This reading explains that each delivery method—impromptu, manuscript, and memorized—has specific strengths and weaknesses depending on the speaking situation. I found it interesting that impromptu speaking, although anxiety-inducing, can actually strengthen public speaking skills because it forces speakers to think quickly and organize ideas on the spot. However, it also carries the risk of rambling or overstating knowledge. Manuscript delivery, on the other hand, offers precision and consistency, especially for complex information, but often reduces audience engagement because the speaker may sound like they are reading rather than speaking naturally.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

This work shows that resistance profiles to a variety of drugs are variable between different mycobacterial species and are not correlated with growth rate or intrabacterial compound concentration (at least for linezolid, bedaquiline, and Rifampicin). Note that intrabacterial compound concentration does not distinguish between cytosolic and periplasmic/cell wall-associated drugs. The susceptibility profiles for a wide range of mycobacteria tested under the same conditions against 15 commonly used antimycobacterial drugs provide the first recorded cross-species comparison which will be a valuable resource for the scientific community. To understand the reasons for the high Rifampicin resistance seen in many mycobacteria, the authors confirm the presence of the arr gene known to encode a Rif ribosyltransferase involved in Rif resistance in M. smegmatis in the resistant mycobacteria after confirming the absence of on-target mutations in the RpoB RRDR. Metabolomic analyses confirm the presence of ribosylated Rif in some of the naturally resistant mycobacteria which may not be entirely surprising but an important confirmation. Presumably M. branderi is highly resistant despite lacking the arr homolog due to the rpoB S45N mutation. M. flavescens has an MIC similar to that of M. smegmatis, despite having both Arr-1 and Arr-X. Various Arr-1 and Arr-X proteins are expressed and characterized for catalytic activity which shows that Arr-X is a faster enzyme,, especially with respect to more hydrophobic rifamycins. M. flavescens has similar MIC values to Rifapentine and Rifabutin to M. smegmatis. Thus, the Arr-1 versus Arr-X comparison does not provide a complete explanation for the underlying reasons driving natural Rif resistance in mycobacteria. Downregulation of Arr-X expression in M. conceptionense confers increased sensitivity to Rifabutin confirming its role as a rifamycin-inactivating enzyme.

Overall, the comparison of cross-species susceptibility profiles is novel; the demonstration that MIC is not correlated with intracellular drug concentration is important but not sufficiently interrogated, the demonstration that Arr-X is also a Rif ADP-ribosyltransferase is a good confirmation and shows that it is more efficient than Arr-1 on hydrophobic rifamycins is interesting but maybe not entirely surprising. The manuscript seems to have two parts that are related, but the rifamycin modification aspect of the work is not strongly linked to the first part since it interrogates the modification of one drug but not the common cause of natural resistance for other drugs.

Reviewer #2 (Public review):

Summary:

The authors use a variety of methods to investigate the mechanisms of innate drug resistance in mycobacteria. They end up focusing on two primary determinants - drug accumulation, which correlates rather poorly with resistance for many species, and, for the rifamycins, ADP-ribosyltransferases. The latter enzymes do appear to account for a good deal of resistance, though it is difficult to extrapolate quantitatively what their relative contributions are.

Overall, they make excellent use of biochemical methods to support their conclusions. Though they set out to draw very broad lessons, much of the focus ends up being on rifamycins. This is still a very interesting set of conclusions.

Strengths:

(1) A very interesting approach and set of questions.

(2) Outstanding technical approaches to measuring intracellular drug concentrations and chemical modification of rifamycins.

(3) Excellent characterization of variant rifamycin ADP-ribosyltransferases

Weaknesses:

(1) Figure 3c/d: These panels show the same experiment done twice, yet they display substantially different results in certain cases. For instance, M. smegmatis appears to show an order of magnitude lower RIF accumulation in panel d compared to M. flavescens, despite them displaying equal accumulation in panel c. The authors should provide justification for this variation, particularly as quantitative intra-species comparisons are central to the conclusions of this figure.

The data in panels 3c and 3d are from different sets of experiments. The reviewer is correct with regards to M. smegmatis. The data indeed is ~ 1 order of magnitude different. However, the data for other species is very similar. The reviewer may also have noticed that the error bars are also larger in 3d, compared to 3c, indicating a greater variation between independent experiments use in 3d. We do not have a good explanation for this, other than the experiments shown in 3d were associated with greater biological variability.

(2) There are several technical concerns with Figure 3 that affect how to interpret the work. According to the methods, the authors did not appear to normalize to an internal standard, only to an external antibiotic standard (which may account for some of the technical variation alluded to above).

We agree that using a labeled drug as an internal standard (IS) would be ideal. However, the experiment initially followed an untargeted metabolomics approach, which later shifted to relative drug quantification. At that stage, normalizing with IS was impractical because proper implementation would require multiple IS across the chromatographic range. Therefore, we opted for total ion current (TIC) normalization, which accounts for variability in overall metabolite abundance—even though the experimental setup was already adjusted for each bacterial species’ growth rate. Additionally, we prepared external standard curves for each drug to enable quantification, and the amount of drug added to each plate was considered when reporting these values.

Second, the authors used different concentrations of drug for each species to try to match the species' MICs. I appreciate the authors' thinking on this, but I think for an uptake experiment it would be more appropriate to treat with the same concentration of drug since uptake is likely saturable at higher drug concentrations. In the current setup, for the species with higher MIC, they have to be able to uptake substantially more antibiotics than the species with low MIC in order to end up with the same normalized uptake value in Figure 3d. It would be helpful to repeat this experiment with a single drug concentration in the media for all species and test whether that gives the same results seen here.

We respectfully disagree with the reviewer. Experiments such as the one proposed by the review work well when MIC values are a few fold apart, for strains of the same species, but have not been tested when MIC values are 100-1000-fold apart, with different species. Furthermore, what would be the interpretation of compound uptake at 1000-fold the MIC for one species and MIC level for another? By using antibiotic concentrations at the respective MIC for each species we are at least under conditions where we know the biological effect of the antibiotic across species is the same, based on its potency.

(3) Figure 4f: This panel seems to argue against the idea that the efficacy of RIF ribosylation is what's driving drug susceptibility. M. flavescens is similarly resistant to RIF as M. smegmatis, yet M. flavescens has dramatically lower riboslyation of RIF. This is perhaps not surprising, as the authors appropriately highlight the number of different rif-modifying enzymes that have been identified that likely also contribute to drug resistance. However, I do think this means that the authors can't make the claim that the resistance they observe is caused by rifamycin modification, so those claims in the text and figure legend should be altered unless the authors can provide further evidence to support them. This experiment also has results that are inconsistent with what appears to be an identical experiment performed in Supplemental Figure 5b. The authors should provide context for why these results differ.

In regard to enzyme efficiency, the apparent rate of all Arr-1 is relatively similar in converting RIF into ADP-Ribosyl-Rif between species. However, Arr-X is much more efficient when compared to Arr-1 in both M. flavescents and M. conceptionense. This is indicated by the apparent rate measured and displayed on figure 5c.

Proteomics data shows that there is upregulation of Arr-1 and Arr-X upon rifampicin treatment in M. flavescens and M. conceptionense. However, the same experiment was not performed in Arr-1 KD. Therefore, we can’t verify through this approach if the activity observed in vivo directly correlates with a higher expression of Arr-X alone. Of note, likely both enzymes contribute to resistance to rifamycins, as per our results with the Arr-X KD and sensitization of M. conceptionense to RIF.

Author response image 1.

It is also worth mentioning that there are other enzymes in the pathway of RIF ribosylation and their efficiency is unknown (Author response image 2). Therefore ADP-Ribosyl-RIF It is not an “end-metabolite” and maybe not the sole determinant of RIF resistance via ADP-ribosylation. Downstream enzymes can also account for the difference observed between M. flavescens and M. smegmatis.

Author response image 2.

It is correct that the Rifampicin MIC for M. flavescens is the same as M. smegmatis.

(4) Fig 4f/5c: M. flavescens has both Arr-1 and Arr-X, yet it appears to not have ribosylated RIF. This result seems to undermine the authors' reliance on the enzyme assay shown in Fig 5c - in that assay, M. flavescens Arr-X is very capable of modifying rifampicin, yet that doesn't appear to translate to the in vivo setting. This is of importance because the authors use this enzyme assay to argue that Arr-X is a fundamentally more powerful RIF resistance mechanism than Arr-1 and that it has specificity for rifabutin. However, the result in Figure 4f would argue that the enzyme assay results cannot be directly translated to in vivo contexts. For the authors to claim that Arr-X is most potent at modifying rifabutin, they could test their CRISPRi knockdowns of Arr-X and Arr-1 under treatment with each of the rifamycins they use in the enzyme assay. The authors mentioned that they didn't do this because all the strains are resistant to those compounds; however, if Arr-X is important for drug resistance, it would be reasonable to expect to see sensitization of the bacteria to those compounds upon knockdown.

The reviewer is reading Fig. 4f incorrectly, probably because it is plotted in a linear scale instead of logarithmic scale. Ribosylated Rif is present in M. flavescens, just at lower levels than M. conceptionense and M. smegmatis. In species where there is no Arr-1 or Arr-3, ribosylated RIF is not detected at all (e.g. M. tuberculosis), i.e., concentration is zero. Therefore, any detection of ribosylated RIF can be considered significant. In addition, as mentioned before, ADP-ribosylation of RIF is not the final product of the reaction and further studies need to be undertaken to understand subsequent reactions.

(5) Figure 5d: The authors use this CRISRPi experiment to claim that ArrX from M. conceptionanse is more potent at inactivating rifabutin than Arr-1. This claim depends on there being equal degrees of knockdown of Arr-1 and Arr-X, so the authors should validate the degree of knockdown they get. This is particularly important because, to my knowledge, nobody has used this system in M. conceptionanse before.

We agree with the reviewer that a qPCR should have been performed to define the extent of interference in the strain. generated Unfortunately, at this time a qPCR was not performed in the strains tested to confirm the extent of down regulation. Although it is the best practice to validate the strain KD, there is no indication that the effect observed is due to unspecific downregulation. The genetic environment in which Arr-X is positioned is different from Arr-1 and the targeting oligonucleotides are specific and would not promiscuously bind to Arr-1. Said that, this is indeed a fault in our setup.

(6) The authors' arguments about Arr-X and Arr-1 would be strengthened by showing by LC/MS that Arr-X knockdown in M. conceptionense results in more loss of ribosyl-rifabutin than knockdown of Arr-1.

We agree with the reviewer that performing the LC-MS analysis of the Arr-x knockdown would have strengthened the argument of our paper. Unfortunately, this experiment was not performed.

Reviewer #3 (Public review):

This manuscript presents a macroevolutionary approach to the identification of novel high-level antibiotic resistance determinants that takes advantage of the natural genetic diversity within a genus (mycobacteria, in this case) by comparing antibiotic resistance profiles across related bacterial species and then using computational, molecular, and cellular approaches to identify and characterize the distinguishing mechanisms of resistance. The approach is contrasted with "microevolutionary" approaches based on comparing resistant and susceptible strains of the same species and approaches based on ecological sampling that may not include clinically relevant pathogens or related species. The potential for new discoveries with the macroevolution-inspired approach is evident in the diversity of drug susceptibility profiles revealed amongst the selected mycobacterial species and the identification and characterization of a new group of rifamycin-modifying ADP-ribosyltransferase (Arr) orthologs of previously described mycobacterial Arr enzymes. Additional findings that intra-bacterial antibiotic accumulation does not always predict potency within this genus, that M. marinum is a better proxy for M. tuberculosis drug susceptibility than the commonly used saprophyte M. smegmatis, and that susceptibility to semi-synthetic antibiotic classes is generally less variable than susceptibility to antibiotics more directly derived from natural products strengthen the claim that the macroevolutionary lens is valuable for elucidating general principles of susceptibility within a genus.

There are some limitations to the work. The argument for the novelty of the approach could be better articulated. While the opportunities for new discoveries presented by the identification of discrepant susceptibility results between related species are evident, it is less clear how the macroevolutionary approach is further leveraged for the discovery of truly novel resistance determinants. The example of the discovery of Arr-X enzymes presented here relied upon foundational knowledge of previously characterized Arr orthologs. There is little clarity on what the pipeline for identifying more novel resistance determinants would look like. In other words, what does the macroevolutionary perspective contribute to discovery from the point of finding interspecies differences in susceptibility? Does the framework still remain distinct from other discovery frameworks and approaches? If so, how?

Thanks for pointing this out, as this is a critical feature of our study and method. Our approach relies on inter-species comparative genomics and phenotypes, and therefore, it is distinct from inter-strains comparison. This difference is dramatic, and it becomes clearer when we are comparing the core genome of M. tuberculosis (one species) 92% with the core genome of the genus, circa of 1%. While we focus on rifamycin in this manuscript, future manuscripts will investigate many of the other dozens of “inconsistencies” observed between the genetic makeup of different mycobacterial species and there actual performance in the presence of different antibiotics.

While the experimentation and analyses performed appear well-designed and rigorous, there are a few instances in which broad claims are based on inferences from sample sets or data sets that are too limited to provide robust support. For example, the claim that rifampicin modification, and precisely ADP-ribosylation, is the dominant mechanism of resistance to rifampicin in mycobacteria may be a bit premature or an over-generalization, as other enzymatic modification mechanisms and other mechanisms such as helR-mediated dissociation of rifampicin-stalled RNA polymerases, efflux, etc were not examined nor were CRISPRi knockdown experiments conducted beyond an experiment to tease out the role of Arr-X and Arr-1 in one strain. The general claim that intra-bacterial antibiotic accumulation does not predict potency in mycobacteria may be another over-generalization based on the limited number of drugs and species studied, but perhaps the intended assertion was that antibiotic accumulation ALONE does not predict potency.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major comments

(1) The metabolomics is done using mycobacteria grown on filters. Initially, mycobacterial cells are grown on the filters for 5 doublings before being transferred to drug-containing (or free) agar for one doubling. Is this based on calculated doubling time in liquid culture or a true determination of the fact that the biomass increases to what would amount to 5 doublings?

The doubling time used is the one determined in liquid media. Although it is possible that the growth kinetics in solid media is slightly different from liquid (±10%), this experimental design is well established for M. tuberculosis (since Proc Natl Acad Sci U S A. 2010 May 25;107(21):9819-24.) and M. smegmatis (unpublished). Therefore, we used the growth rate as a proxy for having the same biomass of cells for each species tested. A maximum difference of 10% was observed between M. tuberculosis growth in liquid and in solid media, however, cells grow exponentially for much longer in filters. This makes filter-based experiments more reliable, as few growth phase-derived differences are present.

(2) The demonstration that intrabacterial drug concentrations vary between mycobacterial species in a manner not related to MIC for at least LZD and RIF, is an important finding. However, intrabacterial does not mean cytoplasmic since a considerable fraction could be present in the periplasmic/cell wall layers. Ideally, this would need to be determined but would of course be a massive undertaking since the method needs validation & optimization for each mycobacterial species. Nevertheless, this has to be mentioned. In addition, three drugs are limiting. Measuring additional drug concentrations in these 5 mycobacteria would at least establish some confirmation about the extent of this lack of correlation. Thus, could the authors measure concentrations of additional drugs with intracellular targets?

Testing additional drugs can be beneficial and would be an expansion of our paper, which will definitely be on future plans for further studies focusing on other antibiotics described here. It would also provide new insights into other possible mechanisms of resistance in mycobacterial species. However, in this study we aimed to first determine the antibiotic response profile in different mycobacterial species, and once we identified interesting resistance phenotypes that could not be readily explained by known mechanisms of resistance, we narrowed it down to certain drugs and species that would potentially provide insights into new mechanisms of antibiotic resistance. Finally, exploring drug concentration across multiple bacterial compartments is a dauting task and it has not been done extensively with any species, not to mention with multiple species, many of which are still lacking any study of their actual cell envelope.

(3) CRISPRi was used to reduce transcription in M. conceptionense. What was the level of gene downregulation?

As mentioned previously, a setback from our setup is that the level of KD was not measured at this instance.

Minor comments:

(1) The introduction mentions the fast and slow-growing mycobacteria which are classified based on the time that it takes to observe colonies on solid agar. However, in liquid medium, there is less correlation between the reported growth on agar and doubling time in liquid (Figure 1b, Figure 2d). This could be mentioned in the results section. In Figure 2d, the filled circles represent fast-growers but this does not hold well for liquid culture and it might make more sense to not distinguish between fast- and slow-growers in these graphs. A small complication would also be the fact that the doubling time represents growth in a liquid medium with Tyloxapol as a detergent whereas the MIC and metabolomics are done on solid agar with no detergent. The metabolomics is done after a doubling but for those where agar growth and liquid growth have large discrepancies in growth rate, there could be some differences.

Apologies for this misunderstanding. Fast- and slow-growth phenotypes are determined in Lowenstein-Jensen (LJ) agar, not in 7H10 agar (used in our study and most studies of mycobacteria). Furthermore, this is a qualitative definition, not a quantitative one. Therefore, our measurements do not need to correlate with fast- and slow-growth phenotypes, unless we had used that one specific medium. Furthermore, in liquid medium, we determined growth rate directly, which is never done with LJ medium.

In addition to adding the same amount of cells to each filter, we also perform TIC normalization, which should account for how rich the samples were – and therefore how much material we had. Therefore, we do not observe discrepancies due to differences in growth rate and the presence/absence of detergent in the media.

It is also worth mentioning that this experimental set up has been well established in many M. tuberculosis labs that study metabolism. Importantly, the use of detergent drastically affects mass spectrometry, and therefore cannot be used.

(2) Figure 1g in the text should be Figure 1f.

Apologies, it has been fixed.

(3) Figure S1 would be ideal to have in (supplementary) table format.

This data is now being provided in a table format.

(4) Table S1 - ethambutol misspelt.

Spelling has been corrected.

(5) MIC for species such as M. abscessus could depend on medium (7H9-based medium can give different MIC values than CAMH).

Indeed, different media can significantly change MIC values, and this is true for many bacterial species, if not all. For this study we used only species that could be grown in 7H9 broth containing 10 % ADC, 0.05% glycerol 0.05% tyloxapol and 7H10 plates containing 10% OADC and 0.05% glycerol. MIC₉₉ was determined in the latter as we found more efficient and robust to do our tests it in solid media. The goal of our experiment was not to the determined the “true” MIC for the antibiotics tested, as this value does not exist. It was to find lack of correlations between relative values and the presence of genes that can account for it.

(6) The statement "the experiment was performed at a concentration of antibiotic equal to its MIC" initially seems confusing. It was not equal to the MIC but performed at 6-fold the respective MIC of the species in question. Maybe re-phrasing this would help.

Apologies for this oversight. It has been corrected.

(7) Note that some mutations outside the RRDR (eg. V170F and I491F) can also cause Rif resistance.

Author response image 3.

A Rainbow diagram of RpoB X-Ray structure coloured according to sequence conservation. Dark purple indicates high conservation, whereas dark orange indicates low conservation. RIF (showed in magenta) is bound to RpoB. Zoomed view displays that the RIF-binding pocket is considerably conserved. B RpoB protein sequence has an 81bp region called Rifampicin Resistance Determining Region (RRDR) that is known to be important for RIF binding and is where most mutations occur in drug-resistant TB. Sequence alignment displays that the RRDR region is conserved with the exception of M. branderi, which has an Asn instead of a Ser residue in position 456 (numbering is related to the M. tuberculosis sequence), highlighted in bold.

Attached we have a structural alignment of RpoB of the species highlighted on this paper. Although there is variability within the sequences, which is also displayed in Author response image 3 with the conservation analysis, the residues that have been implicated with resistance (including V170 and I491) are conserved. Alignment sent on .fasta file that can be opened in jalview.

(8) Discuss how the RpoB S450N mutation in M. branderi confers the observed level of resistance.

That’s a great point, thank you. Now it reads as:

“The rifampicin (RIF) binding pocket is generally conserved, but Mycobacterium branderi has an S450N mutation in the RRDR region. While this specific mutation hasn't been found in clinical isolates, it's located at the binding site and may confer resistance (273). Although both serine (S) and asparagine (N) have similar side chains, related mutations like S450Q have been linked to resistance (156). Thus, M. branderi may be RIF-resistant due to this mutation. In contrast, M. conceptionense, M. flavescens, and M. smegmatis show no target sequence differences that explain their resistance”

(9) The statement that the three tested NTM are sensitive to rifabutin ("resistant to all rifamycins except for rifabutin") needs to be interpreted considering what sensitivity means. The MIC is still high (1.6-3.1 ug/mL) when compared to that of Mtb. The 2-fold differences in MIC between M. smegmatis and M. conceptionense do not really prove or disprove the role of Arr-X in rifabutin resistance.

We fixed the sentence to be more careful with the language on the text. We agree, but it is worth mentioning that generally with bacteria there is a regulation by the CLSI. Each bacterial species has a range that is considered sensitive or resistant, but these are not available for the species used in this study. In general, bacteria with MIC values above 8 µg/mL are considered resistant to rifampin (J Antibiot 2014 67:625).

(10) Figure 1d: It's hard to quantify the sensitivity of the plates. Can this be done by MIC? Was only rifabutin tested or also rifampicin?

The initial experiments described on the paper were all performed using Rifampicin only. Then, the MIC for the remaining rifamycins was determined for M. smegmatis, M. flavescens and M. conceptionense, and can be perused on “Supplementary table 4”. Figure 5d is to illustrate the effect of the KD in M. conceptionense sensitivity to rifabutin.

(11) Is there data to show the ADP-ribosylation of rifabutin in M. conceptionense and the CRISPRi strains?

Unfortunately, we did not perform LC-MS analysis on M. conceptionense CRISPRi strains exposed to rifabutin to measure potential ADP-ribosylation.

Reviewer #2 (Recommendations for the authors):

(1) It would be useful if the authors would complete Figure 1A by determining growth rates for the remaining 18 strains that they currently omitted.

These growth rates were obtained using roller bottles and in at least 3 independent experiments, unfortunately the throughput is far ideal. The goal of the experiment was to highlight difference in growth rate, beyond fast- and slow-growth, which we did. Adding the remaining values would not change this conclusion. Growth rate variation in 7H9 is significant and the point is made in our figure.

(2) The authors should justify their choice of species used in Figures 3-4. It would be useful to know, for instance, if the authors chose these species in an unbiased fashion, or if they were chosen because the authors had already determined that they possess rifamycin-modifying enzymes of interest. In that case, they wouldn't necessarily be a representative sample to use for the correlation analysis of antibiotic uptake and potency in Figure 3.

They were chosen because of their resistance profile for BDQ, LZD and RIF. This has been addressed in the text, which now reads “Given the antibiotic response profiles observed, we selected BDQ, LZD and RIF to explore the molecular causes of these dramatic changes in antibiotic potency observed across the Mycobacterium genus.”

(3) Figure 4b: The data in this panel appear inconsistent - for instance, M. houstonense appears to grow at 10X Mtb MIC, but fails to grow at 1X Mtb MIC. Repeating this experiment would better establish the validity of the authors' claims about the relative susceptibility of these strains to RIF.

The figures got rotated when exported from illustrator. Corrected figure is uploaded, and original plate photos are also uploaded for clarity.

(4) Figure 4e: Does Arr-X get upregulated in these proteomic datasets? The authors' argument that proteomic upregulation correlates with important drug resistance genes would imply that it might be, so that would be useful information to provide.

Arr-X is slightly upregulated, but not statistically significant – this could be due to the native expression of Arr-1. Data is displayed in a previous answer.

(5) I wasn't able to find the supplementary tables that the authors allude to - not sure if that was a file mixup, but those tables would be useful for interpreting the manuscript.

We are sorry that you couldn’t access the table. It must be a file corruption issues, as the other reviewers were able to. We will make sure that all tables are available and accessible.

(6) For LC/MS, the authors use peak height instead of peak area, which they argue correlates better with the amount of drug in cells because of the poor peak shape they observed for linezolid. This is not standard practice, so the authors should provide evidence to support this claim by running an LC/MS standard curve, then showing the correlation between peak height and amount of compound added as well as the correlation between peak area and compound.

Thank you for pointing that out, accuracy calculated and displayed. Both peak area and height can be used, but indeed area is standard practice.

(7) The authors should provide methods information about the LC column and the gradient settings used for LC-MS, as well as the settings of the MS.

The full method has been added to the paper.

Reviewer #3 (Recommendations for the authors):

I have only minor comments aside from the information in the Public Review:

(1) Results, section on Intra-bacterial antibiotic accumulation, line 8: "experiment was performed at a concentration of antibiotic PROPORTIONAL to its MIC" would be more accurate?

Agreed and adjusted according to Reviewer’s suggestion.

(2) Results, section on A minor role for pre-existing target modification, last sentence: the mere presence of RIF-ribosylating enzymes does not, in and of itself indicate that "RIF modification, and precisely ADP-ribosylation, is the dominant mechanism of resistance to RIF in mycobacteria", as other mechanisms and other forms of modifying enzymes are known to confer rifamycin resistance, with redundancy (e.g., other rifampicin-modifying enzymes, or helR-mediated dissociation of rifampicin-stalled RNA polymerases from DNA). It would be more appropriate to suggest the results presented to this point indicate RIF modification is common among mycobacteria. The evidence from the CRISPRi knockdown of Arrs shown in Fig 5d is the kind of evidence that suggests ribosylation as a dominant mechanism, at least against rifabutin in this particular species.

Absolutely, there are other possible modifying enzymes that could be encoded by these mycobacterial species. There is a possibility that M. flavescens and M. smegmatis encode for a putative helR (attached alignment) but further experiments would need to be carried out to confirm its ability to displace RIF in the RNAP. Interestingly, the presence of both Arr and HelR has been studied in M. abscessus and those mechanisms of resistance are independent from each other (Molecular Cell 2022 82(17):3166-3177.e5).

(3) Discussion, 2nd sentence needs grammatical editing.

Rephrased and it reads “Using our mycobacterial library, we identified for the first time high- and ultra-high-level intrinsic resistance (3) to many of the antibiotics tested. Of note, the resistant phenotype is naturally occurring and not a result of mutations due to exposure to the antibiotic in the clinic – which is the more traditional approach for probing mechanisms of antibiotic resistance. Our observations revealed that resistance profiles are highly variable across the genus and do not follow phylogeny, implicating HGT as the key mechanism for acquisition of resistance determinants and evolution of antibiotic resistance in mycobacteria (42).”

(4) Discussion, page 7, first line: the inclusion of LZD and BDQ in this statement seems at odds with Figure 2c and the statements in the first paragraph of page 5 highlighting these as examples of drugs to which most mycobacteria are susceptible.

Indeed, many of the species are susceptible, however the MIC₉₉ levels observed have never been reported before, and therefore we found it to be an interesting finding to highlight. From a treatment perspective, knowing which species are sensitive to which drugs is of course the most useful outcome of our study.

(5) The next sentence..."We found that resistance to these antibiotics in mycobacteria cannot be explained by uptake/efflux mechanisms..." is a bit of an over-generalization and conflicts with the evidence presented earlier that efflux could be playing a role in BDQ resistance and the published evidence establishing a clinically significant role for efflux-mediated BDQ resistance in M. tuberculosis, M. avium complex and M. abscessus complex.

We rephrased it to make it more specific to our findings. It reads “We found that resistance to these antibiotics in mycobacteria do not correlate with by uptake/efflux mechanisms in the species tested and it does not correlate with growth rate. Identification of mycobacterial species highly resistant to BDQ and LZD is worrisome as most of this species, if not all, have never been exposed to these drugs.”

(6) Methods, section on In vitro activity assay of Arr enzymes, line 1: reference(s) should be provided for previously reported methods.

Reference now added.

(7) Figure 2d: the low end of the susceptibility range is not well defined.

In this figure the susceptibility is not defined as the lowest area of the graph, but the lower concentrations are indeed harder to be defined. Hopefully supplementary figure 1 and the additional table containing the MIC can be informative to address this comment.

(8) Figures 3c,d: the presentation of the relative antibiotic concentrations could be harmonized between the graphs in 3c and those in 3d to enable a more ready comparison.

We disagree. The goal of these different panels is exactly to illustrate two distinct points. C gives the relative concentration of antibiotic, while D correlates relative concentration with MIC99. The use of log scale in D further clarifies that there is no correlation between intracellular antibiotic concentration and potency (MIC). This information is not present in C.

(9) Figure 4f and Supplementary Figure 5b: it is difficult to understand the limited amount of ribsosyl-RIF in M. flavescens in Fig 4f relative to Supplementary Figure 5b (esp. when considering M. smeg as a common comparator); and, further, to understand the seeming lack of correlation between RIF susceptibility, ribosylation and Arr number and catalytic efficiency for these two strains without considering additional resistance mechanisms.

In reality the difference between figure 4f and Supplementary figure 5b is mainly due to M. smegmatis – that has an apparent lower production of ribosyl-RIF in the experiment described in the supplementary figure. The values for M. flavescens are relatively similar. In addition, the ADP-Ribosyl-RIF is not the final metabolite of the pathway.

In regards of having the entire picture, it is true that we were unable to completely unravel and correlate MIC value, expression of Arr-1, expression of Arr-3, efficiency of each enzyme, production of ADP-Ribosyl-RIF and the presence of other possible mechanisms of resistance and this is indeed a setback in our study, and of most studies ever published, which usually focus on one resistant determinant.

Author response:

The following is the authors’ response to the original reviews

Many thanks for your helpful and constructive comments for our work examining the effect of inhibiting both the insulin receptor (IR) and IGF1 receptor (IGF1R) in the podocyte. We are pleased to submit an updated manuscript addressing your concerns.

(1) A major concern was a lack of mechanistic insight into how deletion (or knock-down) of both receptors caused the spliceosomal phenotype (Reviewer 1 and Reviewer 3).

We now think this is due to the lack of a network of insulin/IGF phospho-signalling events to a variety of spliceosomal proteins and kinases. The reasons for this are as follows:

A. Since submitting our paper Turewicz et al have published a comprehensive phospho-proteomic paper examining the effects of 100nM insulin on human primary myotubes (DOI: 10.1038/s41467-025-56335-6). They discovered that multiple post-translational phosphorylation events occur in a variety of spliceosomal proteins at differing time points (1 minute to 60 minutes). Furthermore, they show that mRNA splicing is rapidly modified in response to insulin stimulation in their cells. This follows elegant work from Bastista et al who studied diabetic and non-diabetic iPSC derived human myositis and also detected a spliceosome phosphorylation signature (DOI: 10.1016/j.cmet.2020.08.007).

B. We have examined phospho-proteosome changes that occur in wild -type podocytes (expressing both the IR and IGF1R) compared to double (IR and IGF1R) knockout cells using phosho-proteomics. We have done this 3 days after inducing receptor knockdown, before major cell loss, and have stimulated the cells with either 10nM insulin or 100mg IGF1.

Interestingly, we detected several post-translational modifications (PTM) in our data set that are also present in Turewicz’s studies. Of note, 100nM insulin (as used by Turewicz) will signal through both the insulin and IGF1 receptor (and hybrid Insulin/IGF1 receptors) which is relevant to our studies.

Our work shows a cascade of phospho- signalling events affecting multiple components of the spliceosomal complex and evidence of kinase modulation (phosphorylation) (New Figure 7 and supplementary Figure 5). Also new results section in paper (lines 391-425 in track changes version). We acknowledge that we only studied a single time point after stimulation (10 minutes) and could have missed other PTM in the spliceosomal complex and other kinases. This is mentioned in our new limitations of study section (lines 595-606). This will be a focus of future work. We did not find major PTM differences when stimulating with either insulin or IGF1 in our studies and suspect that the doses of insulin (10nM) and IGF1 (100mg) used are still able to signal through cognate receptors.

Furthermore, we have examined the relative contributions of the insulin and IGF1 receptor in detail in the model (addressed in point 13 below).

(2) The phenotype of the mouse is only superficially addressed. The main issues are that the completeness of the mouse KO is never assessed nor is the completeness of the KO in cell lines. The absence of this data is a significant weakness. (Reviewer 1)

We apologise for not making this clear, but we did assess the level of receptor knockdown in both the animal and cell models. The in vivo model showed variable and non-complete levels of insulin receptor and IGF1 receptor podocyte knock down (shown in supplementary Figure 1C). This is why we made the in vitro floxed podocyte cell lines in which we could robustly knockdown both the IR and IGF1R. We show this using Western blotting (shown in Figure 2A). We agree that calling the models knockout is misleading and have changed all to knock down (KD) now.

(3) The mouse experiments would be improved if the serum creatinine’s were measured to provide some idea how severe the kidney injury is. (Reviewer 1)

There is variability in creatinine levels which is not uncommon in transgenic mouse models (probably partly due to variability in receptor knock down levels with cre-lox system). This is part of rationale of developing the robust double receptor knockout cell models where we robustly knocked out both receptors by >80%. We have added measured creatinine levels in a subset of mice in supplementary data (New Supplementary Figure 1E) and mention this in the text (lines 285-286). As some mice died we expect they may have developed acute kidney injury, but we did not serially measure the creatinine’s in every mouse over time. We could have assessed the GFR in a more sensitive way to look at differences. However, we consider the highly significant levels of albuminuria and histological damage observed in our models show a significant kidney phenotype.

(4) An attempt to rescue the phenotype by overexpression of SF3B4 would also be useful. If this didn't work, an explanation in the text would suffice. (Reviewer 1).

We did consider doing this but on reflection think it is very unlikely to rescue the phenotype as an array of different spliceosomal proteins quantitatively changed and were differentially phosphorylated / dephosphorylated throughout the complex (as we hope our revised work illustrates now). We think a single protein rescue is highly unlikely to work. We hope this is an appropriate explanation for this action. We have mentioned this in the text now in our discussion (lines 601-602).

(5) As insulin and IGF are regulators of metabolism, some assessment of metabolic parameters would be an optional add-on. (Reviewer 1).

Thank you for this suggestion. We did not extensively examine the metabolism of the mice however we did perform blood glucose measurement and weight which are included in the paper (Figure 1A and Figure 1B).

(6) The authors should caveat the cell experiments by discussing the ramifications of studying the 50% of the cells that survive vs the ones that died. (Reviewer 1).

We appreciate this and this was the rationale behind cells being studied after 3 days differentiation for total and phospho-proteomics before significant cell loss to avoid the issue of studying the 50% of cells that survive (which happened at 7 days). We have made this clearer in the manuscript. We also have added the data showing less cell death at 3 days in the cell model (New Supp Figure 2B).

(7) It would be helpful to say that tissue scoring was performed by an investigator masked to sample identity. (Reviewer 2)

We did this and have added to manuscript (line 113).

(8) Data are presented as mean/SEM. In general, mean/SD or median/IQR are preferred to allow the reader to evaluate the spread of the data. There may be exceptions where only SEM is reasonable. (Reviewer 2)

All graphs have now been changed to SD rather than SEM.

(9) It would be useful to for the reader to be told the number of over-lapping genes (with similar expression between mouse groups) and the results of a statistical test comparing WT and KO mice. The overlap of intron retention events between experimental repeats was about 30% in both knock-out podocytes. This seems low and I am curious to know whether this is typical for this method; a reference could be helpful. (Reviewer 2)

This is an excellent question. We had 30% overlap as the parameters used for analysis were very stringent. We suspect we could get more than 30% by being less stringent, which still be considered as similar events if requested. Our methods were based on FLAIR analysis (PMID: 32188845). We have added this reference to the manuscript (Line 242 & 680).

(10) With the GLP1 agonists providing renal protection, there is great interest in understanding the role of insulin and other incretins in kidney cell biology. It is already known that Insulin and IGFR signaling play important roles in other cells of the kidney. So, there is great interest in understanding these pathways in podocytes. The major advance is that these two pathways appear to have a role in RNA metabolism, the major limitations are the lack of information regarding the completeness of the KO's. If, for example, they can determine that in the mice, the KO is complete, that the GFR is relatively normal, then the phenotype they describe is relatively mild. (Reviewer 1)

Thank you. The receptor knock-out (KO) in the mice is highly unlikely to be complete (Please see comments above and Supplementary Figure 1C). There are many examples of “KO” animal models targeting other tissues showing that complete KO of these receptors seems difficult to achieve, particularly in reference to the IGF1 receptor. In the brain, which also contains terminally differentiated cells, barely 50% of IGF1R knockdown was achieved in the target cells (PMID:28595357). In ovarian granulosa cells (PMID:28407051) -several tissue specific drivers tried but couldn't achieve any better than 80%. The paper states that 10% of IGF1R is sufficient for function in these cells so they conclude that their knockdown animals are probably still responding to IGF1. Finally, in our recent IGF1R podocyte knockdown model we found Cre levels were important for excision of a single homozygous floxed gene (PMID: 38706850) hence we were not surprised that trying to excise two homozygous floxed genes (insulin receptor and IGF1 receptor) was challenging. This was the rationale for making the double receptor knockout cell lines to understand processes / biology in more detail. As stated earlier, we have changed our description of the mice and cell lines from knock-out to knock-down throughout the revised manuscript as this is more accurate.

(11) For the in vivo studies, the only information given is for mice at 24 weeks of age. There needs to be a full-time course of when the albuminuria was first seen and the rate of development. Also, GFR was not measured. Since the podocin-Cre utilized was not inducible, there should be a determination of whether there was a developmental defect in glomeruli or podocytes. Were there any differences in wither prenatal post-natal development or number of glomeruli? (Reviewer 3)

We have added further urinary Albumin:creatinine ratio (uACR) data at 12, 16 and 20 weeks to manuscript. We do not think there was a major developmental phenotype as albuminuria did not become significantly different until several months of age (new Supp Figure 1B). We did consider using a doxycycline inducible model but we know the excision efficiency is much less than the constitutive podocin-cre driven model Author response image 1. This would likely give a very mild (if any) phenotype when attempting to knockout both receptors and not reveal the biology adequately. We acknowledge the weaknesses of the animal model and this was the rationale for generating the cell models.

(12) Although the in vitro studies are of interest, there are no studies to determine if this is the underlying mechanism for the in vivo abnormalities seen in the mice. Cultured podocytes may not necessarily reflect what is occurring in podocytes in vivo. (Reviewer 3)

This is a good point. We have now immune-stained the DKD and WT mice for Sf3b4 (a spliceosomal change in our in vitro proteomics) and also find a significant reduction in this protein in podocytes of the DKD mice (New Figure 3F).

(13) Given that both receptors are deleted in the podocyte cell line, it is not clear if the spliceosome defect requires deletion of both receptors or if there is redundancy in the effect. The studies need to be repeated in podocyte cell lines with either IR or IGFR single deletions. (Reviewer 3)

We have now performed proteomics and phospho-proteomics in all 4 cell types (Wild-type, Insulin receptor knock down, IGF1R knockdown and double knockdown) at 3 days (New Figure 8 and supplementary Figure 6. Also new results section lines 425 to 450). This shows that both receptors contribute to the pathways (and hence there is a high level of compensation built into the system). For total proteins we detected that spliceosomal tri-snRNP was only reduced when both receptors were lacking but other proteins / pathways had an incremental effect of losing the insulin or IGF1 receptor. Likewise, the spliceosomal phospho-signaling events can go through either the insulin or igf1 receptors predominantly or through both. We think this reflects the complexity of this system and how evolutioatily it has developed in mammals to protect against its loss.

Finally in revision we have rewritten the discussion with a “limitations of the study” section and hopefully in an easier to read fashion for the readership.

Author response image 1.

(A) mT/mG reporter mouse crossed to constitutional podocin Cre heterozygous mouse. Illustrates podocyte specificity for Cre driver and excision Of reporter Figure shows GFP expression in Cre producing cells (top panel scale bar=250vm; bottom panel scale bar=50pm). Cre expression causes GFP to be switched on. (B) mT/mG reporter mouse crossed to podocin RtTA— tet-o-cre heterozygous mouse shows podocyte specificity for driver and approximately 60% excision. (top and bottom panels scale bar=250pm; middle panel scale bar=50pm). Doxycycline required for expression showing not leaky.

lord Capulet enters and mocks Juliet's grief however after he learns that Juliet is rejecting the wedding he gets enraged saying that he would drag her to the church himself he then gives juliet a ultimatium saying if he doesnt marry paris he would disown juliet and leave her a beggar on the streets

tybalt spots romeo and challenges him to a fight but romeo refuses and says that we are closer than you think mercutio sees romeo as a coward and decide to draw his sword challenging tybalt in romeos place

Author response:

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

eLife Assessment

This valuable study examines the role of E2 ubiquitin enzyme, Uev1a in tissue resistance to oncogenic RasV12 in Drosophila melanogaster polyploid germline cells and human cancer cell lines. The incomplete evidence suggests that Uev1a works with the E3 ligase APC/C to degrade Cyclin A, and the strength of evidence could be increased by addressing the expression of CycA in the ovaries and the uev1a loss of function in human cancer cells. This work would be of interest to researchers in germline biology and cancer.

Thank you for your valuable assessment. The requested data on CycA expression (Figure 4E-G) and uev1a loss-of-function in human cancer cells (Figure 8 and Figure 8-figure supplement 2) have been added to the revised manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study uncovers a protective role of the ubiquitin-conjugating enzyme variant Uev1A in mitigating cell death caused by over-expressed oncogenic Ras in polyploid Drosophila nurse cells and by RasK12 in diploid human tumor cell lines. The authors previously showed that overexpression of oncogenic Ras induces death in nurse cells, and now they perform a deficiency screen for modifiers. They identified Uev1A as a suppressor of this Ras-induced cell death. Using genetics and biochemistry, the authors found that Uev1A collaborates with the APC/C E3 ubiquitin ligase complex to promote proteasomal degradation of Cyclin A. This function of Uev1A appears to extend to diploid cells, where its human homologs UBE2V1 and UBE2V2 suppress oncogenic Ras-dependent phenotypes in human colorectal cancer cells in vitro and in xenografts in mice.

Strengths:

(1) Most of the data is supported by a sufficient sample size and appropriate statistics.

(2) Good mix of genetics and biochemistry.

(3) Generation of new transgenes and Drosophila alleles that will be beneficial for the community.

We greatly appreciate your comments.

Weaknesses:

(1) Phenotypes are based on artificial overexpression. It is not clear whether these results are relevant to normal physiology.

Downregulation of Uev1A, Ben, and Cdc27 together significantly increased the incidence of dying nurse cells in normal ovaries (Figure 5-figure supplement 2), indicating that the mechanism we uncovered also protects nurse cells from death during normal oogenesis.

(2) The phenotype of "degenerating ovaries" is very broad, and the study is not focused on phenotypes at the cellular level. Furthermore, no information is provided in the Materials and Methods on how degenerating ovaries are scored, despite this being the most important assay in the study.

Thank you for pointing out this issue. We quantified the phenotype of nurse cell death using “degrading/total egg chambers per ovary”, not “degenerating ovaries”. Normal nurse cell nuclei exhibit a large, round morphology in DAPI staining (see the first panel in Figure 1D). During early death, they become disorganized and begin to condense and fragment (see the second panel in Figure 1D). In late-stage death, they are completely fragmented into small, spherical structures (see the third panel in Figure 1D), making cellular-level phenotypic quantification impossible. Since all nurse cells within the same egg chamber are interconnected, their death process is synchronous. Thus, quantifying the phenotype at the egg-chamber level is more practical than at the cellular level. We have added the description of this death phenotype and its quantification to the main text (Lines 104-108).

(3) In Figure 5, the authors want to conclude that uev1a is a tumor-suppressor, and so they over-express ubev1/2 in human cancer cell lines that have RasK12 and find reduced proliferation, colony formation, and xenograft size. However, genes that act as tumor suppressors have loss-of-function phenotypes that allow for increased cell division. The Drosophila uev1a mutant is viable and fertile, suggesting that it is not a tumor suppressor in flies. Additionally, they do not deplete human ubev1/2 from human cancer cell lines and assess whether this increases cell division, colony formation, and xenograph growth.

We apologize for any misleading description. We aimed to demonstrate that UBE2V1/2, like Uev1A in Drosophila “nos>Ras^G12V+bam-RNAi” germline tumors, suppress oncogenic KRAS-driven overgrowth in diploid human cancer cells. Importantly, this function of Uev1A and UBE2V1/2 is dependent on Ras-driven tumors; there is no evidence that they act as broad tumor suppressors in the absence of oncogenic Ras. Drosophila uev1a mutants were lethal, not viable (see Lines 135-137), and germline-specific knockdown of uev1a (nos>uev1a-RNAi) caused female sterility without inducing tumors. These findings suggest that Uev1A lacks tumor-suppressive activity in the Drosophila female germline in the absence of Ras-driven tumors. We have revised the manuscript to prevent misinterpretation. Furthermore, we have added data demonstrating that the combined knockdown of UBE2V1 and UBE2V2 significantly promotes the growth of KRAS-mutant human cancer cells, as suggested (Figure 8 and Figure 8-figure supplement 2).

(4) A critical part of the model does not make sense. CycA is a key part of their model, but they do not show CycA protein expression in WT egg chambers or in their over-expression models (nos.RasV12 or bam>RasV12). Based on Lilly and Spradling 1996, Cyclin A is not expressed in germ cells in region 2-3 of the germarium; whether CycA is expressed in nurse cells in later egg chambers is not shown but is critical to document comprehensively.

We appreciate your critical comment. CycA is a key cyclin that partners with Cdk1 to promote cell division (Edgar and Lehner, 1996). Notably, nurse cells are post-mitotic endocycling cells (Hammond and Laird, 1985) and typically do not express CycA (Lilly and Spradling, 1996) (see the last sentence, page 2518, paragraph 3 in this 1996 paper). However, their death induced by oncogenic Ras^G12V is significantly suppressed by monoallelic deletion of either cycA or cdk1 (Zhang et al., 2024). Conversely, ectopic CycA expression in nurse cells triggers their death (Figure 4C, D). These findings suggest that polyploid nurse cells exhibit high sensitivity to aberrant division-promoting stress, which may represent a distinct form of cellular stress unique to polyploid cells. In the revised manuscript, we have provided the CycA-staining data, comparing its expression in normal nurse cells versus cells undergoing oncogenic Ras^G12V-induced death (Figure 4E-G).

(5) The authors should provide more information about the knowledge base of uev1a and its homologs in the introduction.

Thank you for your suggestion. In the revised introduction, we have provided a more detailed description of Uev1A (Lines 72-79). Additionally, we have introduced its human homologs, UBE2V1 and UBE2V2, in the main text (Lines 143-145).

Reviewer #2 (Public review):

Summary:

The authors performed a genetic screen using deficiency lines and identified Uev1a as a factor that protects nurse cells from RasG12V-induced cell death. According to a previous study from the same lab, this cell death is caused by aberrant mitotic stress due to CycA upregulation (Zhang et al.). This paper further reveals that Uev1a forms a complex with APC/C to promote proteasome-mediated degradation of CycA.

In addition to polyploid nurse cells, the authors also examined the effect of RasG12V-overexpression in diploid germline cells, where RasG12V-overexpression triggers active proliferation, not cell death. Uev1a was found to suppress its overgrowth as well.

Finally, the authors show that the overexpression of the human homologs, UBE2V1 and UBE2V2, suppresses tumor growth in human colorectal cancer xenografts and cell lines. Notably, the expression of these genes correlates with the survival of colorectal cancer patients carrying the Ras mutation.

Strength:

This paper presents a significant finding that UBE2V1/2 may serve as a potential therapy for cancers harboring Ras mutations. The authors propose a fascinating mechanism in which Uev1a forms a complex with APC/C to inhibit aberrant cell cycle progression.

We greatly appreciate your comments.

Weakness:

The quantification of some crucial experiments lacks sufficient clarity.

Thank you for highlighting this issue. We have provided more details regarding the quantification data in the revised manuscript.

References

Edgar, B.A., and Lehner, C.F. (1996). Developmental control of cell cycle regulators: a fly's perspective. Science 274, 1646-1652.

Hammond, M.P., and Laird, C.D. (1985). Chromosome structure and DNA replication in nurse and follicle cells of Drosophila melanogaster. Chromosoma 91, 267-278.

Lilly, M.A., and Spradling, A.C. (1996). The Drosophila endocycle is controlled by Cyclin E and lacks a checkpoint ensuring S-phase completion. Genes Dev 10, 2514-2526.

Zhang, Q., Wang, Y., Bu, Z., Zhang, Y., Zhang, Q., Li, L., Yan, L., Wang, Y., and Zhao, S. (2024). Ras promotes germline stem cell division in Drosophila ovaries. Stem Cell Reports 19, 1205-1216.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The figure legends insufficiently describe the figures. One example is Figure 3, where there are no details in the figure legend about what conditions apply to each panel and each lane of the gels.

For clarity and brevity, detailed experimental conditions are described in the Materials and Methods section. Figure legends therefore focus on summarizing the key findings. Thank you for your understanding!

(2) The font size on the figure is too small.

Thank you for your constructive suggestion. In response, we have enlarged all font sizes to improve readability.

(3) There are places where the authors overstate their results, and there are issues with the clarity of the text:

(3a) Lines 170: "excessive" is not appropriate. Their prior study showed a mild increase in proliferation.

“Excessive” has been removed in the revised manuscript (Lines 215-216).

(3b) Line 187-8: The authors should restate this sentence. Here's a possibility. Over-expression of Uev1a suppressed the phenotypes caused by CycA over-expression.

This sentence has been restated as “Notably, this cell death was suppressed by co-overexpression of CycA and Uev1A, indicating a genetic interaction between them”. (Lines 229-231).

(3c) Lines 266-7: The properties of Uev1a (ie, lacking a conserved Cys) should be in the introduction.

This information has been added to the revised introduction (Lines 74-76).

(3d) Line 318: "markedly" is an overstatement of the prior results.

Our quantification data revealed that “nos>Ras^G12V; bam^-/-” ovaries are three times larger than “nos>GFP; bam^-/-” control ovaries (see Figure 4A-C in Zhang et al., Stem Cell Reports 19, 1205-1216). Given this substantial difference, we think that using "markedly" is not an overstatement.

(4) Data not shown occurs in a few places in the text. Given the ability to supply supplemental information in eLife preprints, these data should be shown.

Thanks for your suggestion. All “not shown” data have been added to the revised manuscript.

Reviewer #2 (Recommendations for the authors):

Major Comments

(1) Cyclin A (CycA) is a key player in this study, but the authors do not provide evidence showing the upregulation of CycA following Ras overexpression in either polyploid or diploid cells. Data on CycA expression should be included.

Thank you for your constructive suggestion. These data have been added to the revised manuscript (Figure 4E-G).

(2) DNA replication stress, cellular senescence, and cell death should be assessed under Ras overexpression (RasOE) and RasOE + Uev1A RNAi conditions to support the model proposed in Figure 4F.

We apologize for any confusion caused by our initial model. We do not have evidence that DNA replication stress and cellular senescence occur under these conditions. Cell death can be readily detected through the presence of fragmented nuclei and condensed DNA (see Figure 1D). The model has been updated accordingly (Figure 9E).

(3) Appropriate controls should be performed alongside the experimental sets. The same nos>Ras+GFPi data set was repeatedly used in Figures 1I, 2B, 2H, and Figures 2, S2B, which is not ideal.

All these experiments were performed under identical conditions. Therefore, we deem it appropriate to use the same control data across these analyses.

(4) Overall, the microscopic images are too small and hard to see.

Thank you for raising this important point. In the revised manuscript, all images and the font size on figures have been enlarged for improved clarity.

(5) Figure 1H

Why is the frequency of egg chamber degradation quite less in nos>RasG12V+GFP-RNAi (about 40%) than nos > RasG12V (about 80%)? And the authors do not show that there is a significant difference between those two conditions, although it should be there. We will need the explanation from the authors on why there is a difference here.

These overexpression experiments were conducted using the GAL4/UAS system. While both “nos>Ras^G12V+GFP-RNAi” and “nos>Ras^G12V” contain a single nos-GAL4 driver, they differ in UAS copy number: the former incorporates two UAS elements compared to only one in the latter (see the detailed genotypes in Source data 2). These results demonstrate that UAS copy number impacts experimental outcomes in our system.

In the previous paper (Zhang et al. (2024), Figure 7H shows that the frequency of egg chambers in nos>RasG12V is 33%, although this paper shows it as about 80%. There seems to be a difference in flies' age (previous paper: 7d, this paper: 3d), but this data raises the question of why nos>RasG12V shows more egg chamber degradation this time.

We greatly appreciate your careful observation. The nurse-cell-death phenotype exhibits a spectrum from mild to severe manifestations [see Figure 1D and our response to weekness (2) in Reviewer #1’s public reviews]. While our 2024 paper exclusively quantified egg chambers with severe phenotypes as degrading, the current study included both mild and severe cases in this classification. We do not think fly age could account for this substantial phenotypic difference. A detailed description of the nurse-cell-death phenotype and its quantification have been added to the revised manuscript (Lines 104-108).

In the following experiments, only nos>RasG12V+GFP-RNAi is used as a control (Figures 2B, H, S2B). I wonder if these results would give us a different conclusion if nos>RasG12V were used as a control.

As explained above, the UAS copy number does matter in our analyses, so it is important to keep them identical for comparison.

(6) In the abstract, the authors mention that uev1a is an intrinsic factor to protect cells from RasG12V-induced cell death. RasG12V does not induce much cell death of cystocytes with bam-gal4, whereas it induces a lot of nurse cells' death. Does it mean the intrinsic expression level of uev1a is low in nurse cells (or polyploid cells) compared to cystocytes (or diploid cells)?

Overexpression of Ras^G12V driven by bam-GAL4 exhibited only minimal nurse cell death (Figure 1D, E). Additionally, Uev1A exhibited low intrinsic expression levels in both cystocytes and nurse cells (Figure 3E and Figure 5-figure supplement 1).

(7) Is uev1a-RNAi alone sufficient to induce egg chamber degradation? Or does it have any effect on ovarian development? (Related to question #1 in minor comments)

While nos>uev1a-RNAi resulted in female sterility, it alone was insufficient to induce egg chamber degradation. However, simultaneous downregulation of Uev1A, Ben, and Cdc27 triggered significant egg chamber degradation (Figure 5-figure supplement 2).

(8) Which stages of egg chambers get degraded with RasG12V induction?

This is a good question. In our analyses, we noted that degrading egg chambers exhibited considerable size variability (Figure 1D). Because degradation disrupts normal morphological cues, precise staging of these egg chambers is nearly impossible.

(9) I suggest testing the cellular senescence marker as well if the authors mention that CycA-degradation by Uev1a-APC/C complex prevents cellular senescence induced by RasG12V in a schematic image of Figure 4 (e.g., Dap/p21, SA-β-gal).

As addressed in our response to your Major Comment (2), we lacked experimental evidence to support cellular senescence in this context. We have therefore revised the model accordingly (Figure 9E). While this study focuses specifically on cell death, investigating potential roles of cellular senescence remains an important direction for future research. Thank you for your suggestion!

Minor Comments

(1) Figure 1D: Df#7584

It seems that the late-stage egg chamber is missing in this condition. Why does this occur without egg chamber degradation? Is there a possibility that we do not see egg chamber degradation because this deficiency line does not have a properly developed egg chamber that can have a degradation?

While this image represents only a single sample, we have confirmed the presence of late-stage egg chambers in other samples. If “Df#7584/+” females were unable to support late-stage egg chamber development, complete sterility would be expected due to the lack of mature eggs. However, as shown in this image (Figure 1D), the ovary contains mature eggs, and the “Df#7584/+” fly strain remains fertile.

(2) Based on the results that DDR signaling functions as keeping egg chambers from degradation, the authors may be better to check the DNA-damage markers in nos>RasG12V, nos>RasG12V +uev1a. (e.g. γ-H2AX)

Thank you for your constructive recommendation. These data have been added to the revised manuscript (Figure 3C).

Author response:

eLife Assessment

Using genome databases, the authors performed solid bioinformatic analyses to trace the genomic history of the clinically relevant Staphylococcus aureus tetracycline resistance plasmid pT181 over the last seven decades. They discovered that this element has transitioned from a multicopy plasmid to a chromosomally integrated element, and the work represents a valuable demonstration of the use of publicly available data to investigate plasmid biology and inform clinical epidemiology. This work will appeal to researchers interested in staphylococcal evolution and plasmid biology.

Thank you, we agree with this overview. We also think this work is interesting to people interested in antimicrobial resistance and bacterial genome structure.

Public Reviews:

Reviewer #1 (Public review):

The study provides a robust bioinformatic characterization of the evolution of pT181. My main criticism of the work is the lack of experimental validation for the hypotheses proposed by the authors.

Comments on the study:

(1) One potential reason for the decline in pT181 copy number over time may be a high cost associated with the multicopy state. In this sense, it would be interesting if the authors could use (or construct) isogenic strains differing only in the state of the plasmid (multicopy/integrated). With this system, the authors could measure the fitness of the strains in the presence and absence of tetracycline, and they could be able to understand the benefit associated with the plasmid transition. The authors discuss these ideas, but it would be nice to test them.

We agree that the relative fitness of integrated versus multicopy plasmids is interesting and a costly multicopy state could explain the transition of independent pT181 replicons to chromosomal integration. This is a project we are exploring for a future study. However, we think that this additional experimental work goes beyond the scope of the paper.

(2) It would be interesting to know the transfer frequencies of the multicopy mobilizable pT181 plasmid, compared to the transfer frequency of the plasmid integrated into the SSCmec element (which can be co-transferred, integrated in conjugative plasmids, or by transduction).

We agree with the reviewer that this is an interesting question. However, we think inferring these rates from natural sequence data is not feasible in this case given the low heterogeneity of the plasmid sequence. A laboratory-based experimental study could not address the real transfers we observe over the course of decades, as in vitro S. aureus transfer rates are often not good proxies for in vivo (McCarthy et al., 2014). In addition, we do not know what is moving the integrated plasmid. pT181 could be moved by a phage or plasmid, so we are uncertain what the correct experiment would be to explore this.

(3) One important limitation of the study that should be mentioned is that inferring pT181 PCN from whole genome data can be problematic. For example, some DNA extraction methods may underestimate the copy number of small plasmids because the small, circular plasmids are preferentially depleted during the process (see, for example, https://www.nature.com/articles/srep28063).

We will investigate this issue further in the revisions. The kits used to extract DNA for the earlier-collected samples may possibly yield more plasmid DNA relative to the chromosome compared to newer ones on average; however, we think this is not driving the decline that we observe in multicopy pT181 copy number. Multiple BioProjects find the same result, where earlier samples have higher copy number compared to later samples. We expect extraction methods to be consistent within a BioProject, suggesting that this decline is genuine and not technical. In revisions, we intend to evaluate the effect of date of sequencing and additional metadata on copy number.

Reviewer #2 (Public review):

Summary:

The authors performed bioinformatic analyses to trace the genomic history of the clinically relevant pT181 plasmid. Specifically, they:

(1) Tracked the presence of pT181 across different S. aureus strain backgrounds through time. It was first found in one, later multiple strains, though this may reflect changes in sampling over time.

(2) Estimated the mutation rate of the chromosome and plasmid.

(3) Estimated the plasmid copy number of pT181, and found that it decreased over time. The latter was supported by two sets of statistical analyses, first showing that the number of single-copy isolates increased over time, and second, that the multicopy isolates demonstrated a lower PCN over time.

(4) Reported the different integration sites at which pT181 integrated into the genome.

As a caveat, they mentioned that identical plasmid sequences have variable plasmid copy numbers across different genomes in their dataset.

Strengths:

This is a very solid, well-considered bioinformatic study on publicly available data. I greatly appreciate the thoughtful approach the authors have taken to their subject matter, neither over- nor underselling their results. It is a strength that the authors focused on a single plasmid in a single bacterial species, as it allowed them to take into account unique knowledge about the biology of this system and really dive deep into the evolution of this specific plasmid. It makes for a compelling case study. At the same time, I think the introduction and discussion can be strengthened to demonstrate what lessons might be drawn from this case study for other plasmids.

Weaknesses:

The finding that the pT181 copy number declined over time is the most interesting claim of the paper to me, and not something that I have seen done before. While the authors have looked at some confounders in this analysis, I think this could be strengthened further in a revision.

In the revisions, we will further explore the impact that technical variation could have in contributing to copy number variation and update our claims for the decline in copy number of the independent replicon over time and variation for the same plasmid sequence accordingly. Multiple BioProjects show earlier samples have higher copy number compared to later samples; we expect extraction methods to be consistent within a BioProject, supporting our initial findings that this decline over time is not due to technical variation.

For the flow of the storyline, I also think the estimation of mutation rates (starting L181) and integration into the chromosome (starting L255) could be moved to the supplement or a later position in the main text.

We will revisit the text organization for flow and clarity of storyline.

Clearly, the use of publicly available data prevents the authors from controlling the growth and sequencing conditions of the isolates. It is striking that they observe a clear signal in spite of this, but I would have loved to see more discussion of the metadata that came with the publicly available sequences and even more use of that metadata to control for confounding.

In revisions, we will further investigate possible contributors to the observed decline in copy number of multicopy pT181 over time. We have incorporated the date of sample collection and BioProject in our analysis, but not the date of sequencing or extraction technique.

