However, the authors are not required to make further revisions in eLife's new model, and it's not clear how my scores would change if they made those revisions (ie the conceptual limitations would remain, the claims would just now match the more limited scope).

Response: With the above rationales and the adjustments we have made in the manuscripts, we believe that we have thoroughly acknowledged and articulated the limitations of our study. Therefore, we have decided against a complete rewrite of the manuscript.

Public Review:

2) The representations within DLPFC appear to treat 100% Stoop and (to a lesser extent) 100% Simon differently than mixed trials. Within mixed trials, the RDM within this region don't strongly match the predictions of the conflict similarity model. It appears that there may be a more complex relationship encoded in this region.

Suggestion:

2) RSMs in the key region of interest. I don't really understand the authors response here either. e.g,. 'It is essential to clarify that our conclusions were based on the significant similarity modulation effect identified in our statistical analysis using the cosine similarity model, where we did not distinguish between the within-Stroop condition and the other four within-conflict conditions (Fig. 7A, now Fig. 8A). This means that the representation of conflict type was not biased by the seemingly disparities in the values shown here'. In Figure 1C, it does look like they are testing this model.

It seems like a stronger validation would test just the mixture trials (i.e., ignoring Simon-only and stroop-only). However, simon/stroop-only conditions being qualitatively different does beg the question of whether these are being represented parametrically vs categorically.

Response: We apologize for the confusion caused by our previous response. To clarify, our conclusions have been drawn based on the robust conflict similarity effect.

The conflict similarity regressor is defined by higher values in the diagonal cells (representing within-conflict similarity) than the off-diagonal cells (indicating between-conflict similarity), as illustrated in Fig. 1C and Fig. 8A (now Fig. 4B). It is important to note that this regressor may not be particularly sensitive to the variations within the diagonal cells. Our previous response aimed to emphasize that the inconsistencies observed along the diagonal do not contradict our core hypothesis regarding the conflict similarity effect.

We recognized that since the visualization in Fig. S4, based on the raw RSM (i.e., Pearson correlation), may have been influenced by other regressors in our model than the conflict similarity effect. To reflect pattern similarity with confounding factors controlled for, we have visualized the RSM by including only the fixed effect of the conflict similarity and the residual while excluding all other factors. As shown in the revised Figure S4, the difference between the within-Stroop and other diagonal cells was greatly reduced. Instead, it revealed a clear pattern where that the diagonal values were higher than the off-diagonal values in the incongruent condition, aligning with our hypothesis regarding the conflict similarity modulator. Although some visual distinctions persist within the five diagonal cells (e.g., in the incongruent condition, the Stroop, Simon, and StMSmM conditions appear slightly lower than StHSmL and StLSmM conditions), follow-up one-way ANOVAs among these five diagonal conditions showed no significant differences. This held true for both incongruent and congruent conditions, with Fs < 1. Thus, we conclude that there is no strong evidence supporting the notion that Simon- and spatial Stroop-only conditions are systematically different from other conflict types. As a result, we decided not to exclude these two conflict types from analysis.

Author response image 2.

The stronger conflict type similarity effect in incongruent versus congruent conditions. Shown are the summary representational similarity matrices for the right 8C region in incongruent (left) and congruent (right) conditions, respectively. Each cell represents the averaged Pearson correlation (after regressing out all factors except the conflict similarity) of cells with the same conflict type and congruency in the 1400×1400 matrix. Note that the seemingly disparities in the values of withinconflict cells (i.e., the diagonal) did not reach significance for either incongruent or congruent trials, Fs < 1.

Public Review:

3) To orthogonalized their variables, the authors need to employ a complex linear mixed effects analysis, with a potential influence of implementation details (e.g., high-level interactions and inflated degrees of freedom).

Suggestion:

3) The DF for a mixed model should not be the number of observations minus the number of fixed effects. The gold standard is to use satterthwaite correction (e.g. in Matlab, fixedEffects(lme,'DFMethod','satterthwaite')), or number of subjects - number of fixed effects (i.e. you want to generalize to new subjects, not just new samples from the same subjects). Honestly, running a 4-way interaction probably is probably using more degrees of freedom than are appropriate given the number of subjects.

Response: We concur with the reviewer’s comment that our previous estimation of degrees of freedom (DFs) was inaccurate. Following your suggestion, we have now applied the “Satterthwaite” approach to approximate the DFs for all our linear mixed effect model analyses. This adjustment has led to the correction of both DFs and p values. In the Methods section, we have mentioned this revision.

“We adjusted the t and p values with the degrees of freedom calculated through the Satterthwaite approximation method (Satterthwaite, 1946). Of note, this approach was applied to all the mixed-effect model analyses in this study.”

The application of this method has indeed resulted in a reduction of our statistical significance. However, our overall conclusions remained robust. Instead of the highly stringent threshold used in our previous version (Bonferonni corrected p < .0001), we have now adopted a relatively more lenient threshold of Bonferonni correction at p < 0.05, which is commonly employed in the literature. Furthermore, it is worth noting that the follow-up criteria 2 and 3 are inherently second-order analyses. Criterion 2 involves examining the interaction effect (conflict similarity effect difference between incongruent and congruent conditions), and criterion 3 involves individual correlation analyses. Due to their second-order nature, these criteria inherently have lower statistical power compared to criterion 1 (Blake & Gangestad, 2020). We thus have applied a more lenient but still typically acceptable false discovery rate (FDR) correction to criteria 2 and 3. This adjustment helps maintain the rigor of our analysis while considering the inherent differences in statistical power across the various criteria. We have mentioned this revision in our manuscript:

“We next tested whether these regions were related to cognitive control by comparing the strength of conflict similarity effect between incongruent and congruent conditions (criterion 2) and correlating the strength to behavioral similarity modulation effect (criterion 3). Given these two criteria pertain to second-order analyses (interaction or individual analyses) and thus might have lower statistical power (Blake & Gangestad, 2020), we applied a more lenient threshold using false discovery rate (FDR) correction (Benjamini & Hochberg, 1995) on the above-mentioned regions.”

With these adjustments, we consistently identified similar brain regions as observed in our previous version. Specifically, we found that only the right 8C region met the three criteria in the conflict similarity analysis. In addition, the regions meeting the criteria for the orientation effect included the FEF and IP2 in left hemisphere, and V1, V2, POS1, and PF in the right hemisphere. We have thoroughly revised the description of our results, updated the figures and tables in both the revised manuscript and supplementary material to accurately reflect these outcomes.

Reference:

Blake, K. R., & Gangestad, S. (2020). On Attenuated Interactions, Measurement Error, and Statistical Power: Guidelines for Social and Personality Psychologists. Pers Soc Psychol Bull, 46(12), 1702-1711. https://doi.org/10.1177/0146167220913363

Minor:

1. Figure 8 should come much earlier (e.g, incorporated into Figure 1), and there should be consistent terms for 'cognitive map' and 'conflict similarity'.

Response: We appreciate this suggestion. Considering that Figure 7 (“The crosssubject RSA model and the rationale”) also describes the models, we have merged Figure 7 and 8 and moved the new figure ahead, before we report the RSA results. Now you could find it in the new Figure 4, see below. We did not incorporate them into Figure 1 since Figure 1 is already too crowded.

Author response image 3.

Fig. 4. Rationale of the cross-subject RSA model and the schematic of key RSMs. A) The RSM is calculated as the Pearson’s correlation between each pair of conditions across the 35 subjects. For 17 subjects, the stimuli were displayed on the top-left and bottom-right quadrants, and they were asked to respond with left hand to the upward arrow and right hand to the downward arrow. For the other 18 subjects, the stimuli were displayed on the top-right and bottom-left quadrants, and they were asked to respond with left hand to the downward arrow and right hand to the upward arrow. Within each subject, the conflict type and orientation regressors were perfectly covaried. For instance, the same conflict type will always be on the same orientation. To de-correlate conflict type and orientation effects, we conducted the RSA across subjects from different groups. For example, the bottom-right panel highlights the example conditions that are orthogonal to each other on the orientation, response, and Simon distractor, whereas their conflict type, target and spatial Stroop distractor are the same. The dashed boxes show the possible target locations for different conditions. (B) and (C) show the orthogonality between conflict similarity and orientation RSMs. The within-subject RSMs (e.g., Group1-Group1) for conflict similarity and orientation are all the same, but the cross-group correlations (e.g., Group2-Group1) are different. Therefore, we can separate the contribution of these two effects when including them as different regressors in the same linear regression model. (D) and (E) show the two alternative models. Like the cosine model (B), within-group trial pairs resemble betweengroup trial pairs in these two models. The domain-specific model is an identity matrix. The domaingeneral model is estimated from the absolute difference of behavioral congruency effect, but scaled to 0 (lowest similarity) – 1 (highest similarity) to aid comparison. The plotted matrices in B-E include only one subject each from Group 1 and Group 2. Numbers 1-5 indicate the conflict type conditions, for spatial Stroop, StHSmL, StMSmM, StLSmH, and Simon, respectively. The thin lines separate four different sub-conditions, i.e., target arrow (up, down) × congruency (incongruent, congruent), within each conflict type.

In our manuscript, the term “cognitive map/space” was used when explaining the results in a theoretical perspective, whereas the “conflict similarity” was used to describe the regressor within the RSA. These terms serve distinct purposes in our study and cannot be interchangeably substituted. Therefore, we have retained them in their current format. However, we recognize that the initial introduction of the “Cognitive-Space model” may have appeared somewhat abrupt. To address this, we have included a brief explanatory note: “The model described above employs the cosine similarity measure to define conflict similarity and will be referred to as the Cognitive-Space model.”

Author Response

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

Thank you and the reviewers for further providing constructive comments and suggestions on our manuscript. On behalf of all the co-authors, I have enclosed a revised version of the above referenced paper. Below, I have merged similar public reviews and recommendations (if applicable) from each reviewer and provided point-by-point responses.

Reviewer #1:

People can perform a wide variety of different tasks, and a long-standing question in cognitive neuroscience is how the properties of different tasks are represented in the brain. The authors develop an interesting task that mixes two different sources of difficulty, and find that the brain appears to represent this mixture on a continuum, in the prefrontal areas involved in resolving task difficulty. While these results are interesting and in several ways compelling, they overlap with previous findings and rely on novel statistical analyses that may require further validation.

Strengths

1. The authors present an interesting and novel task for combining the contributions of stimulus-stimulus and stimulus-response conflict. While this mixture has been measured in the multi-source interference task (MSIT), this task provides a more graded mixture between these two sources of difficulty.

2. The authors do a good job triangulating regions that encoding conflict similarity, looking for the conjunction across several different measures of conflict encoding. These conflict measures use several best-practice approaches towards estimating representational similarity.

3. The authors quantify several salient alternative hypothesis and systematically distinguish their core results from these alternatives.

4. The question that the authors tackle is important to cognitive control, and they make a solid contribution.

The authors have addressed several of my concerns. I appreciate the authors implementing best practices in their neuroimaging stats.

I think that the concerns that remain in my public review reflect the inherent limitations of the current work. The authors have done a good job working with the dataset they've collected.

Response: We would like to thank the reviewer for the positive evaluation of our manuscript and the constructive comments and suggestions. In response to your suggestions and concerns, we have removed the Stroop/Simon-only and the Stroop+Simon models, revised our conclusion and modified the misleading phrases.

We have provided detailed responses to your comments below.

1. The evidence from this previous work for mixtures between different conflict sources makes the framing of 'infinite possible types of conflict' feel like a strawman. The authors cite classic work (e.g., Kornblum et al., 1990) that develops a typology for conflict which is far from infinite. I think few people would argue that every possible source and level of difficulty will have to be learned separately. This work provides confirmatory evidence that task difficulty is represented parametrically (e.g., consistent with the n-back, MOT, and random dot motion literature).

notes for my public concerns.

In their response, the authors say:

'If each combination of the Stroop-Simon combination is regarded as a conflict condition, there would be infinite combinations, and it is our major goal to investigate how these infinite conflict conditions are represented effectively in a space with finite dimensions.'

I do think that this is a strawman. The paper doesn't make a strong case that this position ('infinite combinations') is widely held in the field. There is previous work (e.g., n-back, multiple object tracking, MSIT, dot motion) that has already shown parametric encoding of task difficulty. This paper provides confirmatory evidence, using an interesting new task, that demand are parametric, but does not provide a major theoretical advance.

Response: We agree that the previous expression may have seemed somewhat exaggerative. While it is not “infinite”, recent research indeed suggests that the cognitive control shows domain-specificity across various “domains”, including conflict types (Egner, 2008), sensory modalities (Yang et al., 2017), task-irrelevant stimuli (Spape et al., 2008), and task sets (Hazeltine et al., 2011), to name a few.

These findings collectively support the notion that cognitive control is contextspecific (Bream et al., 2014). That is, cognitive control can be tuned and associated with different (and potentially large numbers of) contexts. Recently, Kikumoto and Mayr (2020) demonstrated that combinations of stimulus, rule and response in the same task formed separatable, conjunctive representations. They further showed that these conjunctive representations facilitate performance. This is in line with the idea that each stimulus-location combination in the present task may be represented separately in a domain-specific manner. Moreover, domain-general task representation can also become domain-specific with learning, which further increases the number of domain-specific conjunctive representations (Mill et al., 2023). In line with the domain-specific account of cognitive control, we referred to the “infinite combinations” in our previous response to emphasize the extreme case of domainspecificity. However, recognizing that the term “infinite” may lead to ambiguity, we have replaced it with phrases such as “a large number of”, “hugely varied”, in our revised manuscript.

We appreciate the reviewer for highlighting the potential connection of our work to existing literature that showed the parametric encoding of task difficulty (e.g., Dagher et al., 1999; Ritz & Shenhav, 2023). For instance, in Ritz et al.’s (2023) study, they parametrically manipulated target difficulty based on consistent ratios of dot color, and found that the difficulty was encoded in the caudal part of dorsal anterior cingulate cortex. Analogically, in our study, the “difficulty” pertains to the behavioral congruency effect that we modulated within the spatial Stroop and Simon dimensions. Notably, we did identify univariate effects in the right dmPFC and IPS associated with the difficulty in the Simon dimension. This parametric effect may lend support to our cognitive space hypothesis, although we exercised caution in interpreting their significance due to the absence of a clear brain-behavioral relevance in these regions. We have added the connection of our work to prior literature in the discussion. The parametric encoding of conflict also mirrors prior research showing the parametric encoding of task demands (Dagher et al., 1999; Ritz & Shenhav, 2023).

However, our analyses extend beyond solely testing the parametric encoding of difficulty. Instead, we focused on the multivariate representation of different conflict types, which we believe is independent from the univariate parametric encoding. Unlike the univariate encoding that relies on the strength within one dimension, the multivariate representation of conflict types incorporates both the spatial Stroop and Simon dimensions. Furthermore, we found that similar difficulty levels did not yield similar conflict representation, as indicated by the low similarity between the spatial Stroop and Simon conditions, despite both showing a similar level of congruency effect (Fig. S1). Additionally, we also observed an interaction between conflict similarity and difficulty (i.e., congruency, Fig. 4B/D), such that the conflict similarity effect was more pronounced when conflict was present. Therefore, we believe that our findings make contribution to the literature beyond the difficulty effect.

Reference:

Egner, T. (2008). Multiple conflict-driven control mechanisms in the human brain. Trends in Cognitive Sciences, 12(10), 374-380. https://doi.org/10.1016/j.tics.2008.07.001

Yang, G., Nan, W., Zheng, Y., Wu, H., Li, Q., & Liu, X. (2017). Distinct cognitive control mechanisms as revealed by modality-specific conflict adaptation effects. Journal of Experimental Psychology: Human Perception and Performance, 43(4), 807-818. https://doi.org/10.1037/xhp0000351

Spapé MM, Hommel B (2008). He said, she said: episodic retrieval induces conflict adaptation in an auditory Stroop task. Psychonomic Bulletin Review,15(6):1117-21. https://doi.org/10.3758/PBR.15.6.1117

Hazeltine E, Lightman E, Schwarb H, Schumacher EH (2011). The boundaries of sequential modulations: evidence for set-level control. Journal of Experimental Psychology: Human Perception & Performance. 2011 Dec;37(6):1898-914. https://doi.org/10.1037/a0024662

Braem, S., Abrahamse, E. L., Duthoo, W., & Notebaert, W. (2014). What determines the specificity of conflict adaptation? A review, critical analysis, and proposed synthesis. Frontiers in Psychology, 5, 1134. https://doi.org/10.3389/fpsyg.2014.01134

Kikumoto A, Mayr U. (2020). Conjunctive representations that integrate stimuli, responses, and rules are critical for action selection. Proceedings of the National Academy of Sciences, 117(19):10603-10608. https://doi.org/10.1073/pnas.1922166117.

Mill, R. D., & Cole, M. W. (2023). Neural representation dynamics reveal computational principles of cognitive task learning. bioRxiv. https://doi.org/10.1101/2023.06.27.546751

Dagher, A., Owen, A. M., Boecker, H., & Brooks, D. J. (1999). Mapping the network for planning: a correlational PET activation study with the Tower of London task. Brain, 122 ( Pt 10), 1973-1987. https://doi.org/10.1093/brain/122.10.1973

Ritz, H., & Shenhav, A. (2023). Orthogonal neural encoding of targets and distractors supports multivariate cognitive control. https://doi.org/10.1101/2022.12.01.518771

1. (Public Reviews) The degree of Stroop vs Simon conflict is perfectly negatively correlated across conditions. This limits their interpretation of an integrated cognitive space, as they cannot separately measure Stroop and Simon effects. The author's control analyses have limited ability to overcome this task limitation. While these results are consistent with parametric encoding, they cannot adjudicate between combined vs separated representations.

(Recommendations) I think that it is still an issue that the task's two features (stroop and simon conflict) are perfectly correlated. This fundamentally limits their ability to measure the similarity in these features. The authors provide several control analyses, but I think these are limited.

Response: We need to acknowledge that the spatial Stroop and Simon components in the five conflict conditions were not “perfectly” correlated, with r = –0.89. This leaves some room for the preliminary model comparison to adjudicate between these models. However, it’s essential to note that conclusions based on these results must be tempered. In line with the reviewer’s observation, we agree that the high correlation between the two conflict sources posed a potential limitation on our ability to independently investigate the contribution of spatial Stroop and Simon conflicts. Therefore, in addition to the limitation we have previously acknowledged, we have now further revised our conclusion and adjusted our expressions accordingly.

Specifically, we now regard the parametric encoding of cognitive control not as direct evidence of the cognitive space view but as preliminary evidence that led us to propose this hypothesis, which requires further testing. Notably, we have also modified the title from “Conflicts are represented in a cognitive space to reconcile domain-general and domain-specific cognitive control” to “Conflicts are parametrically encoded: initial evidence for a cognitive space view to reconcile the debate of domain-general and domain-specific cognitive control”. Also, we revised the conclusion as: In sum, we showed that the cognitive control can be parametrically encoded in the right dlPFC and guides cognitive control to adjust goal-directed behavior. This finding suggests that different cognitive control states may be encoded in an abstract cognitive space, which reconciles the long-standing debate between the domain-general and domain-specific views of cognitive control and provides a parsimonious and more broadly applicable framework for understanding how our brains efficiently and flexibly represents multiple task settings.

From Recommendations The authors perform control analyses that test stroop-only and simon-only models. However, these analyses use a totally different similarity metric, that's based on set intersection rather than geometry. This metric had limited justification or explanation, and it's not clear whether these models fit worse because of the similarity metric. Even here, Simon-only model fit better than Stroop+Simon model. The dimensionality analyses may reflect the 1d manipulation by the authors (i.e. perfectly corrected stroop and simon effects).

Response: The Jaccard measure is the most suitable method we can conceive of for assessing the similarity between two conflicts when establishing the Stroop-only and Simon-only models, achieved by projecting them onto the vertical or horizontal axes, respectively (Author response image 1A). This approach offers two advantages. First, the Jaccard similarity combines both similarity (as reflected by the numerator) and distance (reflected by the difference between denominator and numerator) without bias towards either. Second, the Jaccard similarity in our design is equivalent to the cosine similarity because the denominator in the cosine similarity is identical to the denominator in the Jaccard similarity (both are the radius of the circle, Author response image 1B).

Author response image 1.

Definition of Jaccard similarity. A) Two conflicts (1 and 2) are projected onto the spatial Stroop/Simon axis in the Stroop/Simon-only model, respectively. The Jaccard similarity for Stroop-only and Simon-only model are and respectively. Letters a-d are the projected vectors from the two conflicts to the two axes. Blue and red colors indicate the conflict conditions. Shorter vectors are the intersection and longer vectors are the union. B) According to the cosine similarity model, the similarity is defined as , where e is the projected vector from conflict 1 to conflict 2, and g is the vector of conflict 1. The Jaccard similarity for this case is defined by , where f is the projector vector from conflict 2 to itself. Because f = g in our design, the Jaccard similarity is equivalent to the cosine similarity.

Therefore, we believe that the model comparisons between cosine similarity model and the Stroop/Simon-Only models were equitable. However, we acknowledge the reviewer’s and other reviewers’ concerns about the correlation between spatial Stroop and Simon conflicts, which reduces the space to one dimension (1d) and limits our ability to distinguish between the Stroop-only and Simon-only models, as well as between Stroop+Simon and cosine similarity models. While these distinctions are undoubtedly important for understanding the geometry of the cognitive space, we recognize that they go beyond the major objective of this study, that is, to differentiate the cosine similarity model from domain-general/specific models. Therefore, we have chosen to exclude the Stroop-only, Simon-only and Stroop+Simon models in our revised manuscript.

Something that raised additional concerns are the RSMs in the key region of interest (Fig S5). The pure stroop task appears to be represented very differently from all of the conditions that include simon conflict.

Together, I think these limitations reflect the structure of the task and research goals, not the statistical approach (which has been meaningfully improved).

Response: We appreciate the reviewer for pointing this out. It is essential to clarify that our conclusions were based on the significant similarity modulation effect identified in our statistical analysis using the cosine similarity model, where we did not distinguish between the within-Stroop condition and the other four within-conflict conditions (Fig. 7A, now Fig. 8A). This means that the representation of conflict type was not biased by the seemingly disparities in the values shown here. Moreover, to specifically test the differences between the within-Stroop condition and the other within-conflict conditions, we conducted a mixed-effect model analysis only including trial pairs from the same conflict type. In this analysis, the primary predictor was the cross-condition difference (0 for within-Stroop condition and 1 for other within-conflict conditions). The results showed no significant cross-condition difference in either the incongruent (t = 1.22, p = .23) or the congruent (t = 1.06, p = .29) trials. Thus, we believe the evidence for different similarities is inconclusive in our data and decided not to interpret this numerical difference. We have added this note in the revised figure caption for Figure S5.

Author response image 2.

Fig. S5. The stronger conflict type similarity effect in incongruent versus congruent conditions. (A) Summary representational similarity matrices for the right 8C region in incongruent (left) and congruent (right) conditions, respectively. Each cell represents the averaged Pearson correlation of cells with the same conflict type and congruency in the 1400×1400 matrix. Note that the seemingly disparities in the values of Stroop and other within-conflict cells (i.e., the diagonal) did not reach significance for either incongruent (t = 1.22, p = .23) or congruent (t = 1.06, p = .29) trials. (2) Scatter plot showing the averaged neural similarity (Pearson correlation) as a function of conflict type similarity in both conditions. The values in both A and B are calculated from raw Pearson correlation values, in contrast to the z-scored values in Fig. 4D.

Minor:

• In the analysis of similarity_orientation, the df is very large (~14000). Here, and throughout, the df should be reflective of the population of subjects (ie be less than the sample size).

Response: The large degrees of freedom (df) in our analysis stem from the fact that we utilized a mixed-effect linear model, incorporating all data points (a total of 400×35=14000). In mixed-effect models, the df is determined by subtracting the number of fixed effects (in our case, 7) from the total number of observations. Notably, we are in line with the literature that have reported the df in this manner (e.g., Iravani et al., 2021; Schmidt & Weissman, 2015; Natraj et al., 2022).

Reference:

Iravani B, Schaefer M, Wilson DA, Arshamian A, Lundström JN. The human olfactory bulb processes odor valence representation and cues motor avoidance behavior. Proc Natl Acad Sci U S A. 2021 Oct 19;118(42):e2101209118. https://doi.org/10.1073/pnas.2101209118.

Schmidt, J.R., Weissman, D.H. Congruency sequence effects and previous response times: conflict adaptation or temporal learning?. Psychological Research 80, 590–607 (2016). https://doi.org/10.1007/s00426-015-0681-x.

Natraj, N., Silversmith, D. B., Chang, E. F., & Ganguly, K. (2022). Compartmentalized dynamics within a common multi-area mesoscale manifold represent a repertoire of human hand movements. Neuron, 110(1), 154-174. https://doi.org/10.1016/j.neuron.2021.10.002.

• it would improve the readability if there was more didactic justification for why analyses are done a certain way (eg justifying the jaccard metric). This will help less technically-savvy readers.

Response: We appreciate the reviewer’s suggestion. However, considering the Stroop/Simon-only models in our design may not be a valid approach for distinguishing the contributions of the Stroop/Simon components, we have decided not to include the Jaccard metrics in our revised manuscript.

Besides, to improve the readability, we have moved Figure S4 to the main text (labeled as Figure 7), and added the domain-general/domain-specific schematics in Figure 8.

Author response image 3.

Figure 8. Schematic of key RSMs. (A) and (B) show the orthogonality between conflict similarity and orientation RSMs. The within-subject RSMs (e.g., Group1-Group1) for conflict similarity and orientation are all the same, but the cross-group correlations (e.g., Group2-Group1) are different. Therefore, we can separate the contribution of these two effects when including them as different regressors in the same linear regression model. (C) and (D) show the two alternative models. Like the cosine model (A), within-group trial pairs resemble between-group trial pairs in these two models. The domain-specific model is an identity matrix. The domain-general model is estimated from the absolute difference of behavioral congruency effect, but scaled to 0(lowest similarity)-1(highest similarity) to aid comparison. The plotted matrices here include only one subject each from Group 1 and Group 2. Numbers 1-5 indicate the conflict type conditions, for spatial Stroop, StHSmL, StMSmM, StLSmH, and Simon, respectively. The thin lines separate four different sub-conditions, i.e., target arrow (up, down) × congruency (incongruent, congruent), within each conflict type.

Reviewer #2:

This study examines the construct of "cognitive spaces" as they relate to neural coding schemes present in response conflict tasks. The authors use a novel experimental design in which different types of response conflict (spatial Stroop, Simon) are parametrically manipulated. These conflict types are hypothesized to be encoded jointly, within an abstract "cognitive space", in which distances between task conditions depend only on the similarity of conflict types (i.e., where conditions with similar relative proportions of spatial-Stroop versus Simon conflicts are represented with similar activity patterns). Authors contrast such a representational scheme for conflict with several other conceptually distinct schemes, including a domain-general, domain-specific, and two task-specific schemes. The authors conduct a behavioral and fMRI study to test which of these coding schemes is used by prefrontal cortex. Replicating the authors' prior work, this study demonstrates that sequential behavioral adjustments (the congruency sequence effect) are modulated as a function of the similarity between conflict types. In fMRI data, univariate analyses identified activation in left prefrontal and dorsomedial frontal cortex that was modulated by the amount of Stroop or Simon conflict present, and representational similarity analyses (RSA) that identified coding of conflict similarity, as predicted under the cognitive space model, in right lateral prefrontal cortex.

This study tackles an important question regarding how distinct types of conflict might be encoded in the brain within a computationally efficient representational format. The ideas postulated by the authors are interesting ones and the statistical methods are generally rigorous.

Response: We would like to express our sincere appreciation for the reviewer’s positive evaluation of our manuscript and the constructive comments and suggestions. In response to your suggestions and concerns, we excluded the StroopOnly, SimonOnly and Stroop+Simon models, and added the schematic of domain-general/specific model RSMs. We have provided detailed responses to your comments below.

The evidence supporting the authors claims, however, is limited by confounds in the experimental design and by lack of clarity in reporting the testing of alternative hypotheses within the method and results.

1. Model comparison

The authors commendably performed a model comparison within their study, in which they formalized alternative hypotheses to their cognitive space hypothesis. We greatly appreciate the motivation for this idea and think that it strengthened the manuscript. Nevertheless, some details of this model comparison were difficult for us to understand, which in turn has limited our understanding of the strength of the findings.

The text indicates the domain-general model was computed by taking the difference in congruency effects per conflict condition. Does this refer to the "absolute difference" between congruency effects? In the rest of this review, we assume that the absolute difference was indeed used, as using a signed difference would not make sense in this setting. Nevertheless, it may help readers to add this information to the text.

Response: We apologize for any confusion. The “difference” here indeed refers to the “absolute difference” between congruency effects. We have now clarified this by adding the word “absolute” accordingly.

"Therefore, we defined the domain-general matrix as the absolute difference in their congruency effects indexed by the group-averaged RT in Experiment 2."

Regarding the Stroop-Only and Simon-Only models, the motivation for using the Jaccard metric was unclear. From our reading, it seems that all of the other models --- the cognitive space model, the domain-general model, and the domain-specific model --- effectively use a Euclidean distance metric. (Although the cognitive space model is parameterized with cosine similarities, these similarity values are proportional to Euclidean distances because the points all lie on a circle. And, although the domain-general model is parameterized with absolute differences, the absolute difference is equivalent to Euclidean distance in 1D.) Given these considerations, the use of Jaccard seems to differ from the other models, in terms of parameterization, and thus potentially also in terms of underlying assumptions. Could authors help us understand why this distance metric was used instead of Euclidean distance? Additionally, if Jaccard must be used because this metric seems to be non-standard in the use of RSA, it would likely be helpful for many readers to give a little more explanation about how it was calculated.

Response: We believe that the Jaccard similarity measure is consistent with the Cosine similarity measure. The Jaccard similarity is calculated as the intersection divided by the union. To define the similarity of two conflicts in the Stroop-only and Simon-only models, we first project them onto the vertical or horizontal axes, respectively (as shown in Author response image 1A). The Jaccard similarity in our design is equivalent to the cosine similarity because the denominator in the Jaccard similarity is identical to the denominator in the cosine similarity (both are the radius of the circle, Author response image 1B).

However, it is important to note that a cosine similarity cannot be defined when conflicts are projected onto spatial Stroop or Simon axis simultaneously. Therefore, we used the Jaccard similarity in the previous version of our manuscript.

Author response image 4.

Definition of Jaccard similarity. A) Two conflicts (1 and 2) are projected onto the spatial Stroop/Simon axis in the Stroop/Simon-only model, respectively. The Jaccard similarity for Stroop-only and Simon-only model are and respectively. Letters a-d are the projected vectors from the two conflicts to the two axes. Blue and red colors indicate the conflict conditions. Shorter vectors are the intersection and longer vectors are the union. B) According to the cosine similarity model, the similarity is defined as , where e is the projected vector from conflict 1 to conflict 2, and g is the vector of conflict 1. The Jaccard similarity for this case is defined by , where f is the projector vector from conflict 2 to itself. Because f = g in our design, the Jaccard similarity is equivalent to the cosine similarity.

However, we agree with the reviewer’s and other reviewers’ concern that the correlation between spatial Stroop and Simon conflicts makes it less likely to distinguish the Stroop+Simon from cosine similarity models. While distinguishing them is essential to understand the detailed geometry of the cognitive space, it is beyond our major purpose, that is, to distinguish the cosine similarity model with the domain-general/specific models. Therefore, we have chosen to exclude the Stroop-only, Simon-only and Stroop+Simon models from our revised manuscript.

When considering parameterizing the Stroop-Only and Simon-Only models with Euclidean distances, one concern we had is that the joint inclusion of these models might render the cognitive space model unidentifiable due to collinearity (i.e., the sum of the Stroop-Only and Simon-Only models could be collinear with the cognitive space model). Could the authors determine whether this is the case? This issue seems to be important, as the presence of such collinearity would suggest to us that the design is incapable of discriminating those hypotheses as parameterized.

Response: We acknowledge that our design does not allow for a complete differentiation between the parallel encoding (StroopOnly+SimonOnly) model and the cognitive space model, given their high correlation (r = 0.85). However, it is important to note that the StroopOnly+SimonOnly model introduces more free parameters, making the model fitting poorer than the cognitive space model.

Additionally, the cognitive space model also shows high correlations with the StroopOnly and SimonOnly models (both rs = 0.66). It is crucial to emphasize that our study’s primary goal does not involve testing the parallel encoding hypothesis (through the StroopOnly+SimonOnly model). As a result, we have chosen to remove the model comparison results with the StroopOnly, SimonOnly and StroopOnly+SimonOnly models. Instead, the cognitive space model shows lower correlation with the purely domain-general (r = −0.16) and domain-specific (r = 0.46) models.

1. Issue of uniquely identifying conflict coding

We certainly appreciate the efforts that authors have taken to address potential confounders for encoding of conflict in their original submission. We broach this question not because we wish authors to conduct additional control analyses, but because this issue seems to be central to the thesis of the manuscript and we would value reading the authors' thoughts on this issue in the discussion.

To summarize our concerns, conflict seems to be a difficult variable to isolate within aggregate neural activity, at least relative to other variables typically studied in cognitive control, such as task-set or rule coding. This is because it seems reasonable to expect that many more nuisance factors covary with conflict -- such as univariate activation, level of cortical recruitment, performance measures, arousal --- than in comparison with, for example, a well-designed rule manipulation. Controlling for some of these factors post-hoc through regression is commendable (as authors have done here), but such a method will likely be incomplete and can provide no guarantees on the false positive rate.

Relatedly, the neural correlates of conflict coding in fMRI and other aggregate measures of neural activity are likely of heterogeneous provenance, potentially including rate coding (Fu et al., 2022), temporal coding (Smith et al., 2019), modulation of coding of other more concrete variables (Ebitz et al., 2020, 10.1101/2020.03.14.991745; see also discussion and reviews of Tang et al., 2016, 10.7554/eLife.12352), or neuromodulatory effects (e.g., Aston-Jones & Cohen, 2005). Some of these origins would seem to be consistent with "explicit" coding of conflict (conflict as a representation), but others would seem to be more consistent with epiphenomenal coding of conflict (i.e., conflict as an emergent process). Again, these concerns could apply to many variables as measured via fMRI, but at the same time, they seem to be more pernicious in the case of conflict. So, if authors consider these issues to be germane, perhaps they could explicitly state in the discussion whether adopting their cognitive space perspective implies a particular stance on these issues, how they interpret their results with respect to these issues, and if relevant, qualify their conclusions with uncertainty on these issues.

Response: We appreciate the reviewer’s insightful comments regarding the representation and process of conflict.

First, we agree that the conflict is not simply a pure feature like a stimulus but often arises from the interaction (e.g., dimension overlap) between two or more aspects. For example, in the manual Stroop, conflict emerges from the inconsistent semantic information between color naming and word reading. Similarly, other higher-order cognitive processes such as task-set also underlie the relationship between concrete aspects. For instance, in a face/house categorization task, the taskset is the association between face/house and the responses. When studying these higher-order processes, it is often impossible to completely isolate them from bottomup features. Therefore, methods like the representational similarity analysis and regression models are among the limited tools available to attempt to dissociate these concrete factors from conflict representation. While not perfect, this approach has been suggested and utilized in practice (Freund et al., 2021).

Second, we agree that conflict can be both a representation and an emerging process. These two perspectives are not necessarily contradictory. According to David Marr’s influential three-level theory (Marr, 1982), representation is the algorithm of the process to achieve a goal based on the input. Therefore, a representation can refer to not only a static stimulus (e.g., the visual representation of an image), but also a dynamic process. Building on this perspective, we posit that the representation of cognitive control consists of an array of dynamic representations embedded within the overall process. A similar idea has been proposed that the abstract task profiles can be progressively constructed as a representation in our brain (Kikumoto & Mayr, 2020).

We have incorporated this discussion into the manuscript:

"Recently an interesting debate has arisen concerning whether cognitive control should be considered as a process or a representation (Freund, Etzel, et al., 2021). Traditionally, cognitive control has been predominantly viewed as a process. However, the study of its representation has gained more and more attention. While it may not be as straightforward as the visual representation (e.g., creating a mental image from a real image in the visual area), cognitive control can have its own form of representation. An influential theory, Marr’s (1982) three-level model proposed that representation serves as the algorithm of the process to achieve a goal based on the input. In other words, representation can encompass a dynamic process rather than being limited to static stimuli. Building on this perspective, we posit that the representation of cognitive control consists of an array of dynamic representations embedded within the overall process. A similar idea has been proposed that the representation of task profiles can be progressively constructed with time in the brain (Kikumoto & Mayr, 2020)."