References

McCarthy, A. J., Loeffler, A., Witney, A. A., Gould, K. A., Lloyd, D. H., & Lindsay, J. A. (2014). Extensive horizontal gene transfer during Staphylococcus aureus co-colonization in vivo. Genome Biology and Evolution, 6(10), 2697–2708. https://doi.org/10.1093/gbe/evu214

When I think about this passage alongside the rise of artificial intelligence (AI), Cook’s emphasis on context feels even more urgent. Terry Cook argues that records are shaped by the functional and structural environments in which they are created. In an AI-driven world, where systems generate, sort, and analyze massive volumes of data automatically, understanding that broader context becomes essential. AI can process content at scale, but without contextual grounding, it risks misinterpreting records or reinforcing surface-level patterns. I see AI as both an opportunity and a challenge for appraisal theory. On one hand, AI tools can help identify patterns across enormous bureaucratic systems, making macro-level analysis more feasible. They can cluster records, detect trends, and even suggest appraisal priorities. This could strengthen Cook’s top-down approach by giving archivists analytical support in mapping institutional functions. On the other hand, AI systems are trained on existing data, which may already reflect institutional biases and power imbalances. If archivists rely too heavily on AI-driven selection, we risk automating those biases. Cook stresses that archivists must actively and consciously shape the archival record. AI does not remove that responsibility—it arguably heightens it. I cannot simply defer judgment to an algorithm.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Abdelmageed et al. investigate age-related changes in the subcellular localization of DNA polymerase kappa (POLK) in the brains of mice. POLK has been actively investigated for its role in translesion DNA synthesis and involvement in other DNA repair pathways in proliferating cells, very little is known about POLK in a tissue-specific context, let alone in post-mitotic cells. The authors investigated POLK subcellular distribution in the brains of young, middle-aged, and old mice via immunoblotting of fractioned tissue extracts and immunofluorescence (IF). Immunoblotting revealed a progressive decrease in the abundance of nuclear POLK, while cytoplasmic POLK levels concomitantly increased. Similar findings were present when IF was performed on brain sections. Further, IF studies of the cingulate cortex (Cg1), the motor cortex (M1, M2), and the somatosensory (S1) cortical regions all showed an age-related decline in nuclear POLK. Nuclear speckles of POLK decrease in each region, meanwhile, the number of cytoplasmic POLK granules decreases in all four regions, but granule size is increasing. The authors report similar findings for REV1, another Y-family DNA polymerase.

The authors then investigate the colocalization of POLK with other DNA damage response (DDR) proteins in either pyramidal neurons or inhibitory interneurons. At 18 months of age, DNA damage marker gH2AX demonstrated colocalization with nuclear POLK, while strong colocalization of POLK and 8-oxo-dG was present in geriatric mice. The authors find that cytoplasmic POLK granules colocalize with stress granule marker G3BP1, suggesting that the accumulated POLK ends up in the lysosome.

Brain regions were further stained to identify POLK patterns in NeuN+ neurons, GABAergic neurons, and other non-neuronal cell types present in the cortex. Microglia associated with pyramidal neurons or inhibitory interneurons were found to have a higher abundance of cytoplasmic POLK. The authors also report that POLK localization can be regulated by neuronal activity induced by Kainic acid treatment. Lastly, the authors suggest that POLK could serve as an aging clock for brain tissue, but POLK deserves further characterization and correlation to functional changes before being considered as a biomarker.

Strengths:

Investigation of TLS polymerases in specific tissues and in post-mitotic cells is largely understudied. The potential changes in sub-cellular localization of POLK and potentially other TLS polymerases open up many questions about DNA repair and damage tolerance in the brain and how it can change with age.

Weaknesses:

The work is quite novel and interesting, and the authors do suggest some potentially interesting roles for POLK in the brain, but these are in and of themselves a bit speculative. The majority of the findings of this paper draw upon findings from POLK antibody and its presumed specificity for POLK. However, this antibody has not been fully validated and needs further work. Further validation experiments using Polk-deficient or knocked-down cells to investigate antibody specificity for both immunoblotting and immunofluorescence should be performed. More mechanistic investigation is needed before POLK could be considered as a brain aging clock.

We are thankful for the overall enthusiasm and positive comments.

(a) Concern over POLK antibody characterization in mouse:

We performed siRNA and shRNA knock downs in mouse primary cortical neurons as well as efficiently transfectable murine lines like 4T1 and Neuro-2A showing knock down of 99kDa and 120kDa bands recognized by sc-166667 anti-POLK antibody (exact figure number Figure 1 and S1). We show that in IF sc-166667 and A12052 (Figure S1G) shows similar immunostaining patterns and we used sc-166667 in all reported figures and western blots.

(b) More mechanistic investigation is needed before POLK could be considered as a brain aging clock:

We sincerely appreciate the valuable suggestion. We agree as a terminal assay POLK nucleo-cytoplasmic status is not practical for longitudinal studies. However, we believe it may serve an investigative/correlative endogenous signal for determining tissue age, that may be useful to "date" brain sections, since not many such cell biological markers exist. We have added clarification texts to address this.

Reviewer #2 (Public review):

Summary:

Abdelmageed et al., demonstrate POLK expression in nervous tissue and focus mainly on neurons. Here they describe an exciting age-dependent change in POLK subcellular localization, from the nucleus in young tissue to the cytoplasm in old tissue. They argue that the cytosolic POLK is associated with stress granules. They also investigate the cell-type specific expression of POLK, and quantitate expression changes induced by cell-autonomous (activity) and cell nonautonomous (microglia) factors.

I think it is an interesting report but requires a few more experiments to support their findings in the latter half of the paper. Additionally, a more mechanistic understanding of the pathways regulating POLK dynamics between the nucleus and cytosol, what is POLK doing in the cytosol, and what is it interacting with; would greatly increase the impact of this report. However, additional mechanistic experiments are mostly not needed to support much of the currently presented results, again, it would simply increase the impact.

(a) Concern on more mechanistic understanding of the pathways regulating POLK dynamics between the nucleus and cytosol:

We sincerely appreciate the reviewer’s enthusiasm and valuable guidance in helping us better understand the mechanism of nuclear-cytoplasmic POLK dynamics. Previously, we developed a modified aniPOND (accelerated native isolation of proteins on nascent DNA) protocol, which we termed iPoKD-MS (isolation of proteins on Pol kappa synthesized DNA followed by mass spectrometry), to capture proteins bound to nascent DNA synthesized by POLK in human cell lines (bioRxiv https://www.biorxiv.org/content/10.1101/2022.10.27.513845v3). In this dataset, we identified potential candidates that may regulate nuclear/cytoplasmic POLK dynamics. These candidates are currently undergoing validation in human cell lines, and we are preparing a manuscript on these findings. Among these, some candidates, including previously identified proteins such as exportin and importin (Temprine et al., 2020, PMID: 32345725), are being explored further as potential POLK nuclear/cytoplasmic shuttles. We are also conducting tests on these candidates in mouse cortical primary neurons to assess their role in POLK dynamics. In the revised version of the manuscript, we have included a discussion of our current understanding.

(b) Question on “… what is POLK doing in the cytosol, and what is it interacting with …”: Our data so far indicate that POLK accumulates in stress granules and lysosomes. We are very grateful for the reviewer’s insightful suggestions and will make every effort to incorporate them in the revised manuscript. We characterized POLK accumulation in the cytoplasm using six additional endo-lysosomal markers, as recommended by the reviewer. This data is now part of entirely new Figure 3.

Reviewer #3 (Public review):

Summary:

In this study, the authors show that DNA polymerase kappa POLK relocalizes in the cytoplasm as granules with age in mice. The reduction of nuclear POLK in old brains is congruent with an increase in DNA damage markers. The cytoplasmic granules colocalize with stress granules and endo-lysosome. The study proposes that protein localization of POLK could be used to determine the biological age of brain tissue sections.

Strengths:

Very few studies focus on the POLK protein in the peripheral nervous system (PNS). The microscopy approach used here is also very relevant: it allows the authors to highlight a radical change in POLK localization (nuclear versus cytoplasmic) depending on the age of the neurons. 

The conclusions of the study are strong. Several types of neurons are compared, the colocalization with several proteins from the NHEJ and BER repair pathways is tested, and microscopy images are systematically quantified.

Weaknesses:

The authors do not discuss the physical nature of POLK granules. There is a large field of research dedicated to the nature and function of condensates: in particular numerous studies have shown that some condensates but not all exhibit liquid-like properties (https://www.nature.com/articles/nrm.2017.7, https://pubmed.ncbi.nlm.nih.gov/33510441/ https://www.mdpi.com/2073-4425/13/10/1846). The change of physical properties of condensates is particularly important in cells undergoing stress and during aging. The authors should discuss this literature.

We highly appreciate the reviewer bringing up the context of biomolecular condensates. Our iPoKD-MS data referenced above suggests candidates from various biomolecular condensates that we are currently investigating. We appreciate the reviewer providing important literature cited these articles in text and potential biomolecular condensates are discussed in the revised version. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The work is quite novel and interesting, and the authors do suggest some potentially interesting roles for POLK in the brain, but these are in of themselves a bit speculative. The majority of the findings of this paper rely upon the POLK antibody and its specificity for POLK, which is not fully characterized and needs further work (validation of antibodies using immunoblots of Polk KO cells or siRNA KD of POLK in murine cells) to provide confidence in the authors' findings. 

Points

siRNA knockdown of Polk in primary neurons showed a dramatic reduction in signal by IF even though qPCR analysis showed a reduction of only ~35% at the transcript level. Typically many DNA repair genes need to be knocked down by 80% or more to see discernable differences at the protein level. siRNA knockdown in a murine cell line (MEFs, neurons, or some other easily transfectable cell type) needs to be performed with immunoblotting with whole cell and fractionated (nuclear/cytoplasmic) lysates in order to better validate the anti-POLK antibodies and which bands that are visualized during immunoblotting are specific to POLK.

We performed siRNA and shRNA knock downs in mouse primary cortical neurons as well as efficiently transfectable murine lines like 4T1 and Neuro-2A showing knock down of 99kDa and 120kDa bands recognized by sc-166667 anti-POLK antibody (exact figure number Figure 1 and S1). We show that in IF sc-166667 and A12052 (Figure S1G) shows similar immunostaining patterns and we used sc-166667 in all reported figures and western blots.

Figure 1B and C, it is not clear which antibody(ies) are used for the immunoblotting of nuclear and cytoplasmic fractions and for a blot with whole tissue lysates. Please place the antibody vendor or clone next to the corresponding blot or describe it in the figure legend. Bands of varying sizes are present in 1B (and Figure S1) but only a band at 99 kDa was shown in 1C. Because there are no bands of equivalent size present in the nuclear and cytoplasmic fractions in Figure 1B, please describe or denote which bands were used for quantification purposes for nuclear and cytoplasmic POLK.

This has been clarified by using only one antibody throughout the manuscript sc-166667. We observed in whole cell lysate an intense ~99kDa and a faint ~120kDa band, which gets intense in nuclear fraction and is absent in cytoplasmic fraction. We have noted this in multiple human cell lines and hiPSC-derived neurons, which is our ongoing work. We do not know yet if the ~120kDa is a modification or isoform of POLK. We have hints from our proteomics data that it may be SUMOylated or ubiquitinylated or other post translational modifications. We added this in the discussion section.

Figure 1I, is there a quantification beyond just the representative image? There is no green staining pattern outside the cytoplasm in the 1-month-old M1 images that is present in all the other images in the panel.

Fig 1I is now Fig S1G in the revised manuscript. Since REV1 and POLH were not central to the study that focused on POLK, they were meant to be exploratory data panels and as such we did not quantify beyond the qualitative evaluation, which broadly resembled POLK’s disposition with age. We have noted there are some sample to sample variability in the background signal. In general, outside the cytoplasm as subcellularly segmented by fluorescent nissl expression, tends to be variable by brain areas but also higher in older brains

"Association with PRKDC further suggests POLK's role in the "gap-filling" step in the NHEJ repair pathway in neurons." There is no strong evidence in the literature for mammalian POLK playing a role in NHEJ. Some description of a role in HR has been described, however. The reference regarding the iPoKD-MS data set that provides evidence of POLK associating with BER and NHEJ factors is listed as Paul, 2022 but is in the reference list as Shilpi Paul 2022.

We removed this speculative statement and citation fixed.

Figure 4A, what is the age of the mouse for the representative images?

19 months and now mentioned in the figure legend

Figure 4C, Could the data from the different ages be plotted side by side to better evaluate the differences for each cell type/region?

Data is plotted side by side

Why was the one-month time point chosen as this could still represent the developing and not mature murine brain? 

Reviewer correctly noted that a 1 month brain is still developing, but mostly from the behavioral and circuit maturation standpoint. However, from cell division and neurogenesis perspective, that is considered to be complete by first postnatal month, with neuron production thereafter largely restricted to specialized adult niches in the dentate gyrus and subventricular zone–olfactory bulb pathway; these adult neurogenic stem cells are embryonically derived and are regulated in ways that are distinct from the early, expansionary developmental waves of neurogenesis. In our study we performed our measurements in the cortical areas only. (Caviness et al., 1995, PMID: 7482802; Ansorg et al., 2012, PMID: 22564330; Ming & Song, 2011, PMID: 21609825; Bond et al., 2015, PMID: 26431181; Bond et al., 2021, PMID: 33706926; Bartkowska et al., 2022, PMID: 36078144). Also, in Figure 6A it was incorrectly mentioned to be just 1month, we rechecked our metadata and noted that young brains were comprised of 1 and 2 month old brains and now it has been corrected.

Furthermore, can the authors describe which sex of mice was used in these experiments and the justification if a single sex was used? If both sexes were used, were there any dimorphic differences in POLK localization patterns?

This is an important aspect, but in the beginning to keep mice numbers within manageable limits, we were focusing more on the age component. While both males and female brains were assayed but due to uneven sample distribution between sexes, we could not estimate if there were any statistically significant sexual dimorphic differences in IN, PN and NNs. Future studies will investigate the sex component as a function of age.

The suggestion of POLK as a brain aging clock may be a bit premature as the functional and behavioral consequences of cytoplasmic POLK sequestration are not fully known. Furthermore, investigation of POLK levels in other genetic models of neurodegeneration or with gerotherapeutics would be needed to establish if the POLK brain clock is responsive to changes that shift brain aging. Lastly, this clock may be impractical and not useful for longitudinal studies due to the terminal nature of assessing POLK levels.

We agree as a terminal assay POLK nucleo-cytoplasmic status is not practical for longitudinal studies. However, we believe it may serve an investigative/correlative endogenous signal for determining tissue age, that may be useful to "date" brain sections, since not many such cell biological markers exist. We have added clarification text.

Some discussion of the Polk-null mice is warranted, as they only have a slightly shortened lifespan, and any disease phenotypes were not reported. This stands in contrast to other DNA repair-deficient mice that mimic premature aging and show behavioral and motor deficits. This calls into question the role of POLK in brain aging.

Discussion statements on Polk-null mice has been added.

Please correct the catalog number for the SCBT anti-POLK antibody to sc-166667

Typographical error has been corrected

Reviewer #2 (Recommendations for the authors):

Results:

Figure by figure 

(1) A progressive age-associated shift in subcellular localization of POLK The authors state that POLK has not been studied in nervous tissue before and they want to see if it is expressed, and if it changes subcellular location as a function of age. The authors argue age = stress like that seen in previous models using genotoxic agents and cancer cells. Indeed, POLK seems to convincingly change subcellular location from the nucleus to larger cytosolic puncta. 

(2) Nuclear POLK co-localizes with DNA damage response and repair proteins This was a difficult dataset for me to decipher. To me, it appears as though POLK colocalizes with these examined proteins in the CYTOSOL, not the nucleus. Especially, in the oldest mice.

We added in the discussion that DNA repair proteins were observed to be present in the cytoplasm and biomolecular condensates citing relevant reviews and primary references.

(3) POLK in the cytoplasm is associated with stress granules and lysosomes in old brains LAMP1 has some issues as a lysosome marker. The authors even state it can be on endosomes. It would be nice to use a marker for mature lysosomes, some fluorescent reporter that is activated only by lysosomal proteases or pH. It is also of interest if POLK is localized to the membrane or the inside of these structures. The authors have access to an airyscan which is sufficient to examine luminal vs membrane localization on larger organelles like lysosomes.

We thank the reviewer for pushing us to investigate the nature of cytoplasmic POLK in endo-lysosomal compartments. We have now added a full-page figure on the cell biological results from six different markers, subset (Cathepsin B and D) are known to present in the lumens of endo-lysosomes, in Figure 3. Further high-resolution membrane vs lumen was not pursued, which is perhaps better suited in cultured neurons rather than thick fixed tissues.

(4) Differentially altered POLK subcellular expression amongst excitatory, inhibitory, and nonneuronal cells in the cortex.

This seems fine. I don't see anything wrong with the author's statement that there is more POLK in neurons vs non-neuronal cells. 

(5) Microglia associated with IN and PN have significantly higher levels of cytoplasmic POLK I don't see really any convincing evidence of the author's claim here. They find a difference at early-old age, but not at old-old, or other ages. This is explained by "However, this effect is lost in late-old age (Figure 5D), likely due to the MG-mediated removal of the INs.". But no trend being observed, no experiment to show sufficiency, and no experiment to uncover a directional relationship; this is a tough claim to stand by.

Changes made in text to reflect speculative nature of this observation

(6) Subcellular localization of POLK is regulated by neuronal activity

Interesting and fairly difficult experiment. Can the authors talk more about what these values mean? I am confused as to why there is a decline in nuclear puncta at 80 min. Also, why are POLK counts in 6c similar at baseline between young and early-old? In Figures 5 and 6 I also worry about statistical analysis. Are all assumptions checked to use t-tests? Why not always use a test that has fewer assumptions?

We have explained in the text the artificial nature of few hour long acute slice preparations is very different and inherently a stressful environment, especially for the old brains, compared to the vascular perfused PFA fixed brain tissues tested between young and old ages.

We don’t have a proper explanation for the initial dip in nuclear puncta in both young and old brains at 80min of very similar magnitude. It could be a separate biological phenomenon that occurs at much shorter time scales that would not otherwise be captured in a fixed tissue assay and needs careful investigation using live tissue fluorescence imaging that is beyond the scope of this manuscript.

We apologize for the typographical error in the figure legend. We rechecked our R code and the tests were all Wilcoxon rank-sum (Mann–Whitney U) two-sided nonparametric.

Figure 6B & E had absurdly small p values due to large sample numbers. So, we implemented random sampling of 100 cells repeating for 200 times and presented the distribution of p values and Cohen’s d in the supplement and reported the median p value and Cohen’s in the main plot.

(7) POLK as an endogenous "aging clock" for brain tissue

Trainable model. What are the criteria for the model, and how does it work? The cutoffs it uses to classify each age group might be interesting in that the model may have identified a trait the researchers were unaware of. Otherwise, it is not especially useful. Maybe as an independent 'blind' analysis of the data?

We have added a better description of the models, assumptions and how two different unsupervised approaches converge on the same set of features with high AUROCs.

Minor questions:

The cartoons (1a, 2a-b, 5a, 6a) help a lot. However, I still had to work a bit to understand some of the graphs (e.g., 5d, 6b-e, fig 7). Is there a simpler way to present them? Maybe simply additional labelling? I'm not sure.

A more thorough discussion of statistical tests is warranted I think. I am not very clear why some were chosen (t-test vs nonparametric with fewer assumptions). Infinitesimally small p values also make me think maybe incorrect tests were done or no power analysis was performed beforehand. A fix for this is just discussing what went into the testing methods and why they were chosen.

Statistical analysis for Fig2 (using Generalized Estimating Equations), and Fig6 (with random repeated subsampling; method explained in text, figure legend updated and supplementary data on the distribution of p values and cohen’s d are added) to address the very small p values. Descriptions rewritten in relevant text.

In the absence of further mechanistic experiments, it would still be interesting to hear what the authors think is going on and what the significance of this altered subcellular location means. How do the authors think this is occurring? I think they are arguing that cytosolic localization of POLK is 100% detrimental to the neuron. ("The reduction of nuclear POLK in old brains is congruent with an increase in DNA damage markers") Do they have any idea what the 'bug' is in the POLK system then?

Statements in the discussion has been added.

Reviewer #3 (Recommendations for the authors):

POLK is detected as small " as small "speckles" inside the nucleus at a young age (1-2 months) and larger "granules" can be seen in the cytoplasm at progressively older time points (>9 months). In the nucleus, is POLK bound to DNA? In the cytoplasm, how are the POLK molecules organized: are they bound to a substrate or are they just organized as a proteins condensate without DNA?

In human U2OS cell line Dnase1 treatment leads to loss of POLK from the nucleus as well as its activity as reported in Fig5 of Paul, S. et. al. 2023 bioRxiv. While we haven’t reproduced these results in mouse primary neurons, we anticipate a similar situation which will be tested in the future. We have addressed limited aspects of the POLK in the cytoplasm in all new Fig3 with six endo-lysosomal markers, and added text.

When POLK proteins accumulate in the cytoplasm in aging cells, do they also repair condensates in the cytoplasm? What is the function of cytoplasmic POLK granules? More generally, is it known if other granules or foci, such as repair foci are found in the cytoplasms in aging cells, or in cells under stress?

Six markers for endo-lysosomes were tested to characterize the cytoplasmic granules now shown in Fig3.

While the authors quantify the number and sizes of the POLK signal, they don't discuss their physical nature. Some membrane-less condensates exhibit liquid-like properties, such as stress granules, P-bodies, or in the nucleus some repair condensates. In some diseased tissues, some condensates lose their liquid properties and become solid-like. Is it known if POLK condensates behave like liquid condensates or they are simply formed by bound molecules on DNA? Since they are larger and fewer in the cytoplasm, is it because several small puncta fused together to form a larger one? It would be worthwhile to discuss these points.

Discussion statements on the nature of condensates in context of the POLK cytoplasmic signal has been added.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The manuscript titled, "Sleep-Wake Transitions Are Impaired in the AppNL-G-F Mouse Model of Early Onset Alzheimer's Disease", is about a study of sleep/wake phenomena in a knockin mouse strain carrying "three mutations in the human App gene associated with elevated risk for early onset AD". Traditional, in-depth characterization of sleep/wake states, EEG parameters, and response to sleep loss are employed to provide evidence, "supporting the use of this strain as a model to investigate interventions that mitigate AD burden during early disease stages". The sleep/wake findings of earlier studies (especially Maezono et al., 2020, as noted by the authors) were extended by several important, genotype-related observations, including age-related hyperactivity onset that is typically associated with increased arousal, a normal response to loss of sleep and to multiple sleep latency testing, and a stronger AD-like phenotype in females. The authors conclude that the AppNL-G-F mice demonstrate many of the human AD prodromal symptoms and suggest that this strain may serve as a model for prodromal AD in humans, confirming the earlier results and conclusions of Maezono et al. Finally, based on state bout frequency and duration analyses, it is suggested that the AppNL-G-F mice may develop disruptions in mechanism(s) involved in state transition.

Strengths:

The study appears to have been, technically, rigorously conducted with high quality, in-depth traditional assessment of both state and EEG characteristics, with the concordant addition of activity and temperature. The major strengths of this study derive from observations that the AppNL-G-F mice: (1) are more hyperactive in association with decreased transitions between states; (2) maintain a normal response to sleep deprivation and have normal MSLT results; and (3) display a sex specific, "stronger" insomnia-like effect of the knockin in females.

Weaknesses:

The weaknesses stem from the study's impact being limited due to its being largely confirmatory of the Maezono et al. study, with advances of importance to a potentially more focused field. Further, the authors conclude that AppNL-G-F mice have disrupted mechanism(s) responsible for state transition; however, these were not directly examined. The rationale for this conclusion is stated by the authors as based on the observations that bouts of both W and NREM tend to be longer in duration and decreased in frequency in AppNL-G-F mice. Although altered mechanism(s) of state transition (it is not clear what mechanisms are referenced here) cannot be ruled out, other explanations might be considered. For example, increased arousal in association with hyperactivity would be expected to result in increased duration of W bouts during the active phase. This would also predictably result in greater sleep pressure that is typically associated with more consolidated NREM bouts, consistent with the observations of bout duration and frequency.

Reviewer 1 succinctly summarizes the advances of this study beyond the ground-breaking Maezono et al (2020) study of this “humanized” mouse model exhibiting amyloid deposition. Whereas Maezono et al. conducted sleep/wake studies on male App^NL-G-F mice at 6 and 12 months of age, we had the unusual opportunity to study both sexes of homozygous App^NL-G-F mice and WT littermates at 14-18 months of age and to conduct a longitudinal assessment of many of the same individuals at 18-22 months. In addition to baseline sleep/wake and EEG spectral analyses, we (1) measured subcutaneous body temperature and activity to obtain a broader picture of the physiology and behavior of this strain at advanced ages; (2) assessed baseline sleepiness in this strain using the murine version of the clinically-relevant Multiple Sleep Latency Test (MSLT); (3) evaluated the response of App^NL-G-F mice and WT littermates to a perturbation of the sleep homeostat; (4) compared the sleep/wake characteristics of male vs. female App^NL-G-F mice at 18-22 months and, (5) to assess the stability of the phenotypes, analyzed these data over a continuous 14-d recording rather than the conventional 24h recordings typical of most sleep/wake studies including Maezono et al. We found that a long wake/short sleep phenotype was characteristic of homozygous App^NL-G-F mice at these advanced ages which is also evident in the Maezono et al. (2020) study at 12 months of age (but not at 6 months), although the authors do not comment on this phenotype and instead focus on the reduced REM sleep which is particularly evident in female App^NL-G-F mice in our study. Remarkably, despite being awake ~20% longer per day, we find that App^NL-G-F mice are no sleepier than WT mice as determined by the MSLT and that their sleep homeostat is intact when challenged by 6-h sleep deprivation. At both advanced ages, the long wake/short sleep phenotype is due primarily to longer Wake bouts and shorter bouts of both NREM and REM sleep during the dark phase. Moreover, hyperactivity develops in older in App^NL-G-F mice, particularly females, which contributes to this phenotype. We agree with Reviewer 1 that “hyperactivity would be expected to result in increased duration of W bouts during the active phase” and that this could result in more consolidated NREM bouts and we will modify the manuscript to discuss this alternative. However, the suggestion of greater sleep pressure is not borne out by the MSLT studies as we did not observe the shorter sleep latencies and increased sleep during the nap opportunities on the MSLT that we have observed in other mouse strains. Moreover, due to their short sleep phenotype, App^NL-G-F mice would be entering the sleep deprivation study with a greater sleep debt than WT mice, yet we did not observe greater EEG Slow Wave Activity in this strain during recovery from sleep deprivation. Thus, we have suggested that App^NL-G-F mice are unable to transition from Wake to sleep as readily as their WT littermates. Our observations summarized above set the stage for subsequent mechanistic studies in aged App^NL-G-F mice, although realistically, mice of this age and genotype are a rare commodity.

Reviewer #2 (Public review):

Summary:

The authors have used a knock-in mouse model to explore late-in-life amyloid effects on sleep. This is an excellent model as the mutated genes are regulated by the endogenous promoter system. The sleep study techniques and statistical analyses are also first-rate.

The group finds an age-dependent increase in motor activity in advanced age in the NLGF homozygous knock-in mice (NLGF), with a parallel age-dependent increase in body temperature, both effects predominate in the dark period. Interestingly, the sleep patterns do not quite follow the sleep changes. Wake time is increased in NLGF mice, and there is no progression in increased wake over time. NREMS and REM sleep are both reduced, and there is no progression. Sleep-wake effects, however, show a robust light:dark effect with larger effects in the dark period. These findings support distinct effects of this mutation on activity and temperature and on sleep. This is the first description of the temporal pattern of these effects. NLGF mice show wake stability (longer bout durations in the dark period (their active period) and fewer brief arousals from sleep. Sleep homeostasis across the lights-on period is normal. Wake power spectral density is unaffected in NLGF mice at either age. Only REM power spectra are affected, with NLGF mice showing less theta and more delta. There are interesting sex differences, with females showing no gene difference in wake bout number, while males show a gene effect. Similarly, gene effects on NREM bout number seem larger in males than in females. Although there was no difference in homeostatic response, there was normalization of sleep-wake activity after sleep deprivation.

Strengths:

Approach (model extent of sleep phenotyping), analysis.

Weaknesses:

The weaknesses are summarized below and are viewed as "addressable".

(1) The term insomnia. Insomnia is defined as a subjective dissatisfaction with sleep, which cannot be ascertained in a mouse model. The findings across baseline sleep in NLGF mice support increased wake consolidation in the active period. The predominant sleep period (lights on) is largely unaffected, and the active period (lights off) shows increased activity and increased wake with longer bouts. There is a fantastic clue where NLGF effects are consistent with increased hypocretinergic (orexinergic) neuron activity in the dark period, and/or increased drive to hypocretin neurons from PVH.

(2) Sleep-wake transitions are impaired: This should not be termed an impairment. It could actually be beneficial to have greater state stability, especially wake stability in the dark or active period. There is reduced sleep in the model that can be normalized by short-term sleep loss. It is fascinating that recovery sleep normalized sleep in the NLGF in the immediate lights-on and light-off period. This is a key finding.

Reviewer 2 suggests a provocative hypothesis to test. Curiously, although a recent Science paper suggests that hyperexcitable hypocretin/orexin neurons in aging mice results in greater sleep/wake fragmentation, hyperexcitability of this system could result in hyperactivity and longer wake bouts in aged App^NL-G-F mice.

Reviewer #3 (Public review):

Summary:

In this study, Tisdale et al. studied the sleep/wake patterns in the biological mouse model of Alzheimer's disease. The results in this study, together with the established literature on the relationship of sleep and Alzheimer's disease progression, guided the authors to propose this mouse model for the mechanistic understanding of sleep states that translates to Alzheimer's disease patients. However, the manuscript currently suffers from a disconnect between the physiological data and the mechanistic interpretations. Specifically, the claim of "impaired transitions" is logically at odds with the observed increase in wake-state stability or possible hyperactivity. Additionally, the description of the methods, the quantification, and the figure presentation could be substantially improved. I detail some of my concerns below.

Strengths:

The selection of the knock-in model is a notable strength as it avoids the artifacts associated with APP overexpression and more closely mimics human pathology. The study utilizes continuous 14-day EEG recordings, providing a unique dataset for assessing chronic changes in arousal states. The assessment of sex as a biological variable identifies a more severe "insomniac-like" phenotype in females, which aligns with the higher prevalence and severity of Alzheimer's disease in women.

Weaknesses:

The study seems to lack a clear hypothesis-driven approach and relies mostly on explorative investigations. Moreover, lack of quantitative analytical methods as well as shaky logical conclusions, possibly not supported by data in its current form, leaves room for major improvement.

Since this paper studied sleep states, the "Methods" section is quite unclear on what specific criteria were used to classify sleep states. There is no quantitative description of classifying sleep based on clear, reproducible procedures. There are many reasonably well-characterized sleep scoring systems used in rat electrophysiological literature, which could be useful here. The authors are generally expected to describe movement speed and/or EMG and/or EEG (theta/delta/gamma) criteria used to classify these epochs. The subjective (manual) nature of this procedure provides no verifiable validation of the accuracy and interpretability of the results.

One of the bigger claims is that "state transition mechanism(s)" are impaired. However, Figure 7 shows that model mice exhibit significantly more long wake bouts (>260s) and fewer short wake bouts (<60s). Logically, an "impaired switch" (the flip-flop model, Saper et al., 2010) results in state fragmentation. The data here show the opposite: the wake state has become too stable. This suggests the primary defect is not in the transition mechanism itself, but possibly in a pathological increase in arousal drive (hyper-arousal), likely linked to the dark-phase hyperactivity shown in Figures 4 and 5. Also, a point to note is that this finding is not new.

Figure 3 heatmaps lack color bars and units. Spectral power must be quantitatively defined and methods well-explained in the Methods section. Without these, the reader cannot discern if the "reduced power" in females is a global suppression of signal or a frequency-specific shift. Additionally, the representative example used to claim shorter sleep bouts lacks the statistical weight required for a major physiological conclusion. How does a cooler color (not clear what range and what the interpretation is) mean shorter sleep bout in female mice? The authors should clearly mark the frequency ranges that support their claims. In this figure, there is a question mark following the theta/delta range. The authors should avoid speculation and state their claims based on facts. They should also add the theta and delta ranges in the plot, such that readers can draw their own conclusions.

Figure 8 and the MSLT results show that model mice are "no sleepier than WT mice" and have a functional homeostatic rebound. This presents a logical flaw in the "insomnia" narrative. True insomnia in AD patients typically involves a failure of the homeostatic process or a debilitating accumulation of sleep debt. If these mice do not show increased sleepiness (shorter latency) despite ~19% less sleep, the authors might be describing a "reduced need" for sleep or a "hyper-aroused" state, possibly not a clinical insomnia phenotype.

In Figure 9, LFP power shown and compared in percentages is problematic, as LFP power distribution is known to be skewed (follows power law). This is particularly problematic here because all the frequencies above ~20 Hz seem to be totally flattened or nonexistent, which makes this comparison of power severely limited and biased towards the relative frequency in the highly skewed portion of the LFP power spectrum, i.e., very low frequency ranges like delta, theta, and possibly beta. This ignores low, mid, and high gamma as well as ripple band frequencies. NREM sleep is known to have relatively greater ripple band (100-250 Hz) power bursts in hippocampal regions, and REM sleep is known to have synchronous theta-gamma relationships.

We agree with the reviewer that the “Classification of arousal states” section was missing the key description of how we scored the recordings into arousal states based on EEG, EMG and locomotor activity; this was an oversight as the corresponding text exists in all our previous sleep/wake studies published over several decades. Reviewer 1 also points out the alternative interpretation that “the wake state has become too stable.” However, I think we are using different words to say the same thing: that the transition from wake to sleep is impaired whether it is due to hyperarousal or to a defect in the flip/flop switch that results in greater Wake stability. We will revise Fig 3 (Reviewer 2 suggests combining with Fig 14) but note that the X-axis is labelled 0-25 Hz and that this figure was intended to be descriptive -- illustrating how unusual the female App^NL-G-F mice are relative to WT -- rather than a quantitative analysis of spectral power as in Fig. 14. Both Reviewer 2 and 3 suggest that we are using “insomnia” incorrectly, which we have simply used to describe less sleep per 24h period. Reviewer 2 states that “Insomnia is defined as a subjective dissatisfaction with sleep” and Reviewer 3 suggests a narrow definition of insomnia as due only to “a failure of the homeostatic process or a debilitating accumulation of sleep debt.” In a revised manuscript, we will define “insomnia” as an operational term to succinctly mean “less sleep”. Regarding the problem of presenting spectral power in percentages, we completely agree with the reviewer. However, we intentionally presented spectral power density, a measure of relative power, as in Figure 3A and 3B of Maezono et al. (2020). At the risk of making Fig. 9 even more busy, we will revise Fig. 9 to add labels for all Y-axes.

In addition to a revised Fig. 9, in the revised manuscript, we will reformat Tables 1-3, Figs. S1 and S2 for legibility and correct an error in Fig. 7.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study by Wu et al. uses endogenous bruchpilot expression in a cell-type-specific manner to assess synaptic heterogeneity in adult Drosophila melanogaster mushroom body output neurons. The authors performed genomic on locus tagging of the presynaptic scaffold protein bruchpilot (BRP) with one part of splitGFP (GFP11) using the CRISPR/Cas9 methodology and co-expressed the other part of splitGFP (GFP1-10) using the GAL4/UAS system. Upon expression of both parts of splitGFP, fluorescent GFP is assembled at the N-terminus of BRP, exactly where BRP is endogenously expressed in active zones. For manageable analysis, a high-throughput pipeline was developed. This analysis evaluated parameters like location of BRP clusters, volume of clusters, and cluster intensity as a direct measure of the relative amount of BRP expression levels on site, using publicly available 3D analysis tools that are integrated in Fiji. Analysis was conducted for different mushroom body cell types in different mushroom body lobes using various specific GAL4 drivers. To test this new method of synapse assessment, Wu et al. performed an associative learning experiment in which an odor was paired with an aversive stimulus and found that, in a specific time frame after conditioning, the new analysis solidly revealed changes in BRP levels at specific synapses that are associated with aversive learning.

Strengths:

Expression of splitGFP bound to BRP enables intensity analysis of BRP expression levels as exactly one GFP molecule is expressed per BRP. This is a great tool for synapse assessment. This tool can be widely used for any synapse as long as driver lines are available to co-express the other part of splitGFP in a cell-type-specific manner. As neuropils and thus the BRP label can be extremely dense, the analysis pipeline developed here is very useful and important. The authors have chosen an exceptionally dense neuropil - the mushroom bodies - for their analysis and convincingly show that BRP assessment can be achieved with such densely packed active zones. The result that BRP levels change upon associative learning in an experiment with odor presentation paired with punishment is likewise convincing, and strongly suggests that the tool and pipeline developed here can be used in an in vivo context.

Weaknesses:

Although BRP is an important scaffold protein and its expression levels were associated with function and plasticity, I am still somewhat reluctant to accept that synapse structure profiling can be inferred from only assessing BRP expression levels and BRP cluster volume. Also, is it guaranteed that synaptic plasticity is not impaired by the large GFP fluorophore? Could the GFP10 construct that is tagged to BRP in all BRP-expressing cells, independent of GAL4, possibly hamper neuronal function? Is it certain that only active zones are labeled? I do see that plastic changes are made visible in this study after an associative learning experiment with BRP intensity and cluster volume as read-out, but I would be reassured by direct measurement of synaptic plasticity with splitGFP directly connected to BRP, maybe at a different synapse that is more accessible.

We appreciate the reviewer’s comments. In the revised manuscript, we have clarified that Brp is an important, but not the only player in the active zone. We have included new data to demonstrate that split-GFP tagging does not severely affect the localization and plasticity of Brp and the function of synapses by showing: (1) nanoscopic localization of Brp::rGFP using STED imaging; (2) colocalization between Brp::rGFP and anti-Brp signals/VGCCs; (3) activity-dependent Brp remodeling in R8 photoreceptors; (4) no defect in memory performance when labeling Brp::rGFP in KCs; These four lines of additional evidence further corroborate our approach to characterize endogenous Brp as a proxy of active zone structure.

Reviewer #2 (Public review):

Summary:

The authors developed a cell-type specific fluorescence-tagging approach using a CRISPR/Cas9 induced spilt-GFP reconstitution system to visualize endogenous Bruchpilot (BRP) clusters as presynaptic active zones (AZ) in specific cell types of the mushroom body (MB) in the adult Drosophila brain. This AZ profiling approach was implemented in a high-throughput quantification process, allowing for the comparison of synapse profiles within single cells, cell types, MB compartments, and between different individuals. The aim is to analyse in more detail neuronal connectivity and circuits in this centre of associative learning. These are notoriously difficult to investigate due to the density of cells and structures within a cell. The authors detect and characterize cell-type-specific differences in BRP-dependent profiling of presynapses in different compartments of the MB, while intracellular AZ distribution was found to be stereotyped. Next to the descriptive part characterizing various AZ profiles in the MB, the authors apply an associative learning assay and detect consequent AZ re-organisation.

Strengths:

The strength of this study lies in the outstanding resolution of synapse profiling in the extremely dense compartments of the MB. This detailed analysis will be the entry point for many future analyses of synapse diversity in connection with functional specificity to uncover the molecular mechanisms underlying learning and memory formation and neuronal network logics. Therefore, this approach is of high importance for the scientific community and a valuable tool to investigate and correlate AZ architecture and synapse function in the CNS.

Weaknesses:

The results and conclusions presented in this study are, in many aspects, well-supported by the data presented. To further support the key findings of the manuscript, additional controls, comments, and possibly broader functional analysis would be helpful. In particular:

(1) All experiments in the study are based on spilt-GFP lines (BRP:GFP11 and UAS-GFP1-10).The Materials and Methods section does not contain any cloning strategy (gRNA, primer, PCR/sequencing validation, exact position of tag insertion, etc.) and only refers to a bioRxiv publication. It might be helpful to add a Materials and Methods section (at least for the BRP:GFP11 line). Additionally, as this is an on locus insertion the in BRP-ORF, it needs a general validation of this line, including controls (Western Blot and correlative antibody staining against BRP) showing that overall BRP expression is not compromised due to the GFP insertion and localizes as BRP in wild type flies, that flies are viable, have no defects in locomotion and learning and memory formation and MB morphology is not affected compared to wild type animals.

We thank the reviewer for suggesting these important validations. We included details of the design of the construct and insertion site to the Methods section, performed several new experiments to validate the split-GFP tagging of Brp, and present the data in the revision.

First, to examine whether the transcription of the brp gene is unaffected by the insertion of GFP₁₁, we conducted qRT-PCR to compare the brp mRNA levels between brp::GFP₁₁, UAS-GFP1-10 and UAS-GFP1-10 and found no difference (Figure 1 - figure supplement 1A).

To further verify the effect of GFP₁₁ tagging at the protein level, we performed anti-Brp (nc82) immunohistochemistry of brains where GFP is reconstituted pan-neuronally. We found unaltered neuropile localization of nc82 signals (Figure 1 - figure supplement 1C). In presynaptic terminals of the mushroom body calyx, we found integration of Brp::rGFP to nc82 accumulation (Figure 1D). We performed super-resolution microscopy to verify the configuration of Brp::rGFP and confirmed the donut-shape arrangement of Brp::rGFP in the terminals of motor neurons (see Wu, Eno et al., 2025 PLOS Biology), corroborating the nanoscopic assembly of Brp::rGFP at active zones (Kittel et al., 2006 Science).

Furthermore, co-expression of RFP-tagged voltage-gated calcium channel alpha subunit Cacophony (Cac) and Brp::rGFP in PAM-γ5 dopaminergic neurons revealed strong presynaptic colocalization of their punctate clusters (Figure 1E), suggesting that rGFP tagging of Brp did not damage key protein assembly at active zones (Kawasaki et al., 2004 J Neuroscience; Kittel et al., Science).

These lines of evidence suggest that the localization of endogenous Brp is barely affected by the C-terminal GFP₁₁ insertion or GFP reconstitution therewith. This is in line with a large body of studies confirming that the N-terminal region and coiled-coil domains, but not the C-terminal, region of Brp are necessary and sufficient for active zone localization (Fouquet et al., 2009 J Cell Biol; Oswald et al., 2010 J Cell Biol; Mosca and Luo, 2014 eLife; Kiragasi et al., 2017 Cell Rep; Akbergenova et al., 2018 eLife; Nieratschker et al., 2009 PLoS Genet; Johnson et al., 2009 PLoS Biol; Hallermann et al., 2010 J Neurosci). We nevertheless report homozygous lethality and found the decreased immunoreactive signals in flies carrying the GFP₁₁ insertion (Figure 1 - figure supplement 1B).

For these reasons, we always use heterozygotes for all the experiments therefore there is no conspicuous defect in locomotion as reported in the original study (Wagh et al., 2005 Neuron). To functionally validate the heterozygotes, we measured the aversive olfactory memory performance of flies where GFP reconstitution was induced in Kenyon cells using R13F02-GAL4. We found that all these transgenes did not alter mushroom body morphology (Figure 7 - figure supplement 1) or memory performance as compared to wild-type flies (Figure 7 - figure supplement 2), suggesting the synapse function required for short-term memory formation is not affected by split-GFP tagging of Brp.

(2) Several aspects of image acquisition and high-throughput quantification data analysis would benefit from a more detailed clarification.

(a) For BRP cluster segmentation it is stated in the Materials and Methods state, that intensity threshold and noise tolerance were "set" - this setting has a large effect on the quantification, and it should be specified and setting criteria named and justified (if set manually (how and why) or automatically (to what)). Additionally, if Pyhton was used for "Nearest Neigbor" analysis, the code should be made available within this manuscript; otherwise, it is difficult to judge the quality of this quantification step.

(b) To better evaluate the quality of both the imaging analysis and image presentation, it would be important to state, if presented and analysed images are deconvolved and if so, at least one proof of principle example of a comparison of original and deconvoluted file should be shown and quantified to show the impact of deconvolution on the output quality as this is central to this study.

We thank the reviewer for suggesting these clarifications. We have included more description to the revised manuscript to clarify the setting of segmentation, which was manually adjusted to optimize the F-score (previous Figure 1D, now moved to Figure 1 -figure supplement 5). We have included the code used for analyzing nearest neighbor distance, AZ density and local Brp density in the revised manuscript (Supplementary file 1), together with a pre-processed sample data sheet (Supplementary file 2).

Regarding image deconvolution, we have clarified the differential use of deconvolved and not-deconvolved images in the revised manuscript. We have also included a quantitative evaluation of Richardson-Lucy iterative deconvolution (Figure 1 - figure supplement 4). We used 20 iterations due to only marginal FWHM improvement beyond this point (Figure 1 - figure supplement 4).

(3) The major part of this study focuses on the description and comparison of the divergent synapse parameters across cell-types in MB compartments, which is highly relevant and interesting. Yet it would be very interesting to connect this new method with functional aspects of the heterogeneous synapses. This is done in Figure 7 with an associative learning approach, which is, in part, not trivial to follow for the reader and would profit from a more comprehensive analysis.

(a) It would be important for the understanding and validation of the learning induced changes, if not (only) a ratio (of AZ density/local intensity) would be presented, but both values on their own, especially to allow a comparison to the quoted, previous AZ remodelling analysis quantifying BRP intensities (ref. 17, 18). It should be elucidated in more detail why only the ratio was presented here.

We thank the reviewer for the suggestion on the presentation of learning-induced Brp remodeling. The reported values in Figure 7C are the correlation coefficient of AZ density and local intensity in each compartment, but not the ratio. These results suggest that subcompartment-sized clusters of AZs with high Brp accumulation (Figure 6) undergo local structural remodeling upon associative learning (Figure 7). For clarity, we have included a schematic of this correlation and an example scatter plot to Figure 6. Unlike the previous studies (refs 17 and 18), we did not observe robust learning-dependent changes in the Brp intensity, possibly due to some confounding factors such as overall expression levels and conditioning protocols as described in the previous and following points, respectively.

(b) The reason why a single instead of a dual odour conditioning was performed could be clarified and discussed (would that have the same effects?).

(c) Additionally, "controls" for the unpaired values - that is, in flies receiving neither shock nor odour - it would help to evaluate the unpaired control values in the different MB compartments.

We use single odor conditioning because it is the simplest way to examine the effect of odor-shock association by comparing the paired and unpaired group. Standard differential conditioning with two odors contains unpaired odor presentation (CS-) even in the ‘paired’ group. We now show that single-odor conditioning induces memory that lasts one day as in differential conditioning (Figure 7B; Tully and Quinn, J Comp Phys A 1985).

(d) The temporal resolution of the effect is very interesting (Figure 7D), and at more time points, especially between 90 and 270 min, this might raise interesting results.

The sampling time points after training was chosen based on approximately logarithmic intervals, as the memory decay is roughly exponential (Figure 7B). This transient remodeling is consistent with the previous studies reporting that the Brp plasticity was short-lived (Zhang et al., 2018 Neuron; Turrel et al., 2022 Current Biol).

(e) Additionally, it would be very interesting and rewarding to have at least one additional assay, relating structure and function, e.g. on a molecular level by a correlative analysis of BRP and synaptic vesicles (by staining or co-expression of SV-protein markers) or calcium activity imaging or on a functional level by additional learning assays.

We thank the reviewer for raising this important point. We have performed calcium imaging of KC presynaptic terminals to correlate the structure and function in another study (see Figure 2 in Wu, Eno et al., 2025 PLOS Biology for more detail). The basal presynaptic calcium pattern along the γ compartments is strikingly similar to the compartmental heterogeneity of Brp accumulation (see also Figure 2 in this study). Considering colocalization of other active-zone components, such as Cac (Figure 1E), we propose that the learning-induced remodeling of local Brp clusters should transiently modulate synaptic properties.

As a response to other reviewers’ interest, we used Brp::rGFP to measure different forms of Brp-based structural plasticity upon constant light exposure in the photoreceptors and upon silencing rab3 in KCs. Since these experiments nicely reproduced the results of previous studies (Sugie et al., Neuron 2013; Graf et al., Neuron 2009), we believe the learning-induced plasticity of Brp clustering in KCs has a transient nature.

Reviewer #3 (Public review):

Summary:

The authors develop a tool for marking presynaptic active zones in Drosophila brains, dependent on the GAL4 construct used to express a fragment of GFP, which will incorporate with a genome-engineered partial GFP attached to the active zone protein bruchpilot - signal will be specific to the GAL4-expressing neuronal compartment. They then use various GAL4s to examine innervation onto the mushroom bodies to dissect compartment-specific differences in the size and intensity of active zones. After a description of these differences, they induce learning in flies with classic odour/electric shock pairing and observe changes after conditioning that are specific to the paired conditioning/learning paradigm.

Strengths:

The imaging and analysis appear strong. The tool is novel and exciting.

Weaknesses:

I feel that the tool could do with a little more characterisation. It is assumed that the puncta observed are AZs with no further definition or characterisation.

We performed additional validation on the tool, including (1) nanoscopic localization of Brp::rGFP using STED imaging; (2) colocalization between Brp::rGFP and anti-Brp signals/VGCCs (Figure 1D-E); 3) activity-dependent active zone remodeling in R8 photoreceptors (Figure 1F). These will be detailed in our point-by-point response below.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The authors keep stating, they profile or assess synaptic structure by analyzing BRP localization, cluster volume, and intensity. However, I do not think that BRP cluster volume and intensity warrant an educated statement about presynaptic structure as a whole. I do not challenge the usefulness of BRP cluster analysis for synapse evaluation, but as there are so many more players involved in synaptic function, BRP analysis certainly cannot explain it all. This should at least be discussed.

It is correct that Brp is not the only player in the active zone. We have included more discussion on the specific role of Brp (line 84 to 89) and other synaptic markers (line 250) and edited potentially misunderstanding text.

(2) I do see that changes in BRP expression were observed following associative learning, but is it certain, that synaptic plasticity is generally unaffected by the large GFP fluorophore? BRP is grabbing onto other proteins, both with its C- and N-termini. As the GFP is right before the stop codon, it should be at the N-terminus. How far could BRP function be hampered by this? Is there still enough space for other proteins to interact?

We thank the reviewer for sharing the concerns. We here provided three lines of evidence to demonstrate that the Brp assembly at active zones required for synaptic plasticity is unaffected by split-GFP tagging.

First, we assessed olfactory memory of flies that have Brp::rGFP labeled in Kenyon cells and found the performance comparable to wild-type (Figure 7 - figure supplement 2), suggesting the Brp function required for olfactory memory (Knapek et al., J Neurosci 2011) is unaffected by split-GFP tagging.

Second, we measured Brp remodeling in photoreceptors induced by constant light exposure (LL; Sugie et al., 2015 Neuron). Consistent with the previous study, we found that LL decreased the numbers of Brp::rGFP clusters in R8 terminals in the medulla, as compared to constant dark condition (DD). This result validates the synaptic plasticity involving dynamic Brp rearrangement in the photoreceptors. We have included this result into the revised manuscript (Figure 1F).

To further validate protein interaction of Brp::rGFP, we focused on Rab3, as it was previously shown to control Brp allocation at active zones (Graf et al., 2009 Neuron). To this end, we silenced rab3 expression in Kenyon cells using RNAi and measured the intensity of Brp::rGFP clusters in γ Kenyon cells. As previously reported in the neuromuscular junction, we found that rab3 knock-down increased Brp::rGFP accumulation to the active zones, suggesting that Brp::rGFP represents the interaction with Rab3. We have included all the new data to the revised manuscript (Figure 1 - figure supplement 3).

(3) It may well be that not only active-zone-associated BRP is labeled but possibly also BRP molecules elsewhere in the neuron. I would like to see more validation, e.g., the percentage of tagged endogenous BRP associated with other presynaptic proteins.

To answer to what extent Brp::rGFP clusters represent active zones, we double-labelled Brp::rGFP and Cac::tdTomato (Cacophony, the alpha subunit of the voltage-gated calcium channels). We found that 97% of Brp::rGFP clusters showed co-localization with Cac::tdTomato in PAM-γ5 dopamine neurons terminals (Figure 1E), suggesting most Brp::rGFP clusters represent functional AZs.

(4) Z-size is ~200 nm, while x/y pixel size is ~75 nm during acquisition. How far down does the resolution go after deconvolution?

The Z-step was 370 nm and XY pixel size was 79 nm for image acquisition. We performed 20 iterations of Richarson-Lucy deconvolution using an empirical point spread function (PSF). We found that the effect of deconvolution on the full-width at half maximum (FWHM) of Brp::rGFP clusters improves only marginally beyond 20 iterations, when the XY FWHM is around 200 nm and the XZ FWHM is around 450 nm (Figure 1 - figure supplement 4).

(5) Figure Legend 7: What is a "cytoplasm membrane marker"? Does this mean membrane-bound tdTom is sticking into the cytoplasm?

We apologize for the typo and have corrected it to “plasma membrane marker”.

(6) At the end of the introduction: "characterizing multiple structural parameters..." - which were these parameters? I was under the assumption that BRP localization, cluster volume, and intensity were assessed. I do not see how these are structural parameters. Please define what exactly is meant by "structural parameters".

We apologize for the confusion. By "structural parameters”, we indeed referred to the volume, intensity and molecular density of Brp::rGFP clusters. We have revised the sentence to “Characterizing the distinct parameters and localization of Brp::rGFP cluster.”

(7) Next to last sentence of the introduction: "Characterizing multiple structural parameters revealed a significant synaptic heterogeneity within single neurons and AZ distribution stereotypy across individuals." What do the authors mean by "significant synaptic heterogeneity"?

By “synaptic heterogeneity”, we refer to the intracellular variability of active zone cytomatrices reported by Brp clusters. For instance, the intensities of Brp::rGFP clusters within Kenyon cell subtypes were variable among compartments (Figure 2). Intracellular variability of the Brp concentration of individual active zones was higher in DPM and APL neurons than Kenyon cells (Figure 3). These variabilities demonstrate intracellular synaptic heterogeneity. We have revised the sentence to be more specific to the different characters of Brp clusters.

(8) I do not understand the last sentence of the introduction. "These cell-type-specific synapse profiles suggest that AZs are organized at multiple scales, ranging from neighboring synapses to across individuals." What do the authors mean by "ranging from neighboring synapses to across individuals"? Does this mean that even neighboring synapses in the same cell can be different?

We have revised the sentence to “These cell-type-specific synapse profiles suggest that AZs are spatially organized at multiple scales, ranging from interindividual stereotypy to neighboring synapses in the same cells.”

By “neighboring synapses", we refer to the nearest neighbor similarity in Brp levels in some cell-types (Figure 6A-C), and also the sub-compartmental dense AZ clusters with high Brp level in Kenyon cells (Figure 6D-H). By “across individuals”, we refer to the individually conserved active zone distribution patterns in some neurons (Figure 5).

(9) The title talks about cell-type-specific spatial configurations. I do not understand what is meant by "spatial configurations"? Do you mean BRP cluster volume? I think the title is a little misleading.

By “spatial configuration”, we refer to the arrangement of Brp clusters within individual mushroom body neurons. This statement is based on our findings on the intracellular synaptic heterogeneity (see also response to comment #7). We have streamlined the text description in the revised manuscript for clarity.

Reviewer #2 (Recommendations for the authors):

(1) For Figure 3A: exemplary two AZs are compared here, a histogram comparing more AZs would aid in making the point that in general, AZ of similar size have different BRP level (intensities) and how much variation exists.

We have included histograms for Brp::rGFP intensity and cluster volumes to Figure 3 in the revised manuscript.

(2) Line 52: "endogenous synapses" is a confusing term; it's probably meant that the protein levels within the synapse are endogenous and not overexpressed. 

We apologize for the confusion and have revised the term to “endogenous synaptic proteins.”

(3) It is not clear from the Materials and Methods section, whether and where deconvolved or not-deconvolved images were used for the quantification pipeline. Please comment on this. 

We have now revised the Method section to clarify how deconvolved or not-deconvolved images were differently used in the pipeline.

(4) Line 664 (C) not bold.

We have corrected the error.

(5) 725 "Files" should be Flies.

We have corrected the error.

(6) 727 two times "first".

We have corrected the error.

(7) Figure 7. All (A) etc., not bold - there should be consistent annotation. 

We want to thank the reviewer for the detailed proof and have corrected all the errors spotted.

Reviewer #3 (Recommendations for the authors):

(1) Has there been an expression of the construct in a non-neuronal cell? Astrocyte-like cell? Any glia? As some sort of control for background and activity?

As the reviewer suggested, we verified the neuronal expression specificity of Brp::rGFP. Using R86E01-GAL4 and Amon-GAL4, we compared Brp::rGFP in astrocyte-like glia and neuropeptide-releasing neurons. We found no Brp::rGFP puncta in the neuropils in astrocyte-like glia compared to neurons, suggesting Brp::rGFP is specific to neurons. We have included this new dataset to the revised manuscript (Figure 1 - figure supplement 2).

(2) Similarly, expression of the construct co-expressed with a channelrhodopsin, and induction of a 'learning'-like regime of activity, similarly in a control type of experiment, expression of an inwardly rectifying channel (e.g. Kir2.1) to show that increases in size of the BRP puncta are truly activity dependent? The NMJ may be an optimal neuron to use to see the 'donut' structures of the AZs and their increase with activity. Also, are these truly AZs we are seeing here? Perhaps try co-expressing cacophony-dsRed? If the GFP Puncta are active zones, then they should be surrounded by cacophony.

We would like to clarify that we did not find Brp::rGFP size increase upon learning. Instead, we demonstrated that associative training transiently remodelled sub-compartment-sized AZ “hot spots” in Kenyon cells, indicated by the correlation of local intensity and AZ density (Figure 6-7).

To demonstrate split-GFP tagging does not affect activity-dependent plasticity associated with Brp, we measured Brp remodeling in photoreceptors induced by constant light exposure (LL; Sugie et al., 2015 Neuron). Consistent with the previous study, we found that LL decreased the numbers of Brp::rGFP clusters in R8 terminals in the medulla, as compared to constant dark condition (DD). This result validates the synaptic plasticity involving dynamic Brp rearrangement in the photoreceptors (Figure 1F).

As the reviewer suggested, we performed the STED microscopy for the larval motor neuron and confirmed the donut-shape arrangement of Brp::rGFP (Wu, Eno et al., PLOS Biol 2025).

Also following the reviewer’s suggestion, we double-labelled Brp::rGFP and Cac::tdTomato (Cacophony, the alpha subunit of the voltage-gated calcium channels). We found that 97% Brp::rGFP clusters showed co-localization with Cac::tdTomato in PAM-γ5 dopamine neurons terminals (Figure 1E), suggesting most Brp::rGFP clusters represent functional AZs.

(3) In the introduction: Intro, a sentence about BRP - central organiser of the active zone, so a key regulator of activity.

We have included a few more sentences about the role Brp in the active zones to the revised manuscript.

(4) Figure 1 E, line 650 'cite the resource here'. 

We thank the reviewer for pointing out the error and we have corrected it.

(5) Many readers may not be MB aficionados, and to make the data more accessible, perhaps use a cartoon of an MB with the cell bodies of the neurons around the MB expressing the constructs highlighted so that the reader can have a wider idea of the anatomy in relation to the MB.

We appreciate these comments and have appended cartoons of the MB to figures to help readers understand the anatomy.

Reviewer #1 (Public review):

Summary:

This study focuses on characterizing the EEG correlates of item-specific proportion congruency effects. Two types of learned associations are characterized, one being associations between stimulus features and control states (SC), and the other being stimulus features and responses (SR). Decoding methods are used to identify time-resolved SC and SR correlates, which are used to test properties of their dynamics.

The conclusion is reached that SC and SR associations can independently and simultaneously guide behavior. This conclusion is based on results showing SC and SR correlates are: (1) not entirely overlapping in cross-decoding; (2) simultaneously observed on average over trials in overlapping time bins; (3) independently correlate with RT; and (4) have a positive within-trial correlation.

Strengths:

Fearless, creative use of EEG decoding to test tricky hypotheses regarding latent associations.

Nice idea to orthogonalize ISPC condition (MC/MI) from stimulus features.

Weaknesses:

I still have my concern from the first round that the decoders are overfit to temporally structured noise. As I wrote before, the SC and SR classes are highly confounded with phase (chunk of session). I do not see how the control analyses conducted in the revision adequately deal with this issue.

In the figures, there are several hints that these decoders are biased. Unfortunately, the figures are also constructed in such a way that hides or diminishes the salience of the clues of bias. This bias and lack of transparency discourage trust in the methods and results.

I have two main suggestions:

(1) Run a new experiment with a design that properly supports this question.

I don't make this suggestion lightly, and I understand that it may not be feasible to implement given constraints; but I feel that this suggestion is warranted. The desired inferences rely on successful identification of SC and SR representations. Solidly identifying SC and SR representations necessitates an experimental design wherein these variables are sufficiently orthogonalized, within-subject, from temporally structured noise. The experimental design reported in this paper unfortunately does not meet this bar, in my opinion (and the opinion of a colleague I solicited).

An adequate design would have enough phases to properly support "cross-phase" cross-validation. Deconfounding temporal noise is a basic requirement for decoding analyses of EEG and fMRI data (see e.g., leave-one-run-out CV that is effectively necessary in fMRI; in my experience, EEG is not much different, when the decoded classes are blocked in time, as here). In a journal with a typical acceptance-based review process, this would be grounds for rejection.

Please note that this issue of decoder bias would seem to weaken the rest of the downstream analyses that are based on the decoded values. For instance, if the decoders are biased, in the within-trial correlation analysis, how can we be sure that co-fluctuations along certain dimensions within their projected values are driven by signal or noise? A similar issue clouds the LMM decoding-RT correlations.

(2) Increase transparency in the reporting of results throughout main text.

Please do not truncate stimulus-aligned timecourses at time=0. Displaying the baseline period is very useful to identify bias, that is, to verify that stimulus-dependent conditions cannot be decoded pre-stimulus. Bias is most expected to be revealed in the baseline interval when the data are NOT baseline-corrected, which is why I previously asked to see the results omitting baseline correction. (But also note that if the decoders are biased, baseline-correcting would not remove this bias; instead, it would spread it across the rest of the epoch, while the baseline interval would, on average, be centered at zero.)

Please use a more standard p-value correction threshold, rather than Bonferroni-corrected p<0.001. This threshold is unusually conservative for this type of study. And yet, despite this conservativeness, stimulus-evoked information can be decoded from nearly every time bin, including at t=0. This does not encourage trust in the accuracy of these p-values. Instead, I suggest using permutation-based cluster correction, with corrected p<0.05. This is much more standard and would therefore allow for better comparison to many other studies.

I don't think these things should be done as control analyses, tucked away in the supplemental materials, but instead should be done as a part of the figures in the main text -- including decoding, RSA, cross-trial correlations, and RT correlations.

Other issues:

Regarding the analysis of the within-trial correlation of RSA betas, and "Cai 2019" bias:

The correction that authors perform in the revision -- estimating the correlation within the baseline time interval and subtracting this estimate from subsequent timepoints -- assumes that the "Cai 2019" bias is stationary. This is a fairly strong assumption, however, as this bias depends not only on the design matrix, but also on the structure of the noise (see the Cai paper), which can be non-stationary. No data were provided in support of stationarity. It seems safer and potentially more realistic to assume non-stationarity.

This analysis was included in the supplemental material. However, given that the correlation analysis presented in the Results is subject to the "Cai 2019" bias, it would seem to be more appropriate to replace that analysis, rather than supplement it.

Regardless, this seems to be a moot issue, given that the underlying decoders seem to be overfit to temporally structured noise (see point above regarding weakening of downstream analyses based on decoder bias).

Outliers and t-values:

More outliers with beta coefficients could be because the original SD estimates from the t-values are influenced more by extreme values. When you use a threshold on the median absolute deviation instead of mean +/-SD, do you still get more outliers with beta coefficients vs t-values?

Random slopes:

Were random slopes (by subject) for all within-subject variables included in the LMMs? If not, please include them, and report this in the Methods.

Author response:

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

eLife Assessment

This useful study uses creative scalp EEG decoding methods to attempt to demonstrate that two forms of learned associations in a Stroop task are dissociable, despite sharing similar temporal dynamics. However, the evidence supporting the conclusions is incomplete due to concerns with the experimental design and methodology. This paper would be of interest to researchers studying cognitive control and adaptive behavior, if the concerns raised in the reviews can be addressed satisfactorily.

We thank the editors and the reviewers for their positive assessment of our work and for providing us with an opportunity to strengthen this manuscript. Please see below our responses to each comment raised in the reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study focuses on characterizing the EEG correlates of item-specific proportion congruency effects. In particular, two types of learned associations are characterized. One being associations between stimulus features and control states (SC), and the other being stimulus features and responses (SR). Decoding methods are used to identify SC and SR correlates and to determine whether they have similar topographies and dynamics.

The results suggest SC and SR associations are simultaneously coactivated and have shared topographies, with the inference being that these associations may share a common generator.

Strengths:

Fearless, creative use of EEG decoding to test tricky hypotheses regarding latent associations. Nice idea to orthogonalize the ISPC condition (MC/MI) from stimulus features.

Thank you for acknowledging the strength in EEG decoding and design. We have addressed all your concerns raised below point by point.

Weaknesses:

(1a) I'm relatively concerned that these results may be spurious. I hope to be proven wrong, but I would suggest taking another look at a few things.

While a nice idea in principle, the ISPC manipulation seems to be quite confounded with the trial number. E.g., color-red is MI only during phase 2, and is MC primarily only during Phase 3 (since phase 1 is so sparsely represented). In my experience, EEG noise is highly structured across a session and easily exploited by decoders. Plus, behavior seems quite different between Phase 2 and Phase 3. So, it seems likely that the classes you are asking the decoder to separate are highly confounded with temporally structured noise.

I suggest thinking of how to handle this concern in a rigorous way. A compelling way to address this would be to perform "cross-phase" decoding, however I am not sure if that is possible given the design.

Thank you for raising this important issue. To test whether decoding might be confounded by temporally structured noise, we performed a control decoding analysis. As the reviewer correctly pointed out, cross-phase decoding is not possible due to the experimental design. Alternatively, to maximize temporal separation between the training and test data, we divided the EEG data in phase 2 and phase 1&3 into the first and second half chronologically. Phase 1 and 3 were combined because they share the same MC and MI assignments. We then trained the decoders on one half and tested them on the other half. Finally, we averaged the decoding results across all possible assignments of training and test data. The similar patterns (Supplementary Fig.1) observed confirmed that the decoding results are unlikely to be driven by temporally structured noise in the EEG data. The clarification has been added to page 13 of the revised manuscript.

(1b) The time courses also seem concerning. What are we to make of the SR and SC timecourses, which have aggregate decoding dynamics that look to be <1Hz?

As detailed in the response to your next comment, some new results using data without baseline correction show a narrower time window of above-chance decoding. We speculate that the remaining results of long-lasting above-chance decoding could be attributed to trials with slow responses (some responses were made near the response deadline of 1500 ms). Additionally, as shown in Figure 6a, the long-lasting above-chance decoding seems to be driven by color and congruency representations. Thus, it is also possible that the binding of color and congruency contributes to decoding. This interpretation has been added to page 17 of the revised manuscript.

(1c) Some sanity checks would be one place to start. Time courses were baselined, but this is often not necessary with decoding; it can cause bias (10.1016/j.jneumeth.2021.109080), and can mask deeper issues. What do things look like when not baselined? Can variables be decoded when they should not be decoded? What does cross-temporal decoding look like - everything stable across all times, etc.?

As the reviewer mentioned, baseline-corrected data may introduce bias to the decoding results. Thus, we cited the van Driel et al (2021) paper in the revised manuscript to justify the use of EEG data without baseline-correction in decoding analysis (Page 27 of the revised manuscript), and re-ran all decoding analysis accordingly. The new results revealed largely similar results (Fig. 2, 4, 6 and 8 in the revised manuscript) with the following exceptions: narrower time window for separatable SC subspace and SR subspace (Fig. 4b), narrower time window for concurrent representations of SC and SR (Fig. 6a-b), and wider time window for the correlations of SC/SR representations with RTs (Fig. 8).

(2) The nature of the shared features between SR and SC subspaces is unclear.

The simulation is framed in terms of the amount of overlap, revealing the number of shared dimensions between subspaces. In reality, it seems like it's closer to 'proportion of volume shared', i.e., a small number of dominant dimensions could drive a large degree of alignment between subspaces.

What features drive the similarity? What features drive the distinctions between SR and SC? Aside from the temporal confounds I mentioned above, is it possible that some low-dimensional feature, like EEG congruency effect (e.g., low-D ERPs associated with conflict), or RT dynamics, drives discriminability among these classes? It seems plausible to me - all one would need is non-homogeneity in the size of the congruency effect across different items (subject-level idiosyncracies could contribute: 10.1016/j.neuroimage.2013.03.039).

Thank you for this question. To test what dimensions are shared between SC and SR subspaces, we first identify which factors can be shared across SC and SR subspaces. For SC, the eight conditions are the four colors × ISPC. Thus, the possible shared dimensions are color and ISPC. Additionally, because the four colors and words are divided into two groups (e.g., red-blue and green-yellow, counterbalanced across subjects, see Methods), the group is a third potential shared dimension. Similarly, for SR decoders, potential shared dimensions are word, ISPC and group. Note that each class in SC and SR decoders has both congruent and incongruent trials. Thus, congruency is not decodable from SC/SR decoders and hence unlikely to be a shared dimension in our analysis. To test the effect of sharing for each of the potential dimensions, we performed RSA on decoding results of the SC decoder trained on SR subspace (SR | SC) (Supplementary Fig. 4a) and the SR decoder trained on SC subspace (SC | SR) (Supplementary Fig. 4b), where the decoders indicated the decoding accuracy of shared SC and SR representations. In the SC classes of SR | SC, word red and blue were mixed within the same class, same were word yellow and green. The similarity matrix for “Group” of SR | SC (Supplementary Fig. 4a) shows the comparison between two word groups (red & blue vs. yellow & green). The similarity matrix for “Group” of SC | SR (Supplementary Fig. 4b) shows the comparison between two color groups (red & blue vs. yellow & green).

The RSA results revealed that the contributions of group to the SC decoder (Supplementary Fig. 5a) and the SR decoder (Supplementary Fig. 5b) were significant. Meanwhile, a wider time window showed significant effect of color on the SC decoder (approximately 100 - 1100 ms post-stimulus onset, Supplementary Fig. 5a) and a narrower time window showed significant effect of word on SR decoder (approximately 100 - 500 ms post-stimulus onset, Supplementary Fig. 5b). However, we found no significant effect of ISPC on either SC or SR decoders. We also performed the same analyses on response-locked data from the time window -800 to 200 ms. The results showed shared representation of color in the SC decoder (Supplementary Fig. 5c) and group in both decoders (Supplementary Fig. 5c-d). Overall, the above results demonstrated that color, word and group information are shared between SC and SR subspaces.

Lastly, we would like to stress that our main hypothesis for the cross-subspace decoding analysis is that SR and SC subspaces are not identical. This hypothesis was supported by lower decoding accuracy for cross-subspace than within-subspace decoders and enables following analyses that treated SC and SR as separate representations.

We have added the interpretation to page 13-14 of the revised manuscript.

(3) The time-resolved within-trial correlation of RSA betas is a cool idea, but I am concerned it is biased. Estimating correlations among different coefficients from the same GLM design matrix is, in general, biased, i.e., when the regressors are non-orthogonal. This bias comes from the expected covariance of the betas and is discussed in detail here (10.1371/journal.pcbi.1006299). In short, correlations could be inflated due to a combination of the design matrix and the structure of the noise. The most established solution, to cross-validate across different GLM estimations, is unfortunately not available here. I would suggest that the authors think of ways to handle this issue.

Thank you for raising this important issue. Because the bias comes from the covariance between the regressors and the same GLM was applied to all time points in our analysis, we assume that the inflation would be similar at different time points. Therefore, we calculated the correlation of SC and SR betas ranging from -200 to 0 ms relative to stimulus onset as a baseline (i.e., no SC or SR representation is expected before the stimulus onset) and compared the post-stimulus onset correlation coefficients against this baseline. We hypothesized that if the positively within-trial correlation of SC and SR betas resulted from the simultaneous representation instead of inflation, we should observe significantly higher correlation when compared with the baseline. To examine this hypothesis, we first performed the linear discriminant analysis (Supplementary Fig. 7a) and RSA regression (Supplementary Fig. 7b) on the -200 - 0 ms window relative to stimulus onset. We then calculated the average r_baseline of SC and SR betas on that time window for each participant (group results at each time point are shown in Supplementary Fig. 7c) and computed the relative correlation at each post-stimulus onset time point using (fisher-z (r) - fisher-z (r_baseline)). Finally, we performed a simple t test at the group level on baseline-corrected correlation coefficients with Bonferroni correction. The results (Fig. 6c) showed significantly more positive correlation from 100 - 500 ms post-stimulus onset compared with baseline, supporting our hypothesis that the positive within-trial correlation of SC and SR betas arise from simultaneous representation rather than inflation. The related interpretation was added to page 17 of the revised manuscript.

(4) Are results robust to running response-locked analyses? Especially the EEG-behavior correlation. Could this be driven by different RTs across trials & trial-types? I.e., at 400 ms poststim onset, some trials would be near or at RT/action execution, while others may not be nearly as close, and so EEG features would differ & "predict" RT.

Thanks for this question. We now pair each of the stimulus-locked EEG analysis in the manuscript with response-locked analysis. To control for RT variations among trial types, when using the linear mixed model (LMM) to predict RTs from trial-wise RSA results, we included a separate intercept for each of the eight trial types in SC or SR. Furthermore, at each time point, we only included trials that have not generated a response (for stimulus-locked analysis) or already started (for response-locked analysis). All the results (Fig. 3, 5, 7, 9 in the revised manuscript) are in support of our hypothesis. We added these detailed to page 31 of the revised manuscript.

(5) I suggest providing more explanation about the logic of the subspace decoding method - what trialtypes exactly constitute the different classes, why we would expect this method to capture something useful regarding ISPC, & what this something might be. I felt that the first paragraph of the results breezes by a lot of important logic.

In general, this paper does not seem to be written for readers who are unfamiliar with this particular topic area. If authors think this is undesirable, I would suggest altering the text.

To improve clarity, we revised the first paragraph of the SC and SR association subspace analysis to list the conditions for each of the SC and SR decoders and explain more about how the concept of being separatable can be tested by cross-decoding between SC and SR subspaces. The revised paragraph now reads:

“Prior to testing whether controlled and non-controlled associations were represented simultaneously, we first tested whether the two representations were separable in the EEG data.

In other words, we reorganized the 16 experimental conditions into 8 conditions for SC (4 colors × MC/MI, while collapsing across SR levels) and SR (4 words × 2 possible responses per word, while collapsing across SC levels) associations separately. If SC and SR associations are not separable, it follows that they encode the same information, such that both SC and SR associations can be represented in the same subspace (i.e., by the same information encoded in both associations). For example, because (1) the word can be determined by the color and congruency and (2) the most-likely response can be determined by color and ISPC, the SR association (i.e., association between word and most-likely response) can in theory be represented using the same information as the SC association. On the other hand, if SC and SR associations are separable, they are expected to be represented in different subspaces (i.e., the information used to encode the two associations is different). Notably, if some, but not all, information is shared between SC and SR associations, they are still separable by the unique information encoded. In this case, the SC and SR subspaces will partially overlap but still differ in some dimensions. To summarize, whether SC and SR associations are separable is operationalized as whether the associations are represented in the same subspace of EEG data. To test this, we leveraged the subspace created by the LDA (see Methods). Briefly, to capture the subspace that best distinguishes our experimental conditions, we trained SC and SR decoders using their respective aforementioned 8 experimental conditions. We then projected the EEG data onto the decoding weights of the LDA for each of the SC and SR decoders to obtain its respective subspace. We hypothesized that if SC and SR subspaces are identical (i.e., not separable), SC/SR decoding accuracy should not differ by which subspace (SC or SR) the decoder is trained on. For example, SC decoders trained in SC subspace should show similar decoding performance as SC decoders trained in SR subspace. On the other hand, if SC and SR association representations are in different subspaces, the SC/SR subspace will not encode all information for SR/SC associations. As a result, decoding accuracy should be higher using its own subspace (e.g., decoding SC using the SC subspace) than using the other subspace (e.g., decoding SC using the SR subspace). We used cross-validation to avoid artificially higher decoding accuracy for decoders using their own subspace (see Methods).” (Page 11-12).

We also explicitly tested what information is shared between SC and SR representations (see response to comment #2). Lastly, to help the readers navigate the EEG results, we added a section “Overview of EEG analysis” to summarize the EEG analysis and their relations in the following manner:

“EEG analysis overview. We started by validating that the 16 experimental conditions (8 unique stimuli × MC/MI) were represented in the EEG data. Evidence of representation was provided by above-chance decoding of the experimental conditions (Fig. 2-3). We then examined whether the SC and SR associations were separable (i.e., whether SC and SR associations were different representations of equivalent information). As our results supported separable representations of SC and SR association (Fig. 4-5), we further estimated the temporal dynamics of each representation within a trial using RSA. This analysis revealed that the temporal dynamics of SC and SR association representations overlapped (Fig. 6a-b, Fig. 7a-b). To explore the potential reason behind the temporal overlap of the two representations, we investigated whether SC and SR associations were represented simultaneously as part of the task representation, independently from each other, or competitively/exclusively (e.g., on some trials only SC association was represented, while on other trials only SR association was represented). This was done by assessing the correlation between the strength of SC and SR representations across trials (Fig. 6c, Fig. 7c). Lastly, we tested how SC and SR representations facilitated performance (Fig.8-9).” (Page 8-9).

Minor suggestions:

(6) I'd suggest using single-trial RSA beta coefficients, not t-values, as they can be more stable (it's a t-value based on 16 observations against 9 or so regressors.... the SE can be tiny).

Thank you for your suggestion. To choose between using betas and t-values, we calculate the proportion of outliers (defined as values beyond mean ± 5 SD) for each predictor of the design matrix and each subject. We found that outliers were less frequent for t-values than for beta coefficients (t-values: mean = 0.07%, SD = 0.009%; beta-values: mean = 0.19%, SD = 0.033%). Thus, we decided to stay with t-values.

(7) Instead of prewhitening the RTs before the HLM with drift terms, try putting those in the HLM itself, to avoid two-stage regression bias.

Thank you for your suggestion. Because our current LMM included each of the eight trial types in SC or SR as separate predictors with their own intercepts (as mentioned above), adding regressors of trial number and mini blocks (1-100 blocks) introduced collinearity (as ISPC flipped during the experiment). We therefore excluded these regressors from the current LMM (Page 31).

(8) The text says classical MDS was performed on decoding *accuracy* - is this accurate?

We now clarify in the manuscript that it is the decoders’ probabilistic classification results (Page 28).

(9) At a few points, it was claimed that a negative correlation between SC and SR would be expected within single trials, if the two were temporally dissociable. Wouldn't it also be possible that they are not correlated/orthogonal?

We agree with the reviewer and revised the null hypothesis in the cross-trial correlation analysis to include no correlation as SC and SR association representations may be independent from each other (Page 17, 22).

Reviewer #2 (Public review):

Summary:

In this EEG study, Huang et al. investigated the relative contribution of two accounts to the process of conflict control, namely the stimulus-control association (SC), which refers to the phenomenon that the ratio of congruent vs. incongruent trials affects the overall control demands, and the stimulus-response association (SR), stating that the frequency of stimulusresponse pairings can also impact the level of control. The authors extended the Stroop task with novel manipulation of item congruencies across blocks in order to test whether both types of information are encoded and related to behaviour. Using decoding and RSA, they showed that the SC and SR representations were concurrently present in voltage signals, and they also positively co-varied. In addition, the variability in both of their strengths was predictive of reaction time. In general, the experiment has a solid design, but there are some confounding factors in the analyses that should be addressed to provide strong support for the conclusions.

Strengths:

(1) The authors used an interesting task design that extended the classic Stroop paradigm and is potentially effective in teasing apart the relative contribution of the two different accounts regarding item-specific proportion congruency effect, provided that some confounds are addressed.

(2) Linking the strength of RSA scores with behavioural measures is critical to demonstrating the functional significance of the task representations in question.

Thank you for your positive feedback. We hope our responses below address your concerns.

Weakness:

(1) While the use of RSA to model the decoding strength vector is a fitting choice, looking at the RDMs in Figure 7, it seems that SC, SR, ISPC, and Identity matrices are all somewhat correlated. I wouldn't be surprised if some correlations would be quite high if they were reported. Total orthogonality is, of course, impossible depending on the hypothesis, but from experience, having highly covaried predictors in a regression can lead to unexpected results, such as artificially boosting the significance of one predictor in one direction, and the other one to the opposite direction. Perhaps some efforts to address how stable the timed-resolved RSA correlations for SC and SR are with and without the other highly correlated predictors will be valuable to raising confidence in the findings.

Thank you for this important point. The results of proportion of variability explained shown in the Author response table 1 below, indicated relatively higher correlation of SC/SR with Color and Identity. We agree that it is impossible to fully orthogonalize them. To address the issue of collinearity, we performed a control RSA by removing predictors highly correlated with others. Specifically, we calculated the variance inflation factor (VIF) for each predictor. The Identity predictor had a high VIF of 5 and was removed from the RSA. All other predictors had VIFs < 4 and were kept in the RSA. The results (Supplementary Fig. 6) showed patterns similar to the results with the Identity predictor, suggesting that the findings are not significantly influenced by collinearity. We have added the interpretation to page 17 of the revised manuscript.

Author response table 1.

Proportion of variability explained (r²) of RSA predictors.

(2) In "task overview", SR is defined as the word-response pair; however, in the Methods, lines 495-496, the definition changed to "the pairing between word and ISPC" which is in accordance with the values in the RDMs (e.g., mccbb and mcirb have similarity of 1, but they are linked to different responses, so should they not be considered different in terms of SR?). This needs clarification as they have very different implications for the task design and interpretation of results, e.g., how correlated the SC and SR manipulations were.

Thank you for pointing out this important issue with how our operationalization captures the concept in questions. In the revised manuscript, we clarified the stimulus-response (SR) association is the link between the word and the most-likely response (i.e., not necessarily the actual response on the current trial). This association is likely to be encoded based on statistical learning over several trials. On each trial, the association is updated based on the stimulus and the actual response. Over multiple trials, the accumulated association will be driven towards the most-common (i.e., most-likely) response. In our ISPC manipulation, a color is presented in mostly congruent/incongruent (MC/MI) trials, which will also pair a word with a most-likely response. For example, if the color blue is MC, the color blue, which leads to the response blue, will co-occur with the word blue with high frequency. In other words, the SR association here is between the word blue and the response blue. As the actual response is not part of the SR association, in the RDM two trial types with different responses may share the same SR association, as long as they share the same word and the same ISPC manipulation, which, by the logic above, will produce the same most-likely response. These clarifications have been added to page 4 and 29 of the revised manuscript.

In the revised manuscript (Page 17), we addressed how much the correlated SC and SR predictors in the RDM could affect the correlation analysis between SC and SR association representation strength. Specifically, we conducted the RSA using the same GLM on EEG data prior to stimulus onset (Supplementary Fig. 7a-b). As no SC and SR associations are expected to be present before stimulus onset, the correlation between SC and SR representation would serve as a baseline of inflation due to correlated predictors in the GLM (Supplementary Fig. 7c, also see comment #3 of R1). The SC-SR correlation coefficients following stimulus onset was then compared to the baseline to control for potential inflation (Fig. 6c). Significantly above-baseline correlation was still observed between ~100-500 ms post-stimulus onset, providing support for the hypothesis that SC and SR are encoded in the same task representation.

Minor suggestions:

(3) Overall, I find that calling SC-controlled and SR-uncontrolled representations unwarranted. How is the level controlledness defined? Both are essentially types of statistical expectation that provide contextual information for the block of tasks. Is one really more automatic and requires less conscious processing than the other? More background/justification could be provided if the authors would like to use these terms.

Following your advice, we have added more discussion on how controlledness is conceptualized in this work and in the literature, which reads:

“We consider SC and SR as controlled and uncontrolled respectively based on the literature investigating the mechanism of ISPC effect. The SC account posits that the ISPC effect results from conflict and involves conflict adaptation, which requires the regulation of attention or control (Bugg & Hutchison, 2013; Bugg et al., 2011; Schmidt, 2018; Schmidt & Besner, 2008). On the other hand, the SR account argues that ISPC effect does not require conflict adaptation but instead reflects contingency leaning. That is, the response can be directly retrieved from the association between the stimulus and the most-likely response without top-down regulation of attention or control. As more empirical evidence emerged, researchers advocating control view began to acknowledge the role of associative learning in cognitive control regarding the ISPC effect (Abrahamse et al., 2016). SC association has been thought to include both automatic that is fast and resource saving and controlled processes that is flexible and generalizable (Chiu, 2019). Overall, we do not intend to claim that SC is entirely controlled or SR is completely automatic. We use SC-controlled and SR-uncontrolled representations to align with the original theoretical motivation and to highlight the conceptual difference between SC and SR associations.” (Page 24-25)

(4) Figures 3c and d: the figures could benefit from more explanation of what they try to show to the readers. Also for 3d, the dimensions were aligned with color sets and congruencies, but word identities were not linearly separable, at least for the first 3 axes. Shouldn't one expect that words can be decoded in the SR subspace if word-response pairs were decodable (e.g., Figure 3b)?

Thank you for the insightful observation. We now clarified that Fig. 3c and d in the original manuscript (Fig. 4c and d in the current manuscript) aim to show how each of the 8 trial types in the SC and SR subspaces are represented. The MDS approach we used for visualization tries to preserve dissimilarity between trial types when projecting from data from a high dimensional to a low dimensional space. However, such projection may also make patterns linearly separatable in high dimensional space not linearly separatable in low dimensional space. For example, if the word blue has two points (-1, -1) and (1, 1) and the word red has two points (-1, 1) and (1, -1), they are not linearly separatable in the 2D space. Yet, if they are projected from a 3D space with coordinates of (-1, -1, -0.1), (1, 1, -0.1), (-1, 1, 0.1) and (1, -1, 0.1), the two words can be linearly separatable using the 3^rd dimension. Thus, a better way to test whether word can be linearly separated in SR subspace is to perform RSA on the original high dimensional space. We performed the RSA with word (Supplementary Fig. 2) on the SR decoder trained on the SR subspace. Note that in Fig. 3c and d of the original script (Fig. 4c and d in the current manuscript) there are two pairs of words that are not linearly separable: red-blue and yellow-green. Thus, we specifically tested the separability within the two pairs using the one predictor for each pair, as shown in Supplementary Fig. 2. The results showed that within both word pairs individual words were presented above chance level (Supplementary Fig. 3). Considering that the decoders are linear, this finding indicates linear separability of the word pairs in the original SR subspace. The clarification has been added to page 13 (the end of the second paragraph) of the revised manuscript.

References

Abrahamse, E., Braem, S., Notebaert, W., & Verguts, T. (2016). Grounding cognitive control in associative learning. Psychological Bulletin, 142(7), 693-728.doi:10.1037/bul0000047.

Bugg, J. M., & Hutchison, K. A. (2013). Converging evidence for control of color-word Stroop interference at the item level. Journal of Experimental Psychology:Human Perception and Performance, 39(2), 433-449. doi:10.1037/a0029145.

Bugg, J. M., Jacoby, L. L., & Chanani, S. (2011). Why it is too early to lose control in accounts of item-specific proportion congruency effects. Journal of Experimental Psychology: Human Perception and Performance, 37(3), 844-859. doi:10.1037/a0019957.

Chiu, Y.-C. (2019). Automating adaptive control with item-specific learning. In Psychology of Learning and Motivation (Vol. 71, pp. 1-37).

Schmidt, J. R. (2018). Evidence against conflict monitoring and adaptation: An updated review. Psychonomic Bulletin & Review, 26(3), 753-771. doi:10.3758/s13423018-1520-z.

Schmidt, J. R., & Besner, D. (2008). The Stroop effect: Why proportion congruent has nothing to do with congruency and everything to do with contingency. Journal of Experimental Psychology: Learning, Memory, and Cognition, 34(3), 514-523. doi:10.1037/0278-7393.34.3.514.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

General Response to Review

We would like to thank all three reviewers for their encouraging comments on our manuscript. We now submit our revised study after considerable efforts to address each of the reviewer concerns. I will first provide a response related to a major change we have made in the revision that addressed a concern common to all three reviewers, followed by a point-by-point response to individual comments.

Replacing LRRK2ARM data with a LRRK2 specific type II kinase inhibitor: The most critical issue for all 3 reviewers was the use of our new CRISPR-generated truncation mutant of LRRK2 that we called LRRK2ARM. We had not provided direct evidence of the protein product of this truncation, which was a significant limitation. To address this we performed proteomics analysis of all clones, and to our surprise, we identified 7 peptides that were C-terminal to our "predicted" stop codon we had engineered into the CRISPR design. A repeat of the deep sequencing analysis in both directions then more clearly revealed site specific mutations leading to 4 amino acid changes at the junction of exon 19, without introducing a stop codon. Given that we could not detect the protein by western blot (even though proteomics now indicated the region of LRRK2 recognized by our antibodies was present) we decided to remove this clone from the manuscript. In the meantime we had compared the ineffectiveness of MLi-2 to block Rab8 phosphorylation during iron overload in the LRRK2G2019S cells with a type II kinase inhibitor called rebastinib. The data showed very clearly that treatment with rebastinib reversed the iron-induced phospho-Rab8 at the plasma membrane (and by western blot, in new Fig 3). Since this inhibitor is very broad spectrum inhibiting ~30% of the kinome we reached out to Sam Reck-Peterson and Andres Leschziner, experts in LRRK2 structure/function, who recently developed a much more selective LRRK2-specific type II kinase inhibitor they called RN341 and RN277 (developed with Stefan Knapp PMID: 40465731). These compounds effectively coupled the MLi-2 compound through an indole ring to a rebastinib type II compound to provide LRRK2 binding specificity to the efficient DYG "out" type II inhibitor. As with rebastinib, the new LRRK-specific kinase inhibitors also effectively reversed the cell surface p-Rab8 seen in LRRK2G2019S, iron loaded cells. These new data provide the first biological paradigm where the kinase activity of LRRK2 is resistant to type I MLi-2, yet remains highly sensitive to type II inhibitors. While the loss of our LRRK2ARM clone marks a significant change in the manuscript we believe the main message is stronger with the addition of the new LRRK2 specific type II kinase inhibitor. Our data show that it is indeed the active kinase function of LRRK2G2019S that is impacting the iron phenotypes we observe but highlight the conformational specificity upon iron overload such that MLi-2 is ineffective. The overall phenotypes we observe in LRRK2G2019S macrophages remain unchanged and are now expanded within the manuscript. We hope reviewers will agree that our work provides important new insights into LRRK2 function in iron homeostasis while opening new avenues of research in future studies.

Given this new information we have changed the title from "LRRK2G2019S acts as a dominant interfering mutant in the context of iron overload" to the more accurate "LRRK2G2019S interferes with NCOA4 trafficking in response to iron overload leading to oxidative stress and ferroptotic cell death."

Response to Reviewer 1

Reviewer 1 (R1): There are two major concerns with the data in their present form. In brief, first, the G2019S cells express much less LRRK2 and more Rab8 that the WT cells and this severely affects interpretability.

Heidi McBride (HM): We agree that the LRRK2G2019S lines express lower levels of LRRK2 than wild type, which is a previously documented phenomenon, presumably as the cell attempts to downregulate the increased kinase activity by reducing protein expression. However, the levels of Rab8 across 10s of experiments do not consistently show any differences between the wild type, G2019S and KO. We have provided more comprehensive quantifications of the blots in the revised version, and the Rab8 levels are consistent across all the blots presented in the manuscript (Figure 1A and 1B).

R1: Second, the investigators used CRISPR to truncate the endogenous LRRK2 locus to produce a hypothetical truncated LRRK2-ARM polypeptide. This appears to have robust effects on NCOA4, in particular, which drives the overall interpretation of the data. However, the expression of this novel LRRK2 species is not confirmed nor compared to WT or G2019S in these cells (although admittedly the investigators did seek to address this with subsequent KO in the ARM cells). It would be premature to account for the changes reported without evidence of protein expression. This latter issue may be more easily addressed and could provide very strong support for a novel function/finding, see more detailed comments below, most seeking clarifications beyond the above.

HM: As described in my common response above, we have removed the LRRK2ARM data from the manuscript.

R1: Need to make clear in the results whether the G2019S CRISPR mutant is heterozygous or homozygous (presumably homozygous, same for ARM)

HM: The RAW cell line we generated is homozygous for the G2019S and the KO alleles. We added this to the beginning of the results section and methods.

R1: The text of the results implies that MLi2 was used in both WT and G2019S Raw cells, but it's only shown for G2019S. Given the premise for the use of RAW cells, it's important to show that there is basal LRRK2 kinase activity in WT cells to go along with its high protein expression. This is particularly important as the G2019S blot suggests minor LRRK2-independent phosphorylation of Rab8a (and other detected pRabs). One would imagine that pRab8 levels in both WT and G2019S would reduce to the same base line or ratio of total Rab in the presence of MLi2, but WT untreated is similar to G2019S with MLi2. This suggests no basal LRRK2 activity in the Raw cells, but I don't think that is the case.

HM: We have included the data from MLi-2 treatment of wild type cells in Fig 3C quantified in D. Again, the baseline levels of Rab8 are unchanged across the genotypes. However, the reviewer is correct that there is some baseline LRRK2 kinase activity that is sensitive to MLi2 in wild type cells. This is seen most clearly on the autophosphorylation of LRRK2 at S1292 in Fig 3C. The pRab8 blots is not as clear in wild type cells. It is likely that LRRK2 must be actively recruited to membranes (as seen by others with LLOME, etc) to easily visualize p-Rabs in wild type cells. Nevertheless, we do clearly see the activity of autophosphorylation in wild type cells. Therefore while we understand the reviewers point that there should be some Rab8 phosphorylation in wild type cells, we don't see a significant, or very convincing, amount of it in our RAW macrophages.

R1: Also, in terms of these cells, the levels of LRRK2 are surprisingly unmatched (Fig 1A, 1D, 1H, S1D, etc.) as are total levels of Rab8 (but in opposite directions) between the WT and G2019S. This is not mentioned in the Results text and is clearly reproducible and significant. Why do the investigators think this is? If Rab8 plays a role in iron, how do these differences affect the interpretation of the G2019S cells (especially given that MLi2 does not rescue)? Are other LRRK2-related Rabs affected at the protein (not phosphorylation level)? Could reduced levels of LRRK2 or increase Rab 8 alone or together account for some of these differences? Substantial further characterization is required as this seriously affects the interpretability of the data. Since pRab8 is not normalized to total Rab8, this G2019S model may not reflect a total increase in LRRK2 kinase activity, and could in fact have both less LRRK2 protein and less cellular kinase activity than WT (in this case).

HM: In our hands, the RAW cells with homozygous LRRK2G2019S mutations show clearly that the total protein levels of LRRK2 is reduced compared to wild type, which is likely a compensatory effect to reduce cellular kinase activity overall. We understand that some of our previous blots were not so clear on the total Rab8 levels across the different experiments. We have repeated many of these experiments and hope the reviewer can see in Figs 1A, 3C, 3E, 3J, and Sup3A that the total Rab8 levels are stable across the conditions. We also present quantifications from 3 independent experiments normalizing the pRab8/Rab8 levels in all three genotypes in untreated and iron-loaded conditions (Supp Fig 3A and B), and upon MLi2 treatment (Fig 3C). In 3C and D the data show the effectiveness of MLi-2 to reduce pRab8 in control conditions, but the resistance to MLi-2 in FAS treated cells.

R1: Presumably, the blots in 1H are whole cell lysates and account for the pooled soluble and insoluble NCOA4 (increased in G2019S), as there is no difference in soluble NCOA4 (Fig 2H). I suspect the prior difference is nicely reflected in the insoluble fraction (Fig 2H). This should be better explained in the Results text. This is a very interesting finding and I wonder what the investigators believe is driving this phenotype? Is the NCOA4 partitioning into a detergent-inaccessible compartment? Does this replicate with other detergents, those perhaps better at solubilizing lipid rafts? Is this a phenotype reversible with MLi2? Very interesting data.

HM: We apologize for not being clearer in the text describing the behavior of NCOA4. The reviewer is correct that the major change in G2019S is the increased triton-X100 insoluble NCOA4. Previous work has established that NCOA4 segregates into detergent-insoluble foci upon iron overload as a way to release it from ferritin cages, and this fraction is then internalized into lysosomes through a microautophagy pathway (see Mizushima's work PMID: 36066504). In Fig 1I we show that the elevation in NCOA4 and ferritin heavy chain seen in untreated G2019S cells can be cleared upon iron chelation with DFO, indicating that the canonical NCOA4 mediated ferritinophagy (macroautophagy) pathway remains intact to recycle the iron in conditions of iron starvation. However in Figure 2 we show that conditions of iron overload, when NCOA4 segregates from ferritin (to allow cytosolic storage of iron), this form of NCOA4 cannot be degraded within the lysosome through the microautophagy pathway, and begins to accumulate. We see this with our live and fixed imaging compared to wild type cells (Fig 2A,D), and by the lack of clearance seen by western blot (Fig 2E). As for the impact of MLi-2, we observe some reversal of NCOA4 accumulation in untreated cells at 4 and 8 hrs after MLi-2 treatment (Supp Fig 2F). However, in iron loaded conditions the high NCOA4 levels in G2019S cells are MLi2 insensitive, while the elevated NCOA4 in wild type cells is reduced upon MLi2 addition (Fig. 2F, compare lates 3vs4 in wt with lanes 7vs8 in G2019S). This is consistent with a block in the microautophagy pathway of phase-separated NCOA4 degradation in G2019S cells.

R1: Figure 2 describes the increased NCOA4-positive iron structures after iron load, but does not emphasize that the G2019S cells begin preloaded with more NCOA4. How do the investigators account for differential NCOA4 in this interpretation? Is this simply a reflection of more NCOA4 available in G2019S cells? This seems reasonable.

HM: The reviewer is correct, we showed that there is some turnover of NCOA4 in untreated conditions through canonical ferritinophagy, but in iron overload this appears to be blocked, the NCOA4 segregates from ferritin and remains within insoluble, phase-separated structures that cannot be degraded through microautophagy. We have written the text to be more clear on these points.

R1: These are very long exposures to iron, some as high as 48 hr which will then take into account novel transcriptomic and protein changes. Did the investigators evaluate cell death? Iron uptake would be trackable much quicker.

HM: We agree that many things will change after our FAS treatments and now provide a full proteomics dataset on wild type and G2019S cells with and without iron overload, which is presented in Figure 4A-B. Indeed Figure 4 is entirely new to this revised submission. The proteomics highlighted a series of cellular changes that reflect major cell stress responses including the upregulation of HMOX1 (western blots to validate in Supp Fig 4A), an NRF2 transcriptional target consistent with our observation that NRF2 is stabilized and translocated to the nucleus in G2019S iron loaded cells (Sup Fig 4B,C). There are several interesting changes, and we highlighted the three major nodes, which are changes in iron response proteins, lysosomal proteins - particularly a loss of catalytic enzymes like lysozymes and granzymes consistent with the loss of hydrolytic capacity we show in Fig. 4C,D. We also noted changes in cytoskeletal proteins we suspect is consistent with the "blebbing" of the plasma membrane we see decorated with pRab8 in Fig 3. To test the activation of lipid oxidation likely resulting from the elevation in Fe2+ and oxidation signatures we employed the C11-bodipy probe and observe strong signal specific to the G2019 iron-loaded cells, particularly labelling endocytic compartments and the cell surface (Fig. 4E-G).

Lastly, an analysis of SYTOX green uptake experiments was done to monitor the uptake of the dye into cells that have died of cell membrane rupture, commonly used to examine ferroptotic cell death. We now show the G2019S cells are very susceptible to this form of death (Fig 4H,I). These data add new functional evidence for the consequence of the G2019S mutation in an increased susceptibility to iron stress.

R1: The legend for 2F is awkward (BSADQRED)

HM: We have changed this to BSA-DQRed, which is a widely used probe to monitor the hydrolytic capacity of the lysosome.

R1: Why are WT cells not included in Fig 2G?

HM: We have now included new panels in Fig 3C,D showing wild type and G2019S +/- FAS and +/-ML-i2 with quantifications of pRab8/Rab8.

R1: The biochemical characterization of NCOA4 in the LRRK2-arm cells is a great experiment and strength of the paper. The field would benefit by a bit further interrogation, other detergents, etc.

HM: We have removed all of the LRRK2ARM data given our confusion over the impact of the 4 amino acid changes in exon 19 and our inability to monitor this protein by western blot. The concept that NCOA4 enters into TX100 insoluble, phase separated compartments has been well established, so we didn't explore other detergents at this point.

R1: Have the investigators looked for aberrant Rab trafficking to lysosomes in the LRRK2-arm cells? Is pRab8 mislocalized compared to WT? Other pRabs?

HM: We did initially show that pRab8 was also at the plasma membrane in the LRRK2ARM cells, and we still focus on this finding for the G2019S, seen in Fig 3A,B,F,H. We did try to look at other p-Rabs known to be targets of LRRK2 but none of them worked in immunofluorescence so we couldn't easily monitor specific traffic and/or localization changes for them.

R1: The expression levels and therefore stability of the ARM fragment is not shown. This is necessary for interpretation. While very intriguing, the data in Aim 3 rely on the assumption that the ARM fragment is expressed, and at comparable levels to G2019S to account for phenotypes. The generation of second clone is admirable, but the expression of the protein must be characterized. This is especially true because of the different LRRK2 levels between WT and G2019S. One could easily conceive of exogenous expression of a tagged-ARM fragment into LRRK2 KO cells, for example, as another proof-of-concept experiment. If it is truly dominant, does this effect require or benefit from some FL LRRK2? It seems easy enough to express the LRRK2-ARM in at least WT and KO RAW cells.

HM: We agree and our attempts to understand this clone resulted in its removal from the manuscript. We did also express cDNA encoding our ARM domain (up to exon 19), but it didn't phenocopy the CRISPR clone, which of course made sense once we had better proteomics and repeated our deep sequencing.

In our further efforts to understand why our phenotype was MLi-2 resistant upon iron overload we expanded to examine the impact of pan-specific TypeII kinase inhibitors, and then reached out to the Reck-Peterson and Leschziner labs to obtain a newly developed LRRK2 selective type II kinase inhibitor. These all very efficiently reversed the pRab8 signals seen at the plasma membrane of G2019S cells upon iron overload (Fig 3E-K). Therefore the G2019S is not dominant negative, as we had initially supposed, rather there is a specific conformation of LRRK2 in high iron that potentially opens the ATP binding pocket to bind the type II inhibitors, but not MLi2. We do not understand exactly what this conformation is but likely involves new protein interactions specific to high iron, or perhaps LRRK2 binds iron directly as a sensor somehow that ultimately leads to the differential sensitivity we observe between type I and type II kinase inhibitors. Our data indicate that MLi-2 treatment in clinic will not be protective against iron toxicity phenotypes that may contribute to PD, where these newer selective type II LRRK2 kinase inhibitors would be effective in this conformation-specific context of iron toxicity.

R1: Does iron overload induce Rab8a phosphorylation in a LRRK2 KO cell? This would be a solid extension on the ARM data and support the important finding that an additional kinase(s) can phosphorylate Rab8a under these conditions, and while not unexpected, this may not have been demonstrated by others as clearly. It also addresses whether the ARM domain is important to this other putative kinase(s), which may add value to the authors' model.

HM: Iron overload does not induce pRab8 in LRRK2 KO cells, as seen by immunofluorescence in Fig 3A,B, and western blot in Supp Fig 3 A,B. With our new type II kinase inhibitor data we can confirm that the plasma membrane localized Rab8 is indeed phosphorylated by LRRK2.

R1: Minor concern - the abstract but not the introduction emphasizes a hypothesis that loss of neuromelanin may promote cell loss in PD (through loss of iron chelation), while post mortem studies are by definition only correlative, early works suggested that the higher melanized DA neurons were preferentially lost when compared to poorly melanized neurons in PD. This speculation in the abstract is not necessary to the novel findings of the paper.

HM: We appreciate that the links to iron in PD are correlative, we have maintained some of our discussion on this point within the manuscript given the lack of attention the field has paid to the cell biology of iron homeostasis in PD models. If there is a cell autonomous nature to the loss of DA neurons in PD, iron is very likely to be a part of this specificity in our opinion. Most of the newer MRI studies looking at iron levels in patient brains are showing higher free iron and working on this as potential biomarkers of disease. The precise timing of this relative to the stability/loss of neuromelanin is, I agree, not really clear.

R1: (Significance (Required)): This study could shed light on a both novel and unexpected behavior of the LRRK2 protein, and open new insights into how pathogenic mutations may affect the cell. While studied in one cell line known for unusually high LRRK2 expression levels, data in this cell type have been broadly applicable elsewhere. Give the link to Parkinson's disease, Rab-dependent trafficking, and iron homeostasis, the findings could have import and relevance to a rather broad audience.

HM: We are so very appreciative that reviewer 1 feels our work will be of interest to the PD and cell biology communities.

Response to Reviewer 2

Reviewer 2 (R2): Major: Please confirm that the observed phenotype is conserved within bone marrow-derived macrophages of LRRK2 G2019S mice. These mice are widely available within the community and frozen bone marrow could be sent to the labs. The main reason for this experiment is that CRISPR macrophage cell lines do sometimes acquire weird phenotypes (at least in our lab they sometimes do!) and it would strengthen the validity of the observations.

HM: We did a series of experiments on primary BMDM derived from 3 pairs of wild type, LRRK2G2019S and LRRK2KO mice. We examined levels of ferritin heavy and light chains in steady state and withFAS treatment experiments. Unfortunately the data did not phenocopy the RAW macrophage lines we present here since FTL and FTH were mostly unchanged. We did observe an increase in NCOA4 levels, consistent with potential issues with microautophagy as observed in our RAW system.

While we understand the danger that our phenotypes are nonspecific and linked to a CRISPR-based anomaly, there are a number of arguments we would make that these data and pathways are potentially very important to our understanding of LRRK2 mutant phenotypes and pathology. The first point is that we now include a LRRK2-specific type II kinase inhibitor that reverses the iron-overload pRab8 accumulation at the plasma membrane in LRRK2G2019S cells, showing that this is at least directly linked to LRRK2 kinase activity, even though it is resistant to MLi2.

Second, Suzanne Pfeffer recently published their single cell RNAseq datasets from brains of untreated LRRK2G2019S mice (PMID: 39088390). She reported major changes in Ferritin heavy chain (it is lost) in very specific cell types of the brain, astrocytes, microglia and oligodendrocytes, with no changes in other cell types at all (her Fig 6 included left). This is consistent with a very context specific impact of LRRK2 on iron homeostasis that we don't yet understand.

Third, the labs of both Cookson, Mamais and Lavoie have been working on the impact of LRRK2 mutations on iron handling in a few different model systems, including iPSCs, and see changes in transferrin recycling and iron accumulation. Those studies did not go into much detail on ferritin, NCOA4 and other readouts of iron homeostasis but are roughly in agreement with our work here. In the last biorxiv study submitted after we sent this work for review they concluded their phenotypes were reversed by MLi2 treatment, however they required 7 days of treatment for a ~20% restoration in iron levels. Given our work it would seem the impact of LRRK2G019S in high iron conditions is also very resistant to MLi2 treatment. In all these studies we do not yet know for sure whether iron overload in the brain may be a precursor to DA neuron cell death, which could be exacerbated in G2019S carriers. But we hope the reviewer will agree that our approach and findings will be useful for the field to expand on these concepts within different models of PD.

R2: Minor comments: Supplementary Fig 1: I don't think one should normalize all controls to 1 and then do a statistical test as obviously the standard deviation of control is 0.

HM: We agree with the reviewer that statistical testing is not appropriate when the WT control is fixed to a value of 1, as this necessarily eliminates variance in that group; accordingly, we have removed both statistical comparisons and standard deviation from the WT control while retaining variability measures for all experimental conditions. Raw densitometry values could not be pooled across independent experiments due to substantial inter-blot variability, and therefore normalization to the WT control was used solely to allow relative comparison within experiments, acknowledging the inherent quantitative limitations of Western blot densitometry. Ultimately the magnitude of the changes relative to the control lanes in each biological replicate was consistent across experiments, even if the absolute density of the bands between experiments was not always the same.

R2: The raw data needs to be submitted to PRIDE or similar.

HM: All of our data is being uploaded to the GEO databases, protocols to protocols.io and raw data deposited on Zenodo site in compliance with our ASAP funding requirements and the journals.

R2: Some of the western blots could be improved. If these are the best shown, I am a little concerned about the reproducibility. How often has they been done?

HM: We now ensure there is quantification of all the blots for at least 3 independent experiments and have worked to improve the quality of them throughout the revision period.

R2: (Significance (Required)): Considering the importance of LRRK2 biology in Parkinson's and the new biology shown, this paper will be of great interest to the community and wider research fields.

HM: We are so very grateful that the reviewer appreciates that the LRRK2 and PD community will find our work of interest. We hope our revisions will prove satisfactory even in the absence of ferritin changes in primary G2019S BMDM.

Response to Reviewer 3

Reviewer 3 (R3): What is missing in the study is the physiological relevance of these findings, mainly whether this effect actually results in higher cell death during iron overload. Since iron overload is known to result in ferroptosis, it is surprising that the authors have not checked whether the LRRK2 G2019S and ARM cells undergo more ferroptosis relative to LRRK2 WT cells.

HM: We thank the reviewer for pushing us to monitor the functional implications of the iron mishandling upon iron overload in the G2019S RAW cell system. We now add a completely new Figure 4 to get to these functional points. We employed two tools to look at established aspects of ferroptosis, first the C11-bodipy probe that labels oxidized lipids and we see significant signals specific to the G2019S iron loaded cells, where it labels endocytic membranes and the cell surface (Fig 4 E-G). This is consistent with the elevation of free iron 2+. We also used the SYTOX green death assay where the dye is internalized into cells when the cell surface is ruptured and show that G2019S cells die upon iron overload, but not the LRRK2KO or wild type cells (Fig 4 H,I). Lastly, we performed full proteomics analysis of the wt and G2019S RAW cells in iron overload conditions. These data provide a better view of the full stress response initiated in the G2019S cells, including the upregulation of HMOX1 (an NRF2 target gene), changes in lysosomal hydrolytic enzymes consistent with the reduction in BSA-DQRed signals, and in cytoskeleton, which is consistent with the plasma membrane blebbing phenotypes we see in G2019S (Fig. 4A-D and Supp. Fig 4 data). We hope these new data help to position the phenotype into a more physiological output.

R3: Moreover, their conclusion of the findings as "resistant to LRRK2 kinase inhibitors" is not convincing, since in most of the studies, they have removed the kinase domain, and this description implies the use of pharmacological kinase inhibition which has not been done in this paper.

HM: We took this comment to heart and, as explained in the general response we removed the LRRK2ARM clones from the study. To understand the kinase function in the iron overload conditions we first explored the pan-specific type II kinase inhibitor rebastinib, shown to inhibit LRRK2. In contrast to MLi2, this drug effectively blocked p-Rab8 in G2019S cells exposed to high iron. However, since it is not specific and likely inhibits about 30-40% of all kinases we reached out to the Reck-Peterson and Leschziner labs who have developed a LRRK2 specific type II kinase inhibitor (published in June 2025 PMID: 40465731). They provided these to us (along with a great deal of discussion) and the two drugs both blocked the effect of LRRK2G2019 on p-Rab8 at the plasma membrane. These data show that the phenotypes we observe are indeed linked to the increased kinase activity of LRRK2, even though they are fully resistant to MLi-2. It suggests that high iron results in some alteration in LRRK2 conformation that alters the ability of MLi2 to block the kinase activity, while still allowing the type II kinase inhibitors that bind deeper in the ATP-binding pocket, to functionally block activity. We believe that these new data remove a great deal of confusion we had in the initial submission to explain the MLi-2 resistance.

R3: There is lower LRRK2 expression in LRRK2 G2019S cells, have the authors checked Rab phosphorylation to validate the mutation?

HM: We agree that the G2019S mutation leads a reduction in total LRRK2 levels in the cell, which is likely a compensatory effect to lower kinase activity in the cell. We do show that the G2019S mutation has clear activation of phosphorylation on both Rab8 and at the autophosphorylation site S1292 of LRRK2, as seen in Fig 1A, quantified in Fig 1B. In untreated conditions, these phosphorylation events are reversible upon treatment with MLi-2. We also provide the sequencing data in the supplement to confirm the presence of the G2019S mutation in this clone, shown in Supp Fig. 1A.

R3: The authors should specify if their cells are heterozygous or homozygous since they are discussing a dominant interfering mutant.

HM: The G2019S and LRRK2 KO are both homozygous. We state this early in the results section and the methods.

R3: The transferrin phenotype validated through proteomics and western blot is solid. HM: We agree, thank you very much!

R3: Quantification in figure 1F-G is problematic, not clear what they mean by "diffuse and lysosomal". Puncta is either colocalising with lysosomes or not colocalising. This needs to be clarified and re-analysed.

HM: We apologize for the confusion. In control cells the Cherry tagged FTL is efficiently cycling through the lysosomes and we don't see a strong cytosolic (diffuse) pool, which likely reflects the relatively iron-poor culture conditions. However, in G2019S cells, there is a highly elevated amount of FTL, with a strong cytosolic/diffuse stain in steady state, with some flux into lysosomes. In this experiment we chelated iron to test whether this cytosolic pool of FTL was capable of clearing through the lysosomes (ferritinophagy). While there is a cytosolic (diffuse) pool that remains, the pool that fluxes into the lysosome increases in G2019S chelated cells. This is also seen by the reduction in total FTL seen by western blot (endogenous FTL). Our conclusion here is that the general ferritinophagy machinery remains functional in G2019S cells. We have changed the term "diffuse" to "cytosolic" and improved our description of this experiment in the text.

R3: Text in the first results part called "LRRK2G2019S RAW macrophages have altered iron homeostasis" is very long. It could be divided into more sections to improve readability. HM: We have improved the text to be more descriptive of the conclusions and added new sections

R3: If the effect is armadillo-dependent, where does LRRK2 G2019S is implicated since there is no kinase domain in these cells?

HM: Our new data employing the LRRK2-specific type II kinase inhibitors now confirm that the effects of the G2019S on iron overload are indeed kinase dependent, it's just insensitive to MLi2.

R3: The authors do not show any controls (PCR, sequencing) confirming knockout or truncation. HM: We did higher resolution proteomics and deep sequencing and learned that the "Arm" mutation was not a truncation but a series of 4 point mutations around exon 19. Therefore we removed all data referring to this clone and replaced it with the use of the type II kinase inhibitor experiments. We feel this removed a lot of confusion and provides much clearer conclusions on the role of the kinase activity in iron overload. We may continue to explore what the 4 amino acid mutations created such strong phenotypes, as it could reflect a critical conformational change that impacts the kinase activity. But that is for future work. We now include the sequencing files of the G2019 and KO as Supplementary Data Files 1 and 2.

R3: The data is interesting and the image quality with the insets is very high. HM: We thank the reviewer for their positive comments!

R3: Mutant not clearly described in text, did the authors remove just the kinase and ROC-COR domains or all the domains downstream of the Armadillo domain? This is not clear. HM: We have removed the clone from the manuscript.

R3: The authors cannot conclude that their phenotype is due to the independence of the kinase domain specifically as they are also interfering with the GTPase activity by removing the ROC-COR domains. HM: We agree and our new drugs allow us to confirm that the phenotypes are due to kinase activity, but there is a new conformation of LRRK2 induced in high iron that renders the kinase domain resistant to MLi-2 inhibition. We discuss this in the manuscript now.

R3: In Figure 3E, is the difference between the "ARM CTRL" and the "ARM FAS" conditions significant? A trend appears to be there, but the p-value is not shown. HM: these data are now removed.

R3: In figure 4A, it would have been important to check if Rab8 phosphorylation is also observed in LRRK2 KO cells after administration of FAS to further evaluate the mechanism through which this Rab8 phosphorylation is occurring.

HM: We show that the pRab8 is specific to the G2019S lines and not seen in LRRK2 KO (Fig 3A,B, Supp. Fig. 3A,B).

R3: The vinculin bands in figure 4A are misaligned with the rest of the bands.

HM: We now provide new blots for all of these experiments (in Fig 3) as we removed the LRRK2ARM data from the manuscript and the appropriate loading controls are all included.

R3: The authors do not have any controls to validate the pRab8 staining in IF. This is an important caveat and needs to be addressed. HM: We now include siRNA validation of Rab8 (vs Rab10) to confirm the specificity of the antibody to pRab8 in IF where it labels the plasma membrane in G2019S iron loaded cells.

R3: The authors should have checked if FAS administration in the LRRK2 G2019S and the ARM cells is leading to ferroptotic cell death (or cell death in general). This is key to validate the link between the altered iron homeostasis in LRRK2 G2019S cells and increased cytotoxicity observed during neurodegeneration.

HM: As mentioned above, we have added extensively to our new Fig 4 to include full proteomics analysis of the changes in iron loaded G2019S cells, we use C11-Bodipy probes to monitor lipid oxidation, and SYTOX green assays to monitor cell death through cell surface rupture (consistent with ferroptosis). We thank the reviewer for pushing us to do these experiments and provide further relevance to the potential for LRRK2 mutations to promote cell toxicity during neurodegeneration.

R3: Regarding the literature, the authors are missing some important papers that are preprinted and these studies need to be discussed. This includes a report with opposite findingshttps://www.biorxiv.org/content/10.1101/2025.09.26.678370v1.full and a report showing kinase independent cell death in macrophages https://www.biorxiv.org/content/10.1101/2023.09.27.559807v1.abstract

HM: We thank the reviewers for alerting us to the biorxiv papers, one of which was submitted after we sent our manuscript to review. We are excited to see the growing interest in the impact of LRRK2 function in iron homeostasis and hope our work will contribute to this. Upon reading the study from the LaVoie lab they do show some sensitivity of the iron loaded phenotype in G2019S cells, however they see a ~20% reduction in lysosomal iron after 7 days of MLi treatment in Astrocytes (their Fig 2L). To us, this is very likely an indication of a relatively high resistance to the drug. I'm sure if they tried these new Type II inhibitors the iron load would be much more rapidly reversed. The specificity of their phenotype to Rab8 is also very interesting considering the cell surface localization we see for pRab8 in our iron loaded system. Similar comments for the Guttierez study in macrophages. We have included the findings of these papers within the manuscript and thank the reviewer for pointing them out.

Author response:

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

Public Reviews:

Reviewer #1 (Public review): 

Summary:

In this study, Lamberti et al. investigate how translation initiation and elongation are coordinated at the single-mRNA level in mammalian cells. The authors aim to uncover whether and how cells dynamically adjust initiation rates in response to elongation dynamics, with the overarching goal of understanding how translational homeostasis is maintained. To this end, the study combines single-molecule live-cell imaging using the SunTag system with a kinetic modeling framework grounded in the Totally Asymmetric Simple Exclusion Process (TASEP). By applying this approach to custom reporter constructs with different coding sequences, and under perturbations of the initiation/elongation factor eIF5A, the authors infer initiation and elongation rates from individual mRNAs and examine how these rates covary.

The central finding is that initiation and elongation rates are strongly correlated across a range of coding sequences, resulting in consistently low ribosome density ({less than or equal to}12% of the coding sequence occupied). This coupling is preserved under partial pharmacological inhibition of eIF5A, which slows elongation but is matched by a proportional decrease in initiation, thereby maintaining ribosome density. However, a complete genetic knockout of eIF5A disrupts this coordination, leading to reduced ribosome density, potentially due to changes in ribosome stalling resolution or degradation.

Strengths:

A key strength of this work is its methodological innovation. The authors develop and validate a TASEP-based Hidden Markov Model (HMM) to infer translation kinetics at single-mRNA resolution. This approach provides a substantial advance over previous population-level or averaged models and enables dynamic reconstruction of ribosome behavior from experimental traces. The model is carefully benchmarked against simulated data and appropriately applied. The experimental design is also strong. The authors construct matched SunTag reporters differing only in codon composition in a defined region of the coding sequence, allowing them to isolate the effects of elongation-related features while controlling for other regulatory elements. The use of both pharmacological and genetic perturbations of eIF5A adds robustness and depth to the biological conclusions. The results are compelling: across all constructs and conditions, ribosome density remains low, and initiation and elongation appear tightly coordinated, suggesting an intrinsic feedback mechanism in translational regulation. These findings challenge the classical view of translation initiation as the sole rate-limiting step and provide new insights into how cells may dynamically maintain translation efficiency and avoid ribosome collisions.

We thank the reviewer for their constructive assessment of our work, and for recognizing the methodological innovation and experimental rigor of our study.

Weaknesses:

A limitation of the study is its reliance on exogenous reporter mRNAs in HeLa cells, which may not fully capture the complexity of endogenous translation regulation. While the authors acknowledge this, it remains unclear how generalizable the observed coupling is to native mRNAs or in different cellular contexts.

We agree that the use of exogenous reporters is a limitation inherent to the SunTag system, for which there is currently no simple alternative for single-mRNA translation imaging. However, we believe our findings are likely generalizable for several reasons.

As discussed in our introduction and discussion, there is growing mechanistic evidence in the literature for coupling between elongation (ribosome collisions) and initiation via pathways such as the GIGYF2-4EHP axis (Amaya et al. 2018, Hickey et al. 2020, Juszkiewicz et al. 2020), which might operate on both exogenous and endogenous mRNAs.

As already acknowledged in our limitations section, our exogenous reporters may not fully recapitulate certain aspects of endogenous translation (e.g., ER-coupled collagen processing), yet the observed initiation-elongation coupling was robust across all tested constructs and conditions.