Reference:

Freund, M. C., Etzel, J. A., & Braver, T. S. (2021). Neural Coding of Cognitive Control: The Representational Similarity Analysis Approach. Trends in Cognitive Sciences, 25(7), 622-638. https://doi.org/10.1016/j.tics.2021.03.011

Marr, D. C. (1982). Vision: A computational investigation into human representation and information processing. New York: W.H. Freeman.

Kikumoto A, Mayr U. (2020). Conjunctive representations that integrate stimuli, responses, and rules are critical for action selection. Proceedings of the National Academy of Sciences, 117(19):10603-10608. https://doi.org/10.1073/pnas.1922166117.

1. Interpretation of measured geometry in 8C

We appreciate the inclusion of the measured similarity matrices of area 8C, the key area the results focus on, to the supplemental, as this allows for a relatively model-agnostic look at a portion of the data. Interestingly, the measured similarity matrix seems to mismatch the cognitive space model in a potentially substantive way. Although the model predicts that the "pure" Stroop and Simon conditions will have maximal self-similarity (i.e., the Stroop-Stroop and Simon-Simon cells on the diagonal), these correlations actually seem to be the lowest, by what appears to be a substantial margin (particularly the Stroop-Stroop similarities). What should readers make of this apparent mismatch? Perhaps authors could offer their interpretation on how this mismatch could fit with their conclusions.

Response: We appreciate the reviewer for bringing this to our attention. It is essential to clarify that our conclusions were based on the significant similarity modulation effect observed in our statistical analysis using the cosine similarity model, where we did not distinguish between the within-Stroop condition and the other four withinconflict conditions (Fig. 7A). This means that the representation of conflict type was not biased by the seemingly disparities in the values shown here. Moreover, to specifically address the potential differences between the within-Stroop condition and the other within-conflict conditions, we conducted a mixed-effect model. In this analysis, the primary predictor was the cross-condition difference (0 for within-Stroop condition and 1 for other within-conflict conditions). The results showed no significant cross-condition difference in either the incongruent trials (t = 1.22, p = .23) or the congruent (t = 1.06, p = .29) trials. Thus, we believe the evidence for different similarities is inconclusive in our data and decided not to interpret this numerical difference.

We have added this note in the revised figure caption for Figure S5.

Author response image 5.

Fig. S5. The stronger conflict type similarity effect in incongruent versus congruent conditions. (A) Summary representational similarity matrices for the right 8C region in incongruent (left) and congruent (right) conditions, respectively. Each cell represents the averaged Pearson correlation of cells with the same conflict type and congruency in the 1400×1400 matrix. Note that the seemingly disparities in the values of Stroop and other within-conflict cells (i.e., the diagonal) did not reach significance for either incongruent (t = 1.22, p = .23) or congruent (t = 1.06, p = .29) trials. (2) Scatter plot showing the averaged neural similarity (Pearson correlation) as a function of conflict type similarity in both conditions. The values in both A and B are calculated from raw Pearson correlation values, in contrast to the z-scored values in Fig. 4D.

1. It would likely improve clarity if all of the competing models were displayed as summarized RSA matrices in a single figure, similar to (or perhaps combined with) Figure 7.

Response: We appreciate the reviewer’s suggestion. We now have incorporated the domain-general and domain-specific models into the Figure 7 (now Figure 8).

Author response image 6.

Figure 8. Schematic of key RSMs. (A) and (B) show the orthogonality between conflict similarity and orientation RSMs. The within-subject RSMs (e.g., Group1-Group1) for conflict similarity and orientation are all the same, but the cross-group correlations (e.g., Group2-Group1) are different. Therefore, we can separate the contribution of these two effects when including them as different regressors in the same linear regression model. (C) and (D) show the two alternative models. Like the cosine model (A), within-group trial pairs resemble between-group trial pairs in these two models. The domain-specific model is an identity matrix. The domain-general model is estimated from the absolute difference of behavioral congruency effect, but scaled to 0(lowest similarity)-1(highest similarity) to aid comparison. The plotted matrices here include only one subject each from Group 1 and Group 2. Numbers 1-5 indicate the conflict type conditions, for spatial Stroop, StHSmL, StMSmM, StLSmH, and Simon, respectively. The thin lines separate four different sub-conditions, i.e., target arrow (up, down) × congruency (incongruent, congruent), within each conflict type.

1. Because this model comparison is key to the main inferences in the study, it might also be helpful for most readers to move all of these RSA model matrices to the main text, instead of in the supplemental.

Response: We thank the reviewer for this suggestion. We have moved the Fig. S4 to the main text, labeled as the new Figure 7.

1. It may be worthwhile to check how robust the observed brain-behavior association (Fig 4C) is to the exclusion of the two datapoints with the lowest neural representation strength measure, as these points look like they have high leverage.

Response: We calculated the Pearson correlation after excluding the two points and found it does not affect the results too much, with the r = 0.50, p = .003 (compared to the original r = 0.52, p = .001).

Additionally, we found the two axes were mistakenly shifted in Fig 4C. Therefore, we corrected this error in the revised manuscript. The correlation results would not be influenced.

Author response image 7.

Fig. 4. The conflict type effect. (A) Brain regions surviving the Bonferroni correction (p < 0.0001) across the regions (criterion 1). Labeled regions are those meeting the criterion 2. (B) Different encoding of conflict type in the incongruent with congruent conditions. * Bonferroni corrected p < .05. (C) The brain-behavior correlation of the right 8C (criterion 3). The x-axis shows the beta coefficient of the conflict type effect from the RSA, and the y-axis shows the beta coefficient obtained from the behavioral linear model using the conflict similarity to predict the CSE in Experiment 2. (D) Illustration of the different encoding strength of conflict type similarity in incongruent versus congruent conditions of right 8C. The y-axis is derived from the z-scored Pearson correlation coefficient, consistent with the RSA methodology. See Fig. S4B for a plot with the raw Pearson correlation measurement. l = left; r = right.

Reviewer #3:

Yang and colleagues investigated whether information on two task-irrelevant features that induce response conflict is represented in a common cognitive space. To test this, the authors used a task that combines the spatial Stroop conflict and the Simon effect. This task reliably produces a beautiful graded congruency sequence effect (CSE), where the cost of congruency is reduced after incongruent trials. The authors measured fMRI to identify brain regions that represent the graded similarity of conflict types, the congruency of responses, and the visual features that induce conflicts. They applied univariate, multivariate, and connectivity analyses to fMRI data to identify brain regions that represent the graded similarity of conflict types, the congruency of responses, and the visual features that induce conflicts. They further directly assessed the dimensionality of represented conflict space.

The authors identified the right dlPFC (right 8C), which shows 1) stronger encoding of graded similarity of conflicts in incongruent trials and 2) a positive correlation between the strength of conflict similarity type and the CSE on behavior. The dlPFC has been shown to be important for cognitive control tasks. As the dlPFC did not show a univariate parametric modulation based on the higher or lower component of one type of conflict (e.g., having more spatial Stroop conflict or less Simon conflict), it implies that dissimilarity of conflicts is represented by a linear increase or decrease of neural responses. Therefore, the similarity of conflict is represented in multivariate neural responses that combine two sources of conflict.

The strength of the current approach lies in the clear effect of parametric modulation of conflict similarity across different conflict types. The authors employed a clever cross-subject RSA that counterbalanced and isolated the targeted effect of conflict similarity, decorrelating orientation similarity of stimulus positions that would otherwise be correlated with conflict similarity. A pattern of neural response seems to exist that maps different types of conflict, where each type is defined by the parametric gradation of the yoked spatial Stroop conflict and the Simon conflict on a similarity scale. The similarity of patterns increases in incongruent trials and is correlated with CSE modulation of behavior.

The main significance of the paper lies in the evidence supporting the use of an organized "cognitive space" to represent conflict information as a general control strategy. The authors thoroughly test this idea using multiple approaches and provide convincing support for their findings. However, the universality of this cognitive strategy remains an open question.

(Public Reviews) Taken together, this study presents an exciting possibility that information requiring high levels of cognitive control could be flexibly mapped into cognitive map-like representations that both benefit and bias our behavior. Further characterization of the representational geometry and generalization of the current results look promising ways to understand representations for cognitive control.

Response: We would like to thank the reviewer for the positive evaluation of our manuscript and for providing constructive comments. In response to your suggestions, we have acknowledged the potential limitation of the design and the cross-subject RSA approach, and incorporated the open questions to the discussions. Please find our detailed responses below.

The task presented in the study involved two sources of conflict information through a single salient visual input, which might have encouraged the utilization of a common space.

Response: We agree that the unified visual input in our design may have facilitated the utilization of a common space. However, we believe the stimuli are not necessarily unified in the construction of the common space. To further test the potential interaction between the concrete stimulus setting and the cognitive space representation, it is necessary to use varied stimuli in future research. We have left this as an open question in the discussion:

Can we effectively map any sources of conflict with completely different stimuli into a single space?

The similarity space was analyzed at the level of between-individuals (i.e., crosssubject RSA) to mitigate potential confounds in the design, such as congruency and the orientation of stimulus positions. This approach makes it challenging to establish a direct link between the quality of conflict space representation and the patterns of behavioral adaptations within individuals.

Response: By setting the variables as random effects at the subject level, we have extracted the individual effects that incorporate both the group-level fixed effects and individual-level random effects. We believe this approach yields results that are as reliable, if not more, than effects calculated from individual data only. First, the mixed effect linear (LME) model has included all the individual data, forming the basis for establishing random effects. Therefore, the individual effects derived from this approach inherently reflect the individual-specific effects. To support this notion, we have included a simulation script (accessible in the online file “simulation_LME.mlx” at https://osf.io/rcq8w) to demonstrate the strong consistency between the two approaches (see Author response image 8). In this simulation, we generated random data (Y) for 35 subjects, each containing 20 repeated measurements across 5 conditions. To streamline the simulation, we only included one predictor (X), which was treated as both fixed and random effects at the subject level. We applied two methods to calculate the individual beta coefficient. The first involved extracting individual beta coefficients from the LME model by summing the fixed effect with the subject-specific random effect. The second method was entailed conducting a regression analysis using data from each subject to obtain the slope. We tested their consistency by calculating the Pearson correlation between the derived beta coefficients. This simulation was repeated 100 times.

Author response image 8.

The consistent individual beta coefficients between the mixed effect model and the individual regression analysis. A) The distribution of Pearson correlation between the two methods for 100 times. B) An example from the simulation showing the highly correlated results from the two methods. Each data point indicates a subject (n=35).

Second, the potential difference between the two methods lies in that the LME model have also taken the group-level variance into account, such as the dissociable variances of the conflict similarity and orientation across subject groups. This enabled us to extract relatively cleaner conflict similarity effects for each subject, which we believe can be better linked to the individual behavioral adaptations. Moreover, we have extracted the behavioral adaptations scores (i.e., the similarity modulation effect on CSE) using a similar LME approach. Conducting behavioral analysis solely using individual data would have been less reliable, given the limited sample size of individual data (~32 points per subject). This also motivated us to maintain consistency by extracting individual neural effects using LME models.

Furthermore, it remains unclear at which cognitive stages during response selection such a unified space is recruited. Can we effectively map any sources of conflict into a single scale? Is this unified space adaptively adjusted within the same brain region? Additionally, does the amount of conflict solely define the dimensions of this unified space across many conflict-inducing tasks? These questions remain open for future studies to address.

Response: We appreciate the reviewer’s constructive open questions. We respond to each of them based on our current understanding.

1) It remains unclear at which cognitive stages during response selection such a unified space is recruited.

We anticipate that the cognitive space is recruited to guide the transference of behavioral CSE at two critical stages. The first stage involves the evaluation of control demands, where the representational distance/similarity between previous and current trials influences the adjustment of cognitive control. The second stage pertains to is control execution, where the switch from one control state to another follows a path within the cognitive space. It is worth noting that future studies aiming to address this question may benefit from methodologies with higher temporal resolutions, such as EEG and MEG, to provide more precise insights into the temporal dynamics of the process of cognitive space recruitment.

2) Can we effectively map any sources of conflict into a single scale?

It is possible that various sources of conflict can be mapped onto the same space based on their similarity, even if finding such an operational defined similarity may be challenging. However, our results may offer an approach to infer the similarity between two conflicts. One way is to examine their congruency sequence effect (CSE), with a stronger CSE suggesting greater similarity. The other way is to test their representational similarity within the dorsolateral prefrontal cortex.

3) Is this unified space adaptively adjusted within the same brain region? We do not have an answer to this question. We showed that the cognitive space does not change with time (Note. S3). What have adjusted is the control demand to resolve the quickly changing conflict conditions from trial to trial. Though, it is an interesting question whether the cognitive space may be altered, for example, when the mental state changes significantly. And if yes, we can further test whether the change of cognitive space is also within the right dlPFC.

4) Additionally, does the amount of conflict solely define the dimensions of this unified space across many conflict-inducing tasks?

Our understanding of this comment is that the amount of conflict refers to the number of conflict sources. Based on our current finding, the dimensions of the space are indeed defined by how many different conflict sources are included. However, this would require the different conflict sources are orthogonal. If some sources share some aspects, the cognitive space may collapse to a lower dimension. We have incorporated the first question into the discussion:

Moreover, we anticipate that the representation of cognitive space is most prominently involved at two critical stages to guide the transference of behavioral CSE. The first stage involves the evaluation of control demands, where the representational distance/similarity between previous and current trials influences the adjustment of cognitive control. The second stage pertains to control execution, where the switch from one control state to another follows a path within the cognitive space. However, we were unable to fully distinguish between these two stages due to the low temporal resolution of fMRI signals in our study. Future research seeking to delve deeper into this question may benefit from methodologies with higher temporal resolutions, such as EEG and MEG.

We have included the other questions into the manuscript as open questions, calling for future research.

Several interesting questions remains to be answered. For example, is the dimension of the unified space across conflict-inducing tasks solely determined by the number of conflict sources? Can we effectively map any sources of conflict with completely different stimuli into a single space? Is the cognitive space geometry modulated by the mental state? If yes, what brain regions mediate the change of cognitive space?

Minor comments:

• The original comment about out-of-sample predictions to examine the continuity of the space was a suggestion for testing neural representations, not behavior (I apologize for the lack of clarity). Given the low dimensionality of the conflict space shown by the participation ratio, we expect that linear separability exists only among specific combinations of conditions. For example, the pair of conflicts 1 and 5 together is not linearly separable from conflicts 2 and 3. But combined with other results, this is already implied.

Response: We apologize for the misunderstanding. In fact, performing a prediction analysis using the extensive RSM in our study does presents certain challenges, primarily due to its substantial size (1400x1400) and the intricate nature of the mixed-effect linear model. In our efforts to simplify the prediction process by excluding random effects, we did observe a correlation between the predicted and original values, albeit a relatively small Pearson correlation coefficient of r = 0.024, p < .001. This small correlation can be attributed to two key factors. First, the exclusion of data points impacts not only the conflict similarity regressor but also other regressors within the model, thereby diminishing the predictive power. Secondly, the large amount of data points in the model heightens the risk of overfitting, subsequently reducing the model’s capacity for generalization and increasing the likelihood of unreliable predictions. Given these potential problems, we have opted not to include this prediction in the revised manuscript.

Author response:

The following is the authors’ response to the previous reviews

Editor's note:

Thank you for taking time and efforts to improve this study. After re-review, two reviewers have a consensus that the connections the fatty acids and sperm motility is still ambiguous. Thus, I recommend to further tone down this conclusion consistently in the title and the text pointed out by reviewers before making a final version of record.

We sincerely appreciate the considerable time and effort you and the reviewers devoted to evaluating our manuscript. We have revised the title and text to express the relationship between fatty acids and sperm motility more consistently and toned down. With these revisions, we would like to proceed with publishing the manuscript as the Version of Record (VoR). Thank you very much for your guidance in improving our study.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this revised report, Yamanaka and colleagues investigate a proposed mechanism by which testosterone modulates seminal plasma metabolites in mice. Based on limited evidence in previous versions of the report, the authors softened the claim that oleic acid derived from seminal vesicle epithelium strongly affects linear progressive motility in isolated cauda epididymal sperm in vitro. Though the report still contains somewhat ambiguous references to the strength of the relationship between fatty acids and sperm motility.

Strengths:

Often, reported epidydimal sperm from mice have lower percent progressive motility compared with sperm retrieved from the uterus or by comparison with human ejaculated sperm. The findings in this report may improve in vitro conditions to overcome this problem, as well as add important physiological context to the role of reproductive tract glandular secretions in modulating sperm behaviors. The strongest observations are related to the sensitivity of seminal vesicle epithelial cells to testosterone. The revisions include the addition of methodological detail, modified language to reflect the nuance of some of the measurements, as well as re-performed experiments with more appropriate control groups. The findings are likely to be of general interest to the field by providing context for follow-on studies regarding the relationship between fatty acid beta oxidation and sperm motility pattern.

Weaknesses:

The connection between media fatty acids and sperm motility pattern remains inconclusive.

We would like to express our sincere gratitude to the judges for their cooperation in reviewing the manuscript and for your helpful comments, which were instrumental in improving manuscript.

Reviewer #2 (Public review):

Using a combination of in vivo studies with testosterone-inhibited and aged mice with lower testosterone levels as well as isolated mouse and human seminal vesicle epithelial cells the authors show that testosterone induces an increase in glucose uptake. They find that testosterone induces a difference in gene expression with a focus on metabolic enzymes. Specifically, they identify increased expression of enzymes regulating cholesterol and fatty acid synthesis, leading to increased production of 18:1 oleic acid. The revised version strengthens the role of ACLY as the main regulator of seminal vesicle epithelial cell metabolic programming. The authors propose that fatty acids are secreted by seminal vesicle epithelial cells and are taken up by sperm, positively affecting sperm function. A lipid mixture mimicking the lipids secreted by seminal vesicle epithelial cells, however, only has a small and mostly non-significant effect on sperm motility, suggesting the authors were not apply to pinpoint the seminal vesicle fluid component that positively affects sperm function.

We greatly appreciate the reviewer’s thoughtful comments and time spent reviewing this manuscript. The relationship between lipids such as fatty acids and sperm motility remains unclear in the current dataset. Therefore, before finalizing the manuscript, we revised the title and text, as suggested by the reviewers, to express this conclusion more cautiously and consistently.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Some additional comments are provided below to aid the authors in improving the quality of the work:

Major Comments:

(1) In the newly added supplemental figure 5, the authors note that the percentage data were arcisine transformed prior to statistical analysis without providing any other justification. This seems strange, especially for such a small sample size. It seems more appropriate for the authors to use a nonparametric test. Forcing symmetry without knowing what the shape of the true distribution is makes the ANOVA hard to interpret. Additionally, why use pairwise comparisons rather than comparing each group to the control (LM 0%). Also, note that the graphs are not individually labeled to distinguish them in the legend (A, B, C, etc.). Ultimately, the treatment differences don't seem that meaningful, even if the authors were able to observe statistical significance with the somewhat over-manipulated method of analysis.

Ultimately, the conclusion of this experiment (Supplemental figure 5) remains unchanged, but we agree that the relationship between fatty acids and sperm motility remains unclear. Therefore, before finalizing the manuscript, we revised the title and text as pointed out by the reviewers to express this conclusion more cautiously and consistently throughout the manuscript.

Arcsin transform is commonly used for percentage data [Zar, J.H. 2010. Biostatistical analysis., McDonald, J.H. 2014. Handbook of biological statistics.]. If the values are low or high, such as 0 to 30% or 70 to 100%, without arcsine transformation will result in a large deviation from the normality of the data. However, even if such a conversion is performed, it does not necessarily mean that the assumptions of normality and homogeneity of variance, which are prerequisites for parametric statistical analysis methods, are satisfied.

Given the small sample size and the possibility of non-normal data, we performed Shapiro–Wilk tests for each group (n = 6) and found no departure from normality (all p > 0.1). Q–Q plots and Levene’s test (p > 0.1) likewise supported the assumptions of ANOVA. Following the reviewer’s recommendation, we repeated the analysis with a Kruskal–Wallis test followed by Dunn’s post-hoc comparisons (Bonferroni corrected). Both approaches led to the same conclusions, with non-parametric p-values equal to or smaller than the parametric ones. In the revised manuscript we now report ANOVA as the primary analysis. The author response image includes effect sizes with 95 % confidence intervals, and provide the non-parametric results for transparency.

Author response image 1.

Results of reanalysis of supplementary Figure 5 using nonparametric tests and effect sizes with 95% confidence intervals. Upper part; Differences between groups were assessed by Kruskal–Wallis test, differences among values were analyzed by Dunn’s post-hoc comparisons (Bonferroni corrected) for multiple comparisons. Different letters represent significantly different groups. Lower part; The effect sizes with 95 % confidence intervals. For example, Cliff's Δ = -1 (95% CI ~ -0.6) in VSL's “LM 0 vs LM1” means that LM 1% values exceed LM 0 %values in all pairs.

(2) I appreciate that the authors toned down the interpretation of the effects of seminal plasma metabolites on sperm motility with a cautionary statement on Lines 397-405 and Line 259. However, they send mixed signals with the title of the report: "Testosterone-Induced Metabolic Changes in Seminal Vesicle Epithelial cells Alter Plasma Components to Enhance Sperm Motility", and on line 265 when the say "ACLY expression is upregulated by testosterone and is essential for the metabolic shift of seminal vesicle epithelial cells that mediates sperm linear motility".

The wording has been softened overall. The title has been changed to “Testosterone-Induced Metabolic Changes in Seminal Vesicle Epithelium Modify Seminal Plasma Components with Potential to Improve Sperm Motility” In the results (lines 265-266), we have stated that “ACLY expression is upregulated by testosterone and is essential for the metabolic shift that is associated with increased linear motility” without implying a causal relationship.

Minor Comments:

(1) Typo on line 31: "understanding the male fertility mechanisms and may perspective for the development of potential biomarkers of male fertility and advance in the treatment of male infertility."

We have made the following corrections. “These findings suggest that testosterone-dependent lipid remodeling may contribute to sperm straight-line motility, and further functional verification is required.”

(2) Line 193: the statement is confusing "Therefore, we analyzed mitochondrial metabolism using a flux analyzer, predicting that more glucose is metabolized, pyruvate is metabolized from phosphoenolpyruvic acid through glycolysis in response to testosterone, and is further metabolized in the mitochondria." For example, 'Metabolized through glycolysis' is an ambiguous way to describe the pyruvate kinase reaction. Additionally, phosphoenolpyruvate has three acid ionizable groups, two of which have pKa's well below physiological pH, so phosphoenolpyruvate is the correct intermediate rather than phosphoenolpyruvic acid. The authors make similar mistakes with other organic acids such as citric acid.

Rewritten as “We therefore examined cellular energy metabolism with a flux analyzer, anticipating that testosterone would elevate glycolytic flux, thereby producing more pyruvate from phosphoenolpyruvate. Because extracellular pyruvate levels simultaneously declined, we inferred that the cells had an increased pyruvate demand and, at that time, hypothesized that the excess pyruvate would enter the mitochondria to support enhanced oxidative metabolism.” (lines 193-198)

The organic acids are now referenced in their appropriate forms (e.g., citrate, phosphoenolpyruvate).

(3) Line: 271: "Acly" should be all capitalized to "ACLY". The report mixes capitalizing through out and could be more consistent.

We appreciate the reviewer’s attention to nomenclature and have standardized the manuscript accordingly. Proteins are written in Roman letters, all in capital letters. Mouse gene symbols: italics, first letter capitalize.

Reviewer #2 (Recommendations for the authors):

Major comments:

(1) 'Once capacitation is complete, sperm cannot maintain that state for a long time'. The publications cited by the author do not support that statement and this reviewer also does not agree. Lower fertilization efficiency from in vitro capacitated epidydimal sperm does not have to mean capacitation is reversed, it can simply mean in vitro capacitation conditions not accurately mimic capacitation in vivo.

We thank the reviewer for pointing this out and would like to clarify our position. Our statement does not suggest a "reversal" of active capacitation. Rather, it reflects the well-documented fact that capacitation is a transient process. Sperm that undergo capacitation too early cannot maintain that state for long enough to retain their ability to fertilize at the moment and location of fertilization in vivo.

(2) How do the authors explain the discrepancy between the results shown in Fig. S1E, the increase in sperm motility upon mixing of sperm with SVF and the results reported in Li et al 2025. Mentioning decapacitating factors without further explanation is insufficient.

We appreciate the reviewer's feedback pointing out the need for a clearer explanation.

Seminal plasma is inherently binary, containing both decapacitation factors that delay or inhibit capacitation and nutrient substrates that promote sperm motility.

In vivo, it is believed that the coating of sperm by decapacitation factors is removed by uterine fluid and albumin as it passes through the female reproductive tract [PMID: 22827391, PMID: 24274412]. In contrast, standard fertilization culture media lack a clearance pathway, so decapacitating factors are retained throughout the culture period. As a result, the cleavage rate after in vitro fertilization using sperm exposed to seminal vesicle fluid decreased dramatically.

Lipids, such as fatty acids, increased sperm motility without directly inducing markers of fertilization. These results suggest that the enhancement of motility by lipids is functionally distinct from the capacitation-inhibiting function of seminal plasma proteins. The data from this study are consistent with the biphasic model. Specifically, decapacitation factors temporarily stabilize the sperm membrane, preventing early capacitation. Meanwhile, lipids enhance sperm motility, enabling them to rapidly pass through the hostile uterine environment.

(3) This reviewer does not see the merit in including a lipid mixture motility experiment compared to using OA alone. The increase in motility is still small and far from comparable to the motility increase with seminal vesicle fluid. In this reviewer's opinion the experiment is still inconclusive and should not be highlighted in the manuscript title.

The wording has been softened overall. The title has been changed to “Testosterone-Induced Metabolic Changes in Seminal Vesicle Epithelium Modify Seminal Plasma Components with Potential to Improve Sperm Motility”. (Please see also Reviewer 1's main comment 1)

Minor comments:

(1) 'This change includes a large amplitude of flagella' does not make sense. Please correct.

The following corrections have been made. “This change is characterized by large-amplitude flagellar beating.” (lines 44-45)

Author response:

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

To the Senior Editor and the Reviewing Editor:

We sincerely appreciate the valuable comments provided by the reviewers, the reviewing editor, and the senior editor. Based on our last response and revision, we are confused by the two limitations noted in the eLife assessment. 

(1) benchmarking against comparable methods is limited.

In our last revision, we added the comparison experiments with TNDM, as the reviewers requested. Additionally, it is crucial to emphasize that our evaluation of decoding capabilities of behaviorally relevant signals has been benchmarked against the performance of the ANN on raw signals, which, as Reviewer #1 previously noted, nearly represents the upper limit of performance. Consequently, we believe that our benchmarking methods are sufficiently strong.

(2) some observations may be a byproduct of their method, and may not constitute new scientific observations.

We believe that our experimental results are sufficient to demonstrate that our conclusions are not byproducts of d-VAE based on three reasons:

(1) The d-VAE, as a latent variable model, adheres to the population doctrine, which posits that latent variables are responsible for generating the activities of individual neurons. The goal of such models is to maximize the explanation of the raw signals. At the signal level, the only criterion we can rely on is neural reconstruction performance, in which we have achieved unparalleled results. Thus, it is inappropriate to focus on the mixing process during the model's inference stage while overlooking the crucial de-mixing process during the generation stage and dismissing the significance of our neural reconstruction results. For more details, please refer to the first point in our response to Q4 from Reviewer #4.

(2) The criterion that irrelevant signals should contain minimal information can effectively demonstrate that our conclusions are not by-products of d-VAE. Unfortunately, the reviewers seem to have overlooked this criterion. For more details, please refer to the third point in our response to Q4 from Reviewer #4

(3) Our synthetic experimental results also substantiate that our conclusions are not byproducts of d-VAE. However, it appears the reviewers did not give these results adequate consideration. For more details, please refer to the fourth point in our response to Q4 from Reviewer #4.

Furthermore, our work presents not just "a useful method" but a comprehensive framework. Our study proposes, for the first time, a framework for defining, extracting, and validating behaviorally relevant signals. In our current revision, to clearly distinguish between d-VAE and other methods, we have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem. To our knowledge, current methods have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals. Similarly, existing research has not yet defined and validated behaviorally relevant signals. For more details, please refer to our response to Q1 from Reviewer #4.

Based on these considerations, we respectfully request that you reconsider the eLife assessment of our work. We greatly appreciate your time and attention to this matter.

The main revisions made to the manuscript are as follows:

(1) We have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem, enabling a clearer distinction between d-VAE and other models.

(2) We have moderated the assertion about linear readout to highlight its conjectural nature and have broadened the discussion regarding this conclusion. 

(3) We have elaborated on the model details of d-VAE and have removed the identifiability claim.

To Reviewer #1

Q1: “As reviewer 3 also points out, I would, however, caution to interpret this as evidence for linear read-out of the motor system - your model performs a non-linear transformation, and while this is indeed linearly decodable, the motor system would need to do something similar first to achieve the same. In fact to me it seems to show the opposite, that behaviour-related information may not be generally accessible to linear decoders (including to down-stream brain areas).”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by linear decoders or downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our opinion, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

Q2: “As in my initial review, I would also caution against making strong claims about identifiability although this work and TNDM seem to show that in practise such methods work quite well. CEBRA, in contrast, offers some theoretical guarantees, but it is not a generative model, so would not allow the type of analysis done in this paper. In your model there is a para,eter \alpha to balance between neural and behaviour reconstruction. This seems very similar to TNDM and has to be optimised - if this is correct, then there is manual intervention required to identify a good model.”

Thank you for your comments. 

Considering your concerns about our identifiability claims and the fact that identifiability is not directly relevant to the core of our paper, we have removed content related to identifiability.

Firstly, our model is based on the pi-VAE, which also has theoretical guarantees. However, it is important to note that all such theoretical guarantees (including pi-VAE and CEBRA) are based on certain assumptions that cannot be validated as the true distribution of latent variables remains unknown.

Secondly, it is important to clarify that the identifiability of latent variables does not impact the conclusions of this paper, nor does this paper make specific conclusions about the model's latent variables. Identifiability means that distinct latent variables correspond to distinct observations. If multiple latent variables can generate the same observation, it becomes impossible to determine which one is correct given the observation, which leads to the issue of nonidentifiability. Notably, our analysis focuses on the generated signals, not the latent variables themselves, and thus the identifiability of these variables does not affect our findings. 

Our approach, dedicated to extracting these signals, distinctly differs from methods such as TNDM, which focuses on extracting behaviorally relevant latent dynamics. To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝑥# denotes generated behaviorally-relevant signals, 𝑥 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓).  Other studies have not explicitly proposed extracting behaviorally-relevant signals, nor have they identified and addressed the key challenges involved in extracting relevant signals. Consequently, our approach is distinct from other methods.

Thank you for your valuable feedback.

Q3: “Somewhat related, I also found that the now comprehensive comparison with related models shows that the using decoding performance (R2) as a metric for model comparison may be problematic: the R2 values reported in Figure 2 (e.g. the MC_RTT dataset) should be compared to the values reported in the neural latent benchmark, which represent well-tuned models (e.g. AutoLFADS). The numbers (difficult to see, a table with numbers in the appendix would be useful, see: https://eval.ai/web/challenges/challenge-page/1256/leaderboard) seem lower than what can be obtained with models without latent space disentanglement. While this does not necessarily invalidate the conclusions drawn here, it shows that decoding performance can depend on a variety of model choices, and may not be ideal to discriminate between models. I'm also surprised by the low neural R2 for LFADS I assume this is condition-averaged) - LFADS tends to perform very well on this metric.”

Thank you for your comments. The dataset we utilized is not from the same day as the neural latent benchmark dataset. Notably, there is considerable variation in the length of trials within the RTT paradigm, and the dataset lacks explicit trial information, rendering trial-averaging unsuitable. Furthermore, behaviorally relevant signals are not static averages devoid of variability; even behavioral data exhibits variability. We computed the neural R2 using individual trials rather than condition-averaged responses. 

Thank you for your valuable feedback.

Q4: “One statement I still cannot follow is how the prior of the variational distribution is modelled. You say you depart from the usual Gaussian prior, but equation 7 seems to suggest there is a normal prior. Are the parameters of this distribution learned? As I pointed out earlier, I however suspect this may not matter much as you give the prior a very low weight. I also still am not sure how you generate a sample from the variational distribution, do you just draw one for each pass?”

Thank you for your questions.

The conditional distribution of prior latent variables 𝑝%(𝒛|𝒚) is a Gaussian distribution, but the distribution of prior latent variables 𝑝(𝒛) is a mixture Gaussian distribution. The distribution of prior latent variables 𝑝(𝒛) is:

where denotes the empirical distribution of behavioral variables

𝒚, and 𝑁 denotes the number of samples, 𝒚(𝒊) denotes the 𝒊th sample, δ(⋅) denotes the Dirac delta function, and 𝑝%(𝒛|𝒚) denotes the conditional distribution of prior latent variables given the behavioral variables parameterized by network 𝑚. Based on the above equation, we can see that 𝑝(𝒛) is not a Gaussian distribution, it is a Gaussian mixture model with 𝑁 components, which is theoretically a universal approximator of continuous probability densities.

Learning this prior is important, as illustrated by our latent variable visualizations, which are not a Gaussian distribution. Upon conducting hypothesis testing for both latent variables and behavioral variables, neither conforms to Gaussian distribution (Lilliefors test and Kolmogorov-Smirnov test). Consequently, imposing a constraint on the latent variables towards N(0,1) is expected to affect performance adversely.

Regarding sampling, during training process, we draw only one sample from the approximate posterior distribution . It is worth noting that drawing multiple samples or one sample for each pass does not affect the experimental results. After training, we can generate a sample from the prior by providing input behavioral data 𝒚(𝒊) and then generating corresponding samples via and . To extract behaviorally-relevant signals from raw signals, we use and .

Thank you for your valuable feedback.

Q5: “(1) I found the figures good and useful, but the text is, in places, not easy to follow. I think the manuscript could be shortened somewhat, and in some places more concise focussed explanations would improve readability.

(2) I would not call the encoding "complex non-linear" - non-linear is a clear term, but complex can mean many things (e.g. is a quadratic function complex?) ”

Thank you for your recommendation. We have revised the manuscript for enhanced clarity.  We call the encoding “complex nonlinear” because neurons encode information with varying degrees of nonlinearity, as illustrated in Fig. 3b, f, and Fig. S3b.

Thank you for your valuable feedback.

To Reviewer #2

Q1: “I still remain unconvinced that the core findings of the paper are "unexpected". In the response to my previous Specific Comment #1, they say "We use the term 'unexpected' due to the disparity between our findings and the prior understanding concerning neural encoding and decoding." However, they provide no citations or grounding for why they make those claims. What prior understanding makes it unexpected that encoding is more complex than decoding given the entropy, sparseness, and high dimensionality of neural signals (the "encoding") compared to the smoothness and low dimensionality of typical behavioural signals (the "decoding")?” 

Thank you for your comments. We believe that both the complexity of neural encoding and the simplicity of neural decoding in motor cortex are unexpected.

The Complexity of Neural Encoding: As noted in the Introduction, neurons with small R2 values were traditionally considered noise and consequently disregarded, as detailed in references [1-3]. However, after filtering out irrelevant signals, we discovered that these neurons actually contain substantial amounts of behavioral information, previously unrecognized. Similarly, in population-level analyses, neural signals composed of small principal components (PCs) are often dismissed as noise, with analyses typically utilizing only between 6 and 18 PCs [4-10]. Yet, the discarded PC signals nonlinearly encode significant amounts of information, with practically useful dimensions found to range between 30 and 40—far exceeding the usual number analyzed. These findings underscore the complexity of neural encoding and are unexpected.

The Simplicity of Neural Decoding: In the motor cortex, nonlinear decoding of raw signals has been shown to significantly outperform linear decoding, as evidenced in references [11,12]. Interestingly, after separating behaviorally relevant and irrelevant signals, we observed that the linear decoding performance of behaviorally relevant signals is nearly equivalent to that of nonlinear decoding—a phenomenon previously undocumented in the motor cortex. This discovery is also unexpected.

Thank you for your valuable feedback.