We have now expanded the Discussion (L393-395) to cite complementary evidence from Dufourt et al. (2021), who used a CRISPR-based approach in Drosophila embryos to measure translation of endogenous genes. We also added a reference to Choi et al. 2025, who uses a ER-specific SunTag reporter to visualize translation at the ER (L395-397).

Additionally, the model assumes homogeneous elongation rates and does not explicitly account for ribosome pausing or collisions, which could affect inference accuracy, particularly in constructs designed to induce stalling. While the model is validated under low-density assumptions, more work may be needed to understand how deviations from these assumptions affect parameter estimates in real data.

We agree with the reviewer that the assumption of homogeneous elongation rates is a simplification, and that our work represents a first step towards rigorous single-trace analysis of translation dynamics. We have explicitly tested the robustness of our model to violations of the low-density assumption through simulations (Figure 2 - figure supplement 2). These show that while parameter inference remains accurate at low ribosome densities, accuracy slightly deteriorates at higher densities, as expected. In fact, our experimental data do provide evidence for heterogeneous elongation: the waiting times between termination events deviate significantly from an exponential distribution (Figure 3 - figure supplement 2C), indicating the presence of ribosome stalling and/or bursting, consistent with the reviewer's concern. We acknowledge in the Limitations section (L402-406) that extending the model to explicitly capture transcript-dependent elongation rates and ribosome interactions remains challenging. The TASEP is difficult to solve analytically under these conditions, but we note that simulation-based inference approaches, such as particle filters to replace HMMs, could provide a path forward for future work to capture this complexity at the single-trace level.

Furthermore, although the study observes translation "bursting" behavior, this is not explicitly modeled. Given the growing recognition of translational bursting as a regulatory feature, incorporating or quantifying this behavior more rigorously could strengthen the work's impact.

While we do not explicitly model the bursting dynamics in the HMM framework, we have quantified bursting behavior directly from the data. Specifically, we measure the duration of translated (ON) and untranslated (OFF) periods across all reporters and conditions (Figure 1G for control conditions and Figure 4G-H for perturbed conditions), finding that active translation typically lasts 10-15 minutes interspersed with shorter silent periods of 5-10 minutes. This empirical characterization demonstrates that bursting is a consistent feature of translation across our experimental conditions. The average duration of silent periods is similar to what was inferred by Livingston et al. 2023 for a similar SunTag reporter; while the average duration of active periods is substantially shorter (~15 min instead of ~40 min), which is consistent with the shorter trace duration in our system compared to theirs (~15 min compared to ~80 min, on average). Incorporating an explicit two-state or multi-state bursting model into the TASEP-HMM framework would indeed be computationally intensive and represents an important direction for future work, as it would enable inference of switching rates alongside initiation and elongation parameters. We have added this point to the Discussion (L415-417).

Assessment of Goals and Conclusions:

The authors successfully achieve their stated aims: they quantify translation initiation and elongation at the single-mRNA level and show that these processes are dynamically coupled to maintain low ribosome density. The modeling framework is well suited to this task, and the conclusions are supported by multiple lines of evidence, including inferred kinetic parameters, independent ribosome counts, and consistent behavior under perturbation.

Impact and Utility:

This work makes a significant conceptual and technical contribution to the field of translation biology. The modeling framework developed here opens the door to more detailed and quantitative studies of ribosome dynamics on single mRNAs and could be adapted to other imaging systems or perturbations. The discovery of initiation-elongation coupling as a general feature of translation in mammalian cells will likely influence how researchers think about translational regulation under homeostatic and stress conditions.

The data, models, and tools developed in this study will be of broad utility to the community, particularly for researchers studying translation dynamics, ribosome behavior, or the effects of codon usage and mRNA structure on protein synthesis.

Context and Interpretation:

This study contributes to a growing body of evidence that translation is not merely controlled at initiation but involves feedback between elongation and initiation. It supports the emerging view that ribosome collisions, stalling, and quality control pathways play active roles in regulating initiation rates in cis. The findings are consistent with recent studies in yeast and metazoans showing translation initiation repression following stalling events. However, the mechanistic details of this feedback remain incompletely understood and merit further investigation, particularly in physiological or stress contexts. 

In summary, this is a thoughtfully executed and timely study that provides valuable insights into the dynamic regulation of translation and introduces a modeling framework with broad applicability. It will be of interest to a wide audience in molecular biology, systems biology, and quantitative imaging.

We appreciate the reviewer's thorough and positive assessment of our work, and that they recognize both the technical innovation of our modeling framework and its potential broad utility to the translation biology community. We agree that further mechanistic investigation of initiation-elongation feedback under various physiological contexts represents an important direction for future research.

Reviewer #2 (Public review):

Summary:

This manuscript uses single-molecule run-off experiments and TASEP/HMM models to estimate biophysical parameters, i.e., ribosomal initiation and elongation rates. Combining inferred initiation and elongation rates, the authors quantify ribosomal density. TASEP modeling was used to simulate the mechanistic dynamics of ribosomal translation, and the HMM is used to link ribosomal dynamics to microscope intensity measurements. The authors' main conclusions and findings are:

(1) Ribosomal elongation rates and initiation rates are strongly coordinated.

(2) Elongation rates were estimated between 1-4.5 aa/sec. Initiation rates were estimated between 0.5-2.5 events/min. These values agree with previously reported values.

(3) Ribosomal density was determined below 12% for all constructs and conditions.

(4) eIF5A-perturbations (KO and GC7 inhibition) resulted in non-significant changes in translational bursting and ribosome density.

(5) eIF5A perturbations resulted in increases in elongation and decreases in initiation rates.

Strengths:

This manuscript presents an interesting scientific hypothesis to study ribosome initiation and elongation concurrently. This topic is highly relevant for the field. The manuscript presents a novel quantitative methodology to estimate ribosomal initiation rates from Harringtonine run-off assays. This is relevant because run-off assays have been used to estimate, exclusively, elongation rates.

We thank the reviewer for their careful evaluation of our work and for recognizing the novelty of our quantitative methodology to extract both initiation and elongation rates from harringtonine run-off assays, extending beyond the traditional use of these experiments.

Weaknesses:

The conclusion of the strong coordination between initiation and elongation rates is interesting, but some results are unexpected, and further experimental validation is needed to ensure this coordination is valid. 

We agree that some of our findings need further experimental investigation in future studies. However, we believe that the coordination between initiation and elongation is supported by multiple results in our current work: (1) the strong correlation observed across all reporters and conditions (Figure 3E), and (2) the consistent maintenance of low ribosome density despite varying elongation rates. While additional experimental validation would be valuable, we note that directly manipulating initiation or elongation independently in mammalian cells remains technically challenging. Nevertheless, our findings are consistent with emerging mechanistic understanding of collision-sensing pathways (GIGYF2-4EHP) that could mediate such coupling, as discussed in our manuscript.

(1) eIF5a perturbations resulted in a non-significant effect on the fraction of translating mRNA, translation duration, and bursting periods. Given the central role of eIF5a, I would have expected a different outcome. I would recommend that the authors expand the discussion and review more literature to justify these findings.

We appreciate this comment. This finding is indeed discussed in detail in our manuscript (Discussion, paragraphs 6-7). As we note there, while eIF5A plays a critical role in elongation, the maintenance of bursting dynamics and ribosome density upon perturbation can be explained by compensatory feedback mechanisms. Specifically, the coordinated decrease in initiation rates that counterbalances slower elongation to maintain homeostatic ribosome density. We also discuss several factors that complicate interpretation: (1) potential RQC-mediated degradation masking stronger effects in proline-rich constructs, (2) differences between GC7 treatment and genetic knockout suggesting altered stalling resolution kinetics, and (3) the limitations of using exogenous reporters that lack ER-coupled processing, which may be critical for eIF5A function in endogenous collagen translation (as suggested by Rossi et al., 2014; Mandal et al., 2016; Barba-Aliaga et al., 2021). The mechanistic complexity and tissue-specific nature of eIF5A function in mammals, which differs substantially from the better-characterized yeast system, likely contributes to the nuanced phenotype we observe. We believe our Discussion adequately addresses these points.

(2) The AAG construct leading to slow elongation is very surprising. It is the opposite of the field consensus, where codon-optimized gene sequences are expected to elongate faster. More information about each construct should be provided. I would recommend more bioinformatic analysis on this, for example, calculating CAI for all constructs, or predicting the structures of the proteins.

We agree that the slow elongation of the AAG construct is counterintuitive and indeed surprising. Following the reviewer's suggestion, we have now calculated the Codon Adaptation Index (CAI) for all constructs (Renilla 0.89, Col1a1 0.78, Col1a1 mutated 0.74). It is therefore unlikely that codon bias explains the slow translation, particularly since we designed the mutated Col1a1 construct with alanine codons selected to respect human codon usage bias, thereby minimizing changes in codon optimality. As we discuss in the manuscript, we hypothesize that the proline-to-alanine substitutions disrupted co-translational folding of the collagen-derived sequence. Prolines are critical for collagen triple-helix formation (Shoulders and Raines, 2009), and their replacement with alanines likely generates misfolded intermediates that cause ribosome stalling (Barba-Aliaga et al., 2021; Komar et al., 2024). This interpretation is supported by the high frequency (>30%) of incomplete run-off traces for AAG, suggesting persistent stalling events. Our findings thus illustrate an important potential caveat: "optimizing" a sequence based solely on codon usage can be detrimental when it disrupts functionally important structural features or co-translational folding pathways.

This highlights that elongation rates depend not only on codon optimality but also on the interplay between nascent chain properties and ribosome progression.

(3) The authors should consider using their methodology to study the effects of modifying the 5'UTR, resulting in changes in initiation rate and bursting, such as previously shown in reference Livingston et al., 2023. This may be outside of the scope of this project, but the authors could add this as a future direction and discuss if this may corroborate their conclusions. 

We thank the reviewer for this excellent suggestion. We agree that applying our methodology to 5'-UTR variants would provide a complementary test of initiation-elongation coupling, and we have now added this as a future direction in the Discussion (L417-420).

(4) The mathematical model and parameter inference routines are central to the conclusions of this manuscript. In order to support reproducibility, the computational code should be made available and well-documented, with a requirements file indicating the dependencies and their versions. 

We have added the Github link in the manuscript (https://github.com/naef-lab/suntag-analysis) and have also deposited the data (.ome.tif) on Zenodo (https://zenodo.org/records/17669332).

Reviewer #3 (Public review):

Disclaimer:

My expertise is in live single-molecule imaging of RNA and transcription, as well as associated data analysis and modeling. While this aligns well with the technical aspects of the manuscript, my background in translation is more limited, and I am not best positioned to assess the novelty of the biological conclusions.

Summary:

This study combines live-cell imaging of nascent proteins on single mRNAs with time-series analysis to investigate the kinetics of mRNA translation.

The authors (i) used a calibration method for estimating absolute ribosome counts, and (ii) developed a new Bayesian approach to infer ribosome counts over time from run-off experiments, enabling estimation of elongation rates and ribosome density across conditions.

They report (i) translational bursting at the single-mRNA level, (ii) low ribosome density (~10% occupancy

{plus minus} a few percents), (iii) that ribosome density is minimally affected by perturbations of elongation (using a drug and/or different coding sequences in the reporter), suggesting a homeostatic mechanism potentially involving a feedback of elongation onto initiation, although (iv) this coupling breaks down upon knockout of elongation factor eIF5A.

Strengths:

(1) The manuscript is well written, and the conclusions are, in general, appropriately cautious (besides the few improvements I suggest below).

(2) The time-series inference method is interesting and promising for broader applications. 

(3) Simulations provide convincing support for the modeling (though some improvements are possible). 

(4) The reported homeostatic effect on ribosome density is surprising and carefully validated with multiple perturbations.

(5) Imaging quality and corrections (e.g., flat-fielding, laser power measurements) are robust.

(6) Mathematical modeling is clearly described and precise; a few clarifications could improve it further.

We thank the reviewer for recognizing the novelty of the approach and its rigour, and for providing suggestions to improve it further.

Weaknesses:

(1) The absolute quantification of ribosome numbers (via the measurement of $i_{MP}$ ) should be improved.This only affects the finding that ribosome density is low, not that it appears to be under homeostatic control. However, if $i_{MP}$ turns out to be substantially overestimated (hence ribosome density underestimated), then "ribosomes queuing up to the initiation site and physically blocking initiation" could become a relevant hypothesis. In my detailed recommendations to the authors, I list points that need clarification in their quantifications and suggest an independent validation experiment (measuring the intensity of an object with a known number of GFP molecules, e.g., MS2-GFP MS2-GFP-labeled RNAs, or individual GEMs).

We agree with the reviewer that the estimation of the number of ribosomes is central to our finding that translation happens at low density on our reporters. This result derives from our measurement of the intensity of one mature protein (i_MP), that we have achieved by using a SunTag reporter with a RH1 domain in the C terminus of the mature protein, allowing us to stabilise mature proteins via actin-tethering. In addition, as suggested by the reviewer, we already validated this result with an independent estimate of the mature protein intensity (Figure 5 - figure supplement 2B), which was obtained by adding the mature protein intensity directly as a free parameter of the HMM. The inferred value of mature protein intensity for each construct (10-15 a.u) was remarkably close to the experimental calibration result (14 ± 2 a.u.). Therefore, we have confidence that our absolute quantification of ribosome numbers is accurate.

(2) The proposed initiation-elongation coupling is plausible, but alternative explanations, such as changes in abortive elongation frequency, should be considered more carefully. The authors mention this possibility, but should test or rule it out quantitatively. 

We thank the reviewer for the comment, but we consider that ruling out alternative explanations through new perturbation experiments is beyond the scope of the present work.

(3) The observation of translational bursting is presented as novel, but similar findings were reported by Livingston et al. (2023) using a similar SunTag-MS2 system. This prior work should be acknowledged, and the added value of the current approach clarified.

We did cite Livingston et al. (2023) in several places, but we recognized that we could add a few citations in key places, to make clear that the observation of bursting is not novel but is in agreement with previous results. We now did so in the Results and Discussion sections.

(4) It is unclear what the single-mRNA nature of the inference method is bringing since it is only used here to report _average_ ribosome elongation rate and density (averaged across mRNAs and across time during the run-off experiments - although the method, in principle, has the power to resolve these two aspects).

While decoding individual traces, our model infers shared (population-level) rates. Inferring transcript-specific parameters would be more informative, but it is highly challenging due to the uncertainty on the initial ribosome distribution on single transcripts. Pooling multiple transcripts together allows us to use some assumptions on the initial distribution and infer average elongation and initiation-rate parameters, while revealing substantial mRNA-to-mRNA variability in the posterior decoding (e.g. Figure 3 - figure Supplement 2C). Indeed, the inference still informs on the single-trace run-off time distribution (Figure 3 A) and the waiting time between termination events (Figure 3 - figure supplement 2C), suggesting the presence of stalling and bursting. In addition, the transcript-to-transcript heterogeneity is likely accounted for by our model better than previous methods (linear fit of the average run-off intensity), as suggested by their comparison (Figure 3 - figure supplement 2 A). In the future the model could be refined by introducing transcript-specific parameters, possibly in a hierarchical way, alongside shared parameters.

(5) I did not find any statement about data availability. The data should be made available. Their absence limits the ability to fully assess and reproduce the findings.

We have added the Github link in the manuscript (https://github.com/naef-lab/suntag-analysis) and have also deposited the data (.ome.tif) on Zenodo (https://zenodo.org/records/17669332).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors): 

Major Comments:

(1) Lack of Explicit Bursting Model

Although translation "bursts" are observed, the current framework does not explicitly model initiation as a stochastic ON/OFF process. This limits insight into regulatory mechanisms controlling burst frequency or duration. The authors should either incorporate a two-state/more-state (bursting) model of initiation or perform statistical analysis (e.g., dwell-time distributions) to quantify bursting dynamics. They should clarify how bursting influences the interpretation of initiation rate estimates.

We agree with the reviewer that an explicit bursting model (e.g., a two-state telegraph model) would be the ideal theoretical framework. However, integrating such a model into the TASEP-HMM inference framework is computationally intensive and complex. As a robust first step, we have opted to quantify bursting empirically based on the decoded single-mRNA traces. As shown in Figure 1G (control) and Figure 4G (perturbed conditions), we explicitly measured the duration of "ON" (translated) and "OFF" (untranslated) periods. This statistical analysis provides a quantitative description of the bursting dynamics without relying on the specific assumptions of a telegraph model. We have clarified this in the text (L123-125) and, as suggested, added a discussion (L415-417) on the potential extensions of the model to include explicit switching kinetics in the Outlook section.

(2) Assumption of Uniform Elongation Rates

The model assumes homogeneous elongation across coding sequences, which may not hold for stalling-prone inserts (e.g., PPG). This simplification could bias inference, particularly in cases of sequence-specific pausing. Adding simulations or sensitivity analysis to assess how non-uniform elongation affects the accuracy of inferred parameters. The authors should explicitly discuss how ribosome stalling, collisions, or heterogeneity might skew model outputs (see point 4).

A strong stalling sequence that affects all ribosomes equally should not deteriorate the inference of the initiation rate, provided that the low-density assumption holds. The scenario where stalling events lead to higher density, and thus increased ribosome-ribosome interactions, is comparable to the conditions explored in Figure 2E. In those simulations, we tested the inference on data generated with varying initiation and elongation rates, resulting in ribosome densities ranging from low to high. We demonstrated that the inference remains robust at low ribosome densities (<10%). At higher densities, the accuracy of the initiation rate estimate decreases, whereas the elongation rate estimate remains comparatively robust. Additionally, the model tends to overestimate ribosome density under high-density conditions, likely because it neglects ribosome interference at the initiation site (Figure 2 figure supplement 2C). We agree that a deeper investigation into the consequences of stochastic stalling and bursting would be beneficial, and we have explicitly acknowledged this in the Limitations section.

(3) Interpretation of eIF5A Knockout Phenotype

The observation that eIF5A KO reduces initiation more than elongation, leading to decreased ribosome density, is biologically intriguing. However, the explanation invoking altered RQC kinetics is speculative and not directly tested. The authors should consider validating the RQC hypothesis by monitoring reporter mRNA stability, ribosome collision markers, or translation termination intermediates.

We thank the reviewer for the comment, but we consider that ruling out alternative explanations through new experiments is beyond the scope of the present work.

(4) To strengthen the manuscript, the authors should incorporate insights from three studies.

- Livingston et al. (PMC10330622) found that translation occurs in bursts, influenced by mRNA features and initiation factors, supporting the coupling of initiation and elongation.

- Madern et al. (PMID: 39892379) demonstrated that ribosome cooperativity enhances translational efficiency, highlighting coordinated ribosome behavior.

- Dufourt et al. (PMID: 33927056) observed that high initiation rates correlate with high elongation rates, suggesting a conserved mechanism across cell cultures and organisms.

Integrating these studies could enrich the manuscript's interpretation and stimulate new avenues of thought.

We thank the reviewer for the valuable comment. We added citations of Livingston et al. in the context of translational bursting. We already cited Madern et al. in multiple places and, although its observations of ribosome cooperativity are very compelling, they cannot be linked with our observations of a feedback between initiation and elongation, and it would be very challenging to see a similar effect on our reporters. This is why we did not expressly discuss cooperativity. We also integrated Dufourt et al. in the Discussion about the possibility of designing genetically-encoded reporter. We also added a sentence about the possibility of using an ER-specific SunTag reporter, as done recently in Choi et al., Nature (2025) (https://doi.org/10.1038/s41586-025-09718-0).

Minor Comments:

(1) Use consistent naming for SunTag reporters (e.g., "PPG" vs "proline-rich") throughout.

Thank you for the comment. However, the term proline-rich always appears together with PPG, so we believe that the naming is clear and consistent.

(2) Consider a schematic overview of the experimental design and modeling pipeline for accessibility.

Thank you for the suggestion. We consider that experimental design and modeling is now sufficiently clearly described and does not justify an additional scheme. 

(3) Clarify how incomplete run-off traces are handled in the HMM inference.

Incomplete run-off traces are treated identically to complete traces in our HMM inference. This is possible because our model relies on the probability of transitions occurring per time step to infer rates. It does not require observing the final "empty" state to estimate the kinetic parameters ɑ and λ. The loss of signal (e.g., mRNA moving out of the focal volume or photobleaching) does not invalidate the kinetic information contained in the portion of the trace that was observed. We have clarified this in the Methods section.

Reviewer #2 (Recommendations for the authors):

(1) Reproducibility:

(1.1) The authors should use a GitHub repository with a timestamp for the release version.

The code is available on GitHub (https://github.com/naef-lab/suntag-analysis).

(1.2) Make raw images and data available in a figure repository like Figshare.

The raw images (.ome.tif) are now available on Zenodo (https://zenodo.org/records/17669332).

(2) Paper reorganization and expansion of the intensity and ribosome quantification:

(2.1) Given the relevance of the initiation and elongation rates for the conclusions of this study, and the fact that the authors inferred these rates from the spot intensities. I recommend that the authors move Figure 1 Supplement 2 to the main text and expand the description of the process to relate spot intensity and number of ribosomes. Please also expand the figure caption for this image.

We agree with the importance of this validation. We have expanded the description of the calibration experiment in the main text and in the figure caption.

(2.2) I suggest the authors explicitly mention the use of HMM in the abstract.

We have now explicitly mentioned the TASEP-based HMM in the abstract.

(2.3) In line 492, please add the frame rate used to acquire the images for the run-off assays.

We have added the specific frame rate (one frame every 20 seconds) to the relevant section.

(3) Figures and captions:

(3.1) Figure 1, Supplement 2. Please add a description of the colors used in plots B, C. 

We have expanded the caption and added the color description.

(3.2) In the Figure 2 caption. It is not clear what the authors mean by "traceseLife". Please ensure it is not a typo.

Thank you for spotting this. We have corrected the typo.

(3.3) Figure 1 A, in the cartoon N(alpha)->N-1, shouldn't the transition also depend on lambda?

The transition probability was explicitly derived in the “Bayesian modeling of run-off traces” section (Eqs. 17-18), and does not depend on λ, but only on the initiation rate under the low-density assumption.

(3.4) Figure 3, Supplement 2. "presence of bursting and stalling.." has a typo.

Corrected.

(3.5) Figure 5, panel C, the y-axis label should be "run-off time (min)."

Corrected.

(3.6) For most figures, add significance bars.

(3.7) In the figure captions, please add the total number of cells used for each condition.

We have systematically indicated the number of traces (n_t) and the number of independent experiments (n_e) in the captions in this format (n_t, n_e).

(4) Mathematical Methods:

We greatly thank the reviewer for their detailed attention to the mathematical notation. We have addressed all points below.

(4.1) In lines 555, Materials and Methods, subsection, Quantification of Intensity Traces, multiple equations are not numbered. For example, after Equation (4), no numbers are provided for the rest of the equations. Please keep consistency throughout the whole document.

We have ensured that all equations are now consistently numbered throughout the document.

(4.2) In line 588, the authors mention "$X$ is a standard normal random variable with mean $\mu$ and standard deviation $s_0$". Please ensure this is correct. A standard normal random variable has a 0 mean and std 1. 

Thank you for the suggestion, we have corrected the text (L678).

(4.3) Line 546, Equation 2. The authors use mu(x,y) to describe a 2d Gaussian function. But later in line 587, the authors reuse the same variable name in equation 5 to redefine the intensity as mu = b_0 + I.

We have renamed the 2D Gaussian function to \mu_{2D}(x,y) in the spot tracking section

(4.4) For the complete document, it could be beneficial to the reader if the authors expand the definition of the relationship between the signal "y" and the spot intensity "I". Please note how the paragraph in lines 582-587 does not properly introduce "y".

We have added an explicit definition of y and its relationship to the underlying spot intensity I in the text to improve readability and clarity.

(4.5) Please ensure consistency in variable names. For example, "I" is used in line 587 for the experimental spot intensity, then line 763 redefines I(t) as the total intensity obtained from the TASEP model; please use "I_sim(t)" for simulated intensities. Please note that reusing the variable "I" for different contexts makes it hard for the reader to follow the text. 

We agree that this was confusing. We have implemented the suggestion and now distinguish simulated intensities using the notation I_S .

(4.6) Line 555 "The prior on the total intensity I is an "uninformative" prior" I ~ half_normal(1000). Please ensure it is not "I_0 ~ half_normal(1000)."? 

We confirm that “I” is the correct variable representing the total intensity in this context; we do not use an “I₀” variable here.

(4.7) In lines 595, equation 6. Ensure that the equation is correct. Shouldn't it be: s_0^2 = ln ( 1 + (sigma_meas^2 / ⟨y⟩^2) )? Please ensure that this is correct and it is not affecting the calculated values given in lines 598.

Thank you for catching this typo. We have corrected the equation in the manuscript. We confirm that the calculations performed in the code used the correct formula, so the reported values remain unchanged.

(4.8) In line 597, "the mean intensity square ^2". Please ensure it is not "the square of the temporal mean intensity."

We have corrected the text to "the square of the temporal mean intensity."

(4.9) In lines 602-619, Bayesian modeling of run-off traces, please ensure to introduce the constant "\ell". Used to define the ribosomal footprint?

We have added the explicit definition of 𝓁 as the ribosome footprint size (length of transcript occupied by one ribosome) in the "Bayesian modeling of run-off traces" section.

(4.10) Line 687 has a minor typo "[...] ribosome distribution.. Then, [...]"

We have corrected the punctuation.

(4.11) In line 678, Equation 19 introduces the constant "L_S", Please ensure that it is defined in the text.

We have added the explicit definition of L_S (the length of the SunTag) to the text surrounding Equation 19.

(4.12) In line 695, Equation 22, please consider using a subscript to differentiate the variance due to ribosome configuration. For example, instead of "sigma (...)^2" use something like "sigma_c ^2 (...)". Ensure that this change is correctly applied to Equation 24 and all other affected equations.

Thank you, we have implemented the suggestions.

(4.13) In line 696, please double-check equations 26 and 27. Specifically, the denominator ^2. Given the previous text, it is hard to follow the meaning of this variable. 

We have revised the notation in Equations 26 and 27 to ensure the denominator is consistent with the definitions provided in the text.

(4.14) In lines 726, the authors mention "[...], but for the purposes of this dissertation [...]", it should be "[...], but for the purposes of this study [...]"

Thank you for spotting this. We have replaced "dissertation" with "study."

(4.15) Equations 5, 28, 37, and the unnumbered equation between Equations 16 and 17 are similar, but in some, "y" does not explicitly depend on time. Please ensure this is correct. 

We have verified these equations and believe they are correct.

(4.16) Please review the complete document and ensure that variables and constants used in the equations are defined in the text. Please ensure that the same variable names are not reused for different concepts. To improve readability and flow in the text, please review the complete Materials and Methods sections and evaluate if the modeling section can be written more clearly and concisely. For example, Equation 28 is repeated in the text.

We have performed a comprehensive review of the Materials and Methods section. To improve conciseness and flow, we have merged the subsection “Observation model and estimation of observation parameters” with the “Bayesian modeling of run-off traces” section. This allowed us to remove redundant definitions and repeated equations (such as the previous Equation 28). We have also checked that all variables and constants are defined upon first use and that variable names remain consistent throughout the manuscript.

Reviewer #3 (Recommendations for the authors):

(1) Data Presentation

(1.1) In main Figures 1D and 4E, the traces appear to show frequent on-off-on transitions ("bursting"), but in supplementary figures (1-S1A and 4-S1A), this behavior is seen in only ~8 of 54 traces. Are the main figure examples truly representative?

We acknowledge the reviewer's point. In Figure 1D, we selected some of the longest and most illustrative traces to highlight the bursting dynamics. We agree that the term "representative" might be misleading if interpreted as "average." We have updated the text to state "we show bursting traces" to more accurately reflect the selection.

(1.2) There are 8 videos, but I could not identify which is which.

Thank you for pointing this out. We have renamed the video files to clearly correspond to the figures and conditions they represent.

(2) Data Availability:

As noted above, the data should be shared. This is in accordance with eLife's policy: "Authors must make all original data used to support the claims of the paper, or that are required to reproduce them, available in the manuscript text, tables, figures or supplementary materials, or at a trusted digital repository (the latter is recommended). [...] eLife considers works to be published when they are posted as preprints, and expects preprints we review to meet the standards outlined here." Access to the time traces would have been helpful for reviewers.

We have now added the Github link for the code (https://github.com/naef-lab/suntag-analysis) and deposited the raw data (.ome.tif files) on Zenodo (10.5281/zenodo.17669332).

(3) Model Assumptions:

(3.1) The broad range of run-off times (Figure 3A) suggests stalling, which may be incompatible with the 'low-density' assumption used on the TASEP model, which essentially assumes that ribosomes do not bump into each other. This could impact the validity of the assumptions that ribosomes behave independently, elongate at constant speed (necessary for the continuum-limit approximation), and that the rate-limiting step is the initiation. How robust are the inferences to this assumption?

We agree that the deviation of waiting times from an exponential distribution (Figure 3 - figure supplement 2C) suggests the presence of stalling, which challenges the strict low-density assumption and constant elongation speed. We explicitly explored the robustness of our model to higher ribosome densities in simulations. As shown in Figure 2 - figure supplement 2, while the model accuracy for single parameters deteriorates at very high densities (overestimating density due to neglected interference), it remains robust for estimating global rates in the regime relevant to our data. We have expanded the discussion on the limitations of the low density and homogeneous elongation rate assumptions in the text (L404-408).

(3.2) Since all constructs share the same SunTag region, elongation rates should be identical there and diverge only in the variable region. This would affect $\gamma (t)$ and hence possibly affect the results. A brief discussion would be helpful.

This is a valid point. Currently, our model infers a single average elongation rate that effectively averages the behavior over the SunTag and the variable CDS regions. Modeling distinct rates for these regions would be a valuable extension but adds significant complexity. While our current "effective rate" approach might underestimate the magnitude of differences between reporters, it captures the global kinetic trend. We have added a brief discussion acknowledging this simplification (L408-412).

(3.3) A similar point applies to the Gillespie simulations: modeling the SunTag region with a shared elongation rate would be more accurate.

We agree. Simulating distinct rates for the SunTag and CDS would increase realism, though our current homogeneous simulations serve primarily to benchmark the inference framework itself. We have noted this as a potential future improvement (L413-414).

(3.4) Equation (13) assumes that switching between bursting and non-bursting states is much slower than the elongation time. First, this should be made explicit. Second, this is not quite true (~5 min elongation time on Figure 3-s2A vs ~5-15min switching times on Figure 1). It would be useful to show the intensity distribution at t=0 and compare it to the expected mixture distribution (i.e., a Poisson distribution + some extra 'N=0' cells). 

We thank the reviewer for this insightful comment. We have added a sentence to the text explicitly stating the assumption that switching dynamics are slower than the translation time. While the timescales are indeed closer than ideal (5 min vs. 5-15 min), this assumption allows for a tractable approximation of the initial conditions for the run-off inference. Comparing the intensity distribution at t=0 to a zero-inflated Poisson distribution is an excellent suggestion for validation, which we will consider for future iterations of the model.

(4) Microscopy Quantifications:

(4.1) Figure 1-S2A shows variable scFv-GFP expression across cells. Were cells selected for uniform expression in the analysis? Or is the SunTag assumed saturated? which would then need to be demonstrated. 

All cell lines used are monoclonal, and cells were selected via FACS for consistent average cytoplasmic GFP signal. We assume the SunTag is saturated based on the established characterization of the system by Tanenbaum et al. (2014), where the high affinity of the scFv-GFP ensures saturation at expression levels similar to ours.

(4.2) As translation proceeds, free scFv-GFP may become limiting due to the accumulation of mature SunTag-containing proteins. This would be difficult to detect (since mature proteins stay in the cytoplasm) and could affect intensity measurements (newly synthesized SunTag proteins getting dimmer over time).

This effect can occur with very long induction times. To mitigate this, we optimized the Doxycycline (Dox) incubation time for our harringtonine experiments to prevent excessive accumulation of mature protein. We also monitor the cytoplasmic background for granularity, which would indicate aggregation or accumulation.

(4.3) The statements "for some traces, the mRNA signal was lost before the run-off completion" (line 195) and "we observed relatively consistent fractions of translated transcripts and trace duration distributions across reporters" (line 340) should be supported by a supplementary figure.

The first statement is supported by Figure 2 - figure supplement 1, which shows representative run-off traces for all constructs, including incomplete ones.

The second statement regarding consistency is supported by the quantitative data in Figure 1E and G, which summarize the fraction of translated transcripts and trace durations across conditions.

(4.4) Measurements of single mature protein intensity $i_{MP}$:

(4.4.1) Since puromycin is used to disassemble elongating ribosomes, calibration may be biased by incomplete translation products (likely a substantial fraction, since the Dox induction is only 20min and RNAs need several minutes to be transcribed, exported, and then fully translated).

As mentioned in the “Live-cell imaging” paragraph, the imaging takes place 40 min after the end of Dox incubation. This provides ample time for mRNA export and full translation of the synthesized proteins. Consequently, the fraction of incomplete products generated by the final puromycin addition is negligible compared to the pool of fully synthesized mature proteins accumulated during the preceding hour.

(4.4.2) Line 519: "The intensity of each spot is averaged over the 100 frames". Do I understand correctly that you are looking at immobile proteins? What immobilizes these proteins? Are these small aggregates? It would be surprising that these aggregates have really only 1, 2, or 3 proteins, as suggested by Figure 1-S2A.

We are visualizing mature proteins that are specifically tethered to the actin cytoskeleton. This is achieved using a reporter where the RH1 domain is fused directly to the C-terminus of the Renilla protein (SunTag-Renilla-RH1). The RH1 domain recruits the endogenous Myosin Va motor, which anchors the protein to actin filaments, rendering it immobile. Since each Myosin Va motor interacts with one RH1 domain (and thus one mature protein), the resulting spots represent individual immobilized proteins rather than aggregates. We have now revised the text and Methods section to make this calibration strategy and the construct design clearer (L130-140).

(4.4.3) Estimating the average intensity $i_{MP}$ of single proteins all resides in the seeing discrete modes in the histogram of Figure 1-S2B, which is not very convincing. A complementary experiment, measuring *on the same microscope* the intensity of an object with a known number of GFP molecules (e.g., MS2-GFP labeled RNAs, or individual GEMs https://doi.org/10.1016/j.cell.2018.05.042 (only requiring a single transfection)) would be reassuring to convince the reader that we are not off by an order of magnitude.

While a complementary calibration experiment would be valuable, we believe our current estimate is robust because it is independently validated by our model. When we inferred i_MP as a free parameter in the HMM (Figure 5 - figure supplement 2B), the resulting value (10-15 a.u.) was remarkably consistent with our experimental calibration (14 ± 2 a.u.). We have clarified this independent validation in the text to strengthen the confidence in our quantification (L264-272).

(4.4.4) Further on the histogram in Figure 1-S2B:

- The gap between the first two modes is unexpectedly sharp. Can you double-check? It means that we have a completely empty bin between two of the most populated bins.

We have double-checked the data; the plot is correct, though the sharp gap is likely due to the small sample size (n=29).

- I am surprised not to see 3 modes or more, given that panel A shows three levels of intensity (the three colors of the arrows).

As noted below, brighter foci exist but fall outside the displayed range of the histogram.

- It is unclear what the statistical test is and what it is supposed to demonstrate.

The Student's t-test compares the means of the two identified populations to confirm they are statistically distinct intensity groups.

- I count n = 29, not 31. (The sample is small enough that the bars of the histogram show clear discrete heights, proportional to 1, 2, 3, 4, and 5 --adding up all the counts, I get 29). Is there a mistake somewhere? Or are some points falling outside of the displayed x-range?

You are correct. Two brighter data points fell outside the displayed range. The total number of foci in the histogram is 29. We have corrected the figure caption and the text accordingly.

(5) Miscellaneous Points: 

(5.1) Panel B in Figure 2-s1 appears to be missing.

The figure contains only one panel.

(5.2) In Equation (7), $l$ is not defined (presumably ribosome footprint length?). Instead, $J$ is defined right after eq (7), as if it were used in this equation.

Thank you for pointing this out, we have corrected it.

(5.3) Line 703, did you mean to write something else than "Equation 26" (since equation 26 is defined after)?

Yes, this was a typo. We have corrected the cross-reference.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Here, the authors aim to investigate the potential improvements of ANNs when used to explain brain data using top-down feedback connections found in the neocortex. To do so, they use a retinotopic and tonotopic organization to model each subregion of the ventral visual (V1, V2, V4, and IT) and ventral auditory (A1, Belt, A4) regions using Convolutional Gated Recurrent Units. The top-down feedback connections are inspired by the apical tree of pyramidal neurons, modeled either with a multiplicative effect (change of gain of the activation function) or a composite effect (change of gain and threshold of the activation function).

To assess the functional impact of the top-down connections, the authors compare three architectures: a brain-like architecture derived directly from brain data analysis, a reversed architecture where all feedforward connections become feedback connections and vice versa, and a random connectivity architecture. More specifically, in the brain-like model the visual regions provide feedforward input to all auditory areas, whereas auditory areas provide feedback to visual regions.

First, the authors found that top-down feedback influences audiovisual processing and that the brain-like model exhibits a visual bias in multimodal visual and auditory tasks. Second, they discovered that in the brain-like model, the composite integration of top-down feedback, similar to that found in the neocortex, leads to an inductive bias toward visual stimuli, which is not observed in the feedforward-only model. Furthermore, the authors found that the brain-like model learns to utilize relevant stimuli more quickly while ignoring distractors. Finally, by analyzing the activations of all hidden layers (brain regions), they found that the feedforward and feedback connectivity of a region could determine its functional specializations during the given tasks.

Strengths:

The study introduces a novel methodology for designing connectivity between regions in deep learning models. The authors also employ several tasks based on audiovisual stimuli to support their conclusions. Additionally, the model utilizes backpropagation of error as a learning algorithm, making it applicable across a range of tasks, from various supervised learning scenarios to reinforcement learning agents. Conversely, the presented framework offers a valuable tool for studying top-down feedback connections in cortical models. Thus, it is a very nice study that also can give inspiration to other fields (machine learning) to start exploring new architectures.

We thank the reviewer for their accurate summary of our work and their kind assessment of its strengths.

Weaknesses:

Although the study explores some novel ideas on how to study the feedback connections of the neocortex, the data presented here are not complete in order to propose a concrete theory of the role of top-down feedback inputs in such models of the brain.

(1) The gap in the literature that the paper tries to fill in the ability of DL algorithms to predict behavior: "However, there are still significant gaps in most deep neural networks' ability to predict behavior, particularly when presented with ambiguous, challenging stimuli." and "[...] to accurately model the brain."

It is unclear to me how the presented work addresses this gap, as the only facts provided are derived from a simple categorization task that could also be solved by the feedforward-only model (see Figures 4 and 5). In my opinion, this statement is somewhat far-fetched, and there is insufficient data throughout the manuscript to support this claim.

We can see now that the way the introduction was initially written led to some confusion about our goal in this study. Our goal here was not to demonstrate that top-down feedback can enable superior matches to human behaviour. Rather, our goal was to determine if top-down feedback had any real implications for processing ambiguous stimuli. The sentence that the reviewer has highlighted was intended as an explanation for why top-down feedback, and its impact on ambiguous stimuli, might be something one would want to examine for deep neural networks. But, here, we simply wanted to (1) provide an overview of the code base we have created, (2) demonstrate that top-down feedback does impact the processing of ambiguous stimuli.

We agree with the reviewer that if our goal was to improve our ability to predict behaviour, then there was a big gap in the evidence we provided here. But, this was not our goal, and we believe that the data we provide here does convincingly show that top-down feedback has an impact on processing of ambiguous stimuli. We have updated the text in the introduction to make our goals more clear for the reader and avoid this misunderstanding of what we were trying to accomplish here. Specifically, the end of the introduction is changed to:

“To study the effect of top-down feedback on such tasks, we built a freely available code base for creating deep neural networks with an algorithmic approximation of top-down feedback. Specifically, top-down feedback was designed to modulate ongoing activity in recurrent, convolutional neural networks. We explored different architectural configurations of connectivity, including a configuration based on the human brain, where all visual areas send feedforward inputs to, and receive top-down feedback from, the auditory areas. The human brain-based model performed well on all audiovisual tasks, but displayed a unique and persistent visual bias compared to models with only driving connectivity and models with different hierarchies. This qualitatively matches the reported visual bias of humans engaged in audio-visual tasks. Our results confirm that distinct configurations of feedforward/feedback connectivity have an important functional impact on a model's behavior. Therefore, top-down feedback captures behaviors and perceptual preferences that do not manifest reliably in feedforward-only networks. Further experiments are needed to clarify whether top-down feedback helps an ANN fit better to neural data, but the results show that top-down feedback affects the processing of stimuli and is thus a relevant feature that should be considered for deep ANN models in computational neuroscience more broadly.”

(2) It is not clear what the advantages are between the brain-like model and a feedforward-only model in terms of performance in solving the task. Given Figures 4 and 5, it is evident that the feedforward-only model reaches almost the same performance as the brain-like model (when the latter uses the modulatory feedback with the composite function) on almost all tasks tested. The speed of learning is nearly the same: for some tested tasks the brain-like model learns faster, while for others it learns slower. Thus, it is hard to attribute a functional implication to the feedback connections given the presented figures and therefore the strong claims in the Discussion should be rephrased or toned down.

Again, we believe that there has been a misunderstanding regarding the goals of this study, as we are not trying to claim here that there are performance advantages conferred by top-down feedback in this case. Indeed, we share the reviewer’s assessment that the feedforward only model seems to be capable of solving this task well. To reiterate: our goal here was to demonstrate that top-down feedback alters the computations in the network and, thus, has distinct effects on behaviour that need to be considered by researchers who use deep networks to model the brain. But we make no claims of “superiority” of the brain-like model.

In-line with this, we’re not completely sure which claims in the discussion the reviewer is referring to. We note that we were quite careful in our claims. For example, in the first section of the discussion we say:

“Altogether, our results demonstrate that the distinction between feedforward and feedback inputs has clear computational implications, and that ANN models of the brain should therefore consider top-down feedback as an important biological feature.”

And later on:

“In summary, our study shows that modulatory top-down feedback and the architectural diversity enabled by it can have important functional implications for computational models of the brain. We believe that future work examining brain function with deep neural networks should therefore consider incorporating top-down modulatory feedback into model architectures when appropriate.”

If we have missed a claim in the discussion that implies superiority of the brain-like model in terms of task performance we would be happy to change it.

(3) The Methods section lacks sufficient detail. There is no explanation provided for the choice of hyperparameters nor for the structure of the networks (number of trainable parameters, number of nodes per layer, etc). Clarifying the rationale behind these decisions would enhance understanding. Moreover, since the authors draw conclusions based on the performance of the networks on specific tasks, it is unclear whether the comparisons are fair, particularly concerning the number of trainable parameters. Furthermore, it is not clear if the visual bias observed in the brain-like model is an emerging property of the network or has been created because of the asymmetries in the visual vs. auditory pathway (size of the layer, number of layers, etc).

We thank the reviewer for raising this issue, and want to provide some clarifications: First, the number of trainable parameters are roughly equal, since we were only switching the direction of connectivity (top-down versus bottom-up), not the number of connections. We confirmed the biggest difference in size is between models with composite and multiplicative feedback; models with composite feedback have roughly ~1K more parameters, and all models are within the 280K parameter range. We now state this in the methods.

Second, because superior performance was not the goal of this study, as stated above, we conducted limited hyperparameter tuning. Given the reviewer’s comment, we wondered whether this may have impacted our results. Therefore, we explored different hyperparameters for the model during the multimodal auditory tasks, which show the clearest example of the visual dominance in the brainlike model (Figure 3).

We explored different hidden state sizes, learning rates and processing times, and examined whether the core results were different. We found that extremely high learning rates (0.1) destabilize all models and that some models perform poorly under different processing times. But overall, the core results are evident across all hyperparameters where the models learn i.e the different behaviors of models with different connectivities and the visual dominance observed in the brainlike model. We now provide these results in a supplementary figure (Fig. S2, showing larger models trained with different learning rates, and Fig S3, which shows the effect of processing time on AS task performance).

Reviewer #2 (Public review):

Summary:

This work addresses the question of whether artificial deep neural network models of the brain could be improved by incorporating top-down feedback, inspired by the architecture of the neocortex.

In line with known biological features of cortical top-down feedback, the authors model such feedback connections with both, a typical driving effect and a purely modulatory effect on the activation of units in the network.

To assess the functional impact of these top-down connections, they compare different architectures of feedforward and feedback connections in a model that mimics the ventral visual and auditory pathways in the cortex on an audiovisual integration task.

Notably, one architecture is inspired by human anatomical data, where higher visual and auditory layers possess modulatory top-down connections to all lower-level layers of the same modality, and visual areas provide feedforward input to auditory layers, whereas auditory areas provide modulatory feedback to visual areas.

First, the authors find that this brain-like architecture imparts the models with a light visual bias similar to what is seen in human data, which is the opposite in a reversed architecture, where auditory areas provide a feedforward drive to the visual areas.

Second, they find that, in their model, modulatory feedback should be complemented by a driving component to enable effective audiovisual integration, similar to what is observed in neural data.

Last, they find that the brain-like architecture with modulatory feedback learns a bit faster in some audiovisual switching tasks compared to a feedforward-only model.

Overall, the study shows some possible functional implications when adding feedback connections in a deep artificial neural network that mimics some functional aspects of visual perception in humans.

Strengths:

The study contains innovative ideas, such as incorporating an anatomically inspired architecture into a deep ANN, and comparing its impact on a relevant task to alternative architectures.

Moreover, the simplicity of the model allows it to draw conclusions on how features of the architecture and functional aspects of the top-down feedback affect the performance of the network.

This could be a helpful resource for future studies of the impact of top-down connections in deep artificial neural network models of the neocortex.

We thank the reviewer for their summary and their recognition of the innovative components and helpful resources therein.

Weaknesses:

Overall, the study appears to be a bit premature, as several parts need to be worked out more to support the claims of the paper and to increase its impact.

First, the functional implication of modulatory feedback is not really clear. The "only feedforward" model (is a drive-only model meant?) attains the same performance as the composite model (with modulatory feedback) on virtually all tasks tested, it just takes a bit longer to learn for some tasks, but then is also faster at others. It even reproduces the visual bias on the audiovisual switching task. Therefore, the claims "Altogether, our results demonstrate that the distinction between feedforward and feedback inputs has clear computational implications, and that ANN models of the brain should therefore consider top-down feedback as an important biological feature." and "More broadly, our work supports the conclusion that both the cellular neurophysiology and structure of feed-back inputs have critical functional implications that need to be considered by computational models of brain function" are not sufficiently supported by the results of the study. Moreover, the latter points would require showing that this model describes neural data better, e.g., by comparing representations in the model with and without top-down feedback to recorded neural activity.

To emphasize again our specific claims, we believe that our data shows that top-down feedback has functional implications for deep neural network behaviour, not increased performance or neural alignment. Indeed, our results demonstrate that top-down feedback alters the behaviour of the networks, as shown by the differences in responses to various combinations of ambiguous stimuli. We agree with the reviewer that if our goal was to claim either superior performance on these tasks, or better fit to neural data, we would need to actually provide data supporting that claim.

Given the comments from the reviewer, we have tried to provide more clarity in the introduction and discussion regarding our claims. In particular, we now highlight that we are not trying to demonstrate that the models with top-down feedback exhibit superior performance or better fit to neural data.

As one final note, yes, the reviewer understood correctly that the “only feedforward” model is a model with only driving inputs. We have renamed the feedforward-only models to drive only models and added additional emphasis in the text to ensure that the distinction is clear for all readers.

Second, the analyses are not supported by supplementary material, hence it is difficult to evaluate parts of the claims. For example, it would be helpful to investigate the impact of the process time after which the output is taken for evaluation of the model. This is especially important because in recurrent and feedback models the convergence should be checked, and if the network does not converge, then it should be discussed why at which point in time the network is evaluated.

This is an excellent point, and we thank the reviewer for raising it. We allowed the network to process the stimuli for seven time-steps, which was enough for information from any one region to be transmitted to any other. We found in some initial investigations that if we shortened the processing time some seeds would fail to solve the task. But, based on the reviewer’s comment, we have now also run additional tests with longer processing times for the auditory tasks where we see the clearest visual bias (Figure 3). We find that different process times do not change the behavioral biases observed in our models, but may introduce difficulties ignoring visual stimuli for some models. Thus, while process time is an important hyperparameter for optimal performance of the model, the central claim of the paper remains. We include this new data in a supplementary figure S3.

Third, the descriptions of the models in the methods are hard to understand, i.e., parameters are not described and equations are explained by referring to multiple other studies. Since the implications of the results heavily rely on the model, a more detailed description of the model seems necessary.

We agree with the reviewer that the methods could have been more thorough. Therefore, we have greatly expanded the methods section. We hope the model details are now more clear.

Lastly, the discussion and testable predictions are not very well worked out and need more details. For example, the point "This represents another testable prediction flowing from our study, which could be studied in humans by examining the optical flow (Pines et al., 2023) between auditory and visual regions during an audiovisual task" needs to be made more precise to be useful as a prediction. What did the model predict in terms of "optic flow", how can modulatory from simple driving effect be distinguished, etc.

We see that the original wording of this prediction was ambiguous, thank you for pointing this out. In the study highlighted (Pines et al., 2023) the authors use an analysis technique for measuring information flow between brain regions, which is related to analysis of optical flow in images, but applied to fMRI scans. This is confusing given the current study, though. Therefore, we have changed this sentence to make clear that we are speaking of information flow here. 

Reviewer #3 (Public review):

Summary:

This study investigates the computational role of top-down feedback in artificial neural networks (ANNs), a feature that is prevalent in the brain but largely absent in standard ANN architectures. The authors construct hierarchical recurrent ANN models that incorporate key properties of top-down feedback in the neocortex. Using these models in an audiovisual integration task, they find that hierarchical structures introduce a mild visual bias, akin to that observed in human perception, not always compromising task performance.

Strengths:

The study investigates a relevant and current topic of considering top-down feedback in deep neural networks. In designing their brain-like model, they use neurophysiological data, such as externopyramidisation and hierarchical connectivity. Their brain-like model exhibits a visual bias that qualitatively matches human perception.

We thank the reviewer for their summary and evaluation of our paper’s strengths.

Weaknesses:

While the model is brain-inspired, it has limited bioplausibility. The model assumes a simplified and fixed hierarchy. In the brain with additional neuromodulation, the hierarchy could be more flexible and more task-dependent.

We agree, there are still many facets of top-down feedback that we have not captured here, and the modulation of hierarchy is an interesting example. We have added some consideration of this point to the limitations section of the discussion.

While the brain-like model showed an advantage in ignoring distracting auditory inputs, it struggled when visual information had to be ignored. This suggests that its rigid bias toward visual processing could make it less adaptive in tasks requiring flexible multimodal integration. It hence does not necessarily constitute an improvement over existing ANNs. It is unclear, whether this aspect of the model also matches human data. In general, there is no direct comparison to human data. The study does not evaluate whether the top-down feedback architecture scales well to more complex problems or larger datasets. The model is not well enough specified in the methods and some definitions are missing.

We agree with the reviewer that we have not demonstrated anything like superior performance (since the brain-like network is quite rigid, as noted) nor have we shown better match to human data with the brain-like network. This was not our intended claim. Rather, we demonstrated here simply that top-down feedback impacts behavior of the networks in response to ambiguous stimuli. We have now added statements to the introduction and discussion to make our specific claims (which are supported by our data, we believe) clear.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

I believe that the work is very nice but not so mature at this stage. Below, you can find some comments that eventually could improve your manuscript.

(1) Intro, last sentence: "Therefore, top-down feedback is a relevant feature that should be considered for deep ANN models in computational neuroscience more broadly." I don't understand what the authors refer to with this sentence. There are numerous models (deep ANNs) that have been used to model the neural activity and are much simpler than the one proposed here which contains very complex models and connectivity. Although I do agree that the top-down connections are very important there is no data to support their importance for modeling the brain.

Respectfully, we disagree with the reviewer that we don’t provide data to demonstrate the importance of top-down feedback for modelling. Indeed, we provided a great deal of data to show that top-down feedback in the networks has real functional implications for behaviour, e.g., it can induce a human-like visual bias. Thus, top-down feedback is a factor that one should care about when modelling the brain. But, we agree with the reviewer that more demonstration of the utility of using top-down feedback for achieving better fits to neural data would be an important next step. 

(2) I suggest adding some extra supplementary simulations where, for example, the number of data for visual and auditory pathways is equal in size (i.e., the same number of examples), the number of layers is identical (3 per pathway), and also the number of parameters. Doing this would help strengthen the claims presented in the paper.

In fact, all of the hyperparameters the reviewer mentions here were identical for the different networks, so the experiments the reviewer is requesting here were already part of the paper. We now clarify this in the text.

(3) Results: I suggest adding Tables with quantifications of the presented results. For example, best performance, epochs to converge, etc. As it is now, it is very hard to follow the evidence shown in Figures.

This is a good suggestion, we have now added this table to the start of the supplemental figures.

(4) Figure 2e, 3e: Although VS3, and AS3 have been used only for testing, the plot shows alignments with respect to training epochs. The authors should clarify in the Methods if they tested the network with all intermediate weights during VS1/VS2 or AS1/AS2 training.

Testing scenarios in this context meant that the model was never shown the scenario/task during training, but the models were indeed evaluated on the VS3 and AS3 after each training epoch. We have added clarifications to the figure legends.

(5) Methods: It would be beneficial to discuss how specific hyperparameters were selected based on prior research, empirical testing, or theoretical considerations. Also, it is not clear how the alignment (visual or audio) is calculated. Do the authors use the examples that have been classified correctly for both stimuli or do they exclude those from the analysis (maybe I have missed it).

As noted above, because superior performance was not the goal of this study, we conducted limited hyperparameter tuning. But we have extended the results with additional hyperparameter tuning in a supplementary figure, and describe the hyperparameter choices more thoroughly in the methods. As well, all data includes all model responses, regardless of whether they were correct or not. We now clarify this in the methods.

(6) Code: The code repository lacks straightforward examples demonstrating how to utilize the modeling approach. Given that it is referred to as a "framework", one would expect it to facilitate easy integration into various models and tasks. Including detailed instructions or clear examples would significantly improve usability and help users effectively apply the proposed methodology.

We agree with the reviewer, this would be beneficial. We have revised the README of the codebase to explain the model and its usage more clearly and included an interactive jupyter notebook with example training on MNIST.

Some minor comments are given below. Generally speaking, the Figures need to be more carefully checked for consistent labels, colors, etc.

(1) Page 4, 1st paragraph - grammar correction: "a larger infragranular layer" or "larger infragranular layers"

Thank you for catching this, we have fixed the text.

(2) Page 4, 2nd para - rephrase: "In three additional control ANNs" → "In the third additional control ANN"

In fact, we did mean three additional control ANNs, each one representing a different randomized connectivity profile. We now clarify this in the text and provide the connectivity of the two other random graphs in the supplemental figures.

(3) Page 4, VAE acronym needs to be defined before its first use

The variational autoencoder is introduced by its full name in the text now.

(4) Page 4: Fig. 2c reference should be Fig. 2b, Fig. 2d should be Fig. 2c, Fig. 2b should be Fig. 2d, VS4; Fig. 2b, bottom should be VS4; Fig. 2f, Fig. 2f to Fig. 2g. Double check the Figure references in the text. Here is very confusing for the reader.

We have now fixed this, thank you for catching it.

(5) Page 5, 1st para: "Altogether, our results demonstrated both" → "Altogether, our results demonstrated that both"

This has been updated.

(6) Figure 2: In the e and g panels the x label is missing.

This was actually because the x-axis were the same across the panels, but we see how this was unclear, so we have updated the figure.

(7) Figure 3: There is no panel g (the title is missing); In panels b, c, e, and g the y label is missing, and in panels e and g the x label is missing. Also, the Feedforward model is shown in panel g but it is introduced later in the text. Please remove it from Figure 3. Also in legend: "AV Reverse graph" → "Reverse graph". Also, "Accuracy" and "Alignment" should be presented as percentages (as in Figure 2).

This has been corrected.

(8) Figure 4; x labels are missing.

As with point (6), this was actually because the x-axis were the same across the panels, but we see how this was unclear, so we have updated the figure.

(9) Page 7; I can’t find the cited Figure S1.

Apologies, we have added the supplemental figure (now as S4). It shows the results of models with multiplicative feedback on the task in Fig 5 (as opposed to models with composite feedback shown in the main figure).

Reviewer #2 (Recommendations for the authors):

(1) Discussion Section 3.1 is only a literature review, and does not really add any value.

Respectfully, we think it is important to relate our work to other computational work on the role of top-down feedback, and to make clear what our specific contribution is. But, we have updated the text to try to place additional emphasis on our study’s contribution, so that this section is more than just a literature review.

“Our study adds to this previous work by incorporating modulatory top-down feedback into deep, convolutional, recurrent networks that can be matched to real brain anatomy. Importantly, using this framework we could demonstrate that the specific architecture of top-down feedback in a neural network has important computational implications, endowing networks with different inductive biases.”

(2) Including ipython notebooks and some examples would be great to make it easier to use the code.

We now provide a demo of how to use the code base in a jupyter notebook.

(3) The description of the model is hard to comprehend. Please name and describe all parameters. Also, a figure would be great to understand the different model equations.

We have added definitions of all model terms and parameters.

(4) The terminology is not really clear to me. For example "The results further suggest that different configurations of top-down feedback make otherwise identically connected models functionally distinct from each other and from traditional feedforward only recurrent models." The feedforward and only recurrent seem to contradict each other. Would maybe driving and modulatory be a better term here? I also saw in the code that you differentiate between three types of inputs, modulatory, threshold offset and basal (like feedforward). How about you only classify connections based on these three type? I was also confused about the feedforward only model, because I was unsure whether it is still feedback connections but with "basal" quality, or whether feedback connections between modalities and higher-to-lower level layers were omitted altogether.

We take the reviewer’s point here. To clarify this, we have updated the text to refer to “driving only” rather than “feedforward only”, to make it obvious that what we change in these models is simply whether the connection has any modulatory impact on the activity. 

(5) "incorporating it into ANNs can affect their behavior and help determine the solutions that the network can discover." -> Do you mean constrain? Overall, I did not really get this point.

Yes, we mean that it constrains the solutions that the network is likely to discover.

(6) "ignore the auditory inputs when they visual inputs were unambiguous" -> the not they

This has been fixed. Thank you for catching it.

(7) xlabel in Figure 4 is missing.

This has been fixed, thank you for catching it.

Reviewer #3 (Recommendations for the authors):

Major:

(1) How alignment is computed is not defined. In addition to a proper definition in the methods section, it would be nice to briefly define it when it first appears in the results section.

We’ve added an explicit definition of how alignment is calculated in the methods and emphasized the calculation when its first explained in the results

(2) A connectivity matrix for the feedforward-only model is missing and could be added.

We have added this to Figure 1.

(3) The connectivity matrix for each random model should also be shown.

We’ve shown each of the random model configurations in the new supplemental figure S1.

(4) Initial parameters are not defined, such as W, b etc. A table with all model parameters would be great.

We have added a table to the methods listing all of the parameters.

(5) Would be nice to show the t-sne plots (not just the NH score) for each model and each task in the appendix.

We can provide these figures on request. They massively increase the file size of the paper pdf, as there’s 49 of them for each task and each model, 980 in total. An example t-SNE plot is provided in figure 6.

Minor:

(1) Page 4:

"we refer to this as Visual-dominant Stimulus case 1, or VS1; Fig. 1a, top)." This should be Fig. 2a.

(2) "In stimulus condition VS1, all of the models were able to learn to use the auditory clues to disambiguate the images (Fig. 2c)."

This should be Fig. 2b.

(3) "In comparison, in VS2, we found that the brainlike model learned to ignore distracting audio inputs quickly and consistently compared to the random models, and a bit more rapidly than the auditory information (Fig 2d)."

This should be Fig. 2c.

(4) "VS3; Fig. 2b, top"

This should be Fig. 2d

(5) "while all other models had to learn to do so further along in training (Fig. 2e)."

It is not stated explicitly, but this suggests that the image-aligned target was considered correct, and that weight updates were happening.

(6) "VS4; Fig. 2b, bottom"

This should be Fig. 2f

(7) "adept at learning (Fig. 2f)."

This should be Fig. 2g

(8) Figure 3:b,c,e y-labels are missing

3f: both x and y labels are missing

(9) Figure labeling in the text is not consistent (Fig. 1A versus Fig. 2a)

(10) Doubled "the" in ""This shows that the inductive bias towards vision in the brainlike model depended on the presence of the multiplicative component of the the feedback"

(11) Page 9 Figure 6: The caption says b shows the latent spaces for the VS2 task, whereas the main text refers to 6b as showing the latent space for the AS2 task. Please correct which task it is.

(12) Methods 4.1 page 13

"which is derived from the feedback input (h_{l−1})"

This should be h_{l+1}

(13) r_l, u_l, u and c are not defined to which aspects of the model they refer to

Even though this is based on a previous model, the methods section should completely describe the model.