(1) Georgopoulos, Apostolos P., Andrew B. Schwartz, and Ronald E. Kettner. "Neuronal population coding of movement direction." Science 233.4771 (1986): 1416-1419.

(2) Hochberg, Leigh R., et al. "Reach and grasp by people with tetraplegia using a neurally controlled robotic arm." Nature 485.7398 (2012): 372-375. 

(3) Inoue, Yoh, et al. "Decoding arm speed during reaching." Nature communications 9.1 (2018): 5243.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(7) Sadtler, Patrick T., et al. "Neural constraints on learning." Nature 512.7515 (2014): 423426.

(8) Golub, Matthew D., et al. "Learning by neural reassociation." Nature neuroscience 21.4 (2018): 607-616.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

(11) Glaser, Joshua I., et al. "Machine learning for neural decoding." Eneuro 7.4 (2020).

(12) Willsey, Matthew S., et al. "Real-time brain-machine interface in non-human primates achieves high-velocity prosthetic finger movements using a shallow feedforward neural network decoder." Nature Communications 13.1 (2022): 6899.

Q2: “I still take issue with the premise that signals in the brain are "irrelevant" simply because they do not correlate with a fixed temporal lag with a particular behavioural feature handchosen by the experimenter. In the response to my previous review, the authors say "we employ terms like 'behaviorally-relevant' and 'behaviorally-irrelevant' only regarding behavioral variables of interest measured within a given task, such as arm kinematics during a motor control task.". This is just a restatement of their definition, not a response to my concern, and does not address my concern that the method requires a fixed temporal lag and continual decoding/encoding. My example of reward signals remains. There is a huge body of literature dating back to the 70s on the linear relationships between neural and activity and arm kinematics; in a sense, the authors have chosen the "variable of interest" that proves their point. This all ties back to the previous comment: this is mostly expected, not unexpected, when relating apparently-stochastic, discrete action potential events to smoothly varying limb kinematics.”

Thank you for your comments. 

Regarding the experimenter's specification of behavioral variables of interest, we followed common practice in existing studies [1, 2]. Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [3-5]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [68].

Concerning the issue of rewards, in the paper you mentioned [9], the impact of rewards occurs after the reaching phase. It's important to note that in our experiments, we analyze only the reaching phase, without any post-movement phase. 

If the impact of rewards can be stably reflected in the signals in the reaching phase of the subsequent trial, and if the reward-induced signals do not interfere with decoding—since these signals are harmless for decoding and beneficial for reconstruction—our model is likely to capture these signals. If the signals induced by rewards during the reaching phase are randomly unstable, our model will likely be unable to capture them.

If the goal is to extract post-movement neural activity from both rewarded and unrewarded trials, and if the neural patterns differ between these conditions, one could replace the d-VAE's regression loss, used for continuous kinematics decoding, with a classification loss tailored to distinguish between rewarded and unrewarded conditions.

To clarify the definition, we have revised it in the manuscript. Specifically, before a specific definition, we briefly introduce the relevant signals and irrelevant signals. Behaviorally irrelevant signals refer to those not directly associated with the behavioral variables of interest and may include noise or signals from variables of no interest. In contrast, behaviorally relevant signals refer to those directly related to the behavioral variables of interest. For instance, rewards in the post-movement phase are not directly related to behavioral variables (kinematics) in the reaching movement phase.

It is important to note that our definition of behaviorally relevant signals not only includes decoding capabilities but also specific requirement at the signal level, based on two key requirements:

(1) they should closely resemble raw signals to preserve the underlying neuronal properties without becoming so similar that they include irrelevant signals. (encoding requirement), and  (2) they should contain behavioral information as much as possible (decoding requirement). Signals that meet both requirements are considered effective behaviorally relevant signals. In our study, we assume raw signals are additively composed of behaviorally-relevant and irrelevant signals. We define irrelevant signals as those remaining after subtracting relevant signals from raw signals. Therefore, we believe our definition is clearly articulated. 

Thank you for your valuable feedback.

(1) Sani, Omid G., et al. "Modeling behaviorally relevant neural dynamics enabled by preferential subspace identification." Nature Neuroscience 24.1 (2021): 140-149.

(2) Buetfering, Christina, et al. "Behaviorally relevant decision coding in primary somatosensory cortex neurons." Nature neuroscience 25.9 (2022): 1225-1236.

(3) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(4) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(5) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(6) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(7) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(8) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(9) Ramkumar, Pavan, et al. "Premotor and motor cortices encode reward." PloS one 11.8 (2016): e0160851.

Q3: “The authors seem to have missed the spirit of my critique: to say "linear readout is performed in motor cortex" is an over-interpretation of what their model can show.”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our view, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Regarding the question of whether the brain employs linear readout, given the limitations of current observational methods and our incomplete understanding of brain mechanisms, it is challenging to ascertain whether the brain employs a linear readout. In many cortical areas, linear decoders have proven to be sufficiently accurate. Consequently, numerous studies [4, 5, 6], including the one you referenced [4], directly employ linear decoders to extract information and formulate conclusions based on the decoding results. Contrary to these approaches, our research has compared the performance of linear and nonlinear decoders on behaviorally relevant signals and found their decoding performance is comparable. Considering both the decoding accuracy and model complexity, our results suggest that the motor cortex may utilize linear readout to decode information from relevant signals. Given the current technological limitations, we consider it reasonable to analyze collected data to speculate on the potential workings of the brain, an approach that many studies have also embraced [7-10]. For instance, a study [7] deduces strategies the brain might employ to overcome noise by analyzing the structure of recorded data and decoding outcomes for new stimuli.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

(4) Jurewicz, Katarzyna, et al. "Irrational choices via a curvilinear representational geometry for value." bioRxiv (2022): 2022-03.

(5) Hong, Ha, et al. "Explicit information for category-orthogonal object properties increases along the ventral stream." Nature neuroscience 19.4 (2016): 613-622.

(6) Chang, Le, and Doris Y. Tsao. "The code for facial identity in the primate brain." Cell 169.6 (2017): 1013-1028.

(7) Ganmor, Elad, Ronen Segev, and Elad Schneidman. "A thesaurus for a neural population code." Elife 4 (2015): e06134.

(8) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

Q4: “Agreeing with my critique is not sufficient; please provide the data or simulations that provides the context for the reference in the fano factor. I believe my critique is still valid.”

Thank you for your comments. As we previously replied, Churchland's research examines the variability of neural signals across different stages, including the preparation and execution phases, as well as before and after the target appears. Our study, however, focuses exclusively on the movement execution phase. Consequently, we are unable to produce comparative displays similar to those in his research. Intuitively, one might expect that the variability of behaviorally relevant signals would be lower; however, since no prior studies have accurately extracted such signals, the specific FF values of behaviorally relevant signals remain unknown. Therefore, presenting these values is meaningful, and can provide a reference for future research. While we cannot compare FF across different stages, we can numerically compare the values to the Poisson count process. An FF of 1 indicates a Poisson firing process, and our experimental data reveals that most neurons have an FF less than 1, indicating that the variance in firing counts is below the mean.  Thank you for your valuable feedback.

To Reviewer #4

Q1: “Overall, studying neural computations that are behaviorally relevant or not is an important problem, which several previous studies have explored (for example PSID in (Sani et al. 2021), TNDM in (Hurwitz et al. 2021), TAME-GP in (Balzani et al. 2023), pi-VAE in (Zhou and Wei 2020), and dPCA in (Kobak et al. 2016), etc). However, this manuscript does not properly put their work in the context of such prior works. For example, the abstract states "One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive", which is not the case given that these prior works have done that. The same is true for various claims in the main text, for example "Furthermore, we found that the dimensionality of primary subspace of raw signals (26, 64, and 45 for datasets A, B, and C) is significantly higher than that of behaviorally-relevant signals (7, 13, and 9), indicating that using raw signals to estimate the neural dimensionality of behaviors leads to an overestimation" (line 321). This finding was presented in (Sani et al. 2021) and (Hurwitz et al. 2021), which is not clarified here. This issue of putting the work in context has been brought up by other reviewers previously but seems to remain largely unaddressed. The introduction is inaccurate also in that it mixes up methods that were designed for separation of behaviorally relevant information with those that are unsupervised and do not aim to do so (e.g., LFADS). The introduction should be significantly revised to explicitly discuss prior models/works that specifically formulated this behavior separation and what these prior studies found, and how this study differs.”  

Thank you for your comments. Our statement about “One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive” is accurate. To our best knowledge, there is no prior works to do this work--- separating accurate behaviorally relevant neural signals at both single-neuron and single-trial resolution. The works you mentioned have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals, namely determining the optimal degree of similarity between the generated relevant signals and raw signals. Those works focus on the latent neural dynamics, rather than signal level.

To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝒙𝒓 denotes generated behaviorally-relevant signals, 𝒙 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓). All the works you mentioned did not have the key part 𝑅(𝒙𝒓).

Regarding the dimensionality estimation, the dimensionality of neural manifolds quantifies the degrees of freedom required to describe population activity without significant information loss.

There are two differences between our work and PSID and TNDM. 

First, the dimensions they refer to are fundamentally different from ours. The dimensionality we describe pertains to a linear subspace, where a neural dimension or neural mode or principal component basis, , with N representing the number of neurons. However, the vector length of a neural mode of PSID and our approach differs; PSID requires concatenating multiple time steps T, essentially making , TNDM, on the other hand, involves nonlinear dimensionality reduction, which is different from linear dimensionality reduction.

Second, we estimate neural dimensionality by explaining the variance of neural signals, whereas PSID and TNDM determine dimensionality through decoding performance saturation. It is important to note that the dimensionality at which decoding performance saturates may not accurately reflect the true dimensionality of neural manifolds, as some dimensions may contain redundant information that does not enhance decoding performance.

We acknowledge that while LFADS can generate signals that contain some behavioral information, it was not specifically designed to do so. Following your suggestion, we have removed this reference from the Introduction.

Thank you for your valuable feedback.

Q2: “Claims about linearity of "motor cortex" readout are not supported by results yet stated even in the abstract. Instead, what the results support is that for decoding behavior from the output of the dVAE model -- that is trained specifically to have a linear behavior readout from its embedding -- a nonlinear readout does not help. This result can be biased by the very construction of the dVAE's loss that encourages a linear readout/decoding from embeddings, and thus does not imply a finding about motor cortex.”

Thank you for your comments. We respectfully disagree with the notion that the ability of relevant signals to be linearly decoded is due to constraints that allow embedding to be linearly decoded. Embedding involves reorganizing or transforming the structure of original signals, and they can be linearly decoded does not mean the corresponding signals can be decoded linearly.

Let's clarify this with three intuitive examples:

Example 1: Image denoising is a well-established field. Whether employing supervised or blind denoising methods [1, 2], both can effectively recover the original image. This denoising process closely resembles the extraction of behaviorally relevant signals from raw signals. Consider if noisy images are not amenable to linear decoding (classification); would removing the noise enable linear decoding? The answer is no. Typically, the noise in images captured under normal conditions is minimal, yet even the clear images remain challenging to decode linearly.

Example 2: Consider the task of face recognition, where face images are set against various backgrounds, in this context, the pixels representing the face corresponds to relevant signals, while the background pixels are considered irrelevant. Suppose a network is capable of extracting the face pixels and the resulting embedding can be linearly decoded. Can the face pixels themselves be linearly decoded? The answer is no. If linear decoding of face pixels were feasible, the challenging task of face recognition could be easily resolved by merely extracting the face from the background and training a linear classifier.

Example 3: In the MNIST dataset, the background is uniformly black, and its impact is minimal. However, linear SVM classifiers used directly on the original pixels significantly underperform compared to non-linear SVMs.

In summary, embedding involves reorganizing the structure of the original signals through a feature transformation function. However, the reconstruction process can recover the structure of the original signals from the embedding. The fact that the structure of the embedding can be linearly decoded does not imply that the structure of the original signals can be linearly decoded in the same way. It is inappropriate to focus on the compression process without equally considering the reconstruction process.

Thank you for your valuable feedback.

(1) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(2) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

Q3: “Related to the above, it is unclear what the manuscript means by readout from motor cortex. A clearer definition of "readout" (a mapping from what to what?) in general is needed. The mapping that the linearity/nonlinearity claims refer to is from the *inferred* behaviorally relevant neural signals, which themselves are inferred nonlinearly using the VAE. This should be explicitly clarified in all claims, i.e., that only the mapping from distilled signals to behavior is linear, not the whole mapping from neural data to behavior. Again, to say the readout from motor cortex is linear is not supported, including in the abstract.” 

Thank you for your comments. We have revised the manuscript to make it more clearly. Thank you for your valuable feedback.

Q4: “Claims about individual neurons are also confounded. The d-VAE distilling processing is a population level embedding so the individual distilled neurons are not obtainable on their own without using the population data. This population level approach also raises the possibility that information can leak from one neuron to another during distillation, which is indeed what the authors hope would recover true information about individual neurons that wasn't there in the recording (the pixel denoising example). The authors acknowledge the possibility that information could leak to a neuron that didn't truly have that information and try to rule it out to some extent with some simulations and by comparing the distilled behaviorally relevant signals to the original neural signals. But ultimately, the distilled signals are different enough from the original signals to substantially improve decoding of low information neurons, and one cannot be sure if all of the information in distilled signals from any individual neuron truly belongs to that neuron. It is still quite likely that some of the improved behavior prediction of the distilled version of low-information neurons is due to leakage of behaviorally relevant information from other neurons, not the former's inherent behavioral information. This should be explicitly acknowledged in the manuscript.”

Thank you for your comments. We value your insights regarding the mixing process. However, we are confident in the robustness of our conclusions. We respectfully disagree with the notion that the small R2 values containing significant information are primarily due to leakage, and we base our disagreement on four key reasons.

(1) Neural reconstruction performance is a reliable and valid criterion.

The purpose of latent variable models is to explain neuronal activity as much as possible. Given the fact that the ground truth of behaviorally-relevant signals, the latent variables, and the generative model is unknow, it becomes evident that the only reliable reference at the signal level is the raw signals. A crucial criterion for evaluating the reliability of latent variable models (including latent variables and generated relevant signals) is their capability to effectively explain the raw signals [1]. Consequently, we firmly maintain the belief that if the generated signals closely resemble the raw signals to the greatest extent possible, in accordance with an equivalence principle, we can claim that these obtained signals faithfully retain the inherent properties of single neurons. 

Reviewer #4 appears to focus on the compression (mixing) process without giving equal consideration to the reconstruction (de-mixing) process. Numerous studies have demonstrated that deep autoencoders can reconstruct the original signal very effectively. For example, in the field of image denoising, autoencoders are capable of accurately restoring the original image [2, 3]. If one persistently focuses on the fact of mixing and ignores the reconstruction （demix） process, even if the only criterion that we can rely on at the signal level is high, one still won't acknowledge it. If this were the case, many problems would become unsolvable. For instance, a fundamental criterion for latent variable models is their ability to explain the original data. If the ground truth of the latent variables remains unknown and the reconstruction criterion is disregarded, how can we validate the effectiveness of the model, the validity of the latent variables, or ensure that findings related to latent variables are not merely by-products of the model? Therefore, we disagree with the aforementioned notion. We believe that as long as the reconstruction performance is satisfactory, the extracted signals have successfully retained the characteristics of individual neurons.

In our paper, we have shown in various ways that our generated signals sufficiently resemble the raw signals, including visualizing neuronal activity (Fig. 2m, Fig. 3i, and Fig. S5), achieving the highest performance among competitors (Fig. 2d, h, l), and conducting control analyses. Therefore, we believe our results are reliable. 

(1) Cunningham, J.P. and Yu, B.M., 2014. Dimensionality reduction for large-scale neural recordings. Nature neuroscience, 17(11), pp.1500-1509.

(2) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(3) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

(2) There is no reason for d-VAE to add signals that do not exist in the original signals.

(1) Adding signals that does not exist in the small R2 neurons would decrease the reconstruction performance. This is because if the added signals contain significant information, they will not resemble the irrelevant signals which contain no information, and thus, the generated signals will not resemble the raw signals. The model optimizes towards reducing the reconstruction loss, and this scenario deviates from the model's optimization direction. It is worth mentioning that when the model only has reconstruction loss without the interference of decoding loss, we believe that information leakage does not happen. Because the model can only be optimized in a direction that is similar to the raw signals; adding non-existent signals to the generated signals would increase the reconstruction loss, which is contrary to the objective of optimization. 

(2) Information carried by these additional signals is redundant for larger R2 neurons, thus they do not introduce new information that can enhance the decoding performance of the neural population, which does not benefit the decoding loss.

Based on these two points, we believe the model would not perform such counterproductive and harmful operations.

(3) The criterion that irrelevant signals should contain minimal information can effectively rule out the leakage scenario.

The criterion that irrelevant signals should contain minimal information is very important, but it seems that reviewer #4 has continuously overlooked their significance. If the model's reconstruction is insufficient, or if additional information is added (which we do not believe will happen), the residuals would decode a large amount of information, and this criterion would exclude selecting such signals. To clarify, if we assume that x, y, and z denote the raw, relevant, and irrelevant signals of smaller R2 neurons, with x=y+z, and the extracted relevant signals become y+m, the irrelevant signals become z-m in this case. Consequently, the irrelevant signals contain a significant amount of information.

We presented the decoding R2 for irrelevant signals in real datasets under three distillation scenarios: a bias towards reconstruction (alpha=0, an extreme case where the model only has reconstruction loss without decoding loss), a balanced trade-off, and a bias towards decoding (alpha=0.9), as detailed in Table 1. If significant information from small R2 neurons leaks from large R2 neurons, the irrelevant signals should contain a large amount of information. However, our results indicate that the irrelevant signals contain only minimal information, and their performance closely resembles that of the model training solely with reconstruction loss, showing no significant differences (P > 0.05, Wilcoxon rank-sum test). When the model leans towards decoding, some useful information will be left in the residuals, and irrelevant signals will contain a substantial amount of information, as observed in Table 1, alpha=0.9. Therefore, we will not choose these signals for analysis.

In conclusion, the criterion that irrelevant signals should contain minimal information is a very effective measure to exclude undesirable signals.

Author response table 1.

Decoding R2 of irrelevant signals

(4) Synthetic experiments can effectively rule out the leakage scenario.

In the absence of ground truth data, synthetic experiments serve as an effective method for validating models and are commonly employed [1-3]. 