Equations 1,2,3: the notation [x;y] is unclear and should be defined.

Equation 5: u should probably be u_l.

(14) Page 14 typo: externopyrmidisation.

(15) It is confusing to use different names for the same thing: the all-feedforward model, the all feedforward network, the feedforward network, and the feedforward-only model are probably all the same? Consistent naming would help here.

Thank you for the detailed comments! We’ve fixed the minor errors and renamed the feedforward models to drive-only models.

Reviewer #1 (Public review):

Summary:

This manuscript presents findings on the adaptation mechanisms of Saccharomyces cerevisiae under extreme stress conditions. The authors try to generalize this to adaptation to stress tolerance. A major finding is that S. cerevisiae evolves a quiescence-like state with high trehalose to adapt to freeze-thaw tolerance independent of their genetic background. The manuscript is comprehensive, and each of the conclusions is well supported by careful experiments.

Strengths:

This is excellent interdisciplinary work.

I have commented on the response of the authors, in-line, below. This is to maintain the conversation thread with the authors.

Comment 1:

Earlier papers have shown that loss of ribosomal proteins, that slow growth, leads to better stress tolerance in S. cerevisiae. Given this, isn't it expected that any adaptation that slows down growth would, overall, increase stress tolerance? Even for other systems, it has been shown that slowing down growth (by spore formation in yeast or bacteria/or dauer formation in C. elegans) is an effective strategy to combat stress and hence is a likely route to adaptation. The authors stress this as one of the primary findings. I would like the authors to explain their position, detailing how their findings are unexpected in the context of the literature.

Response:

We agree that the link between slower growth and higher stress tolerance has been well stud-ied. What is distinctive here is that repeated, near-lethal freeze-thaw selected not only for a tolerant/quiescent-like state but also for a shorter lag on re-entry. In this regime of freeze-thaw-regrowth, cells that are tolerant but slow to restart would be outcompeted by naive fast growers. Our quiescence-based selection simulations reproduce exactly this constraint. We have added this explanation to the Results to make clear that the novelty is the co-evolution of a tolerant, trehalose-rich state together with rapid regrowth under an alternating regime.

Comment to Response: I get the point. I believe that the outcome is highly dependent on how selection pressure is administered. So, generalizing this over all stresses (as done in the abstract) may not be accurate.

Comment 2:

Convergent evolution of traits: I find the results unsurprising. When selecting for a trait, if there is a major mode to adapt to that stress, most of the strains would adapt to that mode, independent of the route. According to me, finding out this major route was the objective of many of the previous reports on adaptive evolution. The surprising part in the previous papers (on adaptive evolution of bacteria or yeast) was the resampling of genes that acquired mutations in multiple replicates of an evolution experiments, providing a handle to understand the major genetic route or the molecular mechanism that guides the adaptation (for example in this case it would be - what guides the over-accumulation of trehalose). I fail to understand why the authors find the results surprising, and I would be happy to understand that from the authors. I may have missed something important.

Response:

Our surprise was precisely that we did not see the classical pattern of "phenotypic convergence + repeated mutations in the same locus/module." All independently evolved lines converged on a trehalose-rich, mechanically reinforced, quiescence-like phenotype, but population sequencing across lines did not reveal a single repeatedly hit gene or small shared pathway, even when we increased selection stringency (1-3 freeze-thaw cycles per round). We have now stated in the manuscript that this decoupling (strong phenotypic convergence, non-overlapping genetic routes) is the central inference: selection is acting on a physiologically defined state that multiple genotypes can reach.

Comment to Response: You indeed saw a case of phenotypic convergence. Converging towards trehalose-rich, mechanically reinforced, quiescent like - are phenotypes that have converged. This is what prevented lysis. The same locus need not be mutated over and over again, if the trehalose pathway is controlled by many processes (it is, and many are still unknown as I point in the next comment), many different mutations on different loci can result in the same regulation! I do not see the decoupling between phenotypic convergence and decoupling of genetic mutations as surprising or novel; molecular and cellular biology is replete with such examples where deletion(mutation) of hundreds of different genes can have the same phenotypic outcome (yeast deletion library screening, indirect effects etc). If this was a specific question unsolved in evolutionary biology, then the matter is different.

A minor point: Here I would also like to point out that the three phenotypes you measure may be linked to each other, so their independent evolution may just be a cause-effect relationship. For example Trehalose accumulation may drive the other two. This has not been deconvoluted in this manuscript.

Comment 3:

Adaptive evolution would work on phenotype, as all of selective evolution is supposed to. So, given that one of the phenotypes well-known in literature to allow free-tolerance is trehalose accumulation, I think it is not surprising that this trait is selected. For me, this is not a case of "non-genetic" adaptation as the authors point out: it is likely because perturbation of many genes can individually result in the same outcome - up-regulation of trehalose accumulation. Thereby, although the adaptation is genetic, it is not homogeneous across the evolving lines - the end result is. Do the authors check that the trait is actually a non-genetic adaptation, i.e., if they regrow the cells for a few generations without the stress, the cells fall back to being similarly only partially fit to freeze-thaw cycles? Additionally, the inability to identify a network that is conserved in the sequencing does not mean that there is no regulatory pathway. A large number of cryptic pathways may exist to alter cellular metabolic states.<br /> This is a point in continuation of point #2, and I would like to understand what I have missed.

Response:

We agree, and we have removed the wording "non-genetic adaptation." The evolved populations retain high survival even after regrowth for {greater than or equal to}25 generations without freeze-thaw, so the adaptation is clearly genetically maintained. What our data show is that there is no single genetic route to the shared phenotype; different mutations can all drive cells into the same trehalose-rich, quiescence-like, mechanochemically reinforced state. We now describe this as "genetic diversification with phenotypic convergence."

Comment to Response: While the last term does explain what is going on, isn't it an outcome that is routine in cell biology (as pointed out in my previous comment to your response)? I apologize for not understanding the punchline that is provided in the last few sentences of the abstract.

Comment 4:

To propose the convergent nature, it would be important to check for independently evolved lines and most probably more than 2 lines. It is not clear from their results section if they have multiple lines that have evolved independently.

Response:

We indeed evolved four independent lines and maintained two independent controls. We have added this information at the start of the Results so that the level of replication is immediately clear.

Comment to Response: Previous large scale studies have done hundreds of sequencing to oversample the pathway and figure out reproducible loci. With pooled sequencing (as mentioned below) and only 4 sample evolution, I am not sure that you would have the power in your study to conclude in the loci are sampled or not! If there were 10 gene LOFs that control Trehalose levels (which you can find from the published deletion screening experiment), then four of the experiments are likely to go through one of these routes; what is the likely event that you would identify the same route in two pools? It is unlikely, and therefore, sequencing of 4 pools cannot tell you if the mutation path is repeatedly sampled or not.

Comment 5:

For the genomic studies, it is not clear if the authors sequenced a pool or a single colony from the evolved strains. This is an important point, since an average sequence will miss out on many mutations and only focus on the mutations inherited from a common ancestral cell. It is also not clear from the section.

Response:

We sequenced population samples from the evolved lines. Our specific question was whether independently evolved lines would show the same high-frequency genetic solution, as is often seen in parallel evolution. Pool sequencing may under-sample rare/private variants, but it is appropriate for detecting such shared, high-frequency routes - and we do not find any. We have clarified this rationale in the Methods/Results.

Comment to Response: Please provide the average sequencing depth of each sequencing run. It is essential to understand the power of this study in identifying mutations. What coverage was used in Xgenome size?

Author response:

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

We thank the editor and the reviewers for the detailed and constructive comments. In revising the manuscript we have: (i) clarified what is new relative to prior stress tolerance work, (ii) made explicit that we observe phenotypic convergence without a shared genetic route, (iii) stated upfront that we evolved four independent lines plus two controls, and (iv) corrected figure legends, statistics, and the missing citations. Below we respond point-by-point.

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript presents findings on the adaptation mechanisms of Saccharomyces cerevisiae under extreme stress conditions. The authors try to generalize this to adaptation to stress tolerance. A major finding is that S. cerevisiae evolves a quiescence-like state with high trehalose to adapt to freeze-thaw tolerance independent of their genetic background. The manuscript is comprehensive, and each of the conclusions is well supported by careful experiments.

Strengths:

This is excellent interdisciplinary work.

Weaknesses:

I have questions regarding the overall novelty of the proposal, which I would like the authors to explain.

(1) Earlier papers have shown that loss of ribosomal proteins, that slow growth, leads to better stress tolerance in S. cerevisiae. Given this, isn’t it expected that any adaptation that slows down growth would, overall, increase stress tolerance? Even for other systems, it has been shown that slowing down growth (by spore formation in yeast or bacteria/or dauer formation in C. elegans) is an effective strategy to combat stress and hence is a likely route to adaptation. The authors stress this as one of the primary findings. I would like the authors to explain their position, detailing how their findings are unexpected in the context of the literature.

We agree that the link between slower growth and higher stress tolerance has been well studied. What is distinctive here is that repeated, near-lethal freeze–thaw selected not only for a tolerant/quiescent-like state but also for a shorter lag on re-entry. In this regime of freeze–thaw–regrowth, cells that are tolerant but slow to restart would be outcompeted by naive fast growers. Our quiescence-based selection simulations reproduce exactly this constraint. We have added this explanation to the Results to make clear that the novelty is the co-evolution of a tolerant, trehaloserich state together with rapid regrowth under an alternating regime.

(2) Convergent evolution of traits: I find the results unsurprising. When selecting for a trait, if there is a major mode to adapt to that stress, most of the strains would adapt to that mode, independent of the route. According to me, finding out this major route was the objective of many of the previous reports on adaptive evolution. The surprising part in the previous papers (on adaptive evolution of bacteria or yeast) was the resampling of genes that acquired mutations in multiple replicates of an evolution experiments, providing a handle to understand the major genetic route or the molecular mechanism that guides the adaptation (for example in this case it would be - what guides the overaccumulation of trehalose). I fail to understand why the authors find the results surprising, and I would be happy to understand that from the authors. I may have missed something important.

Our surprise was precisely that we did not see the classical pattern of “phenotypic convergence + repeated mutations in the same locus/module.” All independently evolved lines converged on a trehalose-rich, mechanically reinforced, quiescence-like phenotype, but population sequencing across lines did not reveal a single repeatedly hit gene or small shared pathway, even when we increased selection stringency (1–3 freeze–thaw cycles per round). We have now stated in the manuscript that this decoupling (strong phenotypic convergence, non-overlapping genetic routes) is the central inference: selection is acting on a physiologically defined state that multiple genotypes can reach.

(3) Adaptive evolution would work on phenotype, as all of selective evolution is supposed to. So, given that one of the phenotypes well-known in literature to allow free-tolerance is trehalose accumulation, I think it is not surprising that this trait is selected. For me, this is not a case of ”non-genetic” adaptation as the authors point out: it is likely because perturbation of many genes can individually result in the same outcome - up-regulation of trehalose accumulation. Thereby, although the adaptation is genetic, it is not homogeneous across the evolving lines - the end result is. Do the authors check that the trait is actually a non-genetic adaptation, i.e., if they regrow the cells for a few generations without the stress, the cells fall back to being similarly only partially fit to freeze-thaw cycles? Additionally, the inability to identify a network that is conserved in the sequencing does not mean that there is no regulatory pathway. A large number of cryptic pathways may exist to alter cellular metabolic states.

This is a point in continuation of point #2, and I would like to understand what I have missed.

We agree, and we have removed the wording “non-genetic adaptation.” The evolved populations retain high survival even after regrowth for ≥25 generations without freeze–thaw, so the adaptation is clearly genetically maintained. What our data show is that there is no single genetic route to the shared phenotype; different mutations can all drive cells into the same trehalose-rich, quiescencelike, mechanochemically reinforced state. We now describe this as “genetic diversification with phenotypic convergence.”

(4) To propose the convergent nature, it would be important to check for independently evolved lines and most probably more than 2 lines. It is not clear from their results section if they have multiple lines that have evolved independently.

We indeed evolved four independent lines and maintained two independent controls. We have added this information at the start of the Results so that the level of replication is immediately clear.

(5) For the genomic studies, it is not clear if the authors sequenced a pool or a single colony from the evolved strains. This is an important point, since an average sequence will miss out on many mutations and only focus on the mutations inherited from a common ancestral cell. It is also not clear from the section.

We sequenced population samples from the evolved lines. Our specific question was whether independently evolved lines would show the same high-frequency genetic solution, as is often seen in parallel evolution. Pool sequencing may under-sample rare/private variants, but it is appropriate for detecting such shared, high-frequency routes — and we do not find any. We have clarified this rationale in the Methods/Results.

Reviewer #2 (Public review):

Summary:

The authors used experimental evolution, repeatedly subjecting Saccharomyces cerevisiae populations to rapid liquid-nitrogen freeze-thaw cycles while tracking survival, cellular biophysics, metabolite levels, and whole-genome sequence changes. Within 25 cycles, viability rose from ~2 % to ~70 % in all independent lines, demonstrating rapid and highly convergent adaptation despite distinct starting genotypes. Evolved cells accumulated about threefold more intracellular trehalose, adopted a quiescence-like phenotype (smaller, denser, non-budding cells), showed cytoplasmic stiffening and reduced membrane damage, and re-entered growth with shorter lag traits that together protected them from ice-induced injury. Whole-genome sequencing indicated that multiple genetic routes can yield the same mechano-chemical survival strategy. A population model in which trehalose controls quiescence entry, growth rate, lag, and freeze-thaw survival reproduced the empirical dynamics, implicating physiological state transitions rather than specific mutations as the primary adaptive driver. The study therefore concludes that extreme-stress tolerance can evolve quickly through a convergent, trehalose-rich quiescence-like state that reinforces membrane integrity and cytoplasmic structure.

Strengths:

The strengths of the paper are the experimental design, data presentation and interpretation, and that it is well-written.

(1) While the phenotyping is thorough, a few more growth curves would be quite revealing to determine the extent of cross-stress protection. For example, comparing growth rates under YPD vs. YPEG (EtOH/glycerol), and measuring growth at 37ºC or in the presence of 0.8 M KCl.

We thank the referee for the interesting suggestions. However, growth rates alone may be difficult to interpret since WT strains also show different growth rates under these conditions. Therefore, comparing the relative fitness or survival of the evolved strains versus the WT under these stresses would be more informative. In the present study we limited growth/survival measurements to what was needed to parameterize the adaptation model in YPD under the freeze–thaw regime. We have now added a statement in the Discussion that, given the shared trehalose/mechanical mechanism, such cross-stress assays are an expected and straightforward follow-up.

(2) Is GEMS integrated prior to evolution? Are the evolved cells transformable?

Yes. GEMs were integrated prior to evolution, because the non-integrated evolved population showed low transformation efficiency, likely due to altered cell-wall properties.

(3) From the table, it looks like strains either have mutations in Ras1/2 or Vac8. Given the known requirements of Ras/PKA signaling for the G1/S checkpoint (to make sure there are enough nutrients for S phase), this seems like a pathway worth mentioning and referencing. Regarding Vac8, its emerging roles in NVJ and autophagy suggest another nutrient checkpoint, perhaps through TORC1. The common theme is rewired metabolism, which is probably influencing the carbon shuttling to trehalose synthesis.

We appreciate the reviewer’s suggestion to consider pathways like Ras/PKA (linked to Ras1/2) and autophagy/TORC1 (linked to Vac8) as potential upstream modulators. While these pathways are involved in nutrient sensing and metabolic regulation, we choose not to emphasize them specifically. This is because (i) some evolved lines lack Ras1/2 or Vac8 variants, and (ii) none of the variants lies directly in trehalose synthesis/degradation pathways. Furthermore, direct links to trehalose accumulation are not well established for these specific variants in this context, and pathways like Ras are global regulators with broad effects. Together with the strongly convergent phenotype, this supports our main inference that multiple genetic/metabolic routes can feed into the same trehalose-rich, mechanochemically reinforced, quiescence-like state. We have added a note in the discussion regarding metabolic rewiring and trehalose.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Generally, the results sections should have more details. The figures should be corrected, and the legends should be checked for correctness. The manuscript seems to have been assembled in haste?

We have expanded the relevant Results subsections with one-sentence motivations (why each measurement was performed) and we have corrected the figure legends for ordering and consistency.

Figure 3: It will be good to have the correct p-values on the figure itself. P-values are typically less than 1, unless there is some special method (here the values presented are , etc). Please explain how the P-values were obtained in the figure legend itself.

Figure 3 now shows the actual p-values. The legend specifies the details and the sample sizes used.

Figure 5: It is not clear what the error bars show in 5B, E (different evolved population/ clones/ cells?). All the figure legends are mixed up, please correct them. It is difficult to follow the paper.

Figure 5 legends now state clearly what the error bars represent (biological replicates) and which panels are from single-cell measurements. We have checked the panel lettering and legend order for consistency with the flow of the main text.

Reviewer #3 (Recommendations for the authors):

Overall, the paper is outstanding, well-written, and insightful.

A point to address is that there are missing citations on lines 60, 91.

We have added the missing citations at both locations. We apologize for the omission, which was due to a compilation error. This error has been fixed, and the bibliography has been corrected (now containing 74 references).

Author response:

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

Public reviews:

Reviewer #1 (Public review):

Summary:

Schafer et al. tested whether the hippocampus tracks social interactions as sequences of neural states within an abstract social space defined by dimensions of affiliation and power, using a task in which participants engaged in narrative-based social interactions. The findings of this study revealed that individual social relationships are represented by unique sequences of hippocampal activity patterns. These neural trajectories corresponded to the history of trial-to-trial affiliation and power dynamics between participants and each character, suggesting an extended role of the hippocampus in encoding sequences of events beyond spatial relationships.

The current version has limited information on details in decoding and clustering analyses which can be improved in the future revision.

Strengths:

(1) Robust Analysis: The research combined representational similarity analysis with manifold analyses, enhancing the robustness of the findings and the interpretation of the hippocampus's role in social cognition.

(2) Replicability: The study included two independent samples, which strengthens the generalizability and reliability of the results.

Weaknesses:

I appreciate the authors for utilizing contemporary machine-learning techniques to analyze neuroimaging data and examine the intricacies of human cognition. However, the manuscript would benefit from a more detailed explanation of the rationale behind the selection of each method and a thorough description of the validation procedures. Such clarifications are essential to understand the true impact of the research. Moreover, refining these areas will broaden the manuscript's accessibility to a diverse audience.

We thank the reviewer for these comments and have addressed them in various ways.

First, we removed the spline-based decoding and spectral clustering analyses. As we detail in our response to the recommendations, these approaches were complex and raised legitimate interpretational concerns, making it unclear how they supported our core claims. The revised manuscript now focuses on a set of representational similarity analyses to show representations consistent with social dimension similarity (affiliation vs. power decision trials) and social location similarity (trajectory/map-like coding based on participant choices).

Second, we expanded the Methods and Results to more clearly explain the analyses, the questions they address, and associated controls and robustness tests. The dimension similarity analysis tests whether hippocampal patterns differentiate affiliation and power decisions in a way consistent with an abstract dimension representation. The location similarity RSAs test whether within-character neural pattern distances scale with Euclidean distance in social space (relationship-specific trajectories), and whether pattern distances across all characters scale with location distances when distances are globally standardized, consistent with a shared map-like coordinate system.

Third, we emphasize new controls. For the dimension similarity RSA, we test for potential confounds such as word count, text sentiment, and reaction time differences between affiliation and power trials. For the location similarity RSA, we control for temporal distance between trials and show (in the Supplement) that the reported effects cannot be explained by temporal autocorrelation in the fMRI data or by the relationship between temporal distance and behavioral location distance.

We believe that these changes address the reviewer’s request for clearer rationale and validation.

Reviewer #2 (Public review):

Summary:

Using an innovative task design and analysis approach, the authors set out to show that the activity patterns in the hippocampus related to the development of social relationships with multiple partners in a virtual game. While I found the paper highly interesting (and would be thrilled if the claims made in the paper turned out to be true), I found many of the analyses presented either unconvincing or slightly unconnected to the claims that they were supposed to support. I very much hope the authors can alleviate these concerns in a revision of the paper.

Strengths & Weaknesses:

(1) The innovative task design and analyses, and the two independent samples of participants are clear strengths of the paper.

We thank the reviewer for this comment.

(2) The RSA analysis is not what I expected after I read the abstract and tile of the result section "The hippocampus represents abstract dimensions of affiliation and power". To me, the title suggests that the hippocampus has voxel patterns, which could be read out by a downstream area to infer the affiliation and power value, independent of the exact identity of the character in the current trial. The presented RSA analysis however presents something entirely different - namely that the affiliation trials and power trials elicit different activity patterns in the area indicated in Figure 3. What is the meaning of this analysis? It is not clear to me what is being "decoded" here and alternative explanations have not been considered. How do affiliation and power trials differ in terms of the length of sentences, complexity of the statements, and reaction time? Can the subsequent decision be decoded from these areas? I hope in the revision the authors can test these ideas - and also explain how the current RSA analysis relates to a representation of the "dimensions of affiliation and power".

We agree that this analysis needed to be better justified and explained. We have revised the text to clarify that by “represents the interaction decision trials along abstract social dimensions” we mean that hippocampal multivoxel patterns differentiate affiliation and power decisions in a way consistent with the conceptual framework of underlying latent dimensions. The analysis tests one simple prediction of this view – that on average these trial types are separable in the neural patterns. We have added details to the Methods, showing how the affiliation and power trials do not differ in word count or in sentiment, but do differ in their semantics, as assessed by a Large Language Model, as we expect from our task assumptions. Thanks to the reviewer’s comment, we also tested for and found a reaction time difference between affiliation and power trials, that we now control for.

(3) Overall, I found that the paper was missing some more fundamental and simpler RSA analyses that would provide a necessary backdrop for the more complicated analyses that followed. Can you decode character identity from the regions in question? If you trained a simple decoder for power and affiliation values (using the LLE, but without consideration of the sequential position as used in the spline analysis), could you predict left-out trials? Are affiliation and power represented in a way that is consistent across participants - i.e. could you train a model that predicts affiliation and power from N-1 subjects and then predict the Nth subject? Even if the answer to these questions is "no", I believe that they are important to report for the reader to get a full understanding of the nature of the neural representations in these areas. If the claim is that the hippocampus represents an "abstract" relationship space, then I think it is important to show that these representations hold across relationships. Otherwise, the claim needs to be adjusted to say that it is a representation of a relationship-specific trajectory, but not an abstract social space.

We appreciate this comment and agree on the value of clear, conceptually simple analyses. To address this concern, we have simplified our main analysis significantly by removing the spline-based analysis and substituting it with a multiple regression representational similarity analysis approach. We test whether within-character neural pattern distances scale with distance in social space (relationship-specific trajectories), and whether pattern distances across all characters scale with location distances when distances are globally standardized. We find evidence for both, consistent with a shared map-like coordinate system.

We agree that decoding character identity and an across-participant decoding approach could be informative. However, our current task is not well designed for such analyses and as such would complicate the paper. Although we agree that these questions are interesting, they would test questions that are outside the scope of this paper. 

(4) To determine that the location of a specific character can be decoded from the hippocampal activity patterns, the authors use a sequential analysis in a lowdimensional space (using local linear embedding). In essence, each trial is decoded by finding the pair of two temporally sequential trials that is closest to this pattern, and then interpolating the power/affiliation values linearly between these two points. The obvious problem with this analysis is that fMRI pattern will have temporal autocorrelation and the power and affiliation values have temporal autocorrelation. Successful decoding could just reflect this smoothness in both time series. The authors present a series of control analyses, but I found most of them to not be incisive or convincing and I believe that they (and their explanation of their rationale) need to be improved. For example, the circular shifting of the patterns preserves some of the autocorrelation of the time series - but not entirely. In the shifted patterns, the first and last items are considered to be neighboring and used in the evaluation, which alone could explain the poor performance. The simplest way that I can see is to also connect the first and last item in a circular fashion, even when evaluating the veridical ordering. The only really convincing control condition I found was the generation of new sequences for every character by shuffling the sequence of choices and re-creating new artificial trajectories with the same start and endpoint. This analysis performs much better than chance (circular shuffling), suggesting to me that a lot of the observed decoding accuracy is indeed simply caused by the temporal smoothness of both time series.

We thank the reviewer for emphasizing this important concern; we agree that we did not sufficiently address this in the initial submission. This concern is one main reason we removed the spline-based analysis and now use regression-based representational similarity analyses in its place. In the revision, we report autocorrelation-related analyses in the supplement, and via controls and additional analysis show that temporal distance (or its square) cannot explain the location-like effects. This substantially improves our ability to interpret the findings.

(5) Overall, I found the analysis of the brain-behavior correlation presented in Figure 5 unconvincing. First, the correlation is mostly driven by one individual with a large network size and a 6.5 cluster. I suspect that the exclusion of this individual would lead to the correlation losing significance. Secondly, the neural measure used for this analysis (determining the number of optimal clusters that maximize the overlap between neural clustering and behavioral clustering) is new, non-validated, and disconnected from all the analyses that had been reported previously. The authors need to forgive me for saying so, but at this point of the paper, would it not be much more obvious to use the decoding accuracy for power and affiliation from the main model used in the paper thus far? Does this correlate? Another obvious candidate would be the decoding accuracy for character identity or the size of the region that encodes affiliation and power. Given the plethora of candidate neural measures, I would appreciate if the authors reported the other neural measures that were tried (and that did not correlate). One way to address this would have been to select the method on the initial sample and then test it on the validation sample - unfortunately, the measure was not pre-registered before the validation sample was collected. It seems that the correlation was only found and reported on the validation sample?

We agree that this analysis was too complicated and under constrained, and thus not convincing. We think that removing this cluster-based analysis is the most conservative response to the reviewer’s concerns and have removed it from the revised paper.

Recommendations to the authors:

Reviewer #1 (Recommendations for the authors):

The manuscript's description of the shuffling analysis performed during decoding is currently ambiguous, particularly concerning the control variables. This ambiguity is present only in the Figure 4 legends and requires a more detailed explanation within the methods section. It is essential to clarify whether the permutation process was conducted within each character's data set or across multiple characters' data sets. If permutations were confined to within-character data, the conclusion would be that the hippocampus encodes context-specific information rather than providing a twodimensional common space.

We thank the reviewer for this comment. We have now removed the spline analysis due to these and other problems and have replaced it with representational similarity analyses that are both more rigorous and easier to interpret. We think these analyses allow us to make the claim that the characters are represented in a common space. 

In the methods, we explain the analyses (page 23-24, lines 475-500):

“We also expected the hippocampus to represent the different characters’ changing social locations, which are implicit in the participant’s choices. We used multiple regression searchlight RSA to test whether hippocampal pattern dissimilarity increases with social location distance, based on participant-specific trial-wise beta images where boxcar regressors spanned each trial’s reaction time.”

“We ran two complementary regression analyses to address two related questions. First, we asked whether the hippocampus represents how a specific relationship changes over time. For this analysis, for each participant and each searchlight, we computed character-specific (i.e., only for same character trial pairs) correlation distances between trial-wise beta patterns and Euclidean distances between the social location behavioral coordinates. Distances were zscored within character trial pairs to isolate character-specific changes. The second analysis asked whether the there is a common map-like representation, where all trials, regardless of relationship, are represented in a shared coordinate system. Here, we included all trial pairs and z-scored the distances globally. For both regression analyses, we included control distances to control for possible confounds. To account for generic time-related changes, we controlled for absolute scan-time difference, as this correlated with location distance across participants (see Temporal autocorrelation of hippocampal beta patterns in the supplement). Although the square of this temporal distance did not explain any additional variance in behavioral distances, we ran a robustness analysis including both temporal distance and its square and saw qualitatively the same clusters with similar effect sizes. As such, we report the main analysis only. We included binary dimension difference (0 = trial pairs of different dimension, 1 = trials pairs of the same dimension), to ensure effects could not be explained by dimension-related effects. In the group-level model, we controlled for sample and the average reaction time between affiliation and power decisions.”

In the results, we describe the results and our interpretation (pages 11-12, lines 185208):

“We have shown that the left hippocampus represents the affiliation and power trials differently, consistent with an abstract dimensional representation. Does it also represent the changing social coordinates of each character? To test this, we multiple-regression RSA searchlight to test whether left hippocampus patterns represent the characters’ changing social locations across interactions (see Figure 3). We restricted the distances to those from trial pairs from the same character and standardized the distances within character (see Figure 3BD). We controlled for temporal distance to ensure the effect was not explainable by the time between trials, and for whether the trials shared the same underlying dimension (affiliation or power; see Location similarity searchlight analyses for more details). At the group level, we controlled for sample and the average reaction time difference between affiliation and power trials. Using the same testing logic as the dimensionality similarity analysis, we first tested our hypothesis in the bilateral hippocampus and found widespread effects in both the left (peak voxel MNI x/y/z = -35/-22/-15, cluster extent = 1470 voxels) and right (peak voxel MNI x/y/z = 37/-19/-14, cluster extent = 1953 voxels) hemispheres. The whole-brain searchlight analysis revealed additional clusters in the left putamen (-27/-3/14, cluster extent = 131 voxels) and left posterior cingulate cortex (-10/-28/41, cluster extent = 304 voxels).”

“We then asked a second, complementary question: does the hippocampus represent all interactions, across characters, within a shared map? To test for this map-like structure, we repeated the analysis but now included all trial pairs, z-scoring distances globally rather than within character (Figure 3E-F). The remainder of the procedure followed the same logic as the preceding analysis. The hippocampus analysis revealed an extensive right hippocampal cluster (27/27/-14, cluster extent = 1667 voxels). The whole-brain analysis did not show any significant clusters.”

We also describe the results in the discussion (page 12, lines 220-226): 

“Then, we show that the hippocampus tracks the changing social locations (affiliation and power coordinates), above and beyond the effects of dimension or time; the hippocampus seemed to reflect both the changing within-character locations, tracking their locations over time, and locations across characters, as if in a shared map. Thus, these results suggest that the hippocampus does not just encode static character-related representations but rather tracks relationship changes in terms of underlying affiliation and power.”

The manuscript's description of the decoding analysis is unclear regarding the variability of the decoded positions. The authors appear to decode the position of a character along a spline, which raises the question of whether this position correlates with time, since characters are more likely to be located further from the center in later trials. There is a concern that the decoded position may not solely reflect the hippocampal encoding of spatial location, but could also be influenced by an inherent temporal association. Given that a character's position at time t is likely to be similar to its positions at t−1 and t+1, it is crucial that the authors clearly articulate their approach to separating spatial representation from temporal autocorrelation. While this issue may have been addressed in the construction of the test set, the manuscript does not seem to adequately explain how such biases were mitigated in the training set.

We agree that temporal confounding needs to be better accounted for, as our claims depend on space-like signals being separable from time-like ones. We address this in several ways in the revised manuscript.

First, we emphasize that this is a narrative-based task, where temporal structure is relevant. As such, our analyses aim to demonstrate that effects go beyond simple temporal confounds, like trial order or time elapsed.

Despite the temporal structure to the task, the decisions for the same character are spaced in time, and interleaved with other characters’ decisions, reducing the chance that a simple temporal confound could explain trajectory-related effects. We now describe the task better in the revised methods (page 16, lines 314-318):

“All six characters’ decision trials are interleaved with one another and with narrative slides. On average, after a decision trial for a given character, participants view ~11 narrative slides and complete ~3 decisions for other characters before returning to that same character, such that each character’s choices are separated by an average of ~20 seconds (range 12 seconds to 10 min).”

To address temporal autocorrelation in the fMRI time series, we used SPM’s FAST algorithm. Briefly, FAST models temporal autocorrelation as a weighted combination of candidate correlation functions, using the best estimate to remove autocorrelated signal.

We also now report the temporal autocorrelation profile of the hippocampal beta series in the supplement, including (pages 29-31, lines 593-656):

“The Social Navigation Task is a narrative-based task, where the relationships with characters evolve over time; trial pairs that are close in time may have more similar fMRI patterns for reasons unrelated to social mapping (e.g., slow drift). It is important to account for the role of time in our analyses, to ensure effects go beyond simple temporal confounds, like the time between decision trials. To aid in this, we quantified how fMRI signals change over time using a pattern autocorrelation function across decision trial lags. We defined the left and right hippocampus and the left and right intracalcarine cortex using the HarvardOxford atlas and thresholded them at 50% probability. We chose intracalcarine corex as an early visual control region that largely corresponds to primary visual cortex (V1), as it is likely to be driven by the visually presented narrative. We used the same trial-wise beta images as in the location similarity RSA (boxcar regressors spanning each decision trial’s reaction time). For each participant and region-of-interest (ROI), we extracted the decision trial-by-voxel beta matrix and quantified three kinds of temporal dependence: beta autocorrelation, multivoxel pattern correlation and multivoxel pattern correlation after regressing out temporal distance.”

“To estimate the temporal autocorrelation of the trial-wise beta values, we treated each voxel’s beta values as a time series across trials and measured how much a voxel’s response on one trial correlated (Pearson) with its response on previous trials. We averaged these voxel wise autocorrelations within each ROI. At one trial apart (lag 1), both the hippocampus and V1 showed small positive autocorrelations, indicating modest trial-to-trial carryover in response amplitude (see Supplemental figure 1) that by three trials apart was approximately 0.”

“Because our representational similarity analyses depend on trial-by-trial pattern similarity, we also estimated how multivoxel patterns were autocorrelated over time. For each lag, we computed the Pearson correlation between each trial’s voxelwise pattern and the pattern from the trial that many trials earlier, then averaged those correlations to obtain a single autocorrelation value for that lag. At one trial apart, both regions showed positive autocorrelation, with V1 having greater autocorrelation than the hippocampus; pattern correlations between trials 3 or 4 trials apart reduced across participants, settling into low but positive values. Then, for each participant and ROI, we regressed out the effect of absolute trial onset differences from all pairwise pattern correlations, to mirror the effects of controlling for these temporal distances in regressions. After removing this temporal distance component, the short lag pattern autocorrelation dropped substantially in both regions. The similarity in autocorrelation profiles between the two regions suggests that significant similarity effects in the hippocampus are unlikely to be driven by generic temporal autocorrelation.”

“Relationship between behavioral location distance and temporal distance “

“We also quantified how temporal distances between trials relates to their behavioral location distances, participant by participant. Our dimension similarity analysis controls for temporal distance between trials by design (see Social dimension similarity searchlight analysis), but our location similarity analysis does not. To decide on covariates to include in the analysis, we tested whether temporal distances can explain behavioral location distances. For each participant, we computed the correlations between trial pairs’ Euclidean distances in social locations and their linear temporal distances (“linear”) and the temporal distances squared (“quadratic”), to test for nonlinear effects. We then summarized the correlations using one-sample t-tests. The linear relationship was statistically significant (t₄₉ = 12.24, p < 0.001), whereas the quadratic relationship was not (t₄₉ = -0.55, p = 0.586). Similarly, in participant specific regressions with both linear and quadratic temporal distances, the linear effect was significant (t₄₉ = 5.69, p < 0.001) whereas the quadratic effect was not (t₄₉ = 0.20, p = 0.84). Based on this, we included linear temporal distances as a covariate in our location similarity analyses (see Location similarity searchlight analyses), and verified that adding a quadratic temporal distance covariate does not alter the results. Thus, the reported location-related pattern similarity effects go beyond what can be explained by temporal distance alone.”

How the free parameter of spectral clustering was determined, if there is any?

The interpretation of the number of hippocampal activity clusters is ambiguous. It is suggested that this number could fluctuate due to unique activity patterns or the fit to behaviorally defined trajectories. A lower number of clusters might indicate either a noisier or less distinct representation, raising the question of the necessity and interpretability of such a complex analysis. This concern is compounded by the potential sensitivity of the clustering to the variance in Euclidean distances of each trial's position relative to the center. If a character's position is consistently near the center, this could artificially reduce the perceived number of clusters. Furthermore, the manuscript should address whether there is any correlation between the number of clusters and behavioral performance. Specifically, what are the implications if participants are able to perform the task adequately with a smaller number of distinct hippocampal representation states?

The rationale for conducting both cluster analysis and position decoding as separate analyses remains unclear. While cluster analysis can corroborate the findings of position decoding, it is not apparent why the authors chose to include trials across characters for cluster analysis but not for decoding analysis. An explanation of the reasoning behind this methodological divergence would help in understanding the distinct contributions of each analysis to the study's findings.

The paper by Cohen et al. (1997), which provides the questionnaire for measuring the social network index, is not cited in the references. Upon reviewing the questionnaire that the author may have used, it appears that the term "social network size" does not refer to the actual size but to a score or index derived from the questionnaire responses. It may be more appropriate to replace the term "size" with a different term to more accurately reflect this distinction.

Thank you for seeking these clarifications. Given the complexity of this analysis, we have decided to drop it to focus instead on our dimension and location representational similarity analysis results.

Reviewer #2 (Recommendations for the authors):

How did the participants' decisions on previous trials influence the future trials that the subjects saw? If the different participants were faced with different decision trials, then how did you compare their decision? If two participants made the same decisions, would they have seen exactly the same sequence of trials (see point X on how the trial sequence was randomized).

All participants experience the same narrative, with the same decisions (i.e., the same available options); their choices (i.e., the options they select) are what implicitly shape each character’s affiliation and power locations, and thus each character’s trajectory. In other words, the narrative is fixed; what changes is the social coordinates assigned to each trial’s outcome depending on the participant’s choice of how to interact from the two narrative options. This means that we can meaningfully compare participants' neural patterns, given that every participant received the same text and images throughout.

We have now added details on the narrative structure, replacing more ambiguous statements with a clearer description (page 16, lines 309-318):

“The sequence of trials, including both narrative and decision trials, were fixed across participants; all that differs are the choices that the participants make. Narrative trials varied in duration, depending on the content (range 2-10 seconds), but were identical across participants. Decision trials always lasted 12 seconds, with two options presented until the participant made a choice, after which a blank screen was presented for the remainder of the duration. All six characters’ decision trials are interleaved with one another, and with the narrative slides. On average, after a decision trial for a given character, participants view ~11 narrative slides and complete ~3 decisions for other characters before returning to another decision with the same character, such that each character’s choices are separated by an average of ~20 seconds (ranging from 12 seconds to 10 min).”

Figure 2B: I assume that "count" is "count of participants"? It would be good to indicate this on the axis/caption.

Thank you for noting this. We have now removed this figure to improve the clarity of our figures. 

We have shown that the hippocampus represents the interaction decision trials along abstract social dimensions, but does it track each relationship's unique sequence of abstract social coordinates?". Please clarify what you mean by "represents the interaction decision trials”.

By “represents the interaction decision trials along abstract social dimensions”, we mean that when the participant makes a choice during the social interactions the hippocampal patterns represent the current social dimension of the choice (affiliation vs power). In other words, the hippocampal BOLD patterns differentiate affiliation and power decisions, consistent with our hypothesis of abstract social dimension representation in the hippocampus. We have clarified this (page 11, lines 185-187):

“We have shown that the left hippocampus represents the affiliation and power trials differently, consistent with an abstract dimensional representation.”

Page 8: "Hippocampal sequences are ordered like trajectories": It is not entirely clear to me what is meant by the split midpoint. Is this the midpoint of the piece-wise linear interpolation between two points, or simply the mean of all piecewise splines from one character? If the latter, is the null model the same as simply predicting the mean affiliation and power value for this character? If yes, please clarify and simplify this for the reader.

Page 8: "Hippocampal sequences track relationship-specific paths". First, I was misled by the "relationship-specific". I first understood this to mean that you wanted to test whether two relationships (i.e. the identity of the partner) had different representations in Hippocampus, even if the power/affiliation trajectories are the same. I suggest changing the title of this section.

The analysis in this section also breaks any temporal autocorrelation of measured patterns - so I am not sure if this is a strong analysis that should be interpreted at all. This analysis seems to not address the claim and conclusion that is drawn from it. I assume that the random trajectories have different choices and different affiliation/power values than the true trajectories. So the fact that the true trajectories can be better decoded simply shows that either choices or affiliation and power (or both) are represented in the neural code - but not necessarily anything beyond this.

Page 9: "Neural trajectories reflect social locations, not just choices". The motivation of this analysis is not clear to me. As I understand this analysis, both social location and choices are changed from the real trajectories. How can it then show that it reflects social locations, not just the choices?

Figure 4 caption: "on the -based approximation" Is there a missing "point"-[based] here?

We agree with the reviewer that this analysis is hard to interpret and does not adequately address concerns regarding temporal autocorrelation, and as such we have removed it from the manuscript. We describe the new results that include controlling for temporal distance between trials (pages 11-12, lines 185-208):

“We have shown that the left hippocampus represents the affiliation and power trials differently, consistent with an abstract dimensional representation. Does it also represent the changing social coordinates of each character? To test this, we multiple-regression RSA searchlight to test whether left hippocampus patterns represent the characters’ changing social locations across interactions (see Figure 3). We restricted the distances to those from trial pairs from the same character and standardized the distances within character (see Figure 3BD). We controlled for temporal distance to ensure the effect was not explainable by the time between trials, and for whether the trials shared the same underlying dimension (affiliation or power; see Location similarity searchlight analyses for more details). At the group level, we controlled for sample and the average reaction time difference between affiliation and power trials. Using the same testing logic as the dimensionality similarity analysis, we first tested our hypothesis in the bilateral hippocampus and found widespread effects in both the left (peak voxel MNI x/y/z = -35/-22/-15, cluster extent = 1470 voxels) and right (peak voxel MNI x/y/z = 37/-19/-14, cluster extent = 1953 voxels) hemispheres. The whole-brain searchlight analysis revealed additional clusters in the left putamen (-27/-3/14, cluster extent = 131 voxels) and left posterior cingulate cortex (-10/-28/41, cluster extent = 304 voxels).”

“We then asked a second, complementary question: does the hippocampus represent all interactions, across characters, within a shared map? To test for this map-like structure, we repeated the analysis but now included all trial pairs, z-scoring distances globally rather than within character (Figure 3E-F). The remainder of the procedure followed the same logic as the preceding analysis. The hippocampus analysis revealed an extensive right hippocampal cluster (27/27/-14, cluster extent = 1667 voxels). The whole-brain analysis did not show any significant clusters.”

We emphasize that the results are robust to the inclusion of temporal distance squared, in the methods (pages 23-24, lines 493-496):

“Although the square of this temporal distance did not explain any additional variance in behavioral distances, we ran a robustness analysis including both temporal distance and its square and saw qualitatively the same clusters with similar effect sizes.”

Page 8: last paragraph: The text sounds like you have already shown that you can decode character identity from the patterns - but I do not believe you have it this point. I would consider this would be an interesting addition to the paper, though.

This section has been removed, and we have been careful to not imply this in the current version of the manuscript. While we agree a character identity decoding would enrich our argument, we do not believe our task is well-suited to capture a character identity effect. Each character only has 12 decision trials, and these trials are partially clustered in time - this is one problem of temporal autocorrelation that we thank the reviewers for pushing us to consider in more detail. Dimension and location patterns, on the other hand, are more natural to analyze in our task, especially in representational similarity analyses that test whether the relevant differences scale with neural distances.

Page 14ff: Why is "Analysis section" not part of "Materials and Methods"? I believe adding the analysis after a careful description of the methods would improve the clarity of this section.

We agree with the reviewer and have now consolidated these two sections.

Two or three examples of Affiliation and Power decision trials should be provided, so the reader can form a more thorough understanding of how these dimensions were operationalized. For the RSA analysis, it is important to consider other differences between these two types of trials.

We agree that adding examples will clarify the operationalization of these dimensions. We now include example affiliation and power trials in a table (page 17-18).

We thank the reviewer for noting the need to rule out alternative hypotheses; we have added several such tests. Affiliation and power trials were not different in word count (page 17, lines 329-332):

“To ensure that any observed neural or behavioral differences were not confounded by trivial features of the text, we tested for differences between the affiliation and power trials (where the two options are concatenated). There were no differences in word count (affiliation average = 26.6, power average = 25.6; t-test p = 0.56).”

They were also not different in their sentiment, as assessed by a Large Language Model (LLM) analysis (page 17, lines 332-335): 

“The text’s sentiment also did not differ between these trial types (t-test p = 0.72), as quantified by comparing sentiment compound scores (from most negative, −1, to most positive, +1), using a Large Language Model (LLM) specialized for sentiment analysis [26]. “

The affiliation and power trials were different in terms of semantic content, consistent with our assumptions (page 17, lines 337-347):

“Our framework assumes that affiliation and power trials differ in their semantic content–that is, in the conceptual meaning of the text, beyond word count or sentiment. To test this assumption, we used an LLM-based semantic embedding analysis. Each decision trial was embedded into a semantic vector. We then measured the cosine similarity between pairs of trials and calculated the difference between average within-dimension similarity (affiliation-affiliation and power-power comparisons) and average between-dimension similarity (affiliationpower comparisons) and assessed its statistical significance with permutation testing (1,000 shuffles of trial labels). As expected, decision trials of the same dimension were more similar to each other than trials of different dimension, across multiple LLMs (OpenAI’s text-embedding-3-small [27]: similarity difference = 0.041, p < 0.001; all-MiniLM-L12-v2 [28]: similarity difference = 0.032, p < 0.001).”

The affiliation and power trials were different in average reaction time. To control for this difference in the dimension RSA analysis, we added each participant’s absolute value reaction time difference between the trial types as a covariate. The results were nearly identical to what they were before. We updated the text to reflect this new control (page 23, lines 471-474):

“However, there was a significant difference in the average reaction time between affiliation and power decisions across participants (t₄₉ = 6.92, p < 0.001; affiliation mean = 4.92 seconds (s), power mean = 4.51 s), so we controlled for this in the group-level analysis.”

The exact implementation and timing of the behavioral tasks should be described better. How many narrative trials were intermixed with the decision trials? Which characters were they assigned to? How was the sequence of trials determined? Was it fixed across participants, or randomized?

We agree that additional details are helpful. In the Methods, we now describe this with more detail (page 16, lines 301-318):

“There are two types of trials: “narrative” trials where background information is provided or characters talk or take actions (a total of 154 trials), and “decision” trials where the participant makes decisions in one-on-one interactions with a character that can change the relationship with that character (a total of 63 trials). On each decision, participants used a button response box to select between the two options. The options (1 or 2, assigned to the index and middle fingers) choice directions (+/-1 arbitrary unit on the current dimension) were counterbalanced.”

“The sequence of trials, including both narrative and decision trials, were fixed across participants; all that differs are the choices that the participants make. Narrative trials varied in duration, depending on the content (range 2-10 seconds), but were identical across participants. Decision trials always lasted 12 seconds, with two options presented until the participant made a choice, after which a blank screen was presented for the remainder of the duration. All six characters’ decision trials are interleaved with one another, and with the narrative slides. On average, after a decision trial for a given character, participants view ~11 narrative slides and complete ~3 decisions for other characters before returning to another decision with the same character, such that each character’s choices are separated by an average of ~20 seconds (ranging from 12 seconds to 10 min).”

What is the exact timing of trials during fMRI acquisition - i.e. how long were the trials, what was the ITI, were there long phases of rest to determine the resting baseline? These are all important factors that will determine the covariance between regressors and should be reported carefully. Ideally, I would like to see the trial-by-trial temporal auto-correlation structure across beta-weights to be reported.

We thank the reviewer for asking for this clarification. We have added the following text to clarify the trial timing (page 16, lines 314-318):

“All six characters’ decision trials are interleaved with one another and with narrative slides. On average, after a decision trial for a given character, participants view ~11 narrative slides and complete ~3 decisions for other characters before returning to that same character, such that each character’s choices are separated by an average of ~20 seconds (range 12 seconds to 10 min).”

We now describe the temporal autocorrelation patterns in the supplement, including how we decided on how to control for temporal distance in representational similarity analyses (pages 29-31, lines 593-656):

“The Social Navigation Task is a narrative-based task, where the relationships with characters evolve over time; trial pairs that are close in time may have more similar fMRI patterns for reasons unrelated to social mapping (e.g., slow drift). It is important to account for the role of time in our analyses, to ensure effects go beyond simple temporal confounds, like the time between decision trials. To aid in this, we quantified how fMRI signals change over time using a pattern autocorrelation function across decision trial lags. We defined the left and right hippocampus and the left and right intracalcarine cortex using the HarvardOxford atlas and thresholded them at 50% probability. We chose intracalcarine corex as an early visual control region that largely corresponds to primary visual cortex (V1), as it is likely to be driven by the visually presented narrative. We used the same trial-wise beta images as in the location similarity RSA (boxcar regressors spanning each decision trial’s reaction time). For each participant and region-of-interest (ROI), we extracted the decision trial-by-voxel beta matrix and quantified three kinds of temporal dependence: beta autocorrelation, multivoxel pattern correlation and multivoxel pattern correlation after regressing out temporal distance.”

“To estimate the temporal autocorrelation of the trial-wise beta values, we treated each voxel’s beta values as a time series across trials and measured how much a voxel’s response on one trial correlated (Pearson) with its response on previous trials. We averaged these voxel wise autocorrelations within each ROI. At one trial apart (lag 1), both the hippocampus and V1 showed small positive autocorrelations, indicating modest trial-to-trial carryover in response amplitude (see Supplemental figure 1) that by three trials apart was approximately 0.”

“Because our representational similarity analyses depend on trial-by-trial pattern similarity, we also estimated how multivoxel patterns were autocorrelated over time. For each lag, we computed the Pearson correlation between each trial’s voxelwise pattern and the pattern from the trial that many trials earlier, then averaged those correlations to obtain a single autocorrelation value for that lag. At one trial apart, both regions showed positive autocorrelation, with V1 having greater autocorrelation than the hippocampus; pattern correlations between trials 3 or 4 trials apart reduced across participants, settling into low but positive values. Then, for each participant and ROI, we regressed out the effect of absolute trial onset differences from all pairwise pattern correlations, to mirror the effects of controlling for these temporal distances in regressions. After removing this temporal distance component, the short lag pattern autocorrelation dropped substantially in both regions. The similarity in autocorrelation profiles between the two regions suggests that significant similarity effects in the hippocampus are unlikely to be driven by generic temporal autocorrelation.”

“Relationship between behavioral location distance and temporal distance “

“We also quantified how temporal distances between trials relates to their behavioral location distances, participant by participant. Our dimension similarity analysis controls for temporal distance between trials by design (see Social dimension similarity searchlight analysis), but our location similarity analysis does not. To decide on covariates to include in the analysis, we tested whether temporal distances can explain behavioral location distances. For each participant, we computed the correlations between trial pairs’ Euclidean distances in social locations and their linear temporal distances (“linear”) and the temporal distances squared (“quadratic”), to test for nonlinear effects. We then summarized the correlations using one-sample t-tests. The linear relationship was statistically significant (t₄₉ = 12.24, p < 0.001), whereas the quadratic relationship was not (t₄₉ = -0.55, p = 0.586). Similarly, in participant specific regressions with both linear and quadratic temporal distances, the linear effect was significant (t₄₉ = 5.69, p < 0.001) whereas the quadratic effect was not (t₄₉ = 0.20, p = 0.84). Based on this, we included linear temporal distances as a covariate in our location similarity analyses (see Location similarity searchlight analyses), and verified that adding a quadratic temporal distance covariate does not alter the results. Thus, the reported location-related pattern similarity effects go beyond what can be explained by temporal distance alone.”

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study by Howe and colleagues investigates the role of the posterolateral cortical amygdala (plCoA) in mediating innate responses to odors, specifically attraction and aversion. By combining optogenetic stimulation, single-cell RNA sequencing, and spatial analysis, the authors identify a topographically organized circuit within plCoA that governs these behaviors. They show that specific glutamatergic neurons in the anterior and posterior regions of plCoA are responsible for driving attraction and avoidance, respectively, and that these neurons project to distinct downstream regions, including the medial amygdala and nucleus accumbens, to control these responses.

Strengths:

The major strength of the study is the thoroughness of the experimental approach, which combines advanced techniques in neural manipulation and mapping with high-resolution molecular profiling. The identification of a topographically organized circuit in plCoA and the connection between molecularly defined populations and distinct behaviors is a notable contribution to understanding the neural basis of innate motivational responses. Additionally, the use of functional manipulations adds depth to the findings, offering valuable insights into the functionality of specific neuronal populations.

Weaknesses:

There are some weaknesses in the study's methods and interpretation. The lack of clarity regarding the behavior of the mice during head-fixed imaging experiments raises the possibility that restricted behavior could explain the absence of valence encoding at the population level.

We agree with idea that head-fixation may alter the state of the animal and the neural encoding of odor. To address this, we have provided further analysis of walking behavior during the imaging sessions, which is provided in Figure S2. Overall, we could not identify any clear patterns in locomotor behavior that are odor-specific. Moreover, when neural activity was sorted depending on the behavioral state (walking, pausing or fleeing) we didn’t observe any apparent patterns in odor-evoked neural activity. This is now discussed in the Results and Limitations sections of the manuscript.

Furthermore, while the authors employ chemogenetic inhibition of specific pathways, the rationale for this choice over optogenetic inhibition is not fully addressed, and this could potentially affect the interpretation of the results.

The rationale was logistical. First, inhibition of over a timescale of minutes is problematic with heat generation during prolonged optical stimulation. Second, our behavioral apparatus has a narrow height between the ceiling and floor, making tethering difficult. This is now explained the results section. The trade-off of using chemogenetics is that we are silencing neurons and not specific projections. However, because we find that NAc- and MeA- projecting neurons have little shared collateralization, we believe the conclusion of divergent pathways still stands. This is now discussed in the Limitations section.

Additionally, the choice of the mplCoA for manipulation, rather than the more directly implicated anterior and posterior subregions, is not well-explained, which could undermine the conclusions drawn about the topographic organization of plCoA.

We targeted the middle region of plCoA because it contains a mixture of cell types found in both the anterior and posterior plCoA, allowing us to test the hypothesis that cell types, not intra plCoA location, elicit different responses. Had we targeted the anterior or posterior regions, we would expect to simply recapitulate the result from activation of random cells in each region. As a result, we think stimulation in the middle plCoA is a better test for the contribution of cell types. We have now clarified this in the text.

Despite these concerns, the work provides significant insights into the neural circuits underlying innate behaviors and opens new avenues for further research. The findings are particularly relevant for understanding the neural basis of motivational behaviors in response to sensory stimuli, and the methods used could be valuable for researchers studying similar circuits in other brain regions. If the authors address the methodological issues raised, this work could have a substantial impact on the field, contributing to both basic neuroscience and translational research on the neural control of behavior.

Reviewer #2 (Public review):

Summary:

The manuscript by the Root laboratory and colleagues describes how the posterolateral cortical amygdala (plCoA) generates valenced behaviors. Using a suite of methods, the authors demonstrate that valence encoding is mediated by several factors, including spatial localization of neurons within the plCoA, glutamatergic markers, and projection. The manuscript shows convincingly that multiple features (spatial, genetic, and projection) contribute to overall population encoding of valence. Overall, the authors conduct many challenging experiments, each of which contains the relevant controls, and the results are interpreted within the framework of their experiments.

Strengths:

- For a first submission the manuscript is well constructed, containing lots of data sets and clearly presented, in spite of the abundance of experimental results.

- The authors should be commended for their rigorous anatomical characterizations and posthoc analysis. In the field of circuit neuroscience, this is rarely done so carefully, and when it is, often new insights are gleaned as is the case in the current manuscript.

- The combination of molecular markers, behavioral readouts and projection mapping together substantially strengthen the results.

- The focus on this relatively understudied brain region in the context is valence is well appreciated, exciting and novel.

Weaknesses:

- Interpretation of calcium imaging data is very limited and requires additional analysis and behavioral responses specific to odors should be considered. If there are neural responses behavioral epochs and responses to those neuronal responses should be displayed and analyzed.

We have now considered this, see response above.

- The effect of odor habituation is not considered.

We considered this, but we did not find any apparent differences in valence encoding as measured by the proportion of neurons with significant valence scores across trials (see Figure 1J).

- Optogenetic data in the two subregions relies on very careful viral spread and fiber placement. The current anatomy results provided should be clear about the spread of virus in A-P, and D-V axis, providing coordinates for this, to ensure readers the specificity of each sub-zone is real.

We were careful to exclude animals for improper targeting. The spread of virus is detailed in Figures S3, S8 & S9.

- The choice of behavioral assays across the two regions doesn't seem balanced and would benefit from more congruency.

The choice of the 4-quadrant assay was used because this study builds off of our prior experiments that demonstrate a role for the plCoA in innate behavior. It is noteworthy that the responses to odor seen in this assay are generally in agreement with other olfactory behavioral assays, so one wouldn’t predict a different result. Moreover, the approach and avoidance responses measured in this assay are precisely the behaviors we wish to understand. We did examine other non-olfactory behavioral readouts (Figures S3, S8), and didn’t observe any effect of manipulation of these pathways.

- Rationale for some of the choices of photo-stimulation experiment parameters isn't well defined.

The parameters for photo-stimulation were based on those used in our past work (Root et al., 2014). We used a gradient of frequency from 1-10 Hz based on the idea that odor likely exists in a gradient and this was meant to mimic a potential gradient, though we don’t know if it exists. The range in stimulation frequencies appears to align with the actual rate of firing of plCoA neurons (Iurilli et al., 2017).

Reviewer #3 (Public review):

Summary:

Combining electrophysiological recording, circuit tracing, single cell RNAseq, and optogenetic and chemogenetic manipulation, Howe and colleagues have identified a graded division between anterior and posterior plCoA and determined the molecular characteristics that distinguish the neurons in this part of the amygdala. They demonstrate that the expression of slc17a6 is mostly restricted to the anterior plCoA whereas slc17a7 is more broadly expressed. Through both anterograde and retrograde tracing experiments, they demonstrate that the anterior plCoA neurons preferentially projected to the MEA whereas those in the posterior plCoA preferentially innervated the nucleus accumbens. Interestingly, optogenetic activation of the aplCoA drives avoidance in a spatial preference assay whereas activating the pplCoA leads to preference. The data support a model that spatially segregated and molecularly defined populations of neurons and their projection targets carry valence specific information for the odors. The discoveries represent a conceptual advance in understanding plCoA function and innate valence coding in the olfactory system.

Strengths:

The strongest evidence supporting the model comes from single cell RNASeq, genetically facilitated anterograde and retrograde circuit tracing, and optogenetic stimulation. The evidence clear demonstrates two molecularly defined cell populations with differential projection targets. Stimulating the two populations produced opposite behavioral responses.

Weaknesses:

There are a couple of inconsistencies that may be addressed by additional experiments and careful interpretation of the data.

Stimulating aplCoA or slc17a6 neurons results in spatial avoidance, and stimulating pplCoA or slc17a7 neurons drives approach behaviors. On the other hand, the authors and others in the field also show that there is no apparent spatial bias in odor-driven responses associated with odor valence. This discrepancy may be addressed better. A possibility is that odor-evoked responses are recorded from populations outside of those defined by slc17a6/a7. This may be addressed by marking activated cells and identifying their molecular markers. A second possibility is that optogenetic stimulation activates a broad set of neurons that and does not recapitulate the sparseness of odor responses. It is not known whether sparsely activation by optogenetic stimulation can still drive approach of avoidance behaviors.

We agree that marking specific genetic or projection defined neurons could help to clarify if there are some neurons have more selective valence responses. However, we are not able to perform these experiments at the moment. We have included new data demonstrating that sparser optogenetic activation evokes behaviors similar in magnitude as the broader activation (see Figure S4).

The authors show that inhibiting slc17a7 neurons blocks approaching behaviors toward 2-PE. Consistent with this result, inhibiting NAc projection neurons also inhibits approach responses. However, inhibiting aplCOA or slc17a6 neurons does not reduce aversive response to TMT, but blocking MEA projection neurons does. The latter two pieces of evidence are not consistent with each other. One possibility is that the MEA projecting neurons may not be expressing slc17a6. It is not clear that the retrogradely labeling experiments what percentage of MEA- and NACprojecting neurons express slc17a6 and slc17a7. It is possible that neurons expressing neither VGluT1 nor VGluT2 could drive aversive or appetitive responses. This possibility may also explain that silencing slc17a6 neurons does not block avoidance.

We have now performed RNAscope staining on retrograde tracing to better define this relationship. Although the VGluT1 and VGluT2 neurons have biased projections to the MeA and NAc, respectively, there is some nuance detailed in Figure S10. Generally, MeA projecting neurons are predominately VGluT2+, whereas NAc projecting have about 20% that express both. Some (less than 35%) retrogradely labeled neurons were not detected as VGluT1 or VGluT2 positive, suggesting that other populations could also contribute. We agree that the discrepancy between MeA-projection and VGluT2 silencing is likely due to incomplete targeting of the MeA-projecting population with the VGluT2-cre line. This is included in the Discussion section.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Main:

(1) For the head-fixed imaging experiments, what is the behavior of the mice during odor exposure? Could the weak reliability of individual neurons be due to a lack of approach or avoidance behavior? Could restricted behavior also explain the lack of valence encoding at the population level?