Our experimental results demonstrate that d-VAE can effectively extract neural signals that more closely resemble actual behaviorally relevant signals (Fig. S2g).  If there were information leakage, it would decrease the similarity to the ground truth signals, hence we have ruled out this possibility. Moreover, in synthetic experiments with small R2 neurons (Fig. S10), results also demonstrate that our model could make these neurons more closely resemble ground truth relevant signals and recover their information. 

In summary, synthetic experiments strongly demonstrate that our model can recover obscured neuronal information, rather than adding signals that do not exist.

(1) Pnevmatikakis, Eftychios A., et al. "Simultaneous denoising, deconvolution, and demixing of calcium imaging data." Neuron 89.2 (2016): 285-299.

(2) Schneider, Steffen, Jin Hwa Lee, and Mackenzie Weygandt Mathis. "Learnable latent embeddings for joint behavioural and neural analysis." Nature 617.7960 (2023): 360-368.

(3) Zhou, Ding, and Xue-Xin Wei. "Learning identifiable and interpretable latent models of high-dimensional neural activity using pi-VAE." Advances in Neural Information Processing Systems 33 (2020): 7234-7247.

Based on these four points, we are confident in the reliability of our results. If Reviewer #4 considers these points insufficient, we would highly appreciate it if specific concerns regarding any of these aspects could be detailed.

Thank you for your valuable feedback.

Q5: “Given the nuances involved in appropriate comparisons across methods and since two of the datasets are public, the authors should provide their complete code (not just the dVAE method code), including the code for data loading, data preprocessing, model fitting and model evaluation for all methods and public datasets. This will alleviate concerns and allow readers to confirm conclusions (e.g., figure 2) for themselves down the line.”

Thanks for your suggestion.

Our codes are now available on GitHub at https://github.com/eric0li/d-VAE. Thank you for your valuable feedback.

Q6: “Related to 1) above, the authors should explore the results if the affine network h(.) (from embedding to behavior) was replaced with a nonlinear ANN. Perhaps linear decoders would no longer be as close to nonlinear decoders. Regardless, the claim of linearity should be revised as described in 1) and 2) above, and all caveats should be discussed.”

Thank you for your suggestion. We appreciate your feasible proposal that can be empirically tested. Following your suggestion, we have replaced the decoding of the latent variable z to behavior y with a nonlinear neural network, specifically a neural network with a single hidden layer. The modified model is termed d-VAE2. We applied the d-VAE2 to the real data, and selected the optimal alpha through the validation set. As shown in Table 1, results demonstrate that the performance of KF and ANN remains comparable. Therefore, the capacity to linearly decode behaviorally relevant signals does not stem from the linear decoding of embeddings.

Author response table 2.

Decoding R2 of behaviorally relevant signals obtained by d-VAE2

Additionally, it is worth noting that this approach is uncommon and is considered somewhat inappropriate according to the Information Bottleneck theory [1]. According to the Information Bottleneck theory, information is progressively compressed in multilayer neural networks, discarding what is irrelevant to the output and retaining what is relevant. This means that as the number of layers increases, the mutual information between each layer's embedding and the model input gradually decreases, while the mutual information between each layer's embedding and the model output gradually increases. For the decoding part, if the embeddings that is not closest to the output (behaviors) is used, then these embeddings might contain behaviorally irrelevant signals. Using these embeddings to generate behaviorally relevant signals could lead to the inclusion of irrelevant signals in the behaviorally relevant signals.

To demonstrate the above statement, we conducted experiments on the synthetic data. As shown in Table 2, we present the performance (neural R2 between the generated signals and the ground truth signals) of both models at several alpha values around the optimal alpha of dVAE (alpha=0.9) selected by the validation set. The experimental results show that at the same alpha value, the performance of d-VAE2 is consistently inferior to that of d-VAE, and d-VAE2 requires a higher alpha value to achieve performance comparable to d-VAE, and the best performance of d-VAE2 is inferior to that of d-VAE.

Author response table 3.

Neural R2 between generated signals and real behaviorally relevant signals

Thank you for your valuable feedback.

(1) Shwartz-Ziv, Ravid, and Naftali Tishby. "Opening the black box of deep neural networks via information." arXiv preprint arXiv:1703.00810 (2017).

Q7: “The beginning of the section on the "smaller R2 neurons" should clearly define what R2 is being discussed. Based on the response to previous reviewers, this R2 "signifies the proportion of neuronal activity variance explained by the linear encoding model, calculated using raw signals". This should be mentioned and made clear in the main text whenever this R2 is referred to.”

Thank you for your suggestion. We have made the modifications in the main text. Thank you for your valuable feedback.

Q8: “Various terms require clear definitions. The authors sometimes use vague terminology (e.g., "useless") without a clear definition. Similarly, discussions regarding dimensionality could benefit from more precise definitions. How is neural dimensionality defined? For example, how is "neural dimensionality of specific behaviors" (line 590) defined? Related to this, I agree with Reviewer 2 that a clear definition of irrelevant should be mentioned that clarifies that relevance is roughly taken as "correlated or predictive with a fixed time lag". The analyses do not explore relevance with arbitrary time lags between neural and behavior data.”

Thanks for your suggestion. We have removed the “useless” statements and have revised the statement of “the neural dimensionality of specific behaviors” in our revised manuscripts.

Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [1-3]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [4-6]. To clarify the definition, we have revised the definition in our manuscript. For details, please refer to the response to Q2 of reviewer #2 and our revised manuscript. We believe our definition is clearly articulated.

Thank you for your valuable feedback.

(1) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(2) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(3) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239. 

Q9: “CEBRA itself doesn't provide a neural reconstruction from its embeddings, but one could obtain one via a regression from extracted CEBRA embeddings to neural data. In addition to decoding results of CEBRA (figure S3), the neural reconstruction of CEBRA should be computed and CEBRA should be added to Figure 2 to see how the behaviorally relevant and irrelevant signals from CEBRA compare to other methods.”

Thank you for your question. Modifying CEBRA is beyond the scope of our work. As CEBRA is not a generative model, it cannot obtain behaviorally relevant and irrelevant signals, and therefore it lacks the results presented in Fig. 2. To avoid the same confusion encountered by reviewers #3 and #4 among our readers, we have opted to exclude the comparison with CEBRA. It is crucial to note, as previously stated, that our assessment of decoding capabilities has been benchmarked against the performance of the ANN on raw signals, which almost represents the upper limit of performance. Consequently, omitting CEBRA does not affect our conclusions.

Thank you for your valuable feedback.

Q10: “Line 923: "The optimal hyperparameter is selected based on the lowest averaged loss of five-fold training data." => why is this explained specifically under CEBRA? Isn't the same criteria used for hyperparameters of other methods? If so, clarify.”

Thank you for your question. The hyperparameter selection for CEBRA follows the practice of the original CEBRA paper. The hyperparameter selection for generative models is detailed in the Section “The strategy for selecting effective behaviorally-relevant signals”.  Thank you for your valuable feedback.

Author response:

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

Reviewer #1 (Public Review):

In this paper, the authors evaluate the utility of brain age derived metrics for predicting cognitive decline by performing a 'commonality' analysis in a downstream regression that enables the different contribution of different predictors to be assessed. The main conclusion is that brain age derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ('brain cognition') as an alternative suited to applications of cognitive decline. While this is less accurate overall than brain age, it explains more unique variance in the downstream regression.  

Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. 

REVISED VERSION: while the authors have partially addressed my concerns, I do not feel they have addressed them all. I do not feel they have addressed the weight instability and concerns about the stacked regression models satisfactorily.

Please see our responses to Reviewer #1 Public Review #3 below

I also must say that I agree with Reviewer 3 about the limitations of the brain age and brain cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain age model that is trained to predict age. This suffers from the same problem the authors raise with brain age and would indeed disappear if the authors had a separate measure of cognition against which to validate and were then to regress this out as they do for age correction. I am aware that these conceptual problems are more widespread than this paper alone (in fact throughout the brain age literature), so I do not believe the authors should be penalised for that. However, I do think they can make these concerns more explicit and further tone down the comments they make about the utility of brain cognition. I have indicated the main considerations about these points in the recommendations section below. 

Thank you so much for raising this point. We now have the following statement in the introduction and discussion to address this concern (see below). 

Briefly, we made it explicit that, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. That is, the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. More importantly, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And this is the third goal of this present study. 

From Introduction:

“Third and finally, certain variation in fluid cognition is related to brain MRI, but to what extent does Brain Age not capture this variation? To estimate the variation in fluid cognition that is related to the brain MRI, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in fluid cognition that is related to the brain MRI and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. This is, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Consequently, if we included Brain Cognition, Brain Age and chronological age in the same model to explain fluid cognition, we would be able to examine the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age. These unique effects of Brain Cognition, in turn, would indicate the amount of co-variation between brain MRI and fluid cognition that is missed by Brain Age.”

From Discussion:

“Third, by introducing Brain Cognition,  we showed the extent to which Brain Age indices were not able to capture the variation in fluid cognition that is related to brain MRI. More specifically, using Brain Cognition allowed us to gauge the variation in fluid cognition that is related to the brain MRI, and thereby, to estimate the upper limit of what Brain Age can do. Moreover, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

From our results, Brain Cognition, especially from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. As explained above, the unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.” 

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. I have some comments that I believe the authors ought to address, which mostly relate to clarity and interpretation 

Reviewer #1 Public Review #1

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. I would suggest the authors nuance their discussion to provide broader considerations of the utility of their method and on the limits of interpretation of brain age models more generally. 

Thank you for your comments on this issue. 

We now discussed the broader consideration in detail:

(1) the consistency between our findings on fluid cognition and other recent works on brain disorders, 

(2) the difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021)

and 

(3) suggested solutions we and others made to optimise the utility of Brain Age for both cognitive functioning and brain disorders.

From Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance,  combining different MRI modalities into the prediction models, similar to our stacked models, ocen leads to the highest performance of age prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We consider the former as a normative type of study and the lader as a case-control type of study (Insel et al., 2010; Marquand et al., 2016). Those case-control Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. On the one hand, this means that case-control studies treat Brain Age as a method to detect anomalies in the neurological/psychological group (Hahn et al., 2021). On the other hand, this also means that case-control studies have to ignore underfided models when applied prediction models built from largely healthy participants to participants with neurological/psychological disorders (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other normative studies focusing on cognitive functioning often build age prediction models from MRI data of largely healthy participants and apply the built age prediction models to participants who are also largely healthy. Accordingly, the age prediction models for explaining cognitive functioning in normative studies, while not allowing us to detect group-level anomalies, do not suffer from being under-fided. This unfortunately might limit the generalisability of our study into just the normative type of study. Future work is still needed to test the utility of brain age in the case-control case.”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder. 

As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest.

Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

Reviewer #1 Public Review #2

Second, from a methods perspective, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand how the stacked regression models were constructed. I would request that the authors provide more information to enable the reader to beUer understand the stacked regression models used to ensure that these models are not overfit. 

Thank you for allowing us an opportunity to clarify our stacked model. We made additional clarification to make this clearer (see below). We wanted to confirm that we did not use test sets to build a stacked model in both lower and higher levels of the Elastic Net models. Test sets were there just for testing the performance of the models.  

From Methods:

“We used nested cross-validation (CV) to build these prediction models (see Figure 7). We first split the data into five outer folds, leaving each outer fold with around 100 participants. This number of participants in each fold is to ensure the stability of the test performance across folds. In each outer-fold CV loop, one of the outer folds was treated as an outer-fold test set, and the rest was treated as an outer-fold training set. Ultimately, looping through the nested CV resulted in a) prediction models from each of the 18 sets of features as well as b) prediction models that drew information across different combinations of the 18 separate sets, known as “stacked models.” We specified eight stacked models: “All” (i.e., including all 18 sets of features),  “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, there were 26 prediction models in total for both Brain Age and Brain Cognition.

To create these 26 prediction models, we applied three steps for each outer-fold loop. The first step aimed at tuning prediction models for each of 18 sets of features. This step only involved the outer-fold training set and did not involve the outer-fold test set. Here, we divided the outer-fold training set into five inner folds and applied inner-fold CV to tune hyperparameters with grid search. Specifically, in each inner-fold CV, one of the inner folds was treated as an inner-fold validation set, and the rest was treated as an inner-fold training set. Within each inner-fold CV loop, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters and applied the estimated model to the inner-fold validation set. Acer looping through the inner-fold CV, we, then, chose the prediction models that led to the highest performance, reflected by coefficient of determination (R2), on average across the inner-fold validation sets. This led to 18 tuned models, one for each of the 18 sets of features, for each outer fold.

The second step aimed at tuning stacked models. Same as the first step, the second step only involved the outer-fold training set and did not involve the outer-fold test set. Here, using the same outer-fold training set as the first step, we applied tuned models, created from the first step, one from each of the 18 sets of features, resulting in 18 predicted values for each participant. We, then, re-divided this outer-fold training set into new five inner folds. In each inner fold, we treated different combinations of the 18 predicted values from separate sets of features as features to predict the targets in separate “stacked” models. Same as the first step, in each inner-fold CV loop, we treated one out of five inner folds as an inner-fold validation set, and the rest as an inner-fold training set. Also as in the first step, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters from our grid. We tuned the hyperparameters of stacked models using grid search by selecting the models with the highest R2 on average across the inner-fold validation sets. This led to eight tuned stacked models.

The third step aimed at testing the predictive performance of the 18 tuned prediction models from each of the set of features, built from the first step, and eight tuned stacked models, built from the second step. Unlike the first two steps, here we applied the already tuned models to the outer-fold test set. We started by applying the 18 tuned prediction models from each of the sets of features to each observation in the outer-fold test set, resulting in 18 predicted values. We then applied the tuned stacked models to these predicted values from separate sets of features, resulting in eight predicted values. 

To demonstrate the predictive performance, we assessed the similarity between the observed values and the predicted values of each model across outer-fold test sets, using Pearson’s r, coefficient of determination (R2) and mean absolute error (MAE). Note that for R2, we used the sum of squares definition (i.e., R2 \= 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020). We considered the predicted values from the outer-fold test sets of models predicting age or fluid cognition, as Brain Age and Brain Cognition, respectively.”

Author response image 1.

Diagram of the nested cross-validation used for creating predictions for models of each set of features as well as predictions for stacked models. 

Note some previous research, including ours (Tetereva et al., 2022), splits the observations in the outer-fold training set into layer 1 and layer 2 and applies the first and second steps to layers 1 and 2, respectively. Here we decided against this approach and used the same outer-fold training set for both first and second steps in order to avoid potential bias toward the stacked models. This is because, when the data are split into two layers, predictive models built for each separate set of features only use the data from layer 1, while the stacked models use the data from both layers 1 and 2. In practice with large enough data, these two approaches might not differ much, as we demonstrated previously (Tetereva et al., 2022).

Reviewer #1 Public Review #3

Please also provide an indication of the different regression strengths that were estimated across the different models and cross-validation splits. Also, how stable were the weights across splits? 

The focus of this article is on the predictions. Still, it is informative for readers to understand how stable the feature importance (i.e., Elastic Net coefficients) is. To demonstrate the stability of feature importance, we now examined the rank stability of feature importance using Spearman’s ρ (see Figure 4). Specifically, we correlated the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, we computed 10 Spearman’s ρ for each prediction model of the same features.  We found Spearman’s ρ to be varied dramatically in both age-prediction (range\=.31-.94) and fluid cognition-prediction (range\=.16-.84) models. This means that some prediction models were much more stable in their feature importance than others. This is probably due to various factors such as a) the collinearity of features in the model, b) the number of features (e.g., 71,631 features in functional connectivity, which were further reduced to 75 PCAs, as compared to 19 features in subcortical volume based on the ASEG atlas), c) the penalisation of coefficients either with ‘Ridge’ or ‘Lasso’ methods, which resulted in reduction as a group of features or selection of a feature among correlated features, respectively, and d) the predictive performance of the models. Understanding the stability of feature importance is beyond the scope of the current article. As mentioned by Reviewer 1, “The predictions can be stable when the coefficients are not,” and we chose to focus on the prediction in the current article.   

Author response image 2.

Stability of feature importance (i.e., Elastic Net Coefficients) of prediction models. Each dot represents rank stability (reflected by Spearman’s ρ) in the feature importance between two prediction models of the same features, used in two different outer-fold test sets. Given that there were five outer-fold test sets, there were 10 Spearman’s ρs for each prediction model.  The numbers to the right of the plots indicate the mean of Spearman’s ρ for each prediction model.  

Reviewer #1 Public Review #4

Please provide more details about the task designs, MRI processing procedures that were employed on this sample in addition to the regression methods and bias correction methods used. For example, there are several different parameterisations of the elastic net, please provide equations to describe the method used here so that readers can easily determine how the regularisation parameters should be interpreted.  

Thank you for the opportunity for us to provide more methodical details.

First, for the task design, we included the following statements:

From Methods:

“HCP-A collected fMRI data from three tasks: Face Name (Sperling et al., 2001), Conditioned Approach Response Inhibition Task (CARIT) (Somerville et al., 2018) and VISual MOTOR (VISMOTOR) (Ances et al., 2009). 

First, the Face Name task (Sperling et al., 2001) taps into episodic memory. The task had three blocks. In the encoding block [Encoding], participants were asked to memorise the names of faces shown. These faces were then shown again in the recall block [Recall] when the participants were asked if they could remember the names of the previously shown faces. There was also the distractor block [Distractor] occurring between the encoding and recall blocks. Here participants were distracted by a Go/NoGo task. We computed six contrasts for this Face Name task: [Encode], [Recall], [Distractor], [Encode vs. Distractor], [Recall vs. Distractor] and [Encode vs. Recall].

Second, the CARIT task (Somerville et al., 2018) was adapted from the classic Go/NoGo task and taps into inhibitory control. Participants were asked to press a budon to all [Go] but not to two [NoGo] shapes. We computed three contrasts for the CARIT task: [NoGo], [Go] and [NoGo vs. Go]. 

Third, the VISMOTOR task (Ances et al., 2009) was designed to test simple activation of the motor and visual cortices. Participants saw a checkerboard with a red square either on the lec or right. They needed to press a corresponding key to indicate the location of the red square. We computed just one contrast for the VISMOTOR task: [Vismotor], which indicates the presence of the checkerboard vs. baseline.” 

Second, for MRI processing procedures, we included the following statements.

From Methods:

“HCP-A provides details of parameters for brain MRI elsewhere (Bookheimer et al., 2019; Harms et al., 2018). Here we used MRI data that were pre-processed by the HCP-A with recommended methods, including the MSMALL alignment (Glasser et al., 2016; Robinson et al., 2018) and ICA-FIX (Glasser et al., 2016) for functional MRI. We used multiple brain MRI modalities, covering task functional MRI (task fMRI), resting-state functional MRI (rsfMRI) and structural MRI (sMRI), and organised them into 19 sets of features.”

“Sets of Features 1-10: Task fMRI contrast (Task Contrast)

Task contrasts reflect fMRI activation relevant to events in each task. Bookheimer and colleagues (2019) provided detailed information about the fMRI in HCP-A. Here we focused on the pre-processed task fMRI Connectivity Informatics Technology Initiative (CIFTI) files with a suffix, “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” These CIFTI files encompassed both the cortical mesh surface and subcortical volume (Glasser et al., 2013). Collected using the posterior-to-anterior (PA) phase, these files were aligned using MSMALL (Glasser et al., 2016; Robinson et al., 2018), linear detrended (see hdps://groups.google.com/a/humanconnectome.org/g/hcp-users/c/ZLJc092h980/m/GiihzQAUAwAJ) and cleaned from potential artifacts using ICA-FIX (Glasser et al., 2016). 

To extract Task Contrasts, we regressed the fMRI time series on the convolved task events using a double-gamma canonical hemodynamic response function via FMRIB Software Library (FSL)’s FMRI Expert Analysis Tool (FEAT) (Woolrich et al., 2001). We kept FSL’s default high pass cutoff at 200s (i.e., .005 Hz). We then parcellated the contrast ‘cope’ files, using the Glasser atlas (Gordon et al., 2016) for cortical surface regions and the Freesurfer’s automatic segmentation (aseg) (Fischl et al., 2002) for subcortical regions. This resulted in 379 regions, whose number was, in turn, the number of features for each Task Contrast set of features. “ 

“Sets of Features 11-13: Task fMRI functional connectivity (Task FC)

Task FC reflects functional connectivity (FC ) among the brain regions during each task, which is considered an important source of individual differences (Elliod et al., 2019; Fair et al., 2007; Gradon et al., 2018). We used the same CIFTI file “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” as the task contrasts. Unlike Task Contrasts, here we treated the double-gamma, convolved task events as regressors of no interest and focused on the residuals of the regression from each task (Fair et al., 2007). We computed these regressors on FSL, and regressed them in nilearn (Abraham et al., 2014). Following previous work on task FC (Elliod et al., 2019), we applied a highpass at .008 Hz. For parcellation, we used the same atlases as Task Contrast (Fischl et al., 2002; Glasser et al., 2016). We computed Pearson’s correlations of each pair of 379 regions, resulting in a table of 71,631 non-overlapping FC indices for each task. We then applied r-to-z transformation and principal component analysis (PCA) of 75 components (Rasero et al., 2021; Sripada et al., 2019, 2020). Note to avoid data leakage, we conducted the PCA on each training set and applied its definition to the corresponding test set. Accordingly, there were three sets of 75 features for Task FC, one for each task. 

Set of Features 14: Resting-state functional MRI functional connectivity (Rest FC) Similar to Task FC, Rest FC reflects functional connectivity (FC ) among the brain regions, except that Rest FC occurred during the resting (as opposed to task-performing) period. HCPA collected Rest FC from four 6.42-min (488 frames) runs across two days, leading to 26-min long data (Harms et al., 2018). On each day, the study scanned two runs of Rest FC, starting with anterior-to-posterior (AP) and then with posterior-to-anterior (PA) phase encoding polarity. We used the “rfMRI_REST_Atlas_MSMAll_hp0_clean.dscalar.nii” file that was preprocessed and concatenated across the four runs.  We applied the same computations (i.e., highpass filter, parcellation, Pearson’s correlations, r-to-z transformation and PCA) with the Task FC. 

Sets of Features 15-18: Structural MRI (sMRI)

sMRI reflects individual differences in brain anatomy. The HCP-A used an established preprocessing pipeline for sMRI (Glasser et al., 2013). We focused on four sets of features: cortical thickness, cortical surface area, subcortical volume and total brain volume. For cortical thickness and cortical surface area, we used Destrieux’s atlas (Destrieux et al., 2010; Fischl, 2012) from FreeSurfer’s “aparc.stats” file, resulting in 148 regions for each set of features. For subcortical volume, we used the aseg atlas (Fischl et al., 2002) from FreeSurfer’s “aseg.stats” file, resulting in 19 regions. For total brain volume, we had five FreeSurfer-based features: “FS_IntraCranial_Vol” or estimated intra-cranial volume, “FS_TotCort_GM_Vol” or total cortical grey mader volume, “FS_Tot_WM_Vol” or total cortical white mader volume, “FS_SubCort_GM_Vol” or total subcortical grey mader volume and “FS_BrainSegVol_eTIV_Ratio” or ratio of brain segmentation volume to estimated total intracranial volume.”

Third, for regression methods and bias correction methods used, we included the following statements:

From Methods:

“For the machine learning algorithm, we used Elastic Net (Zou & Hastie, 2005). Elastic Net is a general form of penalised regressions (including Lasso and Ridge regression), allowing us to simultaneously draw information across different brain indices to predict one target variable. Penalised regressions are commonly used for building age-prediction models (Jirsaraie, Gorelik, et al., 2023). Previously we showed that the performance of Elastic Net in predicting cognitive abilities is on par, if not better than, many non-linear and morecomplicated algorithms (Pat, Wang, Bartonicek, et al., 2022; Tetereva et al., 2022). Moreover, Elastic Net coefficients are readily explainable, allowing us the ability to explain how our age-prediction and cognition-prediction models made the prediction from each brain feature (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022) (see below). 

Elastic Net simultaneously minimises the weighted sum of the features’ coefficients. The degree of penalty to the sum of the feature’s coefficients is determined by a shrinkage hyperparameter ‘a’: the greater the a, the more the coefficients shrink, and the more regularised the model becomes. Elastic Net also includes another hyperparameter, ‘ℓ! ratio’, which determines the degree to which the sum of either the squared (known as ‘Ridge’; ℓ! ratio=0) or absolute (known as ‘Lasso’; ℓ! ratio=1) coefficients is penalised (Zou & Hastie, 2005). The objective function of Elastic Net as implemented by sklearn (Pedregosa et al., 2011) is defined as:

where X is the features, y is the target, and b is the coefficient. In our grid search, we tuned two Elastic Net hyperparameters: a using 70 numbers in log space, ranging from .1 and 100, and ℓ!-ratio using 25 numbers in linear space, ranging from 0 and 1.

To understand how Elastic Net made a prediction based on different brain features, we examined the coefficients of the tuned model. Elastic Net coefficients can be considered as feature importance, such that more positive Elastic Net coefficients lead to more positive predicted values and, similarly, more negative Elastic Net coefficients lead to more negative predicted values (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022). While the magnitude of Elastic Net coefficients is regularised (thus making it difficult for us to interpret the magnitude itself directly), we could still indicate that a brain feature with a higher magnitude weights relatively stronger in making a prediction. Another benefit of Elastic Net as a penalised regression is that the coefficients are less susceptible to collinearity among features as they have already been regularised (Dormann et al., 2013; Pat, Wang, Bartonicek, et al., 2022).

Given that we used five-fold nested cross validation, different outer folds may have different degrees of ‘a’ and ‘ℓ! ratio’, making the final coefficients from different folds to be different. For instance, for certain sets of features, penalisation may not play a big part (i.e., higher or lower ‘a’ leads to similar predictive performance), resulting in different ‘a’ for different folds. To remedy this in the visualisation of Elastic Net feature importance, we refitted the Elastic Net model to the full dataset without spli{ng them into five folds and visualised the coefficients on brain images using Brainspace (Vos De Wael et al., 2020) and Nilern (Abraham et al., 2014) packages. Note, unlike other sets of features, Task FC and Rest FC were modelled acer data reduction via PCA. Thus, for Task FC and Rest FC, we, first, multiplied the absolute PCA scores (extracted from the ‘components_’ attribute of ‘sklearn.decomposition.PCA’) with Elastic Net coefficients and, then, summed the multiplied values across the 75 components, leaving 71,631 ROI-pair indices. “

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Author Response

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

Reviewer #2 (Public Review):

Summary:

In the revised manuscript, the authors aim to investigate brain-wide activation patterns following administration of the anesthetics ketamine and isoflurane, and conduct comparative analysis of these patterns to understand shared and distinct mechanisms of these two anesthetics. To this end, they perform Fos immunohistochemistry in perfused brain sections to label active nuclei, use a custom pipeline to register images to the ABA framework and quantify Fos+ nuclei, and perform multiple complementary analyses to compare activation patterns across groups.

In the latest revision, the authors have made some changes in response to our previous comments on how to fix the analyses. However, the revised analyses were not changed correctly and remain flawed in several fundamental ways.

Critical problems:

(1) Before one can perform higher level analyses such as hiearchal cluster or network hub (or PC) analysis, it is fundamental to validate that you have significant differences of the raw Fos expression values in the first place. First of all, this means showing figures with the raw data (Fos expression levels) in some form in Figures 2 and 3 before showing the higher level analyses in Figures 4 and 5; this is currently switched around. Second and most importantly, when you have a large number of brain areas with large differences in mean values and variance, you need to account for this in a meaningful way. Changing to log values is a step in the right direction for mean values but does not account well for differences in variance. Indeed, considering the large variances in brain areas with high mean values and variance, it is a little difficult to believe that all brain regions, especially brain areas with low mean values, passed corrections for multiple comparisons test. We suggested Z-scores relative to control values for each brain region; this would have accounted for wide differences in mean values and variance, but this was not done. Overall, validation of anesthesia-induced differences in Fos expression levels is not yet shown.

(a) Reordering the figures.

Thank you for your suggestion. We have added Figure 2 (for 201 brain regions) and Figure 2—figure supplement 1 (for 53 brain regions) to demonstrate the statistical differences in raw Fos expression between KET and ISO compared to their respective control groups. These figures specifically present the raw c-Fos expression levels for both KET and ISO in the same brain areas, providing a fundamental basis for the subsequent analyses. Additionally, we have moved the original Figures 4 and 5 to Figures 3 and 4.

(b) Z-score transformation and validation of anesthesia-induced differences in Fos expression.

Thank you for your suggestion. Before multiple comparisons, we transformed the data into log c-Fos density and then performed Z-scores relative to control values for each brain region. Indeed, through Z-score transformation, we have identified a larger number of significantly activated brain regions in Figure 2. The number of brain regions showing significant activation increased by 100 for KET and by 39 for ISO. We have accordingly updated the results section to include these findings in Line 80-181. Besides, we have added the following content in the Statistical Analysis section in Line 489: "…In Figure 2 and Figure 2–figure supplement 1, c-Fos densities in both experimental and control groups were log-transformed. Z-scores were calculated for each brain region by normalizing these log-transformed values against the mean and standard deviation of its respective control group. This involved subtracting the control mean from the experimental value and dividing the result by the control standard deviation. For statistical analysis, Z-scores were compared to a null distribution with a zero mean, and adjustments were made for multiple comparisons using the Benjamini–Hochberg method with a 5% false discovery rate (Q)..…".

Author response image 1.

KET and ISO induced c-Fos expression relative to their respective control group across 201 distinct brain regions. Z-scores represent the normalized c-Fos expression in the KET and ISO groups, calculated against the mean and standard deviation from their respective control groups. Statistical analysis involved the comparison of Z-scores to a null distribution with a zero mean and adjustment for multiple comparisons using the Benjamini–Hochberg method at a 5% false discovery rate (p < 0.05, p < 0.01, **p < 0.001). n = 6, 6, 8, 6 for the home cage, ISO, saline, and KET, respectively. Missing values resulted from zero standard deviations in control groups. Brain regions are categorized into major anatomical subdivisions, as shown on the left side of the graph.

Author response image 2.

KET and ISO induced c-Fos expression relative to their respective control group across 53 distinct brain regions. Z-scores for c-Fos expression in the KET and ISO groups were normalized to the mean and standard deviation of their respective control groups. Statistical analysis involved the comparison of Z-scores to a null distribution with a zero mean and adjustment for multiple comparisons using the Benjamini–Hochberg method at a 5\% false discovery rate (p < 0.05, p < 0.01, **p < 0.001). Brain regions are organized into major anatomical subdivisions, as indicated on the left side of the graph.

(2) Let's assume for a moment that the raw Fos expression analyses indicate significant differences. They used hierarchal cluster analyses as a rationale for examining 53 brain areas in all subsequent analyses of Fos expression following isoflurane versus home cage or ketamine versus saline. Instead, the authors changed to 201 brain areas with no validated rationale other than effectively saying 'we wanted to look at more brain areas'. And then later, when they examined raw Fos expression values in Figures 4 and 5, they assess 43 brain areas for ketamine and 20 brain areas for isoflurane, without any rationale for why choosing these numbers of brain areas. This is a particularly big problem when they are trying to compare effects of isoflurane versus ketamine on Fos expression in these brain areas - they did not compare the same brain areas.

(a) Changing to 201 brain areas with validated rationale.

Thank you for your question. We have revised the original text from “To enhance our analysis of c-Fos expression patterns induced by KET and ISO, we expanded our study to 201 subregions.” to Line 100: "…To enable a more detailed examination and facilitate clearer differentiation and comparison of the effects caused by KET and ISO, we subdivided the 53 brain regions into 201 distinct areas. This approach, guided by the standard mouse atlas available at http://atlas.brain-map.org/atlas, allowed for an in-depth analysis of the responses in various brain regions…". For hierarchal cluster analyses from 53 to 201 brain regions, Line 215: "…To achieve a more granular analysis and better discern the responses between KET and ISO, we expanded our study from the initial 53 brain regions to 201 distinct subregions…"

(b) Compare the same brain areas for KET and ISO and the rationale for why choosing these numbers of brain areas in Figures 3 and 4.

We apologize for the confusion and lack of clarity regarding the selection of brain regions for analysis. In Figure 2 and Figure 2—figure supplement 1, we display the c-Fos expression in the same brain regions affected by KET and ISO. In Figures 3 and 4, we applied a uniform standard to specifically report the brain areas most prominently activated by KET and ISO, respectively. As specified in Line 104: "…Compared to the saline group, KET activated 141 out of a total of 201 brain regions (Figure 2). To further identify the brain regions that are most significantly affected by KET, we calculated Cohen's d for each region to quantify the magnitude of activation and subsequently focused on those regions that had a corrected p-value below 0.05 and effect size in the top 40% (Figure 3, Figure 3—figure supplement 1)…" and Line 142: "…Using the same criteria applied to KET, which involved selecting regions with Cohen's d values in the top 40% of significantly activated areas from Figure 2, we identified 32 key brain regions impacted by ISO (Figure 4, Figure 4—figure supplement 1).…".

Moreover, we illustrate the co-activated brain regions by KET and ISO in Figure 4C. As detailed in Lines 167-180:"…The co-activation of multiple brain regions by KET and ISO indicates that they have overlapping effects on brain functions. Examples of these effects include impacts on sensory processing, as evidenced by the activation of the PIR, ENT 1, and OT2, pointing to changes in sensory perception typical of anesthetics. Memory and cognitive functions are influenced, as indicated by the activation of the subiculum (SUB) 3, dentate gyrus (DG) 4, and RE 5. The reward and motivational systems are engaged, involving the ACB and ventral tegmental area (VTA), signaling the modulation of reward pathways 6. Autonomic and homeostatic control are also affected, as shown by areas like the lateral hypothalamic area (LHA) 7 and medial preoptic area (MPO) 8, emphasizing effects on functions such as feeding and thermoregulation. Stress and arousal responses are impacted through the activation of the paraventricular hypothalamic nucleus (PVH) 10,11 and LC 12. This broad activation pattern highlights the overlap in drug effects and the complexity of brain networks in anesthesia…". Below are the revised Figures 3 and 4.

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(4) Sun, X. et al. Functionally Distinct Neuronal Ensembles within the Memory Engram. Cell 181, 410-423.e417 (2020). https://doi.org:10.1016/j.cell.2020.02.055

(5) Huang, X. et al. A Visual Circuit Related to the Nucleus Reuniens for the Spatial-Memory-Promoting Effects of Light Treatment. Neuron (2021).

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Author response image 3.

Brain regions exhibiting significant activation by KET. (A) Fifty-five brain regions exhibited significant KET activation. These were chosen from the 201 regions analyzed in Figure 2, focusing on the top 40\% ranked by effect size among those with corrected p values less than 0.05. Data are presented as mean ± SEM, with p-values adjusted for multiple comparisons (p < 0.05, p < 0.01, **p < 0.001). (B) Representative immunohistochemical staining of brain regions identified in Figure 3A, with control group staining available in Figure 3—figure supplement 1. Scale bar: 200 µm.

Author response image 4.

Brain regions exhibiting significant activation by ISO. (A) Brain regions significantly activated by ISO were initially identified using a corrected p-value below 0.05. From these, the top 40% in effect size (Cohen’s d) were further selected, resulting in 32 key areas. p-values are adjusted for multiple comparisons (p < 0.01, *p < 0.001). (B) Representative immunohistochemical staining of brain regions identified in Figure 4A. Control group staining is available in Figure 4—figure supplement 1. Scale bar: 200 µm. Scale bar: 200 µm. (C) A Venn diagram displays 43 brain regions co-activated by KET and ISO, identified by the adjusted p-values (p < 0.05) for both KET and ISO. CTX: cerebral cortex; CNU: cerebral nuclei; TH: thalamus; HY: hypothalamus; MB: midbrain; HB: hindbrain.

Less critical comments:

(3) The explanation of hierarchical level's in lines 90-95 did not make sense.

We have revised the section that initially stated in lines 90-95, "…Based on the standard mouse atlas available at http://atlas.brain-map.org/, the mouse brain was segmented into nine hierarchical levels, totaling 984 regions. The primary level consists of grey matter, the secondary of the cerebrum, brainstem, and cerebellum, and the tertiary includes regions like the cerebral cortex and cerebellar nuclei, among others, with some regions extending to the 8th and 9th levels. The fifth level comprises 53 subregions, with detailed expression levels and their respective abbreviations presented in Supplementary Figure 2…". Our revised description, now in line 91: "…Building upon the framework established in previous literature, our study categorizes the mouse brain into 53 distinct subregions1…"

(1) Do JP, Xu M, Lee SH, Chang WC, Zhang S, Chung S, Yung TJ, Fan JL, Miyamichi K, Luo L et al: Cell type-specific long-range connections of basal forebrain circuit. Elife 2016, 5.