We agree that this is a limitation of head-fixed recordings. In the revised manuscript we did attempt to characterize their behavioral response, and look for correlations in odor representation. Although we did find different patterns of odor-evoked walking behavior, these patterns were not reliable or specific to particular odors (Figure S2). For example, one might expect aversive odors to pause walking or elicit a fast fleeing-like response, but we did not observe any apparent differences for locomotion between odors as all odors evoked a mixture of responses (Figure S2A-D, text lines 208-232). We then examined responses to odor depending on the behavioral state (walking, pausing or fleeing) and didn’t observe any apparent patterns in odor responses (Figure S2E,F). Lastly, we acknowledge in the text that the lack of valence encoding may be an artifact of head-fixation (see lines 849-857).

(2) For the optogenetic manipulations of Vglut1 and Vglut2 neurons, why was the injection and fiber targeted to the medial portion of the plCoA, if the hypothesis was that these glutamatergic neuron populations in different regions (anterior or posterior) are responsible for approach and avoidance? 

We targeted the middle region of plCoA because it contains a mixture of cell types found in both the anterior and posterior plCoA, allowing us to test the hypothesis that cell types, not intraplCoA location, elicit different responses. Had we targeted the anterior or posterior regions, we would expect to simply recapitulate the result from activation of random cells in each region. As a result, we think stimulation in the middle plCoA is a better test for the contribution of cell types. We have clarified this in the text (Lines 417-419).

Could this explain the lack of necessity with the DREADD experiments? 

For the loss of function experiments, a larger volume of virus was injected to cover a larger area and we did confirm targeting of the appropriate areas. Though, it is always possible that the lack of necessity is due to incomplete silencing.

Further, why was an optogenetic inhibition approach not utilized? 

Although optogenetic inhibition could have plausibly been used instead, we chose chemogenetic inhibition for two reasons: First, for minutes-long periods of inhibition, optical illumination poses the risk of introducing heat related effects (Owen et al., 2019). In fact, we first tried optical inhibition but controls were exhibited unusually large variance. Second, it is more feasible in our assay as it has a narrow height between the floor and lid that complicates tethering to an optic fiber. Past experiments overcame this with a motorized fiber retraction system (Root et al., 2014), but this is highly variable with user-dependent effects, so we found chemogenetics to be a more practical strategy. We have added a sentence to explain the rationale (see lines 561-563).

(3) The specific subregion of the nucleus accumbens that was targeted should be named, as distinct parts of the nucleus accumbens can have very different functions. 

We attempted to define specific subregions of the nucleus accumbens and found that plCoA projection is not specific to the shell or core, anterior or posterior, rather it broadly innervates the entire structure. We have added a note about this in manuscript (see lines 470-471). Given that we did not find notable subregion-specific outputs within the NAc, targeting was directed to the middle region of NAc, with coordinates stated in the methods. 

(4) Why was an intersectional DREADD approach used to inhibit the projection pathways, as opposed to optogenetic inhibition? The DREADD approach could potentially affect all projection targets, and the authors might want to address how this could influence the interpretation of the results.

This is partly addressed above in point 2. As for interpretation, we acknowledge that the intersectional approach silences the neurons projecting to a given target and not the specific projection and we have been careful with the wording. Although this may complicate the conclusion, we did map the collaterals for NAc and MeA projecting neurons and find that neurons do not appreciably project to both targets and have minimal projections to other targets. We have now taken care to state that we silence the neurons projecting to a structure, not silencing the projection, and we acknowledge this caveat. However, since the MeA- and NAcprojecting neurons appear to be distinct from each other (largely not collateralizing to each other), the conclusion that these divergent pathways are required still stands. We have added discussion of this in the Limitations section (see lines 859-863).

Minor:

(1) Line 402 needs a reference.

We have added the missing reference (now line 441).

(2) The Supplemental Figure labeling in the main text should be checked carefully.

Thank you for pointing this out. We have fixed the prior errors.

(3) Panel letter D is missing from Figure 2.

This has been fixed.

Reviewer #2 (Recommendations for the authors):

Major Concerns, additional experiments:

- In the calcium imaging experiments mice were presented with the same odor many times. Overall responses to odor presentations were quite variable and appear to habituate dramatically (Figure S1F). The general conclusion from these experiments are a lack of consistent valence-specific responses of individual neurons, but I wonder if this conclusion is slightly premature. A few potential explanatory factors that may need additional attention are: -First, despite recording video of the mouse's face during experiments, no behavioral response to any odor is described. Is it possible these odors when presented in head-fixed conditions do not have the same valence?

Yes, we agree that this is a possibility. We have added a discussion in the Limitations section (see lines 849-857). We have also added additional behavioral analysis discussed below.

On trials with neural responses are there behavioral responses that could be quantified? 

We have now added data in which we attempt to characterize their behavioral response, to look for correlations in odor representation (see lines 208-228). Although we did observe different patterns of odor-evoked walking behavior, these patterns were not reliable or specific to particular odors (Figure S2). One might expect aversive odors to pause walking or elicit a fast fleeing-like response, but we did not observe any apparent differences for locomotion between odors (Figure S2A-D). Next, we examined responses to odor depending on the behavioral state (walking, pausing or fleeing) and didn’t observe any meaningful differences in odor responses (Figure S2E,F). Lastly, we acknowledge that the odor representation may be different in freely moving animals that exhibit dynamic responses to odor (see lines 859-857).

- Habituation seems to play a prominent role in the neural signals, is there a larger contribution of valence if you look only at the first delivery (or some subset of the 20 presentations) of an odor type for a given trial? 

Indeed, we considered this, but we did not find any apparent differences in valence encoding as measured by the proportion of neurons with significant valence scores across trials (see Figure 1J).

- Is it reasonable to exclude valence encoding as a possibility when largely neurons were unresponsive to the positive valence odors (2PE and peanut) chosen when looking at the average cluster response (Figure 1F)? 

It is true that we see fewer neurons responding to the appetitive odors (Figure 1H) and smaller average responses within the cluster, but some neurons do respond robustly. If these were valence responses, we would predict that neural responses should be similarly selective, but we do not observe any such selectivity. The sparseness of responses to appetitive odors does cause the average cluster analysis (Figure 1F) to show muted responses to these odors, consistent with the decreased responsivity to appetitive odors. Moreover, single neuron response analysis reveals that a given neuron is not more likely to respond to appetitive or aversive odors with any selectivity greater than chance. For these reasons, we think it is reasonable to conclude an absence of valence responses, which is consistent with the conclusion from another report (Iurilli et al., 2017).

- While the preference and aversion assay with 4 corners is an interesting set-up and provides a lot of data for this particular manuscript. It would be helpful to test additional behaviors to determine whether these circuits are more conserved. As it stands the current manuscript relies on very broad claims using a single behavioral readout. Some attempts to use head-fixed approaches with more defined odor delivery timelines and/or additional valenced behavioral readouts is warranted.

We appreciate the suggestion, but are not able to perform these experiments at the moment. The choice of the 4-quadrant assay was used because it built off of our prior experiments that demonstrate a role for the plCoA in innate behavior. It is noteworthy that the responses to odor seen in this assay are generally in agreement with other olfactory behavioral assays, so one wouldn’t predict a different result. The approach and avoidance responses measured in this assay are precisely the behaviors we wish to understand. Moreover, we did examine other nonolfactory behavioral readouts (Figures S3, S8), and didn’t observe any effect of manipulation of these pathways. Lastly, we have tried to define parameters for head-fixed behavior that would permit correlation of neural responses with behavior, including longer stimulations and closed loop locomotion control of odor concentration, but were unsuccessful at establishing parameters that generated reliable behavioral responses. We acknowledge that one limitation of the study is the limited behavioral tests with two odors and whether the circuits are more broadly necessary for other odors. 

Minor comments:

• Please define PID in the Results when it is first introduced.

Done (see line 154)

• Line 412 Figure S5C-N should be Figure S6C-N.

Fixed. Now Figure S8C-N due to additional figures (see line 451).

• Throughout the Discussion it would be helpful if the authors referred to specific Figure panels that support their statements (e.g. lines 654-656 "[...] which is supported by other findings presented here showing that both VGluT2+ and VGluT1+ neurons project to MeA, while the projection to NAc is almost entirely composed of VGluT1+ neurons".

Thank you for the suggestion. We have added figure references in the discussion.

• Line 778 "producing" should be "produce".

Corrected (see line 840)

• The figures are very busy, especially all the manipulations. The authors are commended for including each data point, but they might consider a more subtle design (translucent lines only for each animal, and one mean dot for the SEM), just to reduce the overall clutter of an already overwhelming figure set. But this is ultimately left to the authors to resolve and style to their liking. 

Thank you for the suggestion. We have tried some different styles but like the original best.

Reviewer #3 (Recommendations for the authors):

If within reach, I suggest that the author determine the percentage of retrogradely labeled neurons to NAc or MEA that expresses GluT1 and GluT2. 

We have done this for the middle region plCoA that has the greatest mixture of cell types (See Figure S10, lines 504-517). We find that the MeA projecting neurons are mostly VGluT2+ with a minority that express both VGluT1 and VGlut2. NAc-projecting neurons are primarily VGluT1+ with about 20% expressing VGlut2 as well.

It would also be nice to sparse label of aplCoA and pplCoA using ChR2 to see if sparse activation drives approach or avoidance. 

We agree that it would be useful to vary the sparseness of the ChR2 expression, to see if produces similar results. We examined this using sparsely labeled odor ensembles, as previously done (Root et al., 2014). Briefly, we used the Arc-CreER mouse to label TMT responsive neurons with a cre-dependent ChR2 AAV vector targeted to the anterior or posterior regions, while previously we had broadly targeted the entirety of plCoA. We had established that this labeling method captures about half of the active cells detected by Arc expression, which is on the order of hundreds of neurons rather than thousands by broad cre-independent expression. Remarkably, we get effects similar in magnitude that are not significantly different from that with broader activation of the anterior or posterior domains (see new Figure S4, lines 267-288). It still remains possible that there is a threshold number of neurons that are necessary to elicit behavior, but that is beyond the scope of the current study. However, these data indicate that the effect of activating anterior and posterior domains is not an artifact of broad stimulation.

Author response:

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

eLife Assessment

We appreciate the positive assessment. We recognize that since all of the work in this manuscript was done in vitro, there are reasonable concerns about the translatability of these data to clinical settings. These results should not directly inform malaria policy, but we hope that these data bring new considerations to the approach for choosing strategic antimalarial combinations. We have modified the manuscript to clarify this distinction.

Public Reviews

Reviewer #1 (Public Review):

We thank the reviewer for their thoughtful summary of this manuscript. It is important to note that DHA-PPQ did show antagonism in RSAs. In this modified RSA, 200 nM PPQ alone inhibited growth of PPQ-sensitive parasites approximately 20%. If DHA and PPQ were additive, then we would expect that addition of 200 nM PPQ would shift the DHA dose response curve to the left and result in a lower DHA IC50. Please refer to Figure 4a and b as examples of additive relationships in dose-response assays. We observed no significant shift in IC50 values between DHA alone and DHA + PPQ. This suggests antagonism, albeit not to the extent seen with CQ. We have modified the manuscript to emphasize this point. As the reviewer pointed out, it is fortunate that despite being antagonistic, clinically used artemisinin-4-aminoquinoline combinations are effective, provided that parasites are sensitive to the 4-aminoquinoline. It is possible that superantagonism is required to observe a noticeable effect on treatment efficacy (Sutherland et al. 2003 and Kofoed et al. 2003), but that classical antagonism may still have silent consequences. For example, if PPQ blocks some DHA activation, this might result in DHA-PPQ acting more like a pseudo-monotherapy. However, as the reviewer pointed out, while our data suggest that DHA-PPQ and AS-ADQ are “non-optimal” combinations, the clinical consequences of these interactions are unclear. We have modified the manuscript to emphasize the later point.

While the Ac-H-FluNox and ubiquitin data point to a likely mechanism for DHA-quinoline antagonism, we agree that there are other possible mechanisms to explain this interaction.  We have addressed this limitation in the discussion section. Though we tried to measure DHA activation in parasites directly, these attempts were unsuccessful. We acknowledge that the chemistry of DHA and Ac-H-FluNox activation is not identical and that caution should be taken when interpreting these data. Nevertheless, we believe that Ac-H-FluNox is the best currently available tool to measure “active heme” in live parasites and is the best available proxy to assess DHA activation in live parasites. These points are now addressed in the discussion section. Both in vitro and in parasite studies point to a roll for CQ in modulating heme, though an exact mechanism will require further examination. Similar to the reviewer, we were perplexed by the differences observed between in vitro and in parasite assays with PPQ and MFQ. We proposed possible hypotheses to explain these discrepancies in the discussion section. Interestingly, our data corelate well with hemozoin inhibition assays in which all three antimalarials inhibit hemozoin formation in solution, but only CQ and PPQ inhibit hemozoin formation in parasites. In both assays, in-parasite experiments are likely to be more informative for mechanistic assessment.

It remains unclear why K13 genotype influences RSA values, but not early ring DHA IC50 values. In K13^WT parasites, both RSA values and DHA IC50 values were increased 3-5 fold upon addition of CQ. This suggests that CQ-mediated resistance is more robust than that conferred by K13 genotype. However, this does not necessarily suggest a different resistance mechanism. We acknowledge that in addition to modulating heme, it is possible that CQ may enhance DHA survival by promoting parasite stress responses. Future studies will be needed to test this alternative hypothesis. This limitation has been acknowledged in the manuscript. We have also addressed the reviewer’s point that other factors, including poor pharmacokinetic exposure, contributed to OZ439-PPQ treatment failure.

Reviewer #2 (Public Review):

We appreciate the positive feedback. We agree that there have been previous studies, many of which we cited, assessing interactions of these antimalarials. We also acknowledge that previous work, including our own, has shown that parasite genetics can alter drug-drug interactions. We have included the author’s recommended citations to the list of references that we cited. Importantly, our work was unique not only for utilizing a pulsing format, but also for revealing a superantagonistic phenotype, assessing interactions in an RSA format, and investigating a mechanism to explain these interactions. We agree with the reviewer that implications from this in vitro work should be cautious, but hope that this work contributes another dimension to critical thinking about drug-drug interactions for future combination therapies. We have modified the manuscript to temper any unintended recommendations or implications.

The reviewer notes that we conclude “artemisinins are predominantly activated in the cytoplasm”. We recognize that the site of artemisinin activation is contentious. We were very clear to state that our data combined with others suggest that artemisinins can be activated in the parasite cytoplasm. We did not state that this is the primary site of activation. We were clear to point out that technical limitations may prevent Ac-H-FluNox signal in the digestive vacuole, but determined that low pH alone could not explain the absence of a digestive vacuole signal.

With regard to the “reproducibility” and “mechanistic definition” of superantagonism, we observed what we defined as a one-sided superantagonistic relationship for three different parasites (Dd2, Dd2 PfCRT^Dd2, and Dd2 K13^R539T) for a total of nine independent replicates. In the text, we define that these isoboles are unique in that they had mean ΣFIC50 values > 2.4 and peak ΣFIC50 values >4 with points extending upward instead of curving back to the axis. As further evidence of the reproducibility of this relationship, we show that CQ has a significant rescuing effect on parasite survival to DHA as assessed by RSAs and IC50 values in early rings.

Reviewer #3 (Public Review):

We thank the reviewer for their positive feedback. We acknowledge that no combinations tested in this manuscript were synergistic. However, two combinations, DHA-MFQ and DHA-LM, were additive, which provides context for contextualizing antagonistic relationships. We have previously reported synergistic and additive isobolograms for peroxide-proteasome inhibitor combinations using this same pulsing format (Rosenthal and Ng 2021). These published results are now cited in the manuscript.

We believe that these findings are specific to 4-aminoquinoline-peroxide combinations, and that these findings cannot be generalized to antimalarials with different mechanisms of action. Note that the aryl amino alcohols, MFQ and LM, were additive with DHA. Since the mechanism of action of MFQ and LM are poorly understood, it is difficult to speculate on a mechanism underlying these interactions.

We agree with the reviewer that while the heme probe may provide some mechanistic insight to explain DHA-quinoline interactions, there is much more to learn about CQ-heme chemistry, particularly within parasites.

The focus of this manuscript was to add a new dimension to considerations about pairings for combination therapies. It is outside the scope of this manuscript to suggest alternative combinations. However, we agree that synergistic combinations would likely be more strategic clinically.

An in vitro setup allows us to eliminate many confounding variables in order to directly assess the impact of partner drugs on DHA activity. However, we agree that in vivo conditions are incredibly more complex, and explicitly state this.

We agree that in the future, modeling studies could provide insight into how antagonism may contribute to real-world efficacy. This is outside the scope of our studies.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the Authors):

The key weaknesses identified in this manuscript are described in the 'weaknesses' section of the public review. The major one is the inconsistency around the H-FluNox response in the chemical vs biological experiments. I can't think of a simple experiment to resolve this issue, but it is good that this data is openly provided in the manuscript. I believe there could be more discussion to clarify this limitation with the current study, and the conclusions, and particularly the title, should be softened regarding the mechanism of antagonism being based on heme reactivity.

We have softened the title and conclusions to take into account the limitations of our studies.

(1) Please double-check the definitions for isobologram interpretation. In most antimicrobial interaction studies, I see the threshold for antagonism at sumFIC50 of 1.5, or even 2. 1.25 is often interpreted as additive in many studies.

We acknowledge that different studies use various cutoff values. Our interpretations for additive versus antagonistic versus superantagonistic were based not only on mean ΣFIC50 values, but also isobologram shape. For example, the flat isoboles for MFQ-DHA were clearly distinct from the curved isoboles of PPQ-DHA. It is unclear what cutoff value(s) would be most clinically relevant.

(2) For the MFQ-PPQ interaction study, please make it clear that these drugs have very long half-lives (weeks), so the 4 h pulse assay isn't really relevant to their overall activity. It probably shows a slower onset of action, but there is plenty of drug remaining for many days in the clinical scenario, so perhaps the data from the traditional 48h assay is more relevant. The same consideration applies to OZ439, which may impact the interpretation of that data.

We have now included the half-lives of these compounds in the discussion section. Our intent was to use a pulsing format to make these isobolograms comparable with the other assays. It is important to note that pulses can reveal stronger phenotypes that might be missed with traditional methods. Thus, while 48 h assays may better mimic in vivo conditions, they could also mask important phenotypes.

Reviewer #3 (Recommendations for the Authors):

I have included most of my concerns in the public review. Below are some additional specific points for consideration:

(1) It is expected to include a synergistic combination as a control (e.g., artemisinin + lumefantrine) to contextualize the degree of antagonism observed. The experimental design should show some synergistic profiles in comparison. Adding a few experiments by including a synergistic control is needed.

Both MFQ-DHA and LM-DHA combinations were additive, which provides context for antagonistic combinations. This is now stated in the results section pertaining to Figure 1. We have also included a reference to our previous publication in which we demonstrated that proteasome inhibitor-peroxide combinations are synergistic to additive using this same pulsing format.

(2) Consider in vivo validation or pharmacokinetic/pharmacodynamic modeling to strengthen the translational relevance of the findings when it comes to doses and the IC50 correlations.

We agree that this would be useful to do in future, but it is outside the scope of the current study.

(3) It would be beneficial to include a discussion section on how the findings are generalizable to different Plasmodium falciparum genotypes (3D7, Dd2, MRA-1284) and their relevance.

Findings were consistent across three parasite backgrounds depending on PfCRT genotype. This point has been included in the discussion section. The background of these parasites is also provided in Table 1.

(4) Potential evaluation criteria to understand where certain combinations should be reconsidered can be included as a suggestion for the wider audience.

Our in vitro studies suggest that pulsing isobolograms would be a useful assay to include when evaluating combination therapies. While we believe that synergistic combinations would be more strategic than antagonistic combinations, we cannot provide evaluation criteria or make recommendations for reconsidering currently used combinations.

(5) Further elaborate on the mechanistic basis of heme inactivation by quinolines. If data are available, please include more data on the specificity of the process.

Despite our best efforts, we were unable to evaluate quinoline-heme interactions in parasites. Even in vitro, this interaction has remined elusive for decades. We agree that this would be an important future step towards supporting a specific mechanism for quinoline-DHA antagonism.

It is very important to understand that things are different in both time a culture. Realizing cultural roots can also help better attach ideas and goals to the things we view as different. For example we may not make an old recipe using the exact same methods but rather make it with modern appliances. So in some ways the recipe is different but the root is the same.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Manuscript number: RC-2025-03280

Corresponding author(s): Stephan Gruber

1. General Statements [optional]

First, we would like to thank the editor at Review Commons for the efficient handling of our manuscript. We also apologize for our delayed response.

We are grateful to all three reviewers for their careful evaluation of our work and for their constructive feedback, which will provide a valuable basis for improving the figures and the text, as described below. We expect to be able to complete the revision following the plan described below quickly.

We note that the reviewer reports (Rev. #1 and Rev. #3) made us realize that the manuscript text was misleading on the following point. Although we used the purified ATP hydrolysis–deficient Smc protein for sybody isolation, this does not restrict the selection to a specific conformation. As described in detail in Vazquez-Nunez et al. (Figure 5), this mutant displays the ATP-engaged conformation only in a smaller fraction of complexes (~25% in the presence of ATP and DNA), consistent with prior in vivo observations reported by Diebold-Durand et al. (Figure 5). Rather than limiting the selection to a particular configuration, our aim was to reduce the prevalence of the predominant rod state in order to broaden the range of conformations represented during sybody selection. Consistent with this interpretation, only a small number of isolated sybodies show strong conformation-specific binding in the presence or absence of ATP/DNA, as observed by ELISA (now included in the manuscript). We will revise the manuscript text accordingly to clarify this point.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

• *

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

Gosselin et al., develop a method to target protein activity using synthetic single-domain nanobodies (sybodies). They screen a library of sybodies using ribosome/ phage display generated against bacillus Smc-ScpAB complex. Specifically, they use an ATP hydrolysis deficient mutant of SMC so as to identify sybodies that will potentially disrupt Smc-ScpAB activity. They next screen their library in vivo, using growth defects in rich media as a read-out for Smc activity perturbation. They identify 14 sybodies that mirror smc deletion phenotype including defective growth in fast-growth conditions, as well as chromosome segregation defects. The authors use a clever approach by making chimeras between bacillus and S. pnuemoniae Smc to narrow-down to specific regions within the bacillus Smc coiled-coil that are likely targets of the sybodies. Using ATPase assays, they find that the sybodies either impede DNA-stimulated ATP hydrolysis or hyperactivate ATP hydrolysis (even in the absence of DNA). The authors propose that the sybodies may likely be locking Smc-ScpAB in the "closed" or "open" state via interaction with the specific coiled-coil region on Smc. I have a few comments that the authors should consider:

Major comments: 1. Lack of direct in vitro binding measurements: The authors do not provide measurements of sybody affinities, binding/ unbinding kinetics, stoichiometries with respect to Smc-ScpAB. Additionally, do the sybodies preferentially interact with Smc in ATP/ DNA-bound state? And, do the sybodies affect the interaction of ScpAB with SMC? It is understandable that such measurements for 14 sybodies is challenging, and not essential for this study. Nonetheless, it is informative to have biochemical characterization of sybody interaction with the Smc-ScpAB complex for at least 1-2 candidate sybodies described here.

We agree with the reviewer that adding such data would be reassuring and that obtaining solid data using purified components is not easy even for a smaller selection of sybodies. We have data that show direct binding of Smc to sybodies by various methods including ELISA, pull-downs and by biophysical methods (GCI). Initially, we omitted these data from the manuscript as we are convinced that the mapping data obtained with chimeric SMC proteins is more definitive and relevant. During the revision we will incorporate the ELISA data showing direct binding and also indicating a lack of preference for a specific state of Smc.

Many modes of sybody binding to Smc are plausible The authors provide an elaborate discussion of sybodies locking the Smc-ScpAB complex in open/ closed states. However, in the absence of structural support, the mechanistic inferences may need to be tempered. For example, is it also not possible for the sybodies to bind the inner interface of the coiled-coil, resulting in steric hinderance to coiled-coil interactions. It is also possible that sybody interaction disrupts ScpAB interaction (as data ruling this possibility out has not been provided). Thus, other potential mechanisms would be worth considering/ discussing. In this direction, did AlphaFold reveal any potential insights into putative binding locations?

We have attempted to map the binding by structure prediction, however, so far, even the latest versions of AlphaFold are not able to clearly delineate the binding interface. Indeed, many ways of binding are possible, including disruption of ScpAB interaction. However, since the main binding site is located on the SMC coiled coils, the later scenario would likely be an indirect consequence of altered coiled coil configuration, consistent with our current interpretation.

1. Sybody expression in vivo Have the authors estimated sybody expression in vivo? Are they all expressed to similar levels?

We have tagged selected sybodies with gfp and performed live cell imaging. This showed that they are all roughly equally expressed and that they localize as foci in the cell presumably by binding to Smc complexes loaded onto the chromosome at ParB/parS sites. We will include this data in the revised version of the manuscript.

1. Sybodies should phenocopy ATP hydrolysis mutant of Smc The sybodies were screened against an ATP hydrolysis deficient mutant of Smc, with the rationale that these sybodies would interfere this step of the Smc duty cycle. Does the expression of the sybodies in vivo phenocopy the ATP hydrolysis deficient mutant of Smc? Could the authors consider any phenotypic read-outs that can indicate whether the sybody action results in an smc-null effect or specifically an ATP hydrolysis deficient effect?

As eluded to above, we think that our selection gave rise to sybodies that bind various, possibly multiple Smc conformations. Consistent with this idea, the phenotypes are similar to null mutant rather than the ATP-hydrolysis defective EQ mutant, which display even more severe growth phenotypes. We will add the following notes to the text:

“These conditions favour ATP-engaged particles alongside the typically predominant ATP-disengaged rod-shaped state (add Vazquez Nunez et al., 2021).”

“ELISA data confirm that nearly all clones bind Smc-ScpAB; however, their binding shows little or no dependence on the presence of ATP or DNA.”

Minor comments: 1. It was surprising that no sybodies were found that could target both bacillus and spneu Smc. For example, sybodies targeting the head regions of Smc that might work in a more universal manner. Could the authors comment on the coverage of the sybodies across the protein structure?

It is rather common that sybodies (like antibodies and nanobodies) exhibit strong affinity differences between highly conserved proteins (> 90 % identity). The underlying reasons for such strong discrimination are i) location of less conserved residues primarily at the target protein surface and ii) the large interaction interface between sybody and target which offers multiple vulnerabilities for disturbance, in particular through bulky side chains resulting in steric clashes. Another frequently observed phenomenon is sybody binding to a dominant epitope, which also often applies to nanobodies and antibodies. A great example for this are the dominant epitopes on SARS-CoV-2 RBDs.

Growth curves (Fig. S3) show a large jump in recovery in growth under sybody induction conditions. Could the authors address this observation here and in the text?

We suppose that this recovery represents suppressor mutants and/or (more likely) improved growth in the absence of functional Smc during nutrient limitation (see Gruber et al., 2013 and Wang et al., 2013). We will add this statement to the text.

L41- Sentence correction: Loop can be removed. Ah, yes, sorry for this confusing error. Thank you. 4. L525 - bsuSmc 'E' :extra E can be removed. To do. Thank you. 5. References need to be properly formatted. To do. Thank you. 6. The authors should add in figure legend for Fig 1i) details on representation of the purple region, and explain the grey strokes for orientation of the loop. To do. 7. How many cells were analysed in the cell biological assays? Legends should include these information. To Be Included.

Reviewer #1 (Significance (Required)):

Overall, this is an impressive study that uses an elegant strategy to find inhibitors of protein activity in vivo. The manuscript is clearly written and the experiments are logical and well-designed. The findings from the study will be significant to the broad field of genome biology, synthetic biology and also SMC biology. Specifically, the coiled coil domain of SMC proteins have been proposed to be of high functional value. The authors have elegantly identified key coiled-coil regions that may be important for function, and parallelly exhibited potential of the use of synthetic sybody/designed binders for inhibition of protein activity.

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

Review: "Single Domain Antibody Inhibitors Target the Coiled Coil Arms of the Bacillus subtilis SMC complex" by Ophélie Gosselin et al, Review Commons RC-2025-03280 Structural Maintenance of Chromosome proteins (SMCs), a family of proteins found in almost all organisms, are organizers of DNA. They accomplish this by a process known as loop extrusion, wherein double-stranded DNA is actively reeled in and extruded into loops. Although SMCs are known to have several DNA binding regions, the exact mechanism by which they facilitate loop extrusion is not understood but is believed to entail large conformational changes. There are currently several models for loop extrusion, including one wherein the coiled coil (CC) arms open, but there is a lack of insightful experimentation and analysis to confirm any of these models. The work presented aims to provide much-needed new tools to investigate these questions: conformation-selective sybodies (synthetic nanobodies) that are likely to alter the CC opening and closing reactions. The authors produced, isolated, and expressed sybodies that specifically bound to Bacillus subtilis Smc-ScpAB. Using chimeric Smc constructs, where the coiled coils were partly replaced with the corresponding sequences from Streptococcus pneumoniae, the authors revealed that the isolated sybodies all targeted the same 4N CC element of the Smc arms. This region is likely disrupted by the sybodies either by stopping the arms from opening (correctly) or forcing them to stay open (enough). Disrupting these functional elements is suggested to cause the Smc-dependent chromosome organization lethal phenotype, implying that arm opening and closing is a key regulatory feature of bacterial Smc-ScpAB. In summary, the authors present a new method for trapping bacterial Smc's in certain conformations using synthetic antibodies. Using these antibodies, they have pinpointed the (previously suggested) 4N region of the coiled coils as an essential site for the opening and closing of the Smc coiled coil arms and that hindering these reactions blocks Smc-driven chromosomal organization. The work has important implications for how we might elucidate the mechanism of DNA loop extrusion by SMC complexes. Some specific comments: Line 75: "likely stabilizing otherwise rare intermediates of the conformational cycle." - sorry, why is that being concluded? Why not stabilizing longer-lived oncformations? We will clarify this statement!

Line 89: Sorry, possibly our lack of understanding: why first ribosome and then phage display?

Ribosome display offers to screen around 10^12 sybodies per selection round (technically unrestricted library size), while for phage display, the library size is restricted to around 10^9 sybodies due to the fact that production of a phage library requires transformation of the phagemid plasmid into E. coli, thereby introducing a diversity bottleneck. This is why the sybody platform starts off with ribosome display. It switches to phage display from round 2 onwards because the output of the initial round of ribosome display is around 10^6 sybodies, which can be easily transferred into the phage display format. Phage display is used to minimize selection biases. For more information, please consult the original sybody paper (PMID: 29792401).

Line 100: Why was only lethality selected? Less severe phenotypes not clear enough?

Yes, colony size is more difficult to score robustly, as the sizes of individual transformant colonies can vary quite widely. The number of isolated sybodies was at the limit of further analysis.

Line 106: Could it be tested somehow if convex and concave library sybodies fold in Bs?

We did not focus on the non-functional sybody candidates and only sybodies of the loop library turned out to cause functional consequences at the cellular level. Notably, we will include gfp-imaging showing that non-lethal sybodies are expressed to similar levels that toxic sybodies. Given the identical scaffold of concave and loop sybodies (they only differ in their CDR3 length), we expect that the concave sybodies fold in the cytoplasm of B. subtilis. For the convex sybodies exhibiting a different scaffold, this will be tested.

Line 125: Could Pxyl be repressed by glucose?

To our knowledge and experience, repression by glucose (catabolite repression) does not work well in this context in B. subtilis.

Line 131: The SMC replacement strain is a cool experiment and removes a lot of doubts!

Thank you! (we agree 😊)

Line 141: The mapping is good and looks reliable, but looks and feels like a tour de force? Of course, some cryo-EM would have been lovely (lines 228-229 understood, it has been tried!).

Yes, we have made several attempts at structural biology. Unfortunately, Smc-ScpAB is not well suited for cryo-EM in our hands and crystallography with Smc fragments and sybodies did not yield well-diffracting crystals.

Line 179: Mmmh. Do we not assume DNA binding on top of the dimerised heads to open the CC (clamp)?

We will clarify the text here.

Line 187: Having sybodies that presumably keep the CC together (closing) and some that do not allow them to come together correctly (opening) is really cool and probably important going forward.

Thank you!

Figure 1 Ai is not very colour-blind friendly.

We are sorry for this oversight. We will try to make the color scheme more inclusive. Thank you for the notification.

Optional: did the authors see any spontaneous mutations emerge that bypass the lethal phenotype of sybody expression?

No, we did not observe spontaneous mutations suppressing the phenotype, possibly due to the limited number of cell generations observed. We tried to avoid suppressors by limiting growth, but this may indeed be a good future approach for further fine map the binding sites and to obtain insights into the mechanism of inhibition.

Optional: we think it would be nice to try some biochemical experiment with BMOE/cysteine-crosslinked B. subtilis Smc in the mid-region (4N or next to it) of the Smc coiled coils to try to further strengthen the story. Some of the authors are experts in this technique and strains might already exist?

We have indeed tried to study the impact of sybody binding on Smc conformation by cysteine cross-linking. However, we were not convinced by the results and thus prefer not to draw any conclusions from them. We will add a corresponding note to the text.

Reviewer #2 (Significance (Required)):

The authors present a new method for trapping bacterial Smc's in certain conformations using synthetic antibodies. Using these antibodies, they have pinpointed the (previously suggested) 4N region of the coiled coils as an essential site for the opening and closing of the Smc coiled coil arms and that hindering these reactions blocks Smc-driven chromosomal organization. The work has important implications for how we might elucidate the mechanism of DNA loop extrusion by SMC complexes. Thank you!

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

Gosselin et al. use the sybody technology to study effects of in vivo inhibition oft he Bacillus subtilis SMC complex. Smc proteins are central DNA binding elements of several complexes that are vital for chromosome dynamics in almost all organisms. Sybodies are selected from three different libraries of the single domain antibodies, using the „transition state" mutant Smc. They identify 14 such mutant sybodies that are lethal when expressed in vivo, because they prevent proper function of Smc. The authors present evidence suggesting that all obtained sybodies bind to a coiled-coil region close to the Smc „neck", and thereby interfere with the Smc activity cycle, as evidenced by defective ATPase activity when Smc is bound to DNA. The study is well done and presented and shows that the strategy is very potent in finding a means to quickly turn off a protein's function in vivo, much quicker than depleting the protein.

The authors also draw conclusions on the molecular mode of action of the SMC complex. The provide a number of suggestive experiments, but in my view mostly indirect evidence for such mechanism.

My main criticism ist hat the authors have used a single - and catalytically trapped form of SMC. They speculate why they only obtain sybodies from one library, and then only idenfity sybodies that bind to a rather small part oft he large Smc protein. While the approach is definitely valuable, it is biassed towards sybodies that bind to Smc in a quite special way, it seems. Using wild type Smc would be interesting, to make more robust statements about the action of sybodies potantially binding to different parts of Smc.

As explained above, we are quite confident the Smc ATPase mutation did not bias the selection in an obvious way. The surprising bias towards coiled coil binding sites has likely other explanations, as they likely form a preferred epitope recognized by sybodies.

Line 105: Alternatively, the other libraries did not produce good binders or these sybodies were 106 not stably expressed in B. subtilis. This could be tested using Western blotting - I am assuming sybody antibodies are commercially avalable. However, this test is not important for the overall study, it would just clarify a minor point.

While there are antibody fragments available to augment the size of sybodies (PMID: 40108246), these recognize 3D-epitopes and are thus not suited for Western blotting. We did not follow up on the negative results much, but would like to point out again that there are several biases that likely emerge for the same reason (bias to library, bias to coiled coil binding site). If correct, then likely few other sybodies are effectively lethal in B. subtilis, with the exception of the ones isolated and characterized. We have added this notion to the manuscript. We have also tested the expression of non-lethal sybodies by gfp-tagging and imaging. These results will be included in the revision.

Fig. 2B: is is odd to count Spo0J foci per cells, as it is clear from the images that several origins must be present within the fluorescent foci. I am fine with the „counting" method, as the images show there is a clear segregation defect when sybodies are expressed, I believe the authors should state, though, that this is not a replication block, but failure to segregate origins.

We agree that this is an important point and will add a corresponding comment to the text.

Testing binding sites of sybodies tot he SMC complex is done in an indirect manner, by using chimeric Smc constructs. I am surprised why the authors have not used in vitro crosslinking: the authors can purify Smc, and mass spectrometry analyses would identify sites where sybodies are crosslinked to Smc. Again, I am fine with the indirect method, but the authors make quite concrete statements on binding based on non-inhibition of chimeric Smc; I can see alternative explanations why a chimera may not be targeted.

We have made several attempts of testing direct binding with mixed outcomes and decided to not include those results in the light of the stronger and more relevant in vivo mapping. However, we will add ELISA results and briefly discuss grating coupled interferometry (GCI) data and pull-downs.

Smc-disrupting sybodies affect the ATPase activity in one of two ways. Again, rather indirect experiments. This leads to the point Revealing Smc arm dynamics through synthetic binders in the discussion. The authors are quite careful in stating that their experiments are suggestive for a certain mode of action of Smc, which is warranted.

In line 245, they state More broadly, the study demonstrates how synthetic binders can trap, stabilize, or block transient conformations of active chromatin-associated machines, providing a powerful means to probe their mechanisms in living cells. This is off course a possible scenario for the use of sybodies, but the study does not really trap Smc in a transient conformation, at least this is not clearly shown.

We agree and will carefully rephrase this statement. Thank you.

Overall, it is an interesting study, with a well-presented novel technology, and a limited gain of knowledge on SMC proteins. We respectfully disagree with the last point, since our unique results highlight the importance of the Smc coiled coils, which are otherwise largely neglected in the SMC literature, likely (at least in part) due the mild effect of single point mutations on coiled coil dynamics.

Reviewer #3 (Significance (Required)):

The work describes the gaining and use of single-binder antibodies (sybodies) to interfere with the function of proteins in bacteria. Using this technology for the SMC complex, the authors demonstrate that they can obtain a significant of binders that target a defined region is SMC and thereby interfere with the ATPase cycle.

The study does not present a strong gain of knowledge of the mode of action of the SMC complex.

As pointed out above, we respectfully disagree with this assertion.

• *

3. Description of the revisions that have already been incorporated in the transferred manuscript

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

• *

4. Description of analyses that authors prefer not to carry out

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

As pointed out above, there are a few minor points that we prefer not to experimentally address. In particular, we do not consider it as necessary to determine the expression levels of sybodies which were non-inhibitory. We also wish to note that we attempted to obtain structural additional biochemical data and to that end performed cryo-EM, crystallography and cysteine cross-linking experiments. Unfortunately, we did not obtain sybody complex structures and the cross-linking data were unfortunately not conclusive. We also wish to note that the first author has finished her PhD and left the lab, which limits our capacity to add additional experiments. However, as the reviewers also pointed out, the main conclusions are well supported by the data already.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Response to Reviewers

We thank the Reviewers for their appreciative comments (Reviewer 1: “first time that a well-established existing mathematical model of signaling response extended and applied to heterogeneous ligand mixtures”)and constructive suggestions for improvement. In this extensive revision, we have not only addressed the suggestions comprehensively but also extended our analysis of signaling antagonism to all doses and at the single-cell level using novel computational workflows. This resulted in the discovery of several mechanismsof antagonism and synergy that are dose-dependent, and dependent on the cell-specific state of the signaling network, thereby manifesting in only a subset of cells.

We have addressed Reviewer comments: we have made substantial revisions to improve clarity, rigor, and biological interpretation. Below we briefly summarize the main concerns raised by Reviewers 1-3 and how we have addressed them.

• We have rewritten the Methods section to clarify our approaches. We have also added the explanation of methodology and the rationale in the main text to improve readability and comprehensiveness (Addressing Reviewer #1 comments). This includes explaining and justifying the signaling codon approaches (Reviewer 1), our core-module parameter matching methodology and discussion (Reviewer #1, point 11, Reviewer #2, point 1), and the model schematic (Reviewer #1, point 5).
• For one of our major conclusions – that macrophages may distinguish stimuli in the context of ligand mixtures – we have validated these results with experiments, which increases confidence in this conclusion (Reviewer #2, point 3, Reviewer #3, point 2).
• We have updated the model for CpG-pIC competition using Michaelis–Menten kinetics without any additional parameters, rather than introducing new free parameters. This change removes parameter freedom for fitting combinatorial conditions, leading to a more constrained and mechanistically grounded model whose predictions align better with experimental data (Updated Figures 2 and S2; Reviewer #2, point 2).
• We have addressed all other editorial and clarification-related concerns as well, as detailed in our point-by-point response below. In addition, we have extended the scope of the manuscript. We have extended our analysis of ligand combinations across a broad dose range, from non-responsive to saturated conditions. This led to several additional discoveries. For example, we show that ultrasensitive IKK activation can underlie synergistic combinations of ligands at low doses. In contrast, beyond the CpG-poly(I:C) antagonism, we identify that competition for CD14 uptake by LPS and Pam can generate antagonism between these ligands within specific dose ranges.

Importantly, such antagonism or synergy is not evident in all cells in the population. It may also not be picked up by studies of the mean behavior. With our new computational workflow that allows for single-cell resolution we identify the conditions that must be met by the signaling network state, for antagonism or synergy to take place.

Further, we examine the hypothesis that such signaling pathway interactions affect stimulus-response specificity in combinatorial stimulus conditions. By comparing models with and without this antagonism, we demonstrate that antagonistic interactions can improve stimulus-response specificity in complex ligand mixtures.

These additional analyses provide a new mechanistic understanding of cellular information processing and elucidate how synergy and antagonism can mechanistically shape signaling fidelity in response to complex ligand mixtures.

Point-by-Point Response

Reviewer #1

Evidence, reproducibility and clarity

The authors extend an existing mathematical model of NFkB signalling under stimulation of various single receptors, to model that describes responses to stimulation of multiple receptors simultaneously. They compare this model to experimental data derived from live-cell imaging of mouse macrophages, and modify the model to account for potential antagonism between TLR3 and TLR9 response due to competition for endosomal transport. Using this framework they show that, despite distinguishability decreasing with increasing numbers of heterogenous stimuli, macrophages are still able in principle to distinguish these to a statistically significant degree. I congratulate the authors on an interesting approach that extends and validates an existing mathematical model, and also provides valuable information regarding macrophage response.

Response: We thank the reviewer for this appreciative assessment and for the careful reading of our work. The constructive comments helped us substantially improve the rigor and clarity of the manuscript.

In addition to revising the text for clarity, we have extended our analysis to systematically investigate dose-response behavior for each pair of ligand combination. Using the experimentally validated model, we explored 10 ligand pairs across a range of doses from non-responsive to saturating. This allowed us to identify mechanistic regimes in which synergy and antagonism arise at the single-cell level. In particular, we found that low-dose synergy can be explained by ultrasensitive IKK activation (Figure 4 and corresponding supplementary figures), while antagonism can emerge from competition for shared components such as CD14 (Figure 5 and corresponding supplementary figures). We further show that antagonism can enhance condition distinguishability in ligand mixtures, thereby contributing to stimulus-response specificity (Figure 5 and corresponding supplementary figures).

There are no major issues affecting the scientific conclusions of the paper, however the lack of detail surrounding the mathematical model and the 'signaling codons' that are used throughout the paper make it difficult to read. This is exacerbated by the fact that I was unable to find Ref 25 which apparently describes the model, however I was able to piece together the essential components from the description in Ref 8 and the supplementary material.

Response: This comment helped us to improve the writing. We apologize that the key reference 25 was still not publicly available. It is now published in Nature Communications. In addition, we have added more details to clarify the mathematical model as well as the signaling codons, in results and in methods. Please see below for details.

Lots of the minor comments below stem from this, however there are also a few other places that could benefit from some additional clarification and explanation.

Significance: 1. '...it remains unclear complex...' -> '...it remains unclear whether complex...' Response: We have rewritten the Significance (now it is Synopsis).

Introduction: 2. 'temporal dynamics of NFkB' - it would be good to be more concrete regarding the temporal dynamics of what aspect of this (expression, binding, conformation, etc), if possible. Response: It refers to the presence of NFκB into nucleus, which represents active NFκB capable of activating gene expression. We have clarified this (Lines 59-61 in introduction paragraph 2). “Upon stimulation, NFκB translocates into the nucleus, … activating immune gene expression (10, 15–19).”

'signaling codons' - the behaviour of these is key to the entire paper, so even if they are well described in the reference, it would be good to have a short description as early as possible so that the reader can get an idea in their mind what exactly is being discussed here. Later, it would be good to have concrete description of exactly what these capture.

Response: We thank the reviewer for this comment. We have added one whole paragraph in the early introduction to describe the concept of Signaling Codons which allow quantitative characterization of NFkB stimulus-response-specific dynamics (Lines 60-67). We have also added more concrete description of Signaling Codons in the results as well as adding an illustration for the signaling codons (Lines 169-175, Figure S2B).

'This challenge...population of macrophages' - this seems a bit out of place, and is a bit of a run on sentence, so I suggest moving this to the next paragraph and working it into the first sentence there '...regulatory mechanisms, and this challenge could be addressed with a model parameterised to account for heterogeneous...Early models ...', or something similar.

Response: We thank the reviewer for this suggestion, we have revised this as suggested. This improves the logic flow (Lines 87-88).

Ref 25: I can't find a paper with this title anywhere, so if it's an accepted preprint then it would be good to have this available as well. That said, I still think it would be difficult to grasp the work done in this paper without some description of the mathematical model here, at least schematically, if not the full set of ODEs. For example, there are numerous references to how this incorporates heterogeneous responses, the 'core module', etc, and the reader has no context of these if they aren't familiar with the structure of the model. Response: We apologize that Ref 25 was not on PubMed. Now it’s published, and we have updated the corresponding information. This comment also helped us to improve the writing by adding a description of the mathematical model in the Introduction (Lines 95-105), the results (Lines 129-141), and a detailed description of the model in the Methods (Simulation of heterogenous NFκB dynamical responses.)

We have also added the schematic of the model topology in Figure S1 (adapted from previous publications Guo et al 2025, Adelaja et al 2021) to make sure the paper is self-contained.

'A key challenge which is...' -> 'A key challenge is...' Response: We have revised the Introduction and removed this sentence.

'With model simulation ...' -> a bit of a run on sentence, I suggest breaking after 'conditions'. Response: We have revised the introduction and removed this sentence.

Results:

1. This section would benefit from a more in-depth description of the model and experimental setup. In particular for the experiment, the reader never really knows what this workflow for this is, nor what the model ingests as input, and what the predictions are of. Response: This comment helped us to improve clarity by adding an in-depth description of the model and experimental setup. We have revised the Results as suggested (Lines 129-141). We also appended the corresponding revision here for reviewer reference.

“This mechanistic model was trained on single-ligand response experimental datasets, capturing the single-ligand stimulus-response specificity of the population of macrophages while accounting for cellular heterogeneity. Specifically, quantitative NFκB dynamic trajectory data from hundreds of single macrophages responding to five single ligands (TNF, pIC, Pam, CpG, LPS) at 3-5 doses was obtained from live cell imaging experiments. The mathematical model (Figure S1) consists of a 52-dimensional system of ordinary differential equations, including 52 intracellular species, 101 reactions and 133 parameters, and is divided into five receptor modules, which respond to the corresponding ligands respectively, and the IKK-NFκB core module that contains the prominent IκBα negative feedback loop. By fitting the single-cell experimental data set with a non-linear mixed effect statistical model (coupling with 52-dimensional NFκB ODE model), the parameter distributions for the single-cell population were inferred. Analyzing the resulting simulated NFκB trajectories with Information theoretic and machine learning classification analyses confirmed that the virtual cell model simulations reproduced key SRS performance characteristics of live macrophages.”

'..mechanistic model was trained...' - trained in this study, or in the previous referenced study? Response: The mechanistic model was trained in a previous study (Guo et al 2025 Nature Comm), and we have clarified this in the revision (Lines 127 - 129).

1. 'determined parameter distributions' - this is where it would be good to have more background on the model. What parameters are these, and what do they correspond to biologically? It would also be nice to see in the methods or supplementary material how this is done (maximum likelihood, etc). Response: This comment helps us to clarify the predetermined parameter distributions. We have revised the methods to include this information (Simulation of heterogenous NFκB dynamical responses, paragraph 3). We have appended the corresponding text here for reviewer’s convenience.

“The ODE model was then fitted to the population of single-cell trajectories to recapitulate the cell-to-cell heterogeneity in the experimental data (2). This is achieved by solving the non-linear mixed effects model (NLME) through stochastic approximation of expectation maximation algorithm (SAEM) (3–6). Seventeen parameters were estimated. Within the core module, the estimated parameters included the rates governing TAK1 activation (k52, k65), the time delays of IκBα transcription regulated by NFκB (k99, k101), and the total cellular NFκB abundance (tot NFκB). Within the receptor module, receptor synthesis rates (k54 for TNF, k68 for Pam, k85 for CpG, k35 for LPS, k77 for pIC), degradation rates of the receptor–ligand complexes (k56, k61, k64 for TNF; k75 for Pam; k93 for CpG; k44 for LPS; k83 for pIC), and endosomal uptake rates (k87 for CpG; k36 and k40 for LPS; k79 for pIC) were fitted. All remaining parameters were fixed at literature-suggested values (1). The single-cell parameters inferred from experimental individual‐cell trajectories then served as empirical distributions for generating the new dataset (see SupplementaryDataset2).”

'matching cells with similar core model...' - it's difficult to follow the logic as to why this is done, so I think this needs to be a little clearer. My guess would be that the assumption is that simulated cells with similar 'core' parameters have a similar downstream signalling response, and therefore the receptors can be 'transplanted'. So it would be nice to see exactly what these distributions are and what the effect of a bad match would be. Response: We thank the reviewer for this comment. In the revision, we have explained the rationale for matching cells with similar core module (Lines 145-152).

“Previous work determined parameter distributions for only the cognate receptor module (and the core module) that provided the best fit for the relevant single ligand experimental data (Figure 1A, Step 1), but other receptor modules’ parameter values were not determined. To simulate stimulus responses to more than two ligands, we imputed the other ligand-receptor module parameters using shared core-module parameters as common variables and employing nearest-neighbor hot-deck imputation (35). In this setup, the core module functions as an “anchor” to harmonize two or more receptor-specific parameter distributions.”

This nearest-neighbor hot-deck imputation approach (the core module matching method) was shown to outperform other approaches, including random matching and rescaled-similarity matching (Guo et al. 2025, Supplementary Figure S11). For the reviewer’s convenience, we have also appended the corresponding figure below.

Figure S11 from (Guo et al., 2025). Assessment of matching techniques for predicting single-cell responses to various ligand stimuli (a-d). Heatmaps illustrating the Wasserstein distance between the signaling codon distributions predicted by the model and those observed in experiments. The analysis employs four distinct matching methods to align the five ligand-receptor module parameters: (a) “Random Matching”, (b) “Similarity Matching” (the method used in our study), (c) “Rescaled-Similarity Matching”, and (d) “Sampling Approximated Distribution”. In the heatmaps, rows represent signaling codons, columns denote ligands, and the color intensity indicates the Wasserstein distance, providing a visual metric of similarity between model predictions and experimental data. e-f. Histogram of the average Wasserstein distance between the model-predicted and experimentally observed signaling codon distributions, summarized across signaling codons (e) and ligands (f).

Some explanation of how this relates to the experimental data the parameters are fit on would also be useful. (a) Is there a correspondence between individual simulated cells and the experimental data for the single ligand stimulation, and then the smallest set of these is taken? Is there also a matching from the simulated multi-receptor modules and the multi-receptor data, and if so, is this done in the same way? Response: This comment to help us clarify the correspondence relationship between model simulations and experimental data.

Yes—there is a correspondence between individual simulated cells and the previously published experimental data (Guo et al., 2025b) for single-ligand stimulation. We have revised the first paragraph of the Results (Lines 136–148) and the Methods (Lines 544-557) to clarify how the model simulations were fit to the previous experimental dataset. See Reviewer 1, Comments 10 for the updates in Methods. We have pasted in the revised Results section below for the reviewer’s reference.

“By fitting the single-cell experimental data set with a non-linear mixed effect statistical model (coupling with 52-dimensional NFκB ODE model), the parameter distributions for the single cell population were inferred.”

'six signaling codons' - here it would be good to recapitulate what these represent, but also what the 'strength' and 'activity' correspond to (total integrated value, maximum value, etc) Response: We thank the reviewer for the suggestion and have clarified this point (Lines 169-175, Figure S2B).

'pre-defined thresholds' - no need to state these numerically in the text (although giving some sense of how/why these were chosen would give some context), but I couldn't find the values of these, nor values corresponding to the signaling codons. Response: We appreciate the reviewer’s comment. We have added this information in the figure legend (Figure 1B-C) and Method -- “Responder fraction” (Lines 666-672). Specifically, for the model simulation data, the integral thresholds are 0.4 (µM·h), 0.5 (µM·h), and 0.6 (µM·h). The peak thresholds are 0.12 (µM), 0.14 (µM), and 0.16 (µM). For the experimental data, the integral thresholds are 0.2 (A.U.·h), 0.3 (A.U.·h), and 0.4 (A.U.·h). The peak thresholds are 0.14 (A.U.), 0.18 (A.U.), and 0.22 (A.U.). Thresholds were selected so that the medium threshold yields 50% responder cells under single-ligand conditions, while the responder ratio remains unsaturated under three-ligand stimulation.

'non-responder cells are likely a result of cellular heterogeneity in receptor modules rather than the core module' - is this the 'ill health' referenced earlier? If so make this clear. Response: Yes, this is the ‘ill health’ referenced earlier, and we have clarified this (Lines 198-199).

It's also very difficult to follow this chain of logic, given that the reader at this point doesn't have any knowledge of what the 'core' module is, nor the significance of the thresholds on the signaling codons. I would suggest making this much clearer, with reference to each of these. Response: We apologize for the poor explanation. We have now explained in the Introduction (Lines 95-106) and the results (Lines 129-141) how the model is structured into receptor-proximal modules that converge on the common core module. We have also added a schematic for clarity (Figure S1). For further clarification of the math models, we have significantly revised the Methods (Simulation of heterogenous NFκB dynamical responses). The defined thresholds are clarified in the Methods -- “Responder fraction”.

'...but the model represented these as independent mass action reactions' - the significance of this may not be clear to someone not familiar with biophysical models, so probably better to make it explicit. Response: We thank the reviewer for this reminder, and we have added a description of the significance of this point (Lines 225-227).

'...we trained a random forest classifier...' - is this trained on the 'raw' experimental time series data, or on the signaling codons? Response: It is trained on the signaling codons calculated from model simulations of NFκB trajectories. We have clarified this (Lines 260-261).

'We also applied a Long Short-Term Memory (LSTM) machine learning model...' - it might be good to reference these three approaches at the beginning of this section, otherwise they seem to come out of the blue a little. Response: We have added the references of these three approaches in the beginning of this section (Lines 242-246).

'We then used machine learning classifiers...' - random forests, LSTMs, or a different model? Response: We have clarified that this as random forest classifier (Line 276).

Discussion:

1. '...over statistical models...' - suggest maybe 'purely statistical models' Response: We thank the reviewer for this suggestion. We have rewritten the whole Discussion to include the new insights of antagonism and synergy and their roles in maintaining unexpectedly high SRS performance. Thus, this sentence was removed.

'We found that endosomal transport...' - A paper by Huang, et. al. (https://www.jneurosci.org/content/40/33/6428) observed a synergistic phagocytic response between CpC and pIC stimulation in microglia. This is still consistent with a saturation effect dependent on dose, but may be worth a mention. Response: We thank the reviewer for referring this interesting paper to us, and this comment helps us to improve the Discussion of inflammatory signaling pathways besides NFκB. This paper demonstratessynergistic effects between CpG and pIC in inhibiting tumor growth and promoting cytokine production(Huang et al., 2020), such as IFN-β and TNF-α, whose expression is also regulated by the IRF and MAPK signaling pathways (Luecke et al., 2021; Sheu et al., 2023). This finding does not contradict our findings that CpG and pIC act antagonistically in the NFκB signaling pathway because of the combinatorial pathways that act on gene expression: CpG can activate the MAPK signaling pathway (Luecke et al., 2024) but not the IRF signaling pathway, whereas pIC activates the IRF signaling pathway (Akira and Takeda, 2004) but only weakly the MAPK pathway. Therefore, their combination can synergistically regulate inflammatory responses. We have added this to the discussion (Lines 515-522).

'...features termed...' -> 'features, termed' Response: We thank the reviewer for their carefully reading, and we have rewritten the Discussion.

'...we applied a Long Short-Term Memory (LSTM) machine learning model..' - maybe make clear that this is on the time-series data (also LSTM has already been defined). Response: We thank the reviewer for their carefully reading, and we have rewritten the Discussion.

Materials and methods:

1. The descriptions in this section are quite vague, so I would suggest expanding this with more detail from the supplementary material, where things are quite well explained. Response: We thank the reviewer for this suggestion, and we have rewritten the whole Methods as suggested.

'sampling distribution' - not clear what this refers to in this context Response: We have clarified this in the revision (Methods -- Simulation of heterogenous NFκB dynamical responses, paragraph 3). “The single-cell signaling-pathway parameter values used for bootstrapping sampling to generate model simulations are given in Supplementary dataset 2.”

'RelA-mVenus mouse strain' - it would be good to mention the relevance of the reporter for NFkB signaling Response: We have added the relevance of the reporter for NFkB signaling (Methods, Lines 624-626).

'...A random forest classifier...' -> a random forest classifier

Response: We have rewritten the methods.

Significance

This study provides mechanistically interpretable insight on the important question of how immune cells perform target recognition in realistic scenarios, and also provides validation of existing mathematical models by extending these beyond their original domain. The paper uses 'signaling codons' as a proxy for information processing, however in this instance it is cross-validated with an LSTM model that is applied directly to the time series data. Nevertheless, the scope of the paper is such that it does not deal with the question of how these signals are transmitted or used in a downstream immune response. To my knowledge, this is the first time that a well established existing mathematical model of signalling response has been extended and applied to heterogeneous ligand mixtures. These results will be of interest to those studying immune cell responses, and to those interested in basic research on mathematical models of signaling and cellular information processing more generally.

My background is in biophysical models, machine learning, and signaling in cancer. I have a basic understanding of immunology, but no experience in experimental cell biology.

Response: We thank the reviewer for highlighting the novelty of our study. We appreciate the reviewer’s recognition that our work advances the understanding of cellular information processing in the context of ligand mixtures, particularly as the first to extend computational models to investigate signaling fidelity under mixed-ligand conditions.

We agree that this work will interest computational biologists focused on signaling network modeling and information processing. In addition, we believe it will also be valuable for all signaling biologists, as we provide fundamental insights. For experimental biologists in particular, our model provides an efficient, quantitative framework for exploring and generating testable hypotheses.

We would also like to gently emphasize that evaluating specificity within signaling pathways is as essential as studying downstream functional responses. While immune function outcomes are certainly important, they rely on the upstream signaling pathways that first respond to environmental cues. Understanding how these signaling pathways achieve specificity and discriminability is therefore crucial. For example, this is particularly relevant for drug development targeting pathways such as NFκB, where assessing the direct signaling output—NFκB activation dynamics—can provide valuable insight into the effects of pharmacological interventions.

Reviewer #2

Evidence, reproducibility and clarity

Guo et al. developed a heterogeneous, single-cell ODE model of NFκB signaling parameterized on five individual ligands (TNF, Pam, LPS, CpG, pIC) and extended it, via core-module parameter matching, to predict responses to all 31 combinations of up to five ligands. They found that simulated responder fractions and signaling codon features generally agreed with live-cell imaging data. A notable discrepancy emerged for the CpG (TLR9) + pIC (TLR3) pair: experiments exhibited non-integrative antagonism unpredicted by the original model. This issue was resolved by incorporating a Hill-type term for competitive, limited endosomal trafficking of these ligands. Finally, by decomposing NFκB trajectories into six "signaling codons" and applying Wasserstein distances plus random-forest and LSTM classifiers, the authors showed that stimulus-response specificity (SRS) declines with ligand complexity but remains statistically significant even for quintuple mixtures. This is a well written and scientifically sound manuscript about complexities of cellular signaling, especially considering the limitations of in vitro experiments in recapitulating in vivo dynamics.

Response: We thank the reviewer for carefully reading the manuscript and for this endorsement. We have significantly improved the manuscript thanks to the reviewer’s insightful comments (see below for point-to-point responses).

Besides addressing the reviewer’s questions, we have further extended our work to investigate how ligand pairs interact across all doses and how those interactions affect stimulus-response specificity. As the reviewer pointed out, experimental studies are limited in recapitulating the multitude of complex physiological contexts. The model is helpful to explore more complex scenarios beyond the feasibility of in-vitro experimental setups. Using computational simulations, we have further explored 360 conditions generated from 10 ligand pairs, each evaluated at 6 doses spanning non-responsive to saturating levels, and with each condition considered 1000 cells to capture the heterogeneity of the population.