(4) I am still perplexed by why the authors consider the prelimbic and infralimbic cortex 'neuroendocrine' brain areas in the abstract. In contrast, the prelimbic and infralimbic were described better in the introduction as "associated information processing" areas.

Thank you for bringing this to our attention. We agree that classifying the prelimbic and infralimbic cortex as 'neuroendocrine' in the abstract was incorrect, which was an oversight on our part. In the revised version, as detailed in line 167, we observed an increased number of brain regions showing overlapping activation by both KET and ISO, which is depicted in Figure 4C. This extensive co-activation across various regions makes it challenging to narrowly define the functional classification of each area. Consequently, we have revised the abstract, updating this in line 21: "…KET and ISO both activate brain areas involved in sensory processing, memory and cognition, reward and motivation, as well as autonomic and homeostatic control, highlighting their shared effects on various neural pathways.…".

(5) It looks like overall Fos levels in the control group Home (ISO) are a magnitude (~10-fold) lower than those in the control group Saline (KET) across all regions shown. This large difference seems unlikely to be due to a biologically driven effect and seems more likely to be due to a technical issue, such as differences in staining or imaging between experiments. The authors discuss this issue but did not answer whether the Homecage-ISO experiment or at least the Fos labeling and imaging performed at the same time as for the Saline-Ketamine experiment?

Thank you for highlighting this important point. The c-Fos labeling and imaging for the Home (ISO) and Saline (KET) groups were carried out in separate sessions due to the extensive workload involved in these processes. This study processed a total of 26 brain samples. Sectioning the entire brain of each mouse required approximately 3 hours, yielding 5 slides, with each slide containing 12 to 16 brain sections. We were able to stain and image up to 20 slides simultaneously, typically comprising 2 experimental groups and 2 corresponding control groups. Imaging these 20 slides at 10x magnification took roughly 7 hours, while additional time was required for confocal imaging of specific areas of interest at 20x magnification. Given the complexity of these procedures, to ensure consistency across all experiments, they were conducted under uniform conditions. This included the use of consistent primary and secondary antibody concentrations, incubation times, and imaging parameters such as fixed light intensity and exposure time. Furthermore, in the saline and KET groups, intraperitoneal injections might have evoked pain and stress responses in mice despite four days of pre-experiment acclimation, which could have contributed to the increased c-Fos expression observed. This aspect, along with the fact that procedures were conducted in separate sessions, might have introduced some variations. Thus, we have included a note in our discussion section in Line 353: "…Despite four days of acclimation, including handling and injections, intraperitoneal injections in the saline and KET groups might still elicit pain and stress responses in mice. This point is corroborated by the subtle yet measurable variations in brain states between the home cage and saline groups, characterized by changes in normalized EEG delta/theta power (home cage: 0.05±0.09; saline: -0.03±0.11) and EMG power (home cage: -0.37±0.34; saline: 0.04±0.13), as shown in Figure 1–figure supplement 1. These changes suggest a relative increase in brain activity in the saline group compared to the home cage group, potentially contributing to the higher c-Fos expression. Additionally, despite the use of consistent parameters for c-Fos labeling and imaging across all experiments, the substantial differences observed between the saline and home cage groups might be partly attributed to the fact that the operations were conducted in separate sessions.…"

Reviewer #3 (Public Review):

The present study presents a comprehensive exploration of the distinct impacts of Isoflurane and Ketamine on c-Fos expression throughout the brain. To understand the varying responses across individual brain regions to each anesthetic, the researchers employ principal component analysis (PCA) and c-Fos-based functional network analysis. The methodology employed in this research is both methodical and expansive. Notably, the utilization of a custom software package to align and analyze brain images for c-Fos positive cells stands out as an impressive addition to their approach. This innovative technique enables effective quantification of neural activity and enhances our understanding of how anesthetic drugs influence brain networks as a whole.

The primary novelty of this paper lies in the comparative analysis of two anesthetics, Ketamine and Isoflurane, and their respective impacts on brain-wide c-Fos expression. The study reveals the distinct pathways through which these anesthetics induce loss of consciousness. Ketamine primarily influences the cerebral cortex, while Isoflurane targets subcortical brain regions. This finding highlights the differing mechanisms of action employed by these two anesthetics-a top-down approach for Ketamine and a bottom-up mechanism for Isoflurane. Furthermore, this study uncovers commonly activated brain regions under both anesthetics, advancing our knowledge about the mechanisms underlying general anesthesia.

We are thankful for your positive and insightful comments on our study. Your recognition of the study's methodology and its significance in advancing our understanding of anesthetic mechanisms is greatly valued. By comprehensively mapping c-Fos expression across a wide range of brain regions, our study reveals the distinct and overlapping impacts of these anesthetics on various brain functions, providing a valuable foundation for future research into the mechanisms of general anesthesia, potentially guiding the development of more targeted anesthetic agents and therapeutic strategies. Thus, we are confident that our work will captivate the interest of our readers.

Author Response

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

We appreciate the reviewers for their insightful feedback, which has substantially improved our manuscript. Following the suggestions of the reviewers, we have undertaken the following major revisions:

a. Concerning data transformation, we have adjusted the methodology in Figures 2 and 3. Instead of normalizing c-Fos density to the whole brain c-Fos density as initially described, we now normalize to the c-Fos density of the corresponding brain region in the control group. b. We have substituted the PCA approach with hierarchical clustering in Figures 2 and 3.

c. In the discussion section, we added a subsection on study limitations, focusing on the variations in drug administration routes and anesthesia depth.

Enclosed are our detailed responses to each of the reviewer's comments.

Reviewer #1:

1a. The addition of the EEG/EMG is useful, however, this information is not discussed. For instance, there are differences in EEG/EMG between the two groups (only Ket significantly increased delta/theta power, and only ISO decreased EMG power). These results should be discussed as well as the limitation of not having physiological measures of anesthesia to control for the anesthesia depth.

1b. The possibility that the differences in fos observed may be due to the doses used should be discussed.

1c. The possibility that the differences in fos observed may be due kinetic of anesthetic used should be discussed.

Thank you for your suggestions. We have now discussed EEG/EMG result, limitation of not having physiological measures of anesthesia to control for the anesthesia depth, The possibility that the differences in fos observed may be due to the doses, The possibility that the differences in Fos observed may be due kinetic of anesthetic in the revised manuscript (Lines 308-331, also shown below).

Lines 308-331: "...Our findings indicate that c-Fos expression in the KET group is significantly elevated compared to the ISO group, and the saline group exhibits notably higher c-Fos expression than the home cage group, as seen in Supplementary Figures 2 and 3. Intraperitoneal saline injections in the saline group, despite pre-experiment acclimation with handling and injections for four days, may still evoke pain and stress responses in mice. Subtle yet measurable variations in brain states between the home cage and saline groups were observed, characterized by changes in normalized EEG delta/theta power (home cage: 0.05±0.09; saline: -0.03±0.11) and EMG power (home cage: -0.37±0.34; saline: 0.04±0.13), as shown in Supplementary Figure 1. These changes suggest a relative increase in overall brain activity in the saline group compared to the home cage group, potentially contributing to the higher c-Fos expression. Although the difference in EEG power between the ISO group and the home cage control was not significant, the increase in EEG power observed in the ISO group was similar to that of KET (0.47 ± 0.07 vs 0.59 ± 0.10), suggesting that both agents may induce loss of consciousness in mice. Regarding EMG power, ISO showed a significant decrease in EMG power compared to its control group. In contrast, the KET group showed a lesser reduction in EMG power (ISO: -1.815± 0.10; KET: -0.96 ± 0.21), which may partly explain the higher overall c-Fos expression levels in the KET group. This is consistent with previous studies where ketamine doses up to 150 mg/kg increase delta power while eliciting a wakefulness-like pattern of c-Fos expression across the brain [1]. Furthermore, the observed differences in c-Fos expression may arise in part from the dosages, routes of administration, and their distinct pharmacokinetic profiles. This variation is compounded by the lack of detailed physiological monitoring, such as blood pressure, heart rate, and respiration, affecting our ability to precisely assess anesthesia depth. Future studies incorporating comprehensive physiological monitoring and controlled dosing regimens are essential to further elucidate these relationships and refine our understanding of the effects of anesthetics on brain activity"

1. Lu J, Nelson LE, Franks N, Maze M, Chamberlin NL, Saper CB: Role of endogenous sleep-wake and analgesic systems in anesthesia. J Comp Neurol 2008, 508(4):648-662.

2b. I am confused because Fig 2C seems to show significant decrease in %fos in the hypothalamus, midbrain and cerebellum after KET, while the author responded that " in our analysis, we did not detect regions with significant downregulation when comparing anesthetized mice with controls." Moreover the new figure in the rebuttal in response to reviewer 2 suggests that Ket increases Fos in almost every single region (green vs blue) which is not the conclusion of the paper.

Your concern regarding the apparent discrepancy is well-founded. The inconsistency arose due to an inappropriate data transformation, which affected the interpretation. We have now rectified this by adjusting the data transformation in Figures 2 and 3. Specifically, we have recalculated the log relative c-Fos density values relative to the control group for each brain region. This revision has resolved the issue, confirming that our analysis did not detect any regions with significant downregulation in the anesthetized mice compared to controls. We have also updated the results, discussion, and methods sections of Figures 2 and 3 to accurately reflect these changes and ensure consistency with our findings.

Author response image 1.

Figure 2. Whole-brain distributions of c-Fos+ cells induced by ISO and KET. (A) Hierarchical clustering was performed on the log relative c-Fos density data for ISO and KET using the complete linkage method based on the Euclidean distance matrix, with clusters identified by a dendrogram cut-off ratio of 0.5. Numerical labels correspond to distinct clusters within the dendrogram. (B) Silhouette values plotted against the ratio of tree height for ISO and KET, indicating relatively higher Silhouette values at 0.5 (dashed line), which is associated with optimal clustering. (C) The number of clusters identified in each treatment condition at different ratios of the dendrogram tree height, with a cut-off level of 0.5 corresponding to 4 clusters for both ISO and KET (indicated by the dashed line). (D) The bar graph depicts Z scores for clusters in ISO and KET conditions, represented with mean values and standard errors. One-way ANOVA with Tukey's post hoc multiple comparisons. ns: no significance; ***P < 0.001. (E) Z-scored log relative density of c-Fos expression in the clustered brain regions. The order and abbreviations of the brain regions and the numerical labels correspond to those in Figure 2A. The red box denotes the cluster with the highest mean Z score in comparison to other clusters. CTX: cortex; TH: thalamus; HY: hypothalamus; MB: midbrain; HB: hindbrain.

Author response image 2.

Figure 3. Similarities and differences in ISO and KET activated c-Fos brain areas. (A) Hierarchical clustering was performed on the log-transformed relative c-Fos density data for ISO and KET using the complete linkage method based on the Euclidean distance matrix, with clusters identified by a dendrogram cut-off ratio of 0.5. (B) Silhouette values are plotted against the ratio of tree height from the hierarchical clustered dendrogram in Figure 3A. (C) The relationship between the number of clusters and the tree height ratio of the dendrogram for ISO and KET, with a cut-off ratio of 0.5 resulting in 3 clusters for ISO and 5 for KET (indicated by the dashed line). (D) The bar graph depicts Z scores for clusters in ISO and KET conditions, represented with mean values and standard errors. One-way ANOVA with Tukey's post hoc multiple comparisons. ns: no significance; ***P < 0.001. (E) Z-scored log relative density of c-Fos expression within the identified brain region clusters. The arrangement, abbreviations of the brain regions, and the numerical labels are in accordance with Figure 3A. The red boxes highlight brain regions that rank within the top 10 percent of Z score values. The white boxes denote brain regions with an Z score less than -2.

1. There are still critical misinterpretations of the PCA analysis. For instance, it is mentioned that " KET is associated with the activation of cortical regions (as evidenced by positive PC1 coefficients in MOB, AON, MO, ACA, and ORB) and the inhibition of subcortical areas (indicated by negative coefficients) " as well as " KET displays cortical activation and subcortical inhibition, whereas ISO shows a contrasting preference, activating the cerebral nucleus (CNU) and the hypothalamus while inhibiting cortical areas. To reduce inter-individual variability." These interpretations are in complete contradiction with the answer 2b above that there was no region that had decreased Fos by either anesthetic.

Thank you for bringing this to our attention. In response to your concerns, we have made significant revisions to our data analysis. We have updated our input data to incorporate log-transformed relative c-Fos density values, normalized against the control group for each brain region, as illustrated in Figures 2 and 3. Instead of PCA, we have applied this updated data to hierarchical clustering analysis. The results of these analyses are consistent with our original observation that neither anesthetic led to a decrease in Fos expression in any region.

1. I still do not understand the rationale for the use of that metric. The use of a % of total Fos makes the data for each region dependent on the data of the other regions which wrongly leads to the conclusion that some regions are inhibited while they are not when looking at the raw data. Moreover, the interdependence of the variable (relative density) may affect the covariance structure which the PCA relies upon. Why not using the PCA on the logarithm of the raw data or on a relative density compared to the control group on a region-per-region basis instead of the whole brain?

Thank you for your insightful suggestion. Following your advice, we have revised our approach and now utilize the logarithm of the relative density compared to the control group on a region-by-region basis. We attempted PCA analyses using the logarithm of the raw data, the logarithm of the Z-score, and the logarithm of the relative density compared to control, but none yielded distinct clusters.

Author response image 3.

As a result, we employed hierarchical cluster analysis. We then examined the Z-scores of the log-transformed relative c-Fos densities (Figures 2E and 3E) to assess expression levels across clusters. Our analysis revealed that neither ISO nor KET treatments led to a significant suppression of c-Fos expression in the 53 brain regions examined. In the ISO group alone, there were 10 regions that demonstrated relative suppression (Z-score < -2, indicated by white boxes) as shown in Figure 3.

Fig. 2B: it's unclear to me why the regions are connected by a line. Such representation is normally used for time series/within-subject series. What is the rationale for the order of the regions and the use of the line? The line connecting randomly organized regions is meaningless and confusing.

Thank you for your suggestion. We have discontinued the use of PCA calculations and have removed this figure.

Fig 6A. The correlation matrices are difficult to interpret because of the low resolution and arbitrary order of brain regions. I recommend using hierarchical clustering and/or a combination of hierarchical clustering and anatomical organization (e.g. PMID: 31937658). While it is difficult to add the name of the regions on the graph I recommend providing supplementary figures with large high-resolution figures with the name of each brain region so the reader can actually identify the correlation between specific brain regions and the whole brain, Rationale for Metric Choice: Note that I do not dispute the choice of the log which is appropriate, it is the choice of using the relative density that I am questioning.

Thank you for your constructive feedback. In line with your suggestion, we have implemented hierarchical clustering combined with anatomical organization as per the referenced literature. Additionally, we have updated the vector diagrams in Figure 6A to present them with greater clarity.

Furthermore, we have revised our network modular division method based on cited literature recommendations. We used hierarchical clustering with correlation coefficients to segment the network into modules, illustrated in Figure 6—figure supplement 1. Due to the singular module structure of the KET network and the sparsity of intermodular connections in the home cage and saline networks, the assessment of network hub nodes did not employ within-module degree Z-score and participation coefficients, as these measures predominantly underscore the importance of connections within and between modules. Instead, we used degree, betweenness centrality, and eigenvector centrality to detect the hub nodes, as detailed in Figure 6—figure supplement 2. With this new approach, the hub node for the KET condition changed from SS to TeA. Corresponding updates have been made to the results section for Figure 6, as well as to the related discussions and the abstract of our paper.

Author response image 4.

Figure 6. Generation of anesthetics-induced networks and identification of hub regions. (A) Heatmaps display the correlations of log c-Fos densities within brain regions (CTX, CNU, TH, HY, MB, and HB) for various states (home cage, ISO, saline, KET). Correlations are color-coded according to Pearson's coefficients. The brain regions within each anatomical category are organized by hierarchical clustering of their correlation coefficients. (B) Network diagrams illustrate significant positive correlations (P < 0.05) between regions, with Pearson’s r exceeding 0.82. Edge thickness indicates correlation magnitude, and node size reflects the number of connections (degree). Node color denotes betweenness centrality, with a spectrum ranging from dark blue (lowest) to dark red (highest). The networks are organized into modules consistent with the clustering depicted in Supplementary Figure 8. Figure 6—figure supplement 1

Author response image 5.

Figure 6—figure supplement 1. Hierarchical clustering of brain regions under various conditions: home cage, ISO, saline, and KET. (A) Heatmaps show the relative distances among brain regions assessed in naive mice. Modules were identified by sectioning each dendrogram at a 0.7 threshold. (B) Silhouette scores plotted against the dendrogram tree height ratio for each condition, with optimal cluster definition indicated by a dashed line at a 0.7 ratio. (C) The number of clusters formed at different cutoff levels. At a ratio of 0.7, ISO and saline treatments result in three clusters, whereas home cage and KET conditions yield two clusters. (D) The mean Pearson's correlation coefficient (r) was computed from interregional correlations displayed in Figure 6A. Data were analyzed using one-way ANOVA with Tukey’s post hoc test, ***P < 0.001.

Author response image 6.

Figure 6—figure supplement 2. Hub region characterization across different conditions: home cage (A), ISO (B), saline (C), and KET (D) treatments. Brain regions are sorted by degree, betweenness centrality, and eigenvector centrality, with each metric presented in separate bar graphs. Bars to the left of the dashed line indicate the top 20% of regions by rank, highlighting the most central nodes within the network. Red bars signify regions that consistently appear within the top rankings for both degree and betweenness centrality across the metrics.

1. I am still having difficulties understanding Fig. 3.

Panel A: The lack of identification for the dots in panel A makes it impossible to understand which regions are relevant.

Panel B: what is the metric that the up/down arrow summarizes? Fos density? Relative density? PC1/2?

Panel C: it's unclear to me why the regions are connected by a line. Such representation is normally used for time series/within-subject series. What is the rationale for the order of the regions?