From this extended analysis, we identified the mechanistic bases for observations of both synergy and antagonism. Synergy for certain low-dose ligand combinations can be explained by ultrasensitive IKK activation (Figure 4), while antagonism between LPS and Pam arises from competition for the cofactor CD14 (Figure 5). We show that these phenomena are dependent on the signaling network state and therefore are not observed in all cells of the population. We define the network conditions that must be met for antagonism and synergy to occur. Importantly, we then show that antagonism can contribute to stimulus-response specificity in ligand mixtures (Figure 5).

Here are a few comments and recommendations:

1. The modeling approach used in this manuscript, while interesting, might need further validation. Inferring multi-ligand receptor parameters by matching single-ligand cells on core-module similarity may not capture true co-variation in receptor expression or adaptor availability. Single cell measurements of receptor expressions could be done (e.g. via flow cytometry) to ground this assumption in real data. If the authors think this is out of scope for this manuscript, they could fit core-matched single cell models with two receptor modules from scratch to the two-ligand experimental data. Would this fitted model produce similar receptor parameters compared to the presented approach? At least the authors should add a bit more explanation for why their modeling approach is better (or valid) than fitting the models with 2/3/4/5 receptor modules from scratch to the experimental data.

Response: We thank the reviewer for this comment, this helped us improve the explanation of the methodology, the rationale, and the validation. The methodology is based on the well-established statistical method of nearest-neighbor hot-deck imputation (Andridge and Little, 2010). In this implementation, the core module functions as a stabilizing “anchor” (common variables) to harmonize various receptor-specific parameter distributions. Similar methodologies have been successfully applied to correct batch effects or integrate single-cell RNAseq datasets using anchor cell types (Stuart et al., 2019). Our workflow has been validated on single-ligand stimuli conditions in a previous study (Guo et al., 2025) (See below 3rdparagraph). Here, we used this method to generate predictions for ligand mixtures and have validated them with experimental studies of the dual-ligand stimuli, and we found that our predictions align well with the experimental data. As the reviewer suggested in point 3, in the revision, we also added experimental validation on the binary classifiers of macrophage determines whether specific stimuli are presented in the ligand mixture. The question we are interested in in this work is how macrophage process ligand-specific information in the context of ligand mixtures. For this question, the experimental results align with the model predictions, reaching consistent conclusions.

In the revision, we have explained the rationale for using the nearest-neighbor hot-deck imputation by matching cells with similar core module (Lines 143-150).

“Previous work determined parameter distributions for only the cognate receptor module (and the core module) that provided the best fit for the single ligand experimental data (Figure 1A, Step 1), and other receptor modules parameter information is missing. To simulate stimulus responses to more than two ligands, we imputed the other ligand–receptor module parameters using shared core-module parameters as common variables and employing nearest-neighbor hot-deck imputation (35). In this setup, the core module functions as an “anchor” to harmonize two or more receptor-specific parameter distributions. This was achieved by by minimizing Euclidean distance between the core module parameters associated with the independently parameterized single-ligand models (Figure 1A, Step 2). ”

In Guo et al. (2025) (see Supplementary Figure S11), the nearest-neighbor hot-deck imputation approach (core module similarity matching method) was compared with other approaches, including random matching and rescaled-similarity matching. The results show that, after matching, the core module method best preserves the single-ligand stimulus signaling codon distributions. For the reviewer’s convenience, we have also appended the figure in the response to Reviewer 1, Comment 11.

The advantage of our workflow is that it does not need to be fit to new experimental data and still gives reliable predictions on signaling dynamics. For the reviewer’s interest, we have tried to fit core-matched single cell models with two receptor modules. As fitting parameters require sufficiently large and high-quality datasets, single-ligand stimulation data with more than 1,000 cells can be adequate to estimate 6~7 parameters (Guo et al., 2025) (approx. 1400 cells to 2000 cells per ligand). However, our current experimental dataset for combinatorial-ligand conditions contains only 500~1,000 cells, and we have tested these datasets but results show a poor fit of heterogeneous signaling dynamics. This is due to an insufficient number of cells for estimating 8~10 parameters. We estimate that at least ~1,500 cells would be needed for reliable parameter estimation under dual-ligand stimulation (and more cells may be needed for combinatorial ligand stimuli involving more ligands). This is currently not feasible to obtain for mixed ligands given the large number of combinatorial conditions.

Overall, in this paper, the nearest-neighbor hot-deck imputation approach is presented as a feasible and acceptable approach that best reflects our current understanding of the signaling network. Importantly, it helps identify potential gaps by highlighting discrepancies between model predictions and experimental observations.

(a) The refined model posits competitive, saturable endosomal transport for CpG and pIC, but no direct measurements of endosomal uptake rates or compartmental saturation thresholds are provided, leaving the Hill parameters under-constrained. The authors could produce dose-response curves for CpG and pIC individually and in combination across a range of concentrations to fit the Hill parameters for competitive uptake. (b) If this is out of scope for this paper, the authors should at least comment on why the endosome hypothesis is better than others e.g. crosstalks and other parallel pathway activations. Especially given that even the refined model simulations with Hill equations for CpG and pIC do not quite match with the experimental data (Fig 2 B,E).

Response: (a) The reviewer’s comments helped us to improve our work by employing the Michaelis-Menten Kinetics for substrate competition reactions, which increases the mathematic rigor of the CpG-pIC competition model. In this updated model, there is no free parameters to tune, as all the Vmax, Kd, should be consistent with the single-ligand scenario. And the Hill is same as single-ligand case, equal to 1.

The comments on examining dose-response curves for CpG and pIC inspired us to extend the dose-response curves for all ligand pair combination, allowing us to identify the synergy in low-dose ligand pairs and antagonism for high-dose LPS-Pam, besides CpG-pIC (new Figure 4 & 5).

(b) Regarding alternative hypotheses for antagonism—such as crosstalk or parallel-pathway activation: any antagonistic effect would have to arise from negative regulation acting within the first 30 min. However, IκBα-mediated feedback only becomes appreciable after ~30 min (Hoffmann et al., 2002), and A20-dependent attenuation requires ≥2 h (Werner et al., 2005). Beyond these delayed feedback, NFκB activation depends primarily on phosphorylation and K63-linked ubiquitination, for which no mechanism produces true antagonism; at most, combinatorial inputs saturate the response to the level of the strongest single ligand. We have added this rationale to the Discussion to explain why we favor the endosome saturation hypothesis over other mechanisms (Lines 459-465). While this may not capture every nuance, it represents the simplest model extension capable of reproducing the observed antagonism.

Authors asses the distinguishability of single-ligand stimuli and combinatorial ligands stimuli using the simulations from the refined model. While this is informative, the simulated data could propagate deviations from the experimental data to the classifiers. How would the classifiers fare when the experimental data is used to assess the single-stimulus distinguishability? The authors could use the experimental data they already have and confirm their main claim of the paper, that cells retain stimulus-response specificity even with multiple ligand exposure. In short, how would Fig 3E look when trained/validated on available experimental data?

Response: We thank the reviewer’s valuable comments, and they helped us strengthen the rigor of our analysis by incorporating cross-model testing. Specifically, we refined our analysis of ligand presence/absence classification by including ROC AUC and balanced accuracy metrics. This adjustment accounts for the fact that the experimental data did not cover all combinatorial conditions, thereby mitigating potential biases from data imbalance and threshold choice. The experimental results are qualitatively consistent with the simulations, though—as expected—they show somewhat lower ligand distinguishability compared to the noise-free simulated dataset. We have updated Figures 3E–F (previously Figure 3E), added Figure S8, and revised the manuscript accordingly (Lines 292–301). For the reviewer’s convenience, we have also pasted in the revised manuscript text below.

“Classifiers trained to distinguish TNF-present from TNF-absent conditions achieved a Receiver Operating Characteristic-Area Under the Curve (ROC AUC) of 0.96, significantly above the 0.5 baseline (Figure 3D, Figure S8A). Extending this analysis to other ligands, cells detected LPS (0.85), Pam (0.84), pIC (0.73), and CpG (0.63) in mixtures (Figure 3D, S8A). Using experimental data from double- and triple-ligand stimuli (Figure 1D), ROC AUC values were TNF 0.74, LPS 0.74, Pam 0.66, pIC 0.75, and CpG 0.66 (Figure 3E, S8B). Classifier accuracies yielded consistent results (Figure S8C-D). These results indicated a remarkable capability of preserving ligand-specific dynamic features within complex NFκB signal trajectories that enable nuclear detection of extracellular ligands even in complex stimulus mixtures.”

While the approach of presented here with multiple simultaneous ligand exposures is a major step towards the in vivo-like conditions, the temporal aspect is still missing. That is, temporal phasing i.e. sequential exposure to multiple ligands as one would expect in vivo rather than all at once. This is probably out of scope for this paper but the authors could comment how how their work could be taken forward in such direction and would the SRS be better or worse in such conditions. Response: We thank the reviewer for this insightful comment. We have added “the temporal aspect of multiple ligand exposures” to the discussion (Lines 503-510), and we pasted the corresponding paragraph here for reviewer’s references (black fonts are previous version, and blue fonts is the revised new texts):

“Cells may be expected to interpret not only the combination of signals but also their timing and duration to mount appropriate transcriptional responses (58, 59). For example, acute inflammation integrates pathogen-derived cues with pro- and anti-inflammatory signals over a timeframe of hours to days (58), to coordinate the pathogen removal and tissue repairing process. Investigating sequential stimulus combinations in our model is therefore crucial for understanding how cells process complex physiological inputs. Simulations that account for longer timescales may require additional feedback mechanisms, as described in some of our previous studies for NFκB (15, 60). ** ”

There is no caption for Figure 3F in the figure legend nor a reference in the main text.

Response: In the revised manuscript we actually removed Figure 3F.

Significance

General assessment: This is a good manuscript in it's present form which could get better with revision. There needs more supporting data and validation to back the main claim presented in the manuscript.

Significance/impact/readership: When revised this manuscript could be of interest to a broad community involving single cells biology, cell and immune signaling, and mathematical modeling. Especially the models presented here could be used a starting point to more complex and detailed modeling approaches.

Response: We thank the reviewer for this endorsement. The reviewer’s constructive suggestion helped us significantly improve the clarity and rigor of our main conclusion.

In summary, we have strengthened the computational framework in several ways. We improved the model’s fit to experimental single-ligand training data and reformulated the antagonistic CpG-pIC model using Michaelis–Menten kinetics, thereby reducing parameter arbitrariness and increasing mechanistic interpretability. These changes led to better agreement between model predictions and experimental observations for combinatorial ligand responses (Updated Figure 2 and Figure S2), which we hope will further increase experimentalists’ confidence in the modeling results. We have also validated one key conclusion (“cells retain stimulus-response specificity even with multiple ligand exposure”) using the experimental dataset, and it aligns with the model predictions.

In addition, we have further extended our analysis and the scope. Inspired by the reviewer’s advice (and Reviewer 3’s comment 1b) on dose-combination study for CpG-pIC pair, we expanded our research to dose-response relationships for all dual-ligand combinations (Lines 302-406, Figure 4-5). This additional comprehensive analysis allowed us to identify the mechanism of synergistic and antagonistic effects in single-cell responses and to pinpoint the corresponding dose ranges among different ligand pairs.

Interestingly, we found that IKK ultrasensitive activation may lead to low-dose ligand combinations synergistic response for single cells. We also found that CD14 uptake competition between LPS and Pam may lead to antagonistic/non-integrative combination. Our simulation-based finding of non-integrative combination of LPS-Pam stimuli aligns with previous independent experimental finding of non-integrative response for LPS and Pam combination (Kellogg et al., 2017), and this independent experimental study validated our model prediction.

We further analyzed stimulus-response specificity under conditions predicted to exhibit synergy or antagonism. Our results indicate that antagonistic combinations of ligands can increase stimulus-response specificity in the context of ligand mixtures.

Reviewer #3

Evidence, reproducibility and clarity

The authors investigate experimentally single macrophages' NF-kB responses to five ligands, separately and to 3 pairs of ligands. Using the single ligand stimulations, they train an existing mathematical model to replicate single-cell NF-kB nuclear trajectories. From what I understand, for each single cell trajectory in response to a given ligand, the best fit parameters of the core module and the receptor module (specific for the given ligand) are found.

Then (again, from what I understand), single ligand models are used to generate responses to combinations of ligands. The parametrizations of single ligand models (to be combined) are chosen to have the most similar core modules. It is not described how the responses to more than one ligand are calculated - I expect that respective receptor modules work in parallel, providing signals to the core module. After observing that the response to CpG+pIC is lower (in terms of duration and total) than for CpG alone, the model is modified to account for competition for endosomal transport required by both ligands.

Having the trained model, simulations of responses to all 31 combinations of ligands are performed, and each NF-κB trajectory is described by six signaling codons-Speed, Peak, Duration, Total, Early vs. Late, and Oscillations. Next, these codons are used to reconstruct (using a random forest model) the stimuli (which may be the combination of ligands). The single and even the two ligand stimuli are relatively well recognized, which is interpreted as the ability of macrophages to distinguish ligands even if present in combination.

We thank the reviewer for careful reading of the manuscript.

Major comments

1) The demonstrated ability to recognize stimuli is based on several key assumptions that can hardly be met in reality.

Response: We thank the reviewer for this comment, which prompted us to carefully reflect on the rigor of our work, inspired us to extend our analysis to a broad range of ligand-dose combinations, and helped us improve clarifying the limitations of our approach. Please see our detailed responses below.

a) The cell knows the stimulation time, and then it can use speed as a codon. Look on fig. S4A: The trajectories in response to plC are similar to those in response to TNF, but just delayed. Response: We thank the reviewer for this comment. We updated the model parameterization to better fit to the single-ligand pIC condition (Lines 557-559). In the updated model, the simulated responses to TNF and pIC are quite different (Fig. S2A-B, Fig. S5A-B). Specifically, the Peak, Duration, EarlyVsLate, and Total signaling codons have different values. In addition, the literature suggests that timing difference of NFκB activation are sufficient to elicit differences in downstream gene expression responses, especially for the early response genes (ERG) and intermediate response genes (ING) (Figure 1 in Ando, et al, 2021). For reviewer’s convenience, we have also appended the figures. Specifically, within the first 60 minutes, ctrl exhibit higher Speed of NFκB activation, and the NFκB regulated ERG and ING show differences in the first 60 minutes (Below Fig 1a,b). Ando et al then identified the gene regulatory mechanism that is able to distinguish between differences in the Speed codon. Importantly, this mechanism does not require knowledge of t=0, i.e. when the timer was started.

The signaling codon Speed, which is based on derivatives, is one way to quantify such timing differences in activation. It was selected from a library of more than 900 different dynamic features using an information maximizing algorithm (Adelaja et al., 2021). It is possible that other ways of measuring time, e.g. time to half-max, might not be distinguished that well by these regulatory mechanisms.

b) The increase of stimulus concentration typically increases Peak, Duration, and Total, so a similar effect can be achieved by changing the ligand or concentration. Response: This (“the increase of stimulus concentration typically increases Peak, Duration, and Total”) is not an assumption. What the reviewer described (“a similar effect can be achieved by changing the ligand or concentration”) may occur or may not. The six informative signaling codons can vary under different ligands or doses. For example, with increasing doses of Pam, the NFκB response shows a higher peak, potentially making it appear more like LPS stimulation. However, as the Pam dose increases, the response duration decreases, which distinguishes it from LPS stimulation (See experimental data shown in Figure 4A, second row, and Figure 3A, second row in Luecke et al., (2024), we also pasted the corresponding figure below for reviewer’s convenience).

Figure 4A and Figure 3A from Luecke et al., (2024). Figure 4A: NFκB activity dynamics in the single cells in response to 0, 0.01, 0.1, 1, 10, and 100 ng/ml P3C4 stimulation. Eight hours were measured by fluorescence microscopy of reporter hMPDMs. Each row of the heatmap represents the p38 or NFκB signaling trajectory of one cell. Trajectories are sorted by the maximum amplitude of p38 activity. Data from two pooled biological replicates are depicted. Total # of cells: 898, 834, 827, 787, 778, and 923. Figure 3A: NFκB activity dynamics in the single cells in response to 100 ng/ml LPS stimulation. Eight hours were measured by fluorescence microscopy of reporter hMPDMs. Each row of the heatmap represents the NFκB signaling trajectory of one cell (with p38 measured shown in the original paper). Trajectories are sorted by the maximum amplitude of p38 activity. Data from two pooled biological replicates are depicted.

Inspired by the reviewer’s comment (and also Reviewer 2’s comments), in the revision, we expanded our research to dose-response relationships for all dual-ligand combinations (Lines 302-406, Figure 4-5). This additional comprehensive analysis allowed us to identify the mechanism of synergistic and antagonistic effects in single-cell responses and to pinpoint the corresponding dose ranges among different ligand pairs.

Interestingly, we found that IKK ultrasensitive activation may lead to synergistic responses to low-dose ligand combinations but only in a subset of single cells. We also found that CD14 uptake competition between LPS and Pam may lead to antagonistic/non-integrative combination. Our simulation-based finding of non-integrative combination of LPS-Pam stimuli aligns with previous independent experimental findings of non-integrative response for LPS and Pam combination (Kellogg et al., 2017).

c) Distinguishing a given ligand in the presence of some others, even stronger bases, on the assumption that these ligands were given at the same time, which is hardly justified. Response: We agree with the reviewer that ligands could be given at different times. Considering time delays between ligands (the inset and also removal) dramatically adds to the combinatorial complexity. Some initial studies by the Tay lab are beginning to explore some scenarios of time-shifted ligand pairs (Wang et al 2025). Here we focus on a systematic exploration of all ligand combinations at 6 different doses. The fact that we do not consider time delays is not an assumption but admittedly a limitation that may well be addressed in future studies. We have included a brief discussion of this issue in the discussion (Lines 503-514). We’ve appended here for reviewer’s convenience.

“Cells may be expected to interpret not only the combination of signals but also their timing and duration to mount appropriate transcriptional responses (Kumar et al., 2004; Son et al., 2023). For example, acute inflammation integrates pathogen-derived cues with pro- and anti-inflammatory signals over a timeframe of hours to days (Kumar et al., 2004), to coordinate the pathogen removal and tissue repairing process. Investigating sequential stimulus combinations in our model is therefore crucial for understanding how cells process complex physiological inputs. Simulations that account for longer timescales may require additional feedback mechanisms, as described in some of our previous studies for NFκB (Werner et al., 2008, 2005). ”

We would like to suggest that despite (or maybe because) limiting our study to coincident stimuli, we made some noteworthy discoveries.

2) For single ligands, it would be nice to see how the random forest classifier works on experimental data, not only on in silico data (even if generated by a fitted model).

Response: This comment and Reviewer 2 comment 3 have helped us strengthen the rigor of our analysis by incorporating cross-model testing. We pasted the response below.

Specifically, we refined our analysis of ligand presence/absence classification by including ROC AUC and balanced accuracy metrics. This adjustment accounts for the fact that the experimental data did not cover all combinatorial conditions, thereby mitigating potential biases from data imbalance and threshold choice. The experimental results are qualitatively consistent with the simulations, though—as expected—they show somewhat lower ligand distinguishability compared to the noise-free simulated dataset. We have updated Figures 3E–F (previously Figure 3E), added Figure S8, and revised the manuscript accordingly (Lines 292–301). For the reviewer’s convenience, we have also included the revised manuscript text below.

“Classifiers trained to distinguish TNF-present from TNF-absent conditions achieved a Receiver Operating Characteristic-Area Under the Curve (ROC AUC) of 0.96, significantly above the 0.5 baseline (Figure 3D, Figure S8A). Extending this analysis to other ligands, cells detected LPS (0.85), Pam (0.84), pIC (0.73), and CpG (0.63) in mixtures (Figure 3D, S8A). Using experimental data from double- and triple-ligand stimuli (Figure 1D), ROC AUC values were TNF 0.74, LPS 0.74, Pam 0.66, pIC 0.75, and CpG 0.66 (Figure 3E, S8B). Classifier accuracies yielded consistent results (Figure S8C-D). These results indicated a remarkable capability of preserving ligand-specific dynamic features within complex NFκB signal trajectories that enable nuclear detection of extracelular ligands even in complex stimulus mixtures.”

3) My understanding of ligand discrimination is such that it is rather based on a combination of pathways triggered than solely on a single transcription factor response trajectory, which varies with ligand concentration and ligand concentration time profile (no reason to assume it is OFF-ON-OFF). For example, some of the considered ligands (plC and CpG) activate IRF3/IRF7 in addition to NF-kB, which leads to IFN production and activation of STATs. This should at least be discussed.

Response: We thank the reviewer for this comment and fully agree. In the previous version, we discussed different signaling pathways combinatorically distinguishing stimulus. In the revision, we have extended this discussion to include the example of pIC and CpG activation, as suggested (Lines 515-522). We pasted the corresponding text below.

“Furthermore, innate immune responses do not solely rely on NFκB but also involve the critical functions of AP1, p38, and the IRF3-ISGF3 axis. The additional pathways are likely activated in a coordinated manner and provide additional information (Luecke et al., 2021). This is exemplified by the studies demonstrating synergistic effects between CpG and pIC in inhibiting tumor growth and promoting cytokine production (Huang et al., 2020), such as IFNβ and TNFα, whose expression is also regulated by the IRF and MAPK signaling pathways (Luecke et al., 2021; Sheu et al., 2023). Therefore the inclusion of parallel pathways of AP1 and MAPK, as well as the type I interferon network (Cheng et al., 2015; Davies et al., 2020; Hanson and Batchelor, 2022; Luecke et al., 2024; Paek et al., 2016; Peterson et al., 2022) are next steps for expanding the mathematical models presented here.”

Technical comments

1) Reference 25: X. Guo, A. Adelaja, A. Singh, W. Roy, A. Hoffmann, Modeling single-cell heterogeneity in signaling dynamics of macrophages reveals principles of information transmission. Nature Communications (2025) does not lead to any paper with the same or a similar title and author list. This Ref is given as a reference to the model. Fortunately, Ref 8 is helpful. Nevertheless, authors should include a schematic of the model.

Response: We apologize for the paper not being accessible on time. It is now. We have also added a schematic of the model as suggested (Figure S1) and have added detailed description of the model and simulations in introduction (Lines 95-106), results (Lines 129-141), and methods (Simulation of heterogenous NFκB dynamical responses).

2) Also Mendeley Data DOI:10.17632/bv957x6frk.1 and GitHub https://github.com/Xiaolu-Guo/Combinatorial_ligand_NFkB lead to nowhere.

Response: We thank the reviewer for this comment, and we have made the GitHub codes public. Mendeley Data DOI:10.17632/bv957x6frk.1 can be accessed via the shared link: https://data.mendeley.com/preview/bv957x6frk?a=6d56e079-d7b0-482e-951f-8a8e06ee8797

and will be public once the paper accepted.

3) Dataset 1 is not described. Possibly it contains sets of parameters of receptor modules (different numbers of sets for each module, why?), but the names of parameters never appear in the text, which makes it impossible to reproduce the data.

Response: We thank the reviewer for this comment, and we have added the description of the dataset (S3 SupplementaryDataset2_NFkB_network_single_cell_parameter_distribution.xlsx) and added the parameter names in the methods (Simulation of heterogenous NFκB dynamical responses).

4) It is difficult to understand how the simulations in response to more than one ligand are performed.

Response: We thank the reviewer for this comment, and we have improved the explanation of the methods (Results, Lines 145-152) and included a detailed description of the model and simulations for combinatorial ligands (Methods, Predicting heterogeneous single-cell responses to combinatorial-ligand stimulation).

Significance

A lot of work has been done, the methodology is interesting, but the biological conclusions are overstated.

Response: We thank the reviewer for their interest in the methodology. We have revised the title, the abstract, and added the discussion about our finding to more accurately document what we have found. In the revision, we have increased the clarity and rigor of the work. For the key conclusion that macrophages maintain some level of NFκB signaling fidelity in response to ligand mixtures, we have validated the binary classifier results on experimental data as reviewer suggested.

In the revision, we have also extended our methodology to explore further, the dose-response curves for different dosage combination for ligand pairs. This further work allowing us identified the synergistic and antagonistic regimes. By comparing the stimulus response specificity for antagonistic model vs the non-antagonistic model, we demonstrated that signaling antagonism may increase the distinguishability of presence or absence of specific ligands within complex ligand mixtures. This provides a mechanism of how signaling fidelity is maintained to the surprising degree we reported.

REFERENCES

Adelaja, A., Taylor, B., Sheu, K.M., Liu, Y., Luecke, S., Hoffmann, A., 2021. Six distinct NFκB signaling codons convey discrete information to distinguish stimuli and enable appropriate macrophage responses. Immunity 54, 916-930.e7. https://doi.org/10.1016/j.immuni.2021.04.011

Akira, S., Takeda, K., 2004. Toll-like receptor signalling. Nat Rev Immunol 4, 499–511. https://doi.org/10.1038/nri1391

Andridge, R.R., Little, R.J.A., 2010. A Review of Hot Deck Imputation for Survey Non-response. Int Stat Rev 78, 40–64. https://doi.org/10.1111/j.1751-5823.2010.00103.x

Cheng, Z., Taylor, B., Ourthiague, D.R., Hoffmann, A., 2015. Distinct single-cell signaling characteristics are conferred by the MyD88 and TRIF pathways during TLR4 activation. Sci Signal 8, ra69. https://doi.org/10.1126/scisignal.aaa5208

Davies, A.E., Pargett, M., Siebert, S., Gillies, T.E., Choi, Y., Tobin, S.J., Ram, A.R., Murthy, V., Juliano, C., Quon, G., Bissell, M.J., Albeck, J.G., 2020. Systems-Level Properties of EGFR-RAS-ERK Signaling Amplify Local Signals to Generate Dynamic Gene Expression Heterogeneity. Cell Systems 11, 161-175.e5. https://doi.org/10.1016/j.cels.2020.07.004

Guo, X., Adelaja, A., Singh, A., Roy, W., Hoffmann, A., 2025a. Modeling single-cell heterogeneity in signaling dynamics of macrophages reveals principles of information transmission. Nature Communications.

Guo, X., Adelaja, A., Singh, A., Wollman, R., Hoffmann, A., 2025b. Modeling heterogeneous signaling dynamics of macrophages reveals principles of information transmission in stimulus responses. Nat Commun 16, 5986. https://doi.org/10.1038/s41467-025-60901-3

Hanson, R.L., Batchelor, E., 2022. Coordination of MAPK and p53 dynamics in the cellular responses to DNA damage and oxidative stress. Molecular Systems Biology 18, e11401. https://doi.org/10.15252/msb.202211401

Huang, Y., Zhang, Q., Lubas, M., Yuan, Y., Yalcin, F., Efe, I.E., Xia, P., Motta, E., Buonfiglioli, A., Lehnardt, S., Dzaye, O., Flueh, C., Synowitz, M., Hu, F., Kettenmann, H., 2020. Synergistic Toll-like Receptor 3/9 Signaling Affects Properties and Impairs Glioma-Promoting Activity of Microglia. J. Neurosci. 40, 6428–6443. https://doi.org/10.1523/JNEUROSCI.0666-20.2020

Kellogg, R.A., Tian, C., Etzrodt, M., Tay, S., 2017. Cellular Decision Making by Non-Integrative Processing of TLR Inputs. Cell Rep 19, 125–135. https://doi.org/10.1016/j.celrep.2017.03.027

Kumar, R., Clermont, G., Vodovotz, Y., Chow, C.C., 2004. The dynamics of acute inflammation. Journal of Theoretical Biology 230, 145–155. https://doi.org/10.1016/j.jtbi.2004.04.044

Luecke, S., Guo, X., Sheu, K.M., Singh, A., Lowe, S.C., Han, M., Diaz, J., Lopes, F., Wollman, R., Hoffmann, A., 2024. Dynamical and combinatorial coding by MAPK p38 and NFκB in the inflammatory response of macrophages. Molecular Systems Biology 20, 898–932. https://doi.org/10.1038/s44320-024-00047-4

Luecke, S., Sheu, K.M., Hoffmann, A., 2021. Stimulus-specific responses in innate immunity: Multilayered regulatory circuits. Immunity 54, 1915–1932. https://doi.org/10.1016/j.immuni.2021.08.018

Paek, A.L., Liu, J.C., Loewer, A., Forrester, W.C., Lahav, G., 2016. Cell-to-Cell Variation in p53 Dynamics Leads to Fractional Killing. Cell 165, 631–642. https://doi.org/10.1016/j.cell.2016.03.025

Peterson, A.F., Ingram, K., Huang, E.J., Parksong, J., McKenney, C., Bever, G.S., Regot, S., 2022. Systematic analysis of the MAPK signaling network reveals MAP3K-driven control of cell fate. Cell Systems 13, 885-894.e4. https://doi.org/10.1016/j.cels.2022.10.003

Sheu, K.M., Guru, A.A., Hoffmann, A., 2023. Quantifying stimulus-response specificity to probe the functional state of macrophages. Cell Systems 14, 180-195.e5. https://doi.org/10.1016/j.cels.2022.12.012

Son, M., Wang, A.G., Keisham, B., Tay, S., 2023. Processing stimulus dynamics by the NF-κB network in single cells. Exp Mol Med 55, 2531–2540. https://doi.org/10.1038/s12276-023-01133-7

Stuart, T., Butler, A., Hoffman, P., Hafemeister, C., Papalexi, E., Mauck, W.M., Hao, Y., Stoeckius, M., Smibert, P., Satija, R., 2019. Comprehensive Integration of Single-Cell Data. Cell 177, 1888-1902.e21. https://doi.org/10.1016/j.cell.2019.05.031

Werner, S.L., Barken, D., Hoffmann, A., 2005. Stimulus Specificity of Gene Expression Programs Determined by Temporal Control of IKK Activity. Science 309, 1857–1861. https://doi.org/10.1126/science.1113319

Werner, S.L., Kearns, J.D., Zadorozhnaya, V., Lynch, C., O’Dea, E., Boldin, M.P., Ma, A., Baltimore, D., Hoffmann, A., 2008. Encoding NF-kappaB temporal control in response to TNF: distinct roles for the negative regulators IkappaBalpha and A20. Genes Dev 22, 2093–2101. https://doi.org/10.1101/gad.1680708

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #1

Evidence, reproducibility and clarity

The authors extend an existing mathematical model of NFkB signalling under stimulation of various single receptors, to model that describes responses to stimulation of multiple receptors simultaneously. They compare this model to experimental data derived from live-cell imaging of mouse macrophages, and modify the model to account for potential antagonism between TLR3 and TLR9 response due to competition for endosomal transport. Using this framework they show that, despite distinguishability decreasing with increasing numbers of heterogenous stimuli, macrophages are still able in principle to distinguish these to a statistically significant degree. I congratulate the authors on an interesting approach that extends and validates an existing mathematical model, and also provides valuable information regarding macrophage response.

There are no major issues affecting the scientific conclusions of the paper, however the lack of detail surrounding the mathematical model and the 'signaling codons' that are used throughout the paper make it difficult to read. This is exacerbated by the fact that I was unable to find Ref 25 which apparently describes the model, however I was able to piece together the essential components from the description in Ref 8 and the supplementary material.

Lots of the minor comments below stem from this, however there are also a few other places that could benefit from some additional clarification and explanation.

Significance:

'...it remains unclear complex...' -> '...it remains unclear whether complex...'

Introduction: 'temporal dynamics of NFkB' - it would be good to be more concrete regarding the temporal dynamics of what aspect of this (expression, binding, conformation, etc), if possible.

'signaling codons' - the behaviour of these is key to the entire paper, so even if they are well described in the reference, it would be good to have a short description as early as possible so that the reader can get an idea in their mind what exactly is being discussed here. Later, it would be good to have concrete description of exactly what these capture.

'This challenge...population of macrophages' - this seems a bit out of place, and is a bit of a run on sentence, so I suggest moving this to the next paragraph and working it into the first sentence there '...regulatory mechanisms, and this challenge could be addressed with a model parameterised to account for heterogeneous...Early models ...', or something similar.

Ref 25: I can't find a paper with this title anywhere, so if it's an accepted preprint then it would be good to have this available as well. That said, I still think it would be difficult to grasp the work done in this paper without some description of the mathematical model here, at least schematically, if not the full set of ODEs. For example, there are numerous references to how this incorporates heterogeneous responses, the 'core module', etc, and the reader has no context of these if they aren't familiar with the structure of the model.

'A key challenge which is...' -> 'A key challenge is...'

'With model simulation ...' -> a bit of a run on sentence, I suggest breaking after 'conditions'.

Results:

This section would benefit from a more in-depth description of the model and experimental setup. In particular for the experiment, the reader never really knows what this workflow for this is, nor what the model ingests as input, and what the predictions are of.

'..mechanistic model was trained...' - trained in this study, or in the previous referenced study?

'determined parameter distributions' - this is where it would be good to have more background on the model. What parameters are these, and what do they correspond to biologically? It would also be nice to see in the methods or supplementary material how this is done (maximum likelihood, etc).

'matching cells with similar core model...' - it's difficult to follow the logic as to why this is done, so I think this needs to be a little clearer. My guess would be that the assumption is that simulated cells with similar 'core' parameters have a similar downstream signalling response, and therefore the receptors can be 'transplanted'. So it would be nice to see exactly what these distributions are and what the effect of a bad match would be.

Some explanation of how this relates to the experimental data the parameters are fit on would also be useful. Is there a correspondence between individual simulated cells and the experimental data for the single ligand stimulation, and then the smallest set of these is taken? Is there also a matching from the simulated multi-receptor modules and the multi-receptor data, and if so, is this done in the same way?

'six signaling codons' - here it would be good to recapitulate what these represent, but also what the 'strength' and 'activity' correspond to (total integrated value, maximum value, etc)

'pre-defined thresholds' - no need to state these numerically in the text (although giving some sense of how/why these were chosen would give some context), but I couldn't find the values of these, nor values corresponding to the signaling codons.

'non-responder cells are likely a result of cellular heterogeneity in receptor modules rather than the core module' - is this the 'ill health' referenced earlier? If so make this clear.

It's also very difficult to follow this chain of logic, given that the reader at this point doesn't have any knowledge of what the 'core' module is, nor the significance of the thresholds on the signaling codons. I would suggest making this much clearer, with reference to each of these.

'...but the model represented these as independent mass action reactions' - the significance of this may not be clear to someone not familiar with biophysical models, so probably better to make it explicit.

'...we trained a random forest classifier...' - is this trained on the 'raw' experimental time series data, or on the signaling codons?

'We also applied a Long Short-Term Memory (LSTM) machine learning model...' - it might be good to reference these three approaches at the beginning of this section, otherwise they seem to come out of the blue a little.

'We then used machine learning classifiers...' - random forests, LSTMs, or a different model?

Discussion:

'...over statistical models...' - suggest maybe 'purely statistical models'

'We found that endosomal transport...' - A paper by Huang, et. al. (https://www.jneurosci.org/content/40/33/6428) observed a synergistic phagocytic response between CpC and pIC stimulation in microglia. This is still consistent with a saturation effect dependent on dose, but may be worth a mention.

'...features termed...' -> 'features, termed'

'...we applied a Long Short-Term Memory (LSTM) machine learning model..' - maybe make clear that this is on the time-series data (also LSTM has already been defined).

Materials and methods:

The descriptions in this section are quite vague, so I would suggest expanding this with more detail from the supplementary material, where things are quite well explained.

'sampling distribution' - not clear what this refers to in this context

'RelA-mVenus mouse strain' - it would be good to mention the relevance of the reporter for NFkB signaling

'...A random forest classifier...' -> a random forest classifier

Significance

This study provides mechanistically interpretable insight on the important question of how immune cells perform target recognition in realistic scenarios, and also provides validation of existing mathematical models by extending these beyond their original domain. The paper uses 'signaling codons' as a proxy for information processing, however in this instance it is cross-validated with an LSTM model that is applied directly to the time series data. Nevertheless, the scope of the paper is such that it does not deal with the question of how these signals are transmitted or used in a downstream immune response. To my knowledge, this is the first time that a well established existing mathematical model of signalling response has been extended and applied to heterogeneous ligand mixtures. These results will be of interest to those studying immune cell responses, and to those interested in basic research on mathematical models of signaling and cellular information processing more generally.

My background is in biophysical models, machine learning, and signaling in cancer. I have a basic understanding of immunology, but no experience in experimental cell biology.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper presents maRQup, a Python pipeline for automating the quantitative analysis of preclinical cancer immunotherapy experiments using bioluminescent imaging in mice. maRQup processes images to quantify tumor burden over time and across anatomical regions, enabling large-scale analysis of over 1,000 mice. The study uses this tool to compare different CAR-T cell constructs and doses, identifying differences in initial tumor control and relapse rates, particularly noting that CD19.CD28 CAR-T cells show faster initial killing but higher relapse compared to CD19.4-1BB CAR-T cells. Furthermore, maRQup facilitates the spatiotemporal analysis of tumor dynamics, revealing differences in growth patterns based on anatomical location, such as the snout exhibiting more resistance to treatment than bone marrow.

Strengths:

(1) The maRQup pipeline enables the automatic processing of a large dataset of over 1,000 mice, providing investigators with a rapid and efficient method for analyzing extensive bioluminescent tumor image data.

(2) Through image processing steps like tail removal and vertical scaling, maRQup normalizes mouse dimensions to facilitate the alignment of anatomical regions across images. This process enables the reliable demarcation of nine distinct anatomical regions within each mouse image, serving as a basis for spatiotemporal analysis of tumor burden within these consistent regions by quantifying average radiance per pixel.

Weaknesses:

(1) While the pipeline aims to standardize images for regional assessment, the reliance on scaling primarily along the vertical axis after tail removal may introduce limitations to the quantitative robustness of the anatomically defined regions. This approach does not account for potential non-linear growth across dimensions in animals of different ages or sizes, which could result in relative stretching or shrinking of subjects compared to an average reference.

Our answer to this comment is included in the Supplemental Methods. The standard deviation of the mouse pixels was calculated to ensure that the image processing steps did not alter the shape or size of the mice. Such consistency is particularly striking because our dataset was accrued by nine lab members over the last five years, before we conceived and carried out our analysis (c.f., answer to point #2). In fact, it is the very consistency of this IVIS measurement that led us to conceive our pipeline. As seen from Supplemental Figure 4G, there is minimal difference in the shape or size of the mice across 7,534 images. A total of 99 images were removed either due to being too slanted (91/7663, 1.2%) or due to processing errors (8/7633, 0.1%). Also, the vertical scaling was conducted while keeping the aspect ratio unchanged to prevent any non-anatomical scaling. Hence, we did not record any nonlinear growth of the mice that would warrant more convoluted alignment and/or batch correction for our images.

(2) Furthermore, despite excluding severely slanted images, the pipeline does not fully normalize for variations in animal pose during image acquisition (e.g., tucked body, leaning). This pose variability not only impacts the precise relative positioning of internal anatomical regions, potentially making their definition based on relative image coordinates more qualitative than truly quantitative for precise regional analysis, but it also means that the bioluminescent light signal from the tumor will not propagate equally to the camera, as photons will travel differentially through the tissue. This differing light path through tissues due to variable positioning can introduce large variability in the measured radiance that was not accounted for in the analysis algorithm. Achieving more robust anatomical and quantitative normalization might require methods that control animal posture using a rigid structure during imaging.

Reviewer #1 is correct that different mouse postures would be an issue when aligning the images and normalizing for size. However, all experiments are conducted for luminescence measurements in the IVIS system (i.e., this requires anesthesia and long integration time for imaging). In our experience and in our 1000+ mouse dataset, we noticed that all experiments (n=37) did place the anesthetized mice in a stretched/elongated position. Of note, these experiments were conducted by nine different researchers who were not instructed on how to place the mice on the machine for ideal image processing, thus showing that the standard protocol of imaging mice on IVIS does not introduce large variations in animal pose during image acquisition. We think the issue raised by Reviewer #1 is moot in the context of classical settings for mouse luminescence imaging.

Reviewer #2 (Public review):

Summary:

The authors developed a method that automatically processes bioluminescent tumor images for quantitative analysis and used it to describe the spatiotemporal distribution of tumor cells in response to CD19-targeting CAR-T cells, comprising CD28 or 4-1BB costimulatory domains. The conclusion highlights the dependence of tumor decay and relapse on the number of injected cells, the type of cells, and the initial growth rate of tumors (where initial is intended from the first day of therapy). The authors also determined the spatiotemporal analysis of tumor response to CAR T therapy in different regions of the mouse body in a model of acute lymphoblastic leukemia (ALL).

Strengths:

The analysis is based on a large number of images and accounts for many variables. The results of the analysis largely support their claims that the kinetics of tumor decay and relapse are dependent on the CAR T co-stimulatory domain and number of cells injected and tumor growth rates. 

Weaknesses:

The study does not specify how a) differences in mouse positioning (and whether they excluded not-aligned mice) and b) tumor spread at the start of therapy influenced their data. The study does not take into account the potential heterogeneity of CAR T cells in terms of CAR T expression or T cell immunophenotype (differentiation, exhaustion, fitness...).

See answer #2 to Reviewer #1.

Author response image 1.

Author response image 1 shows the average tumor radiance on day zero (when CAR-T cell therapy was administered) for all mice. While there is some spread, most mice had tumor localized to the liver or bone marrow.

Reviewer #3 (Public review):

Summary:

The paper "The 1000+ mouse project: large-scale spatiotemporal parametrization and modeling of preclinical cancer immunotherapies" is focused on developing a novel methodology for automatic processing of bioluminescence imaging data. It provides quantitative and statistically robust insights into preclinical experiments that will contribute to optimizing cell-based therapies. There is an enormous demand for such methods and approaches that enable the spatiotemporal evaluation of cell monitoring in large cohorts of experimental animals.

Strengths:

The manuscript is generally well written, and the experiments are scientifically sound. The conclusions reflect the soundness of experimental data. This approach seems to be quite innovative and promising to improve the statistical accuracy of BLI data quantification. 

This methodology can be used as a universal quantification tool for BLI data for in vivo assessment of adoptively transferred cells due to the versatility of the technology.

Weaknesses: 

No weaknesses were identified by this Reviewer. 

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

In this paper, the authors propose a significant advancement in optical image data analysis by employing automation. They effectively demonstrate the valuable insights that can be gained from analyzing extensive datasets with a more unbiased methodology. At present, I do not have any specific suggestions for improvement.

However, it is important to note that this work is limited in its operational scope. Specifically, it relies on predefined ROIs rather than aligning the signal site with anatomical systems. The scaling model and image cropping are simplistic, animal pose is not taken into account, and the data output needs to be called semi-quantitative or qualitative, and would have been stronger utilizing an AI agent. Nevertheless, this work underscores the potential of automated systems in preclinical image analysis, which is a crucial step towards developing more sophisticated approaches to optical image data analysis.

While our analysis used predefined ROIs, the maRQup pipeline allows users to manually draw ROIs on the mouse image.

Reviewer #2 (Recommendations for the authors):

The writing and presentation of data are clear and accurate, but some additional information should be added regarding the imaging protocol used to acquire the original data. 

The authors mention fluorescence in Figure 1. I expected all the data to be generated from bioluminescent NALM-6 tumors, since bioluminescence is indeed measured in average radiance and can be per pixel (p/sec/cm2/sr/pixel). Fluorescence should be measured using radiance efficiency (p/sec/cm2/sr)/(µW/cm2), a unit that compensates for non-uniform excitation light pattern in the instrument. Would the author find different results if fluorescence data were analyzed separately?

Reviewer #2 is correct that the unit for fluorescence would be radiance efficiency. The word “fluorescent” was included in the label of Figure 1a  to highlight that our workflow could be applied to other types of light-generating methods (i.e., fluorescence vs. bioluminescence). However, in this study, measurements of bioluminescent tumors only were analyzed. If fluorescence measurements are to be analyzed, our methods of image acquisition and processing would be directly applicable.

Did the author ever check the signal of the snout in mice with no tumor?

In mice with no tumor, there is no detectable signal in the snout (or anywhere else, for that matter).

The urine of mice contains phosphor, and might give a background signal, especially if longer exposure is used at the end of the study.

For the mice with no tumor injection, the luminescence signal was below background (<10² p/sec/cm²/sr/pixel). In particular, we do not detect any signal in the bladder/urine. Additionally, as described in the Supplemental Methods and Figure 1b, only pixels that were on the mouse as determined from the brightfield image were used to calculate the tumor burden from the radiance of the luminescent image. This method ensures that any background signal (e.g., from phosphor in mouse urine) would be excluded in the radiance quantification and not bias the results.

Additionally, as described in the Methods, the exposure time was held constant at 30 seconds for each IVIS measurement across all 37 experiments.

The data using more than 2 million cells comes from only 10 mice, and maybe the biological relevance of this group is limited since it will not be achievable and translatable in humans (PMID: 33653113).

We appreciate Reviewer #2’s attention to this issue. The effect observed in our study is large enough to reach statistical significance despite the small number of mice. Note that the dosing regimen used was optimized for the murine NSG model and would require appropriate scaling before clinical application. Nonetheless, NSG mice remain the gold standard for pre‑clinical in vivo evaluation and their use is generally required by regulatory agencies, such as the FDA, for assessing novel CAR‑T cell therapies; thus these findings are relevant for advancing such treatments.

Mary Smith Cranch’s letters show that women were deeply engaged in political debates even though they could not vote or hold office. Her discussions of currency policy, legal reforms, and Shays’s Rebellion reveal that she closely followed national issues and believed women had a responsibility to support the country through informed opinions and economic sacrifice.

Author response:

eLife Assessment

This useful study examines whether the sugar trehalose, coordinates energy supply with the gene programs that build muscle in the cotton bollworm (Helicoverpa armigera). The evidence for this currently is incomplete. The central claim - that trehalose specifically regulates an E2F/Dp-driven myogenic program - is not supported by the specificity of the data: perturbations and sequencing are systemic, alternative explanations such as general energy or amino-acid scarcity remain plausible, and mechanistic anchors are also limited. The work will interest researchers in insect metabolism and development; focused, tissue-resolved measurements together with stronger mechanistic controls would substantially strengthen the conclusions.

We thank the reviewer for the thoughtful and constructive evaluation of our work and for recognizing its potential relevance to researchers working on insect metabolism and development. We fully agree that our current evidence is preliminary and that the mechanistic link between trehalose and the E2F/Dp‑driven myogenic program needs to be strengthened.

Our intention was to present trehalose-E2F/Dp coupling as a working model emerging from our data, rather than as a fully established pathway. We agree that systemic manipulations of trehalose and whole‑larval RNA‑seq cannot fully differentiate global metabolic stress from specific effects on myogenic programs. In the revision, we plan to include additional metabolic readouts (e.g., ATP/AMP ratio, key amino acids where available) to better discuss the overall energetic and nutritional state. We will reanalyze our RNA‑seq data to more clearly distinguish broad stress/metabolic signatures from cell‑cycle/myogenic signatures. Furthermore, we will reframe our discussion to explicitly state that we cannot completely rule out a contribution of general energy or amino‑acid scarcity at this stage.

We acknowledge that, with our current experiments, the specificity for an E2F/Dp‑driven program is inferred mainly from enrichment of E2F targets among differentially expressed genes, and expression changes in canonical E2F partners and downstream cell‑cycle/myogenic regulators. To address this more rigorously, we are performing targeted qRT-PCR for a panel of well‑characterized E2F/Dp target genes and myogenic markers in larval muscle versus non‑muscle tissues, following trehalose perturbation. Where technically feasible, testing whether partial knockdown of HaE2F or HaDp modifies the effect of trehalose manipulation on selected myogenic markers. These data, even if limited, will help to provide a more direct functional link, and we will include them in the manuscript if completed in time. In parallel, we will soften statements that imply a fully established, trehalose‑specific regulation of E2F/Dp and instead present this as a strong candidate pathway suggested by the current data.

We fully agree that tissue‑resolved analyses are essential to move from systemic correlations to causality in muscle. We are in the process of standardizing larval muscle dissections and isolating thoracic/abdominal body wall muscle for trehalose, glycogen, and expression assays. Comparing expression of key metabolic and myogenic genes in muscle versus fat body and midgut, under trehalose manipulation. These tissue‑resolved data will directly address whether the transcriptional changes we report are preferentially localized to muscle.

We are grateful for the reviewer’s critical but encouraging comments. We will moderate our central claims, also explicitly consider and discuss alternative explanations. Further, we will add tissue‑resolved and more focused mechanistic data as far as possible within the current revision. We believe these changes will substantially strengthen the manuscript and better align our conclusions with the evidence we presently have.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work by Mohite et al., they have used transcriptomic and metabolic profiling of H. armigera, muscle development, and S. frugiperda to link energy trehalose metabolism and muscle development. They further used several different bioinformatics tools for network analysis to converge upon transcriptional control as a potential mechanism of metabolite-regulated transcriptional programming for muscle development. The authors have also done rescue experiments where trehalose was provided externally by feeding, which rescues the phenotype. Though the study is exciting, there are several concerns and gaps that lead to the current results as purely speculative. It is difficult to perform any genetic experiments in non-model insects; the authors seem to suggest a similar mechanism could also be applicable in systems like Drosophila; it might be possible to perform experiments to fill some missing mechanistic details.

A few specific comments below:

The authors used N-(phenylthio) phthalimide (NPP), a trehalose-6-phosphate phosphatase (TPP) inhibitor. They also find several genes, including enzymes of trehalose metabolism, that change. Further, several myogenic genes are downregulated in bulk RNA sequencing. The major caveat of this experiment is that the NPP treatment leads to reduced muscle development, and so the proportion of the samples from the muscles in bulk RNA sequencing will be relatively lower, which might have led to the results. So, a confirmatory experiment has to be performed where the muscle tissues are dissected and sequenced, or some of the interesting targets could be validated by qRT-PCR. Further to overcome the off-target effects of NPP, trehalose rescue experiments could be useful.

Thank you for this valuable comment. We will validate the gene expression data using qRT-PCR on muscle tissue samples from both treated and control groups. This will help determine whether the gene expression patterns observed in the RNA-seq data are muscle-specific or systemic.

Even the reduction in the levels of ADP, NAD, NADH, and NMN, all of which are essential for efficient energy production and utilization, could be due to the loss of muscles, which perform predominantly metabolic functions due to their mitochondria-rich environment. So it becomes difficult to judge if the levels of these energy molecules' reduction are due to a cause or effect.

We thank the reviewer for this thoughtful comment and agree that reduced levels of ADP, NAD, NADH, and NMN could arise either from a disturbance of energy metabolism or from loss of mitochondria‑rich muscles. Our current data cannot fully separate these two possibilities. Still, several studies support the interpretation that perturbing trehalose metabolism causes a primary systemic energy deficit that is coupled to mitochondrial function, not merely a passive consequence of tissue loss.

For example:

(1) Our previous study in H. armigera showed that chemical inhibition of trehalose synthesis results in depletion of trehalose, glucose, glucose‑6‑phosphate, and suppression of the TCA cycle, indicating reduced energy levels and dysregulated fatty‑acid oxidation (Tellis et al., 2023).

(2) Chang et al. (2022) showed that trehalose catabolism and mitochondrial ATP production are mechanistically linked. HaTreh1 localizes to mitochondria and physically interacts with ATP synthase subunit α. 20‑hydroxyecdysone increases HaTreh1 expression, enhances its binding to ATP synthase, and elevates ATP content, while knockdown of HaTreh1 or HaATPs‑α reduces ATP levels.

(3) Similarly, our previous study inhibition of Treh activity in H. armigera generates an “energy‑deficient condition” characterized by deregulation of carbohydrate, protein, fatty‑acid, and mitochondria‑related pathways, and a concomitant reduction in key energy metabolites (Tellis et al., 2024).

(4) The starvation study in H. armigera has shown that reduced hemolymph trehalose is associated with respiratory depression and large‑scale reprogramming of glycolysis and fatty‑acid metabolism (Jiang et al., 2019).

These findings support a direct coupling between trehalose availability and systemic energy/redox state. Therefore, the coordinated decrease in ADP, NAD, NADH, and NMN following TPS/TPP silencing is consistent with a primary disturbance of systemic energy and mitochondrial metabolism rather than exclusively a secondary consequence of muscle loss. We agree, however, that the present whole‑larva metabolite measurements do not allow a quantitative partitioning between changes due to altered muscle mass and those due to intrinsic metabolic impairment at the cellular level. Thus, tissue-specific quantification of these metabolites would allow us to directly test whether altered energy metabolites are a cause or consequence of muscle loss.

References:

(1) Tellis, M. B., Mohite, S. D., Nair, V. S., Chaudhari, B. Y., Ahmed, S., Kotkar, H. M., & Joshi, R. S. (2024). Inhibition of Trehalose Synthesis in Lepidoptera Reduces Larval Fitness. Advanced Biology, 8(2), 2300404.

(2) Chang, Y., Zhang, B., Du, M., Geng, Z., Wei, J., Guan, R., An, S. and Zhao, W., 2022. The vital hormone 20-hydroxyecdysone controls ATP production by upregulating the binding of trehalase 1 with ATP synthase subunit α in Helicoverpa armigera. Journal of Biological Chemistry, 298(2).

(3) Tellis, M., Mohite, S. and Joshi, R., 2024. Trehalase inhibition in Helicoverpa armigera activates machinery for alternate energy acquisition. Journal of Biosciences, 49(3), p.74.

(4) Jiang, T., Ma, L., Liu, X.Y., Xiao, H.J. and Zhang, W.N., 2019. Effects of starvation on respiratory metabolism and energy metabolism in the cotton bollworm Helicoverpa armigera (Hübner)(Lepidoptera: Noctuidae). Journal of Insect Physiology, 119, p.103951.

The authors have used this transcriptomic data for pathway enrichment analysis, which led to the E2F family of transcription factors and a reduction in the level of when trehalose metabolism is perturbed. EMSA experiments, though, confirm a possibility of the E2F interaction with the HaTPS/TPP promoter, but it lacks proper controls and competition to test the actual specificity of this interaction. Several transcription factors have DNA-binding domains and could bind any given DNA weakly, and the specificity is ideally known only from competitive and non-competitive inhibition studies.

We thank the reviewer for this important comment and fully agree that EMSA alone, without appropriate competition and control reactions, cannot establish the specificity or functional relevance of a transcription factor-DNA interaction. In our study, we found the E2F family from GRN analysis of the RNA seq data obtained upon HaTPS/TPP silencing, suggesting a potential regulatory connection. After that, we predicted E2F binding sites on the promoter of HaTPS/TPP. The EMSA experiments were intended as preliminary evidence that E2F can associate with the HaTPS/TPP promoter in vitro. We will clarify this in the manuscript by softening our conclusion to indicate that our data support a “possible E2F-HaTPS/TPP interaction”. We also perform EMSA with specific and non‑specific competitors to confirm the E2F binding to the HaTPS/TPP promoter.

The work seems to have connected the trehalose metabolism with gene expression changes, though this is an interesting idea, there are no experiments that are conclusive in the current version of the manuscript. If the authors can search for domains in the E2F family of transcription factors that can bind to the metabolite, then, if not, a chip-seq is essential to conclusively suggest the role of E2F in regulating gene expression tuned by the metabolites.

A previous study in D. melanogaster, Zappia et al., (2016) showed vital role of E2F in skeletal muscle required for animal viability. They have shown that Dp knockdown resulted in reduced expression of genes encoding structural and contractile proteins, such as Myosin heavy chain (Mhc), fln, Tropomyosin 1 (Tm1), Tropomyosin 2 (Tm2), Myosin light chain 2 (Mlc2), sarcomere length short (sals) and Act88F, and myogenic regulators, such as held out wings (how), Limpet (Lmpt), Myocyte enhancer factor 2 (Mef2) and spalt major (salm). Also, ChiP-qRT-PCR showed upstream regions of myogenic genes, such as how, fln, Lmpt, sals, Tm1 and Mef2, were specifically enriched with E2f1, E2f2, and Dp antibodies in comparison with a nonspecific antibody. Further, Zappia et al. (2019) reported a chip-seq dataset that suggests that E2F/Dp directly activates the expression of glycolytic and mitochondrial genes during muscle development. Zappia et al., (2023) showed the regulation of one of the glycolytic genes, Phosphoglycerate kinase (Pgk) by E2F during Drosophila development.

However, the regulation of trehalose metabolic genes by E2F/Dp and vice versa was not studied previously. So here in our study, we tried to understand the correlation of trehalose metabolism and E2F/Dp in the muscle development of H. armigera.

References:

(1) Zappia, M.P. and Frolov, M.V., 2016. E2F function in muscle growth is necessary and sufficient for viability in Drosophila. Nature Communications, 7(1), p.10509.

(2) Zappia, M.P., Rogers, A., Islam, A.B. and Frolov, M.V., 2019. Rbf activates the myogenic transcriptional program to promote skeletal muscle differentiation. Cell reports, 26(3), pp.702-719.

(3) Zappia, M. P., Kwon, Y.-J., Westacott, A., Liseth, I., Lee, H. M., Islam, A. B., Kim, J., & Frolov, M. V. (2023a). E2F regulation of the Phosphoglycerate kinase gene is functionally important in Drosophila development. Proceedings of the National Academy of Sciences, 120(15), e2220770120.

Some of the above concerns are partially addressed in experiments where silencing of E2F/Dp shows similar phenotypes as with NPP and dsRNA. It is also notable that silencing any key transcription factor can have several indirect effects, and delayed pupation and lethality could not be definitely linked to trehalose-dependent regulation.

Yes. It’s true that silencing of any key transcription factor can have several indirect effects. Our intention was not to argue that delayed pupation and lethality are exclusively due to trehalose-dependent regulation, but that E2F/Dp and HaTPS/TPP silencing showed a consistent set of phenotypes and molecular changes, such as (i) transcriptomic enrichment of E2F targets upon trehalose perturbation, (ii) reduced HaTPS/TPP expression following E2F/Dp silencing, (iii) reduced myogenic gene expression that parallels the phenotypes observed with HaTPS/TPP silencing and (iv) restoration of E2F and Dp expression in E2F/Dp‑silenced insects upon trehalose feeding in the rescue assay. Together, these findings support a functional association between E2F/Dp and trehalose homeostasis. At the same time, we fully acknowledge that these results do not exclude additional, trehalose‑independent roles of E2F/Dp in development.

Trehalose rescue experiments that rescue phenotype and gene expression are interesting. But is it possible that the fed trehalose is metabolized in the gut and might not reach the target tissue? In which case, the role of trehalose in directly regulating transcription factors becomes questionable. So, a confirmatory experiment is needed to demonstrate that the fed trehalose reaches the target tissues. This could possibly be done by measuring the trehalose levels in muscles post-rescue feeding. Also, rescue experiments need to be done with appropriate control sugars.

Yes, it’s possible that, to some extent, trehalose is metabolized in the gut. Even though trehalase is present in the insect gut, some of the trehalose will be absorbed via trehalose transporters on the gut lining. Trehalose feeding was not rescued in insects fed with the control diet (empty vector and dsHaTPP), which contains chickpea powder, which is composed of an ample amount of amino acids and carbohydrates. Insects fed exclusively on a trehalose-containing diet are rescued, but not on a control diet that contains other carbohydrates. We agree that direct measurement of trehalose in target tissues will provide important confirmation. In the manuscript, we will measure trehalose levels in muscle, gut, and haemolymph after trehalose feeding.

No experiments are performed with non-target control dsRNA. All the experiments are done with an empty vector. But an appropriate control should be a non-target control.

Yes, there was no experiment with non-target dsRNA. Earlier, we have optimized a protocol for dsRNA delivery and its effectiveness in target knockdown (concentration, time) experiment, and published several research articles using a similar protocol:

(1) Chaudhari, B.Y., Nichit, V.J., Barvkar, V.T. and Joshi, R.S., 2025. Mechanistic insights in the role of trehalose transporter in metabolic homeostasis in response to dietary trehalose. G3: Genes, Genomes, Genetics, p. jkaf303.

(2) Barbole, R.S., Sharma, S., Patil, Y., Giri, A.P. and Joshi, R.S., 2024. Chitinase inhibition induces transcriptional dysregulation altering ecdysteroid-mediated control of Spodoptera frugiperda development. Iscience, 27(3).

(3) Patil, Y.P., Wagh, D.S., Barvkar, V.T., Gawari, S.K., Pisalwar, P.D., Ahmed, S. and Joshi, R.S., 2025. Altered Octopamine synthesis impairs tyrosine metabolism affecting Helicoverpa armigera vitality. Pesticide Biochemistry and Physiology, 208, p.106323.

(4) Tellis, M.B., Chaudhari, B.Y., Deshpande, S.V., Nikam, S.V., Barvkar, V.T., Kotkar, H.M. and Joshi, R.S., 2023. Trehalose transporter-like gene diversity and dynamics enhances stress response and recovery in Helicoverpa armigera. Gene, 862, p.147259.

(5) Joshi, K.S., Barvkar, V.T., Hadapad, A.B., Hire, R.S. and Joshi, R.S., 2025. LDH-dsRNA nanocarrier-mediated spray-induced silencing of juvenile hormone degradation pathway genes for targeted control of Helicoverpa armigera. International Journal of Biological Macromolecules, p.148673.

The same vector backbone and preparation procedures were used for both control and experimental constructs, allowing us to specifically compare the effects of the target dsRNA. The phenotypes and gene expression changes we observed were specific to the target genes and were not seen in the empty vector controls, suggesting that the effects are not due to nonspecific responses of dsRNA delivery or vector components.<br /> We acknowledge your suggestions, and in future studies, we will keep non-target dsRNA as a control in silencing assays.

Reviewer #2 (Public review):

Summary:

This study shows that the knockdown of the effects of TPS/TPP in Helicoverpa armigera and Spodoptera frugiperda can be rescued by trehalose treatment. This suggests that trehalose metabolism is necessary for development in the tissues that NPP and dsRNA can reach.

Strengths:

This study examines an important metabolic process beyond model organisms, providing a new perspective on our understanding of species-specific metabolism equilibria, whether conserved or divergent.

Weaknesses:

While the effects observed may be truly conserved across Lepidopterans and may be muscle-specific, the study largely relies on one species and perturbation methods that are not muscle-specific. The technical limitations arising from investigations outside model systems, where solid methods are available, limit the specificity of inferences that may be drawn from the data.

Thank you for this potting out this experimental weakness. We will validate the gene expression data using qRT-PCR on muscle tissue samples from both treated and control groups. We will also perform metabolite analysis with muscle samples. This will help to determine whether the observed gene expression patterns and metabolite changes are muscle-specific or systemic.

Reviewer #3 (Public review):

The hypothesis is that Trehalose metabolism regulates transcriptional control of muscle development in lepidopteran insects.

The manuscript investigates the role of Trehalose metabolism in muscle development. Through sequencing and subsequent bioinformatics analysis of insects with perturbed trehalose metabolism (knockdown of TPS/TPP), the authors have identified transcription factor E2F, which was validated through RT-PCR. Their hypothesis is that trehalose metabolism regulates E2F, which then controls the myogenic genes. Counterintuitive to this hypothesis, the investigators perform EMSAs with the E2F protein and promoter of the TPP gene and show binding. Their knockdown experiments with Dp, the binding partner of E2F, show direct effect on several trehalose metabolism genes. Similar results are demonstrated in the trehalose feeding experiment, where feeding trehalose leads to partial rescue of the phenotype observed as a result of Dp knockdown. This seems contradictory to their hypothesis. Even more intriguing is a similar observation between paramyosin, a structural muscle protein, and E2F/Dp - they show that paramyosin regulates E2F/Dp and E2F/Dp regulated paramyosin. The only plausible way to explain the results is the existence of a feed-forward loop between TPP-E2F/Dp and paramyosin-E2F/Dp. But the authors have mentioned nothing in this line. Additionally, I think trehalose metabolism impacts amino acid content in insects, and that will have a direct bearing on muscle development. The sequencing analysis and follow-up GSEA studies have demonstrated enrichment of several amino acid biosynthetic genes. Yet authors make no efforts to measure amino acid levels or correlate them with muscle development. Any study aiming to link trehalose metabolism and muscle development and not considering the above points will be incomplete.

We appreciate the reviewer’s efforts in the careful evaluation of this manuscript and constructive comments. From our and earlier data we found it was difficult to consider linear pathway “trehalose → E2F → muscle,” but rather a regulatory module in which trehalose metabolism and E2F/Dp form an interdependent circuit controlling myogenic genes. E2F/Dp binds and activates trehalose metabolism genes (TPS/TPP, Treh1) and myogenic structural genes, consistent with EMSA (TPS/TPP-E2F) and predicted binding sites of E2F on metabolic genes, Treh1, Pgk, and myogenic genes such as Act88F, Prm, Tm1, Fln, etc. At the same time, perturbing trehalose synthesis reduces E2F/Dp expression and myogenic gene expression, and trehalose feeding partially restores all three. This bidirectional influence is similar to E2F‑dependent control of carbohydrate metabolism and systemic sugar homeostasis described in D. melanogaster, where E2F/Dp both regulates metabolic genes and is itself constrained by metabolic state (Zappia et al., 2023a; Zappia et al., 2021).

The reciprocal regulation between Prm and E2F/Dp is indeed intriguing. Rather than a paradox, we interpret this as evidence that E2F/Dp couples metabolic genes and structural muscle genes within a shared module, and that key sarcomeric components (such as paramyosin) feed back on this transcriptional program. Similar cross‑talk between E2F‑controlled metabolic programs and tissue function has been documented in D. melanogaster muscle and fat body, where E2F loss in one tissue elicits systemic changes in the other (Zappia et al., 2021). For further confirmation of E2F-regulated Prm, we will perform EMSA on the Prm promoter with appropriate controls.

We fully agree that amino‑acid metabolism is a critical missing piece. In the manuscript, we will quantify the amino acid levels and include the results: “Amino acids display differential levels showing cysteine, leucine, histidine, valine, and proline showed significant reductions, while isoleucine and lysine showed non-significant reductions upon trehalose metabolism perturbation. These results are consistent with previous reports published by Tellis et al. (2024) and Shi et al. (2016)”. We will reframe our conclusions more cautiously as establishing a trehalose-E2F/Dp-muscle development, while stating that “definitive causal links via amino‑acid metabolism remain to be demonstrated”.

Reference:

(1) Zappia, M. P., Kwon, Y.-J., Westacott, A., Liseth, I., Lee, H. M., Islam, A. B., Kim, J., & Frolov, M. V. (2023a). E2F regulation of the Phosphoglycerate kinase gene is functionally important in Drosophila development. Proceedings of the National Academy of Sciences, 120(15), e2220770120.

(2) Zappia, M.P., Guarner, A., Kellie-Smith, N., Rogers, A., Morris, R., Nicolay, B., Boukhali, M., Haas, W., Dyson, N.J. and Frolov, M.V., 2021. E2F/Dp inactivation in fat body cells triggers systemic metabolic changes. elife, 10, p.e67753.

(3)Tellis, M., Mohite, S. and Joshi, R., 2024. Trehalase inhibition in Helicoverpa armigera activates machinery for alternate energy acquisition. Journal of Biosciences, 49(3), p.74.

(4) Shi, J.F., Xu, Q.Y., Sun, Q.K., Meng, Q.W., Mu, L.L., Guo, W.C. and Li, G.Q., 2016. Physiological roles of trehalose in Leptinotarsa larvae revealed by RNA interference of trehalose-6-phosphate synthase and trehalase genes. Insect Biochemistry and Molecular Biology, 77, pp.52-68.

Author response image 1.

The result section of the manuscript is quite concise, to my understanding (especially the initial few sections), which misses out on mentioning details that would help readers understand the paper better. While technical details of the methods should be in the Materials and Methods section, the overall experimental strategy for the experiments performed should be explained in adequate detail in the results section itself or in figure legends. I would request authors to include more details in the results section. As an extension of the comment above, many times, abbreviations have been used without introducing them. A thorough check of the manuscript is required regarding this.

Thank you very much for pointing out this issue. We will revise the manuscript content according to these suggestions.

The Spodoptera experiments appear ad hoc and are insufficient to support conservation beyond Helicoverpa. To substantiate this claim, please add a coherent, minimal set of Spodoptera experiments and present them in a dedicated subsection. Alternatively, consider removing these data and limiting the conclusions (and title) to H. armigera.

We thank the reviewer for this helpful comment. We agree that, in this current version of the manuscript, the S. frugiperda experiments are not sufficiently systematic to support strong claims about conservation beyond H. armigera. Our primary focus in this study is indeed on H. armigera, and the addition of the S. frugiperda data was intended only as preliminary, supportive evidence rather than a central component of our conclusions. To avoid over‑interpretation and to keep the manuscript focused and coherent, we will remove all S. frugiperda data from the revised version, including the corresponding text and figures. We will also adjust the title, abstract, and conclusion to clearly state that our findings are limited to H. armigera.

In order to check the effects of E2F/Dp, a dsRNA-mediated knockdown of Dp was performed. Why was the E2F protein, a primary target of the study, not chosen as a candidate? The authors should either provide justification for this or perform the suggested experiments to come to a conclusion. I would like to point out that such experiments were performed in Drosophila.

Thank you for this thoughtful comment and the specific suggestion. We agree that directly targeting E2F would, in principle, be an informative complementary approach. In our study, however, we prioritized Dp knockdown for two main reasons. First, E2F is a large family, and E2F-Dp functions as an obligate heterodimer. Previous work in D. melanogaster has shown that depletion of Dp is sufficient to disrupt E2F-dependent transcription broadly, often with more efficient loss of complex activity than targeting individual E2F isoforms (Zappia et al., 2021; Zappia et al., 2016). Second, in our preliminary trials, we performed a dsRNA feeding assay with dsHaE2F, dsHaDp, and combined dsHaE2F plus dsHaDp. In that assay, we did not achieve silencing of E2F in dsRNA targeting HaE2F (dsHaE2F). So here, as E2F is a large family, other E2F isoforms may be compensating for the silencing effect of targeted HaE2F. However, HaE2F showed significantly reduced expression upon dsHaDp and combined dsHaE2F plus dsHaDp feeding (Figure A), whereas HaDp showed a significant reduction in its expression in all three conditions (Figure B).  As we observed reduced expression of both HaE2F and HaDp upon combined feeding of dsHaE2F and dsHaDp, we further performed a rescue assay by exogenous feeding of trehalose. We observed the significant upregulation of HaE2F, HaDp, trehalose metabolic genes (HaTPS/TPP and HaTreh1), and myogenic genes (HaPrm and HaTm2) (Figure C). For these reasons, we focused on Dp silencing as a more reliable way to impair E2F/Dp complex function in H. armigera.

Author response image 2.

References:

(1) Zappia, M.P. and Frolov, M.V., 2016. E2F function in muscle growth is necessary and sufficient for viability in Drosophila. Nature Communications, 7(1), p.10509.

(2) Zappia, M.P., Guarner, A., Kellie-Smith, N., Rogers, A., Morris, R., Nicolay, B., Boukhali, M., Haas, W., Dyson, N.J. and Frolov, M.V., 2021. E2F/Dp inactivation in fat body cells triggers systemic metabolic changes. elife, 10, p.e67753.

Silencing of HaDp resulted in a significant decrease in HaE2F expression. I find this observation intriguing. DP is the cofactor of E2F, and they both heterodimerise and sit on the promoter of target genes to regulate them. I would request authors to revisit this result, as it contradicts the general understanding of how E2F/Dp functions in other organisms. If Dp indeed controls E2F expression, then further experiments should be conducted to come to a conclusion convincingly. Additionally, these results would need thorough discussion with citations of similar results observed for other transcription factor-cofactor complexes.

Thank you for highlighting this point and for prompting us to examine these data more carefully. Silencing HaDp leading to reduced HaE2F mRNA is indeed unexpected if one only considers the canonical view of E2F/Dp as a heterodimer that co-occupies target promoters without strongly regulating each other’s expression. However, several lines of work suggest that transcription factor-cofactor networks frequently include feedback loops in which cofactors influence the expression of their partner TFs. First, in multiple systems, transcription factors and their cofactors are known to regulate each other’s transcription, forming positive or negative feedback loops. For example, in hematopoietic cells, the transcription factor Foxp3 controls the expression of many of its own cofactors, and some of these cofactors in turn facilitate or stabilize Foxp3 expression, forming an interconnected regulatory network rather than a simple one‑way interaction (Rudra et al., 2012). Second, E2F/Dp complexes exhibit non‑canonical regulatory mechanisms and can regulate broad sets of targets, including other transcriptional regulators. Several studies show that E2F/Dp proteins not only control classical cell‑cycle genes but also participate in diverse processes such as DNA damage signaling, mitochondrial function, and differentiation (Guarner et al., 2017; Ambrus et al., 2013; Sánchez-Camargo et al., 2021). In D. melanogaster, complete loss of dDP alters the expression of direct targets E2F/DP, including dATM (Guarner et al., 2017).

All these reports indicate that the E2F-Dp complex sits at the top of multi‑layer regulatory hierarchies. Such architectures make it plausible that Dp silencing in H. armigera could modulate HaE2F expression in a non-canonical way.

References:

(1) Rudra, D., DeRoos, P., Chaudhry, A., Niec, R.E., Arvey, A., Samstein, R.M., Leslie, C., Shaffer, S.A., Goodlett, D.R. and Rudensky, A.Y., 2012. Transcription factor Foxp3 and its protein partners form a complex regulatory network. Nature immunology, 13(10), pp.1010-1019.

(2) Guarner, A., Morris, R., Korenjak, M., Boukhali, M., Zappia, M.P., Van Rechem, C., Whetstine, J.R., Ramaswamy, S., Zou, L., Frolov, M.V. and Haas, W., 2017. E2F/DP prevents cell-cycle progression in endocycling fat body cells by suppressing dATM expression. Developmental cell, 43(6), pp.689-703.

(3) Ambrus, A.M., Islam, A.B., Holmes, K.B., Moon, N.S., Lopez-Bigas, N., Benevolenskaya, E.V. and Frolov, M.V., 2013. Loss of dE2F compromises mitochondrial function. Developmental cell, 27(4), pp.438-451.

(4) Sánchez-Camargo, V.A., Romero-Rodríguez, S. and Vázquez-Ramos, J.M., 2021. Non-canonical functions of the E2F/DP pathway with emphasis in plants. Phyton, 90(2), p.307.

I consider the overall bioinformatics analysis to remain very poorly described. What is specifically lacking is clear statements about why a particular dry lab experiments were conducted.

We again thank the reviewer for advising us to give a biological context/motivation for every bioinformatics analysis performed. The bioinformatics analyses devised here, try to explain the systems-level perturbations of HaTPS/TPP silencing to explain the observed phenotype and to discover transcription factors potentially modulating the HaTPS/TPP induced gene regulatory changes.

(1) Gene set enrichment analyses:

Differential gene expression analyses of the bulk RNA sequencing data followed by qRT-PCR confirmed the transcriptional changes in myogenic genes and gene expression alterations in metabolic and cell cycle-related genes. These perturbations merely confirmed the effect induced by HaTPS/TPP silencing in obviously expected genes. We wanted to see whether using an “unbiased” system-level statistical analyses like gene set enrichment analyses (GSEA), can reveal both expected and novel biological processes that underlie HaTPS/TPP silencing. GSEA results revealed large-scale transcriptional changes in 11 enriched processes, including amino acid metabolism, energy metabolism, developmental regulatory processes, and motor protein activity. GSEA not only divulged overall transcriptionally enriched pathways but also identified the genes undergoing synchronized pathway-level transcriptional change upon HaTPS/TPP silencing.

(2) Gene regulatory network analysis:

Although GSEA uncovered potential pathway-level changes, we were also interested in identifying the gene regulatory network associated with such large-scale process-level transcriptional perturbations. Interestingly, the biological processes undergoing perturbations were also heterogeneous (e.g., motor protein activity, energy metabolism, amino acid metabolism, etc.). We hypothesized that the inference of a causal gene regulatory network associated with the genes associated with GSEA-enriched biological processes should predict core/master transcription factors that might synchronously regulate metabolic and non-metabolic processes related to HaTPS/TPP silencing, thereby providing a broad understanding of the perturbed phenotype. The gene regulatory network analysis statistically inferred an “active” gene regulatory network corresponding to the GSEA-enriched KEGG gene sets. Ranking the transcription factors (TFs) based on the number of outgoing connections (outdegree centrality) within the active gene regulatory network, E2F family TFs were identified to be top-ranking, highly connected transcription factors associated with the transcriptionally enriched processes. This suggests that E2F family TFs are central to controlling the flow of regulatory information within this network. Intriguingly, E2F has been previously implicated in muscle development in insects (Zappia et al., 2016). Further extracting the regulated targets of E2F family TFs within this network revealed the mechanistic connection with the 11 enriched processes. This GRN analysis was crucial in discovering and prioritizing E2F TFs as central transcription factors mediating HaTPS/TPP silencing effects, which was not apparent using trivial analyses like differential gene expression analysis.

As per the reviewer’s suggestions, we will add these outlined points in the text of the manuscript (Results section) to further give context and clarity to the bioinformatics analyses conducted in this study.

In my judgement, the EMSA analysis presented is technically poor in quality. It lacks positive and negative controls, does not show mutation analysis or super shifts. Also, it lacks any competition assays that are important to prove the binding beyond doubt. I am not sure why protein is not detected at all in lower concentrations. Overall, the EMSA assays need to be redone; I find the current results to be unacceptable.

Thank you for pointing out this issue. We will reperform the EMSA analysis with appropriate controls.  Although the gel image was not clear, there was a light band of protein (indicated by the white square) observed in well No. 8, where we used 8 μg of E2F protein and 75 ng of HaTPS/TPP promoter, upon gel stained with SYPRO Ruby protein stain, suggesting weak HaTPS/TPP-E2F complex formation.

GSEA studies clearly indicate enrichment of the amino acid synthesis gene in TPP knockdown samples. This supports the plausible theory that a lack of Trehalose means a lack of enough nutrients, therefore less of that is converted to amino acids, and therefore muscle development is compromised. Yet the authors make no effort to measure amino acid levels. While nutrients can be sensed through signalling pathways leading to shut shutdown of myogenic genes, a simple and direct correlation between less raw material and deformed muscle might also be possible.

We quantified amino acid levels as per the suggestion, and we observed differential levels of amino acids upon trehalose metabolism perturbation.

However, we observed that insect were failed to rescue when fed a control chickpea-based artificial diet that contained nutrients required for normal growth and development. Based on this observation, we conclude that trehalose deficiency is the only possible cause for the defect in muscle development.

The authors are encouraged to stick to one color palette while demonstrating sequencing results. Choosing a different color palette for representing results from the same sequencing analysis confuses readers.

Thank you for the comment. We will revise the color palette as per the suggestion.

Expression of genes, as understood from sequencing analysis in Figure 1D, Figure 2F, and Figure 3D, appears to be binary in nature. This result is extremely surprising given that the qRT-PCR of these genes have revealed a checker and graded expression.

Thank you for pointing out this issue. We will revise the scale range for these figures to get more insights about gene expression levels and include figures as per the suggestion.

In several graphs, non-significant results have been interpreted as significant in the results section. In a few other cases, the reported changes are minimal, and the statistical support is unclear; please recheck the analyses and include exact statistics. In the results section, fold changes observed should be discussed, as well as the statistical significance of the observed change.

We will revise the analyses and include exact statistics as per the suggestion.

Finally, I would add that trehalose metabolism regulates cell cycle genes, and muscle development genes establish correlation and causation. The authors should ensure that any comments they make are backed by evidence.

We thank the reviewer for this insightful comment.  Although direct evidence in insects is currently lacking, multiple independent studies in yeast, plants and mammalian systems support a regulatory link between trehalose metabolism and the cell cycle. In budding yeast Saccharomyces cerevisiae, neutral Treh (Nth1) is directly phosphorylated and activated by the major cyclin‑dependent kinase Cdk1 at G1/S, routing stored trehalose into glycolysis to fuel DNA replication and mitosis (Ewald et al., 2016). CDK‑dependent regulation of trehalase activity has also been reported in plants, where CDC28‑mediated phosphorylation channels glucose into biosynthetic pathways necessary for cell proliferation (Lara-núñez et al., 2025). Furthermore, budding yeast cells accumulate trehalose and glycogen upon entry into quiescence and subsequently mobilize these stores to generate a metabolic “finishing kick” that supports re‑entry into the cell cycle (Silljé et al., 1999; Shi et al., 2010). Exogenous trehalose that perturbs the trehalose cycle impairs glycolysis, reduces ATP, and delays cell cycle progression in S. cerevisiae, highlighting a dose‑ and context‑dependent control of growth versus arrest (Zhang, Zhang and Li, 2020). In mammalian systems, trehalose similarly modulates proliferation-differentiation decisions. In rat airway smooth muscle cells, low trehalose concentrations promote autophagy, whereas higher doses induce S/G2–M arrest, downregulate Cyclin A1/B1, and trigger apoptosis, indicating a shift from controlled growth to cell elimination at higher exposure (Xiao et al., 2021). In human iPSC‑derived neural stem/progenitor cells, low‑dose trehalose enhances neuronal differentiation and VEGF secretion, while higher doses are cytotoxic, again highlighting a tunable impact on cell‑fate outcomes (Roose et al., 2025). In wheat, exogenous trehalose under heat stress reduces growth, lowers auxin, gibberellin, abscisic acid and cytokinin levels, and represses CycD2 and CDC2 expression, suggesting that trehalose signalling integrates with hormone pathways and core cell‑cycle regulators to restrain proliferation during stress (Luo, Liu, and Li, 2021). Together, these studies showed the importance of trehalose metabolism in cell‑cycle regulation to decide whether cells and tissues proliferate, differentiate, or remain quiescent.

With respect to muscle development, previous work has implicated glycolytic metabolism in myogenesis and muscle growth. Tixier et al. (2013) showed that loss of key glycolytic genes results in abnormally thin muscles, while Bawa et al. (2020) demonstrated that loss of TRIM32 decreases glycolytic flux and reduces muscle tissue size. These findings indicate that carbohydrate and energy metabolism pathways are important determinants of muscle structure and growth. However, there are no previous studies about the role of trehalose metabolism in muscle development, other than as an energy source, so here we specifically set out to establish the involvement of trehalose metabolism in muscle development.

References:

(1) Ewald, J.C. et al. (2016) “The yeast cyclin-dependent kinase routes carbon fluxes to fuel cell cycle progression,” Molecular cell, 62(4), pp. 532–545.

(2) Lara-núñez, A. et al. (2025) “The Cyclin-Dependent Kinase activity modulates the central carbon metabolism in maize during germination,” (January), pp. 1–16.

(3) Silljé, H.H.W. et al. (1999) “Function of trehalose and glycogen in cell cycle progression and cell viability in Saccharomyces cerevisiae,” Journal of bacteriology, 181(2), pp. 396–400.

(4) Shi, L. et al. (2010) “Trehalose Is a Key Determinant of the Quiescent Metabolic State That Fuels Cell Cycle Progression upon Return to Growth,” 21, pp. 1982–1990.

(5) Zhang, X., Zhang, Y. and Li, H. (2020) “Regulation of trehalose, a typical stress protectant, on central metabolisms, cell growth and division of Saccharomyces cerevisiae CEN. PK113-7D,” Food Microbiology, 89, p. 103459.

(6) Xiao, B. et al. (2021) “Trehalose inhibits proliferation while activates apoptosis and autophagy in rat airway smooth muscle cells,” Acta Histochemica, 123(8), p. 151810.

(7) Roose, S.K. et al. (2025) “Trehalose enhances neuronal differentiation with VEGF secretion in human iPSC-derived neural stem / progenitor cells,” Regenerative Therapy, 30, pp. 268–277.

(8) Luo, Y., Liu, X. and Li, W. (2021) “Exogenously-supplied trehalose inhibits the growth of wheat seedlings under high temperature by affecting plant hormone levels and cell cycle processes,” Plant Signaling & Behavior, 16(6).

(9) Tixier, V., Bataillé, L., Etard, C., Jagla, T., Weger, M., DaPonte, J.P., Strähle, U., Dickmeis, T. and Jagla, K., 2013. Glycolysis supports embryonic muscle growth by promoting myoblast fusion. Proceedings of the National Academy of Sciences, 110(47), pp.18982-18987.

(10) Bawa, S., Brooks, D.S., Neville, K.E., Tipping, M., Sagar, M.A., Kollhoff, J.A., Chawla, G., Geisbrecht, B.V., Tennessen, J.M., Eliceiri, K.W. and Geisbrecht, E.R., 2020. Drosophila TRIM32 cooperates with glycolytic enzymes to promote cell growth. elife, 9, p.e52358.

Finally, we appreciate the meticulous review of this manuscript and constructive comments. We will perform the recommended experiments, data analysis, and revise the manuscript accordingly.

Author response:

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

Public Reviews:

Reviewer #1 (Public reviews):

(1) The absence of replicate paired-end datasets limits confidence in peak localization.

The reviewer was under the impression that that we did not perform biological replicates of our ChIP-seq experiments. All ChIP-seq (and ATAC-seq) experiments were performed with biological replicates and the Pearson’s correlations (all >0.9) between replicates were provided in Supplementary Table 1. We had indicated this in the text and methods but will try to make this even clearer.

(2) The analyses are primarily correlative, making it difficult to fully assess robustness or to support strong mechanistic conclusions.

Histone modifications are difficult to alter genetically because of the high copy number of histone genes and inhibition of HATs/HDACs in general leads to alterations in other histone modifications. It is an inherent challenge in establishing causality of histone modifications, especially histone acetylation marks.

(3) Some claims (e.g., specificity for CpG islands, "dynamic" regulation during differentiation) are not fully supported by the analyses as presented.

We have modified the text in response to this point. The new text reads: “Non-CGI promoters have lower overall levels of transcription compared to CGI promoters, and for this promoter class H3K115ac enrichment detected by ChIP is only really seen for the highest quartile of transcription (4SU) quartile of expression (Figure 1G). CGI promoters on the other hand, exhibit significant levels of detected H3K115ac even for the lowest quartile of expression. These results suggest a special link between CGI promoters and H3K115ac”.

(4) Overall, the study introduces an intriguing new angle on globular PTMs, but additional rigor and mechanistic evidence are needed to substantiate the conclusions.

We agree that the paper does not provide mechanistic details or solid causality of H3K115ac. We have only emphasized the potential role of H3K115ac in nucleosome fragility based on our in vivo data and previously published in-vitro experiments (Manohar et.al., 2009, Chatterjee et. al., 2015). We do provide the evidence that H3K115ac is enriched on subnucleosomal particles via sucrose gradient sedimentation of MNase-digested chromatin (Figure 3C-D).

Reviewer #2 (Public review):

(1) I am not fully convinced about the specificity of the antibody. Although the experiment in Figure S1A shows a specific binding to H3K115ac-modified peptides compared to unmodified peptides, the authors do not show any experiment that shows that the antibody does not bind to unrelated proteins. Thus, a Western of a nuclear extract or the chromatin fraction would be critical to show. Also, peptide competition using the H3K115ac peptide to block the antibody may be good to further support the specificity of the antibody. Also, I don't understand the experiment in Figure S1B. What does it tell us when the H3K115ac histone mark itself is missing? The KLF4 promoter does not appear to be a suitable positive control, given that hundreds of proteins/histone modifications are likely present at this region. It is important to clearly demonstrate that the antibody exclusively recognizes H3K115ac, given that the conclusion of the manuscript strongly depends on the reliability of the obtained ChIP-Seq data.

ChIP-qPCR in S1B includes competition from native chromatin and shows high specificity to its target. We have provided antibody validation in three ways:

- Western blot with dot-blot of synthetic peptides (Figure S1A).

- Western blots with Whole cell extracts (Figure 4D).

- ChIP-qPCR on native chromatin spiked with a cocktail of synthetic mono-nucleosomes, each carrying a single acetylation and a specific barcode (SNAP-ChIP K-AcylStat Panel).

We could not include H3K115ac marked nucleosomes as they are not available in the panel. Figure S1B shows that the H3K115ac antibody exhibits negligible binding to known K-acyl marks, comparable to an unmodified nucleosome. Because of the absence of a H3K115ac modified barcoded nucleosome, we used the KLF4 promoter from mESCs as a positive control, in agreement with ChIP-seq signal shown in the genome browser profile (Figure 1E), the KLF4 promoter shows a significantly higher signal than the gene body.

(2) The association of H3K115ac with fragile nucleosomes is based on MNase-sensitivity and fragment length, which are indirect methods and can have technical bias. Experiments that support that the H3K115ac modified nucleosomes are indeed more fragile are missing.

We have performed ChIP-seq on MNase digested mESC chromatin fractionated on sucrose gradients and this shows that H3K115ac is enriched in fractions containing sub-nucleosomal and fragile nucleosomes but depleted in fractions containing stable nucleosomes (Figure 3D).

(3) The comparison of H3K115ac with H3K122ac and H3K64ac relies on publicly available datasets. Since the authors argue that these marks are distinct, data generated under identical experimental conditions would be more convincing. At a minimum, the limitations of using external datasets should be discussed.

H3K64ac and H3K122ac datasets were generated by us in a previous publication (Pradeepa et. al., 2016) using same native MNase ChIP protocol as used here. The ChIP-seq datasets for H3K122ac and H3K27ac are processed in an identical manner, with the same computational pipelines, to the H3K115ac data sets generated in this paper.

(4) The enrichment of H3K115ac at enhancers and CTCF binding sites is notable but remains descriptive. It would be interesting to clarify whether H3K115ac actively influences transcription factor/CTCF binding or is a downstream correlate.

We agree with the reviewer’s comment, but we have not claimed causality.

(5) No information is provided about how H3K115ac may be deposited/removed. Without this information, it is difficult to place this modification into established chromatin regulatory pathways.

Due to broad target specificity, redundancies and crosstalk among different classes of HATs and HDACs, it is not tractable to answer this question in the current manuscript.

Reviewer #3 (Public reviews):

Reviewer 3 is mistaken in thinking our ChIP experiments are performed under cross-linked conditions. As clearly stated in the main text and methods, all our ChIP-seq for histone modifications is done on native MNase-digested chromatin – with no cross-linking. This includes the spike-in experiment shown in Fig S1B to test H3K115ac antibody specificity against the bar-coded SNAP-ChIP® K-AcylStat Panel from Epicypher. We could not include H3K115ac bar-coded nucleosomes in that experiment since they are not available in the panel.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I have two primary concerns that resound through the entire paper:

(a) Overall, the manuscript is making strong claims based on entirely correlative datasets. No quantitative analyses are performed to demonstrate co-occupancy/localization. Please see more detailed descriptions below.

Our responses to specific points are provided against each comment below.

(b) Lack of paired-end replicates for H3K115ac ChIP-seq. While the reviewer token for the deposited data was not made accessible to me, looking at Supplementary Table 1, it appears there are two H3K115ac ChIP-seq datasets. One is paired-end and is single-read. So are peaks called with only one replicate of PE? Or are inaccurate peaks called with SR datasets? Either way, this is not a rigorous way to evaluate H3K115ac localization.

We are sorry that this reviewer was not able to access the data – the token for the GEO accession was provided for reviewers at the journal’s request. All ChIP-seq (and ATAC-seq) experiments (paired and single-end) were performed with two biological replicates and the Pearson’s correlations (all >0.9) between replicates were provided in Supplementary Table 1. This was indicated in both the main text and in the methods. In the revised manuscript we have tried to make this even clearer and have put the relevant Pearsons coefficient (r) into the text at the appropriate places. For the reviewer’s information, here is the complete list of data samples in the GEO Accession:

Author response image 1.

While I agree that H3K115ac occupancy is high at +CGIs, the authors downplay that H3K122ac and H3K27ac is also more highly enriched at these locations (page 7, last sentence of first paragraph). I imagine this is all due to the more highly transcribed nature of these genes. Sub-stratifying the K27ac and K122ac by transcription (as in Figure 1G) would help to demonstrate a unique nature of H3K115ac. But even better would be to do an analysis that plots H3K115ac enrichment vs transcription for every individual gene rather than aggregate analyses that are biased by single locations. For example, make an XY scatterplot of RNAPII occupancy or 4SU-seq signal vs H3K115ac level, where each point represents a single gene. Because the interpretation that it is CGI-based and not transcription is confounded with the fact that -CGI are more lowly transcribed. So, looking at Figure 1G, even the -CGI occupancy of H3K115ac is correlated with transcription, but it is just more lowly transcribed.

We thank the reviewer for these suggestions but point out that Figure 1G shows H3K115ac signal for CGI+ and CGI– TSS that are matched for expressions levels (quartiles of 4SU-seq). Fig 1F shows that H3k115ac is much more of a discriminator between CGI+ and – than H3K27ac or H3K122ac.

(2) H3K115ac, H3K27ac, and H3K122ac are all more enriched (in aggregate) at +CGI locations (Fig 1F); so do these locations just have more positioned nucleosomes? More H3.3? So that these PTMs are just more enriched due to the opportunity?

Positioned nucleosomes are generally found downstream of the TSS of active CpG island promoters, so what the reviewer suggests may well account for the relative enrichment of H327ac and H3K122ac at CGI+ vs CGI- promoters in Fig.1F. But H3K115ac localisation is distinct, with the peak at the nucleosome-depleted region not the +1 nucleosome. This is also confirmed by the contour plots in Fig 3. Our observation is also not explained by an enrichment of H3.3 at CGI promoters, since we show that H3K115ac is not specific to H3.3 (Fig 4D).

(3) The authors note in paragraph 2 of page 7 that "H3K115ac does not scale linearly with gene expression..." but the authors never show a quantification of this; stratification in four clusters is not able to make a linear correlation. Furthermore, in the second line of page 7, the authors state that the levels do generally correlate with transcription. To claim it is a specific CGI link and not transcription is tricky, but I encourage the authors to consider more quantifiable ways, rather than correlations, to demonstrate this point, if it is observed.

We thank the reviewer for this comment, and taking it into consideration, we have decided to re-phrase this paragraph. The new text reads: “Non-CGI promoters have lower overall levels of transcription compared to CGI promoters, and for this promoter class H3K115ac enrichment detected by ChIP is only really seen for the highest quartile of transcription (4SU) quartile of expression (Figure 1G). CGI promoters on the other hand, exhibit significant levels of detected H3K115ac even for the lowest quartile of expression. These results suggest a special link between CGI promoters and H3K115ac”.

(4) The authors claim on page 7 that "on average, transcription increased from TSS that also gained H3K115ac but to a modest extent, compared with the more substantial loss of H3K115ac from downregulated TSS". However, both upregulated and downregulated are significant; the difference in magnitude could simply be due to more highly or more lowly transcribed locations, meaning that fold change could be more robustly detected. I caution the authors to substantiate claims like this rather than stating a correlation.

We thank the reviewer for this comment which relates to the data in Fig 2A. It is Fig. 2B shows that the association of H3K115ac loss with downregulation is statistically stronger than H3K115ac gain with upregulation, but only for CGI promoters. With regard to the text on the original pg 7 that is referred to, we have now reworded this to read “Average levels of transcription increased from TSS that also gained H3K115ac, and there was loss of H3K115ac from downregulated TSS (Figure 2A).”

(5) For Figure 2C, the authors argue that H3K115ac correlate with bivalent locations. So this is all qualitative and aggregate localization; please quantitatively demonstrate this claim.

Figure S2D provides statistics for this (observed/expected and Fishers exact test).

(6) The authors claim in Figure 2 that H3115ac is dynamic during differentiation (title of Figure 2). However, there are locations that gain and lose, or maintain H3K115ac. In fact, the most discussed locations are H3K115ac with no change (2C); which means it is NOT dynamic during differentiation. So what is the message for the role during differentiation? From Supplemental Table 1, it appears there is a single ChIP experiment for H3K115ac in NPC, and it is a single read. So this is also a difficult claim with one replicate. Related to this, in S2A, the authors show K115ac where there is no change in transcription; so what is the role of H3K115ac at TSSs relevant to differentiation - it is at both locations changed and unchanged in transcription, but H3K115ac levels itself do not change at these subsets. So, how is this dynamic? This is very confusing, and clearer analyses and descriptions are necessary to deconvolute these data.

We apologise for the misleading title for Figure 2. This has now been amended to “Changes in H3K115ac during differentiation”. The message of this figure is that whilst changes in H3K115ac at TSS are small (panels A-C), at enhancers the changes are much more dramatic (panel D). The reviewer is incorrect about the number of replicates for NPCs – there are two biological replicates (see response to point 1b).

(7) The authors go on to examine H3K115ac enrichment on fragile nucleosomes through sucrose gradient sedimentation. A control for H3K27ac or H3K122ac would be nice for comparison.

We do not have the material available to perform these experiments

(8) When discussing Figures 3 and SF3, the authors mention performing a different MNase for a second ChIP. Showing the MNase distribution for both the more highly digested and the lowly digested would be nice. a) Related to the above, the authors show input in SF3E to argue that the difference in H3K115ac vs H3K27ac is not due to the library, but they do not show the MNase digestion patterns, which is more important for this argument.

Input libraries (first two graphs of FigS3E) are the MNase-digested chromatin. Comparison of nucleotide frequencies from millions of reads is more robust method than the fragment length patterns.

(9) The authors move on to examine H3K115ac at enhancers. Just out of curiosity, given what was found at promoters, is H3K115ac enriched at +CGI enhancers? And what is the correlation with enhancer transcription?

This is an interesting point, but the number of enhancers associated with CGI is not very high and so we did not focus on this. We have not analysed a correlation with eRNAs in this paper.

(10) The authors state on page 14 that the most frequent changes in H3K115ac during differentiation are at these enhancers. So do these changes connect with differentiation-specific genes, and/or genes that have altered transcription during differentiation? Just trying to understand the functional role.

Given the challenges of connecting enhancers with target genes, we have not addressed this question quantitatively. However, we draw the reviewer’s attention to the Genome Browser shots in Figures 2D and S2C, which show clear gain of H3K115ac (and ATAC-seq peaks) at intra and intergenic regions close to genes whose transcription is activated during the differentiation to NPCs.

(11) Related, at the end of page 14, the authors state that the changes in H3K115ac correlate with changes in ATAC-seq; I imagine this dynamic is not unique for H3K115ac and this is observed for other PTMs (H3K27ac), so assessing and clarifying this, to again get to the specific interest of H3K115ac, would be ideal.

We have not claimed that chromatin accessibility is unique to H3K115ac. It is the location of H3K115ac which is found inside the ATAC-seq peak region while H3K27ac is found only upstream/downstream of the ATAC peak that is so striking. This is apparent in Fig 4C.

(12) The authors examine levels of H3K115ac in H3.3 KO cell lines via western blot (Figure 4D), but no replicates and/or quantification are shown.

We now provide a biological replicate for the Western Blot (new FigS4H) together with an image of the whole gel for the data in Fig 4D

(13) In Figure S4 and at the end of page 17, the authors are arguing that there is a link to pioneer TF complexes, based on Oct4 binding. First, while Oct4 has pioneering activity, not all Oct4 sites (or motifs) are pioneering; this has been established. So if you want to use Oct4, substratifying by pioneer vs no pioneer is necessary. Second, demonstrating this is unique to pioneer and not to non-pioneer TFs would be an important control.

In response to the reviewer’s comment, we have removed the term “pioneer” from the manuscript.

(14) Minor point: Figure 4 A and B, there are some formatting issues with the scale bars.

We thank the reviewer for pointing this out, and the errors have been corrected in the revised figure.

(15) Minor point is that it should be clear when single replicates of data are used and when PE/SR sequences are combined or which one is used in each analysis, as this was hard to discern when reading the paper and figure legends.

We have clearly stated in the text that, after Figure2, we repeated all experiments in paired-end mode. All processing steps are defined separately for single end and paired end datasets in the method section. Details of biological replicates are provided in Sup. Table 1. These concerns are also addressed in our response to Reviewer’s public comment-1.

(16) Minor point: it is surprising that different MNase and different units were used in the ChIP vs sucrose sedimentation. Could the authors clarify why?

Chromatin prep for sucrose gradients were done on a much larger scale than for ChIP-seq and required different setups to obtain the right level of MNase digestion.

(17) The authors note that fragile nucleosomes contain H2A.Z and H3.3, but they never perform an analysis of available data to demonstrate a correlation (or better a quantifiable correlation) between H3K115ac occupancy and these marks at the locations they identify H3K115ac.

Since have shown (Fig. 4) that depletion of H3.3 does not affect overall levels of H3K115ac, we do not think there is value in further quantitative correlative analyses of H3K115ac and variant histones.

(18) Minor point: What is the overlap in peaks for H3K115ac, H3K122ac, and H3K27ac (Figure 1C)?

Nearly all H3K115ac peaks overlap with H3K122ac and/or H3K27ac. Its most distinct properties are its association with CGI promoters, fragile nucleosomes and its unique localisation within the NDRs, three points that the manuscript is focussed on.

Reviewer #3 (Recommendations for the authors):

(1) The western blot results in Figure 4D probing for H3, H3.3, and H3K115ac use Ponceau S staining, presumably of an area of the membrane where histones might be expected to migrate, as a measure of loading. However, the Ponceau S bands appear uniformly weaker in the H3.3KO lanes, yet despite this, blotting with H3.3 antibody detects a band in H3.3 knockout ESCs, suggesting that the antibody does not have a high degree of specificity. Again, a blocking experiment with appropriate peptides would instill more confidence in the specificity of these reagents, and/or the authors could provide independent validation of the knockout model to differentiate between a partial knockout or antibody cross-reactivity (e.g., by Sanger sequencing).

In a revised Fig. S4H we now show the whole gel corresponding to this blot but including co-staining with an antibody for H4 to provide a better loading control. We also provide a biological replicate of this Western blot in the lower panel of Fig. S4H.

(2) The manuscript would benefit from in vitro follow-up and validation, but if the authors intend to keep the manuscript primarily in silico, I suggest dedicating a few lines in each section to explain the plots, their axes, and their purpose, as well as to assist with interpretation, rather than directly discussing the results. This would make the manuscript more accessible and understandable for a broader audience in the field of epigenetics.

In the revised version, we have tried to improve the text to make the data more accessible to a broad audience.

Reviewer #4 (Public review):

I maintain that the images in Figure 12 (new Figure 14) do not support the authors' interpretation that 2-cell embryos resulted from in vitro fertilization (IVF) of Amrc-/- rescued sperm. They are clearly not normal 2-cell embryos and instead look very much like fragmented eggs that can be seen occasionally following in vitro fertilization procedures even when that is done with wild type eggs and sperm. The only portion of current Figure 14 that has normal looking 2-cell embryos is in panel 14A4, where wild type B6D2 sperm were used. Even in that panel, there are some fragmented eggs that the authors identify as 2-cell embryos.

The authors offer the explanation that CD1 eggs fertilized by B6D2F1 hybrid male sperm do not develop beyond the 2-cell stage, citing a 2008 paper published in Biology of Reproduction by Fernandez-Goonzalez et al. I read through that paper very carefully and even had a colleague read through it in case I missed something, but that paper says nothing at all about strain incompatibilities, much less 2-cell arrest due to them. The only crosses done in that paper are CD1 eggs x CD1 sperm and B6D2 eggs x B6D2 sperm, all by intracytoplasmic sperm injection and not standard in vitro fertilization. [Note that the paper does mention performing in vitro fertilization but says nothing about how it was done or what mouse strains were used.] I even searched the literature for information regarding incompatibility between these strains and could find nothing relevant. But even if the authors are correct and there happens to be a strain incompatibility and 2-cell arrest is expected, what the authors are calling 2-cell embryos are clearly not.

A second explanation offered by the authors is that they used collagenase to remove the cumulus cells and that this may have affected the appearance of the embryos. This technique is actually used to remove both the cumulus cells and the zona pellucida and has been described as a gentler way to do so than other standard methods (hyaluronidase treatment followed by acid Tyrodes to remove the zona pellucida) (Yamatoya et al., Reprod Med Biol 2011, DOI 10.1007/s12522-011-0075-8). I think it is highly relevant to the current study that the method they used to remove cumulus cells also dissolves the zona, either partially or completely. Given that many of the eggs, fragmented eggs, and 2-cell embryos (from the WT sperm) in Figure 14A are lacking a zona pellucida, it seems very likely that many of the eggs were either zona-free or had partial zona dissolution from the start. In fact, the authors state in the Methods section that "Cumulus-free and zona-free eggs were collected..." for how IVF was done. Partial zona dissolution is standard in some protocols for performing IVF using frozen mouse sperm, which usually have much lower motility and overall efficacy than fresh sperm. In any case, it would improve transparency if the manuscript made clear somewhere other than buried in the Methods that the IVF procedure was done on eggs with partially or fully removed zonas, to allow proper interpretation.

In the rebuttal, the authors go on to state: "To provide additional functional evidence, we complemented the IVF experiments with ICSI using rescued Armc2-/- sperm and B6D2 oocytes, which allowed embryos to develop to the blastocyst stage. In these experiments, 25% of injected oocytes reached the blastocyst stage with rescued sperm compared to 13% for untreated Armc2-/- sperm (Supplementary Fig. 9) These results support the functional competence of rescued sperm and demonstrate partial recovery of fertilization ability following Armc2 mRNA electroporation."

Their conclusion that the data support partial recovery of fertilization ability following Armc2 mRNA electroporation in my opinion has no basis. This experiment was done only once, and no information is provided regarding how many eggs underwent ICSI or how many reached the blastocyst stage. The authors claim that the rescued sperm were better than the Armc2-/- sperm in producing blastocysts, but this is based on a simple percentage report of 25% vs 13% without any statistical analysis, even on the results from the single experiment presented.

Overall, the paper shows rescue of some sperm motility by the new method they use, and the new title is therefore appropriate. The authors have also dealt reasonably with many of the original concerns regarding documenting that their methodology was effective in producing protein (at least the GFP marker) in spermatogenic cells. In my view the authors have, however, not shown any indication of functional recovery over what is already known for the knockout sperm, that ICSI can support blastocyst stage embryo development. They also have not, in my view, justified the claims at the end of the abstract "These motile sperm were able to produce embryos by IVF..." and that "...mRNA electroporation can restore...partially fertilizing ability..."

You don't have to host -- why not just evaluate and curte?

Or you can have a compromise -- a 'traditional summary' in the journal, linking to the interactive version created by the author, the latter being the canonical one

NB, I think interactive content is high value, but the authors can produce it, especially given Claude code etc

post to the whole class

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

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

Summary: This manuscript reports the identification of putative orthologues of mitochondrial contact site and cristae organizing system (MICOS) proteins in Plasmodium falciparum - an organism that unusually shows an acristate mitochondrion during the asexual part of its life cycle and then this develops cristae as it enters the sexual stage of its life cycle and beyond into the mosquito. The authors identify PfMIC60 and PfMIC19 as putative members and study these in detail. The authors at HA tags to both proteins and look for timing of expression during the parasite life cycle and attempt (unsuccessfully) to localise them within the parasite. They also genetically deleted both gene singly and in parallel and phenotyped the effect on parasite development. They show that both proteins are expressed in gametocytes and not asexuals, suggesting they are present at the same time as cristae development. They also show that the proteins are dispensible for the entire parasite life cycle investigated (asexuals through to sporozoites), however there is some reduction in mosquito transmission. Using EM techniques they show that the morphology of gametocyte mitochondria is abnormal in the knock out lines, although there is great variation.

Major comments: The manuscript is interesting and is an intriguing use of a well studied organism of medical importance to answer fundamental biological questions. My main comments are that there should be greater detail in areas around methodology and statistical tests used. Also, the mosquito transmission assays (which are notoriously difficult to perform) show substantial variation between replicates and the statistical tests and data presentation are not clear enough to conclude the reduction in transmission that is claimed. Perhaps this could be improved with clearer text?

We would like to thank the reviewer for taking the time to review our manuscript. We are happy to hear the reviewer thinks the manuscript is interesting and thank the reviewer for their constructive feedback.

To clarify the statistical analyses used, we included a new supplementary dataset with all statistical analyses and p-values indicated per graph. Furthermore, figure legends now include the information on the exact statistical test used in each case.

Regarding mosquito experiments, while we indeed reported a reduction in transmission and oocysts numbers we are aware that this effect might be due to the high variability in mosquito feeding assays. To highlight this point, we deleted the sentence "with the transmission reduction of [numbers]...." and we included the sentence "The high variability encountered in the standard membrane feeding assays, though, partially obstructs a clear conclusion on the biological relevance of the observed reduction in oocyst numbers"

More specific comments to address: Line 101/Fig1E (and figure legend) - What is this heatmap showing. It would be helpful to have a sentence or two linking it to a specific methodology. I could not find details in the M+M section and "specialized, high molecular mass gels" does not adequately explain what experiments were performed. The reference to Supplementary Information 1 also did not provide information.

We added the information "high molecular mass gels with lower acrylamide percentage" to clarify methodology in the text. Furthermore, we extended the figure legend to include all relevant information. Further experimental details can be found in the study cited in this context, where the dataset originates from (Evers et al., 2021).

Line 115 and Supplementary Figure 2C + D - The main text says that the transgenic parasites contained a mitochondrially localized mScarlet for visualization and localization, but in the supplementary figure 2 it shows mitotracker labelling rather than mScarlet. This is very confusing. The figure legend also mentions both mScarlet and MitoTracker. I assume that mScarlet was used to view in regular IFAs (Fig S2C) and the MitoTracker was used for the expansion microscopy (Fig S2D)? Please clarify.

We thank the reviewer for pointing this out - this was indeed incorrectly annotated. We used the endogenous mito-mScarlet signal in IFA and mitoTracker in U-ExM. The figure annotation has now been corrected.

Figure 2C - what is the statistical test being used (the methods say "Mean oocysts per midgut and statistical significance were calculated using a generalized linear mixed effect model with a random experiment effect under a negative binomial distribution." but what test is this?)?

The statistic test is now included in the material and method section with the sentence "The fitted model was used to obtain estimated means and contrasts and were evaluated using Wald Statistics". The test is now also mentioned in the figure legend.

Also the choice of a log10 scale for oocyst intensity is an unusual choice - how are the mosquitoes with 0 oocysts being represented on this graph? It looks like they are being plotted at 10^-1 (which would be 0.1 oocysts in a mosquito which would be impossible).

As the data spans three orders of magnitude with low values being biologically meaningful, we decided that a log scale would best facilitate readability of the graph. As the 0 values are also important to show, we went with a standard approach to handle 0s in log transformed data and substituted the 0s with a small value (0.001). We apologize for not mentioning this transformation in the manuscript. To make this transformation transparent, we added a break at the lower end of the log‑scaled y‑axis and relabelled the lowest tick as '0'. This ensures that mosquitoes with zero oocysts are shown along the x‑axis without being assigned an artificial value on the log scale. We would furthermore like to highlight that for statistics we used the true value 0 and not 0.001.

Figure 2D - it is great that the data from all feeding replicates has been shared, however it is difficult to conclude any meaningful impact in transmission with the knock-out lines when there is so much variation and so few mosquitoes dissected for some datapoints (10 mosquitoes are very small sample sizes). For example, Exp1 shows a clear decrease in mic19- transmission, but then Exp2 does not really show as great effect. Similarly, why does the double knock out have better transmission than the single knockouts? Sure there would be a greater effect?

We agree with the reviewer and with the new sentence added, as per major point, we hope we clarified the concept. Note that original Figure 2D has been moved to the supplementary information, as per minor comment of another reviewer.

Figure 3 legend - Please add which statistical test was used and the number of replicates.

Done

Figure 4 legend - Please add which statistical test was used and the number of replicates.

Done. Regarding replicates, note that while we measured over 100 cristae from over 30 mitochondria, these all stem from the same parasite culture.

Figure 5C - the 3D reconstructions are very nice, but what does the red and yellow coloring show?

Indeed, the information was missing. We added it to the figure legend.

Line 352 - "Still, it is striking that, despite the pronounced morphological phenotype, and the possibly high mitochondrial stress levels, the parasites appeared mostly unaffected in life cycle propagation, raising questions about the functional relevance of mitochondria at these stages." How do the authors reconcile this statement with the proven fact that mitochondria-targeted antimalarials (such as atovaquone) are very potent inhibitors of parasite mosquito transmission?

Our original sentence was reductive. What we wanted to state was related to the functional relevance of crista architecture and overall mitochondrial morphology rather than the general functional relevance of the mitochondria. We changed the sentence accordingly.

Furthermore, even though we do not discuss this in the article, we are aware of mitochondria targeting drugs that are known to block mosquito transmission. We want to point out that it is difficult to discern the disruption of ETC and therefore an impact on energy conversion with the impact on the essential pathway of pyrimidine synthesis, highly relevant in microgamete formation. Still, a recent paper from Sparkes et al. 2024 showed the essentiality of mitochondrial ATP synthesis during gametogenesis so it is very likely that the mitochondrial energy conversion is highly relevant for transmission to the mosquito.

Reviewer #1 (Significance (Required)):

This manuscript is a novel approach to studying mitochondrial biology and does open a lot of unanswered questions for further research directions. Currently there are limitations in the use of statistical tests and detail of methodology, but these could be easily be addressed with a bit more analysis/better explanation in the text. This manuscript could be of interest to readers with a general interest in mitochondrial cell biology and those within the specific field of Plasmodium research. My expertise is in Plasmodium cell biology.

We thank the reviewer for the praise.

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

Major comments: 1) In my opinion, the authors tend to sensationalize or overinterpret their results. The title of the manuscript is very misleading. While MICOS is certainly important for crista formation, it is not the only factor, as ATP synthase dimer rows make a highly significant contribution to crista morphology. Thus, one can argue with equal validity that ATP synthase should be considered the 'architect', as it's the conformation of the dimers and rows modulate positive curvature. Secondly, while cristae are still formed upon mic60/mic19 gene knockout (KO), they are severely deformed, and likely dysfunctional (see below). Thus, I do not agree with the title that MICOS is dispensable for crista formation, because the authors results show that it clearly is essential. So, the title should be changed.

We thank the reviewer for taking the time to review our manuscript.

Based on the reviewers' interpretation we conclude the title does not come across as intended. We have changed the title to: "The role of MICOS in organizing mitochondrial cristae in malaria parasites"

The Discussion section starting from line 373 also suffers from overinterpretation as well as being repetitive and hard to understand. The authors infer that MICOS stability is compromised less in the single KOs (sKO) in compared to the mic60/mic19 double KO (dKO). MICOS stability was never directly addressed here and the composition of the MICOS complex is unaddressed, so it does not make sense to speculate by such tenuous connections. The data suggest to me that mic60 and mic19 are equally important for crista formation and crista junction (CJ) stabilization, and the dKO has a more severe phenotype than either KO, further demonstrating neither is epistatic.

We do agree with the reviewer's notion that we did not address complex stability, and our wording did not make this sufficiently clear. We shortened and rephrased the paragraph in question.

The following paragraphs (line 387 to 422) continues with such unnecessary overinterpretation to the point that it is confusing and contradictory. Line 387 mentions an 'almost complete loss of CJs' and then line 411 mentions an increase in CJ diameter, both upon Mic60 ablation. I do not think this discussion brings any added value to the manuscript and should be shortened. Yes, maybe there are other putative MICOS subunits that may linger in the KOS that are further destabilized in the dKO, or maybe Mic60 remains in the mic19 KO (and vice versa) to somehow salvage more CJs, which is not possible in the dKO. It is impossible to say with confidence how ATP synthase behaves in the KOs with the current data.

We shortened this paragraph.

2) While the authors went through impressive lengths to detect any effect on lifecycle progression, none was found except for a reduction in oocyte count. However, the authors did not address any direct effect on mitochondria, such as OXPHOS complex assembly, respiration, membrane potential. This seems like a missed opportunity, given the team's previous and very nice work mapping these complexes by complexome profiling. However, I think there are some experiments the authors can still do to address any mitochondrial defects using what they have and not resorting to complexome profiling (although this would be definitive if it is feasible):

i) Quantification of MitoTracker Red staining in WT and KOs. The authors used this dye to visualize mitochondria to assay their gross morphology, but unfortunately not to assay membrane potential in the mutants. The authors can compare relative intensities of the different mitochondria types they categorized in Fig. 3A in 20-30 cells to determine if membrane potential is affected when the cristae are deformed in the mutants. One would predict they are affected.

Interesting suggestion. As our staining and imaging conditions are suitable for such analysis (as demonstrated by Sarazin et al., 2025, https://www.biorxiv.org/content/10.1101/2025.11.27.690934v1), we performed the measurements on the same dataset which we collected for Figure 3. We did, however, not detect any difference in mitotracker intensity between the different lines. The result of this analysis is included in the new version of Supplementary figure S6.

ii) Sporozoites are shown in Fig S5. The authors can use the same set up to track their motion, with the hypothesis that they will be slower in the mutants compared to WT due to less ATP. This assumes that sporozoite mitochondria are active as in gametocytes.

While theoretically plausible and informative, we currently do not know the relevance of mitochondrial energy conversion for general sporozoite biology or specifically features of sporozoite movement. Given the required resources and time to set this experiment up and the uncertainty whether it is a relevant proxy for mitochondrial functioning, we argue it is out of scope for this manuscript.

iii) Shotgun proteomics to compare protein levels in mutants compared to WT, with the hypothesis that OXPHOS complex subunits will be destabilized in the mutants with deformed cristae. This could be indirect evidence that OXPHOS assembly is affected, resulting in destabilized subunits that fail to incorporate into their respective complexes.

While this experiment could potentially further our understanding of the interaction between MICOS and levels of OXPHOS complex subunits we argue that the indirect nature of the evidence does not justify the required investments.

To expedite resubmission, the authors can restrict the cell lines to WT and the dKO, as the latter has a stronger phenotype that the individual KOs and conclusions from this cell line are valid for overall conclusions about Plasmodium MICOS.

I will also conclude that complexome/shotgun proteomics may be a useful tool also for identifying other putative MICOS subunits by determining if proteins sharing the same complexome profile as PfMic60 and Mic19 are affected. This would address the overinterpretation problem of point 1.

3) I am aware of the authors previous work in which they were not able to detect cristae in ABS, and thus have concluded that these are truly acristate. This can very well be true, or there can be immature cristae forms that evaded detection at the resolution they used in their volumetric EM acquisitions. The mitochondria and gametocyte cristae are pretty small anyway, so it not unreasonable to assume that putative rudimentary cristae in ABS may be even smaller still. Minute levels of sampled complex III and IV plus complex V dimers in ABS that were detected previously by the authors by complexome profiling would argue for the presence of miniscule and/or very few cristae.

I think that authors should hedge their claim that ABS is acrisate by briefly stating that there still is a possibility that miniscule cristae may have been overlooked previously.

We acknowledge that we cannot demonstrate the absolute absence of any membrane irregularities along the inner mitochondrial membrane. At the same time, if such structures were present, they would be extremely small and unlikely to contain the full set of proteins characteristic of mature cristae. For this reason, we consider it appropriate to classify ABS mitochondria as acristate. To reflect the reviewer's point while maintaining clarity for readers, we have slightly adjusted our wording in the manuscript, changing 'fully acristate' to 'acristate'.

This brings me to the claim that Mic19 and Mic60 proteins are not expressed in ABS. This is based on the lack of signal from the epitope tag; a weak signal is detected in gametocytes. Thus, one can counter that Mic19 and Mic60 are also expressed, but below the expression limits of the assay, as the protein exhibits low expression levels when mitochondrial activity is upregulated.

We agree with the reviewer that the absence of a detectable epitope‑tag signal does not definitively exclude low‑level expression, and we have therefore replaced the term 'absent' with 'undetectable' throughout the manuscript. In context with previous findings of low-level transcripts of the proteins in a study by Lopez-Berragan et al. and Otto et al., we also added the sentence "The apparent absence could indicate that transcripts are not translated in ABS or that the proteins' expression was below detection limits of western blot analysis." to the discussion. _At the same time, we would like to clarify that transcript levels for both genes fall within the

To address this point, the authors should determine of mature mic60 and mic19 mRNAs are detected in ABS in comparison to the dKO, which will lack either transcript. RT-qPCR using polyT primers can be employed to detect these transcripts. If the level of these mRNAs are equivalent to dKO in WT ABS, the authors can make a pretty strong case for the absence of cristae in ABS.

We appreciate the reviewer's suggestion. As noted in the Discussion, existing transcriptomic datasets already show detectable MIC19 and MIC60 mRNAs in ABS. For this reason, we expect RT-qPCR to reveal low (but not absent) levels of both transcripts, unlike the true loss expected to be observed in the dKO. Because such residual signals have been reported previously and their biological relevance remains uncertain, we do not believe transcript levels alone can serve as a definitive indicator of cristae absence in ABS.

They should highlight the twin CX9C motifs that are a hallmark of Mic19 and other proteins that undergo oxidative folding via the MIA pathway. Interestingly, the Mia40 oxidoreductase that is central to MIA in yeast and animals, is absent in apicomplexans (DOI: 10.1080/19420889.2015.1094593).

Searching for the CX9C motifs is a valuable suggestion. In response to the reviewer´s suggestion we analysed the conservation of the motif in PfMIC19 and included this in a new figure panel (Figure 1 F).

Did the authors try to align Plasmodium Mic19 orthologs with conventional Mic19s? This may reveal some conserved residues within and outside of the CHCH domain.

In response to this comment we made Figure 1 F, where we show conserved residues within the CHCH domains of a broad range of MIC19 annotated sequences across the opisthokonts, and show that the Cx9C motifs are conserved also in PfMIC19. Outside the CHCH domain, we did not find any meaningful conservation, as PfMIC19 heavily diverges from opisthokont MIC19.

5) Statistcal significance. Sometimes my eyes see population differences that are considered insignificant by the statistical methods employed by the authors, eg Fig. 4E, mutants compared to WT, especially the dKO. Have the authors considered using other methods such as student t-test for pairwise comparisons?

The graphs in figures 3, 4 and 5 got a makeover, such that they now are in linear scale and violin plots (also following a suggestion from further down in the reviewer's comments). We believe that this improves interpretability. ANOVA was kept as statistical testing to assure the correction for multiple comparisons that cannot be performed with standard t-test. A full overview of statistics and exact p-values can also be found in the newly added supplementary information 2.

Minor comments: Line 33. Anaerobes (eg Giardia) have mitochondria that do produce ATP, unlike aerobic mitochondria

We acknowledge that producing ATP via OXPHOS is not a characteristic of all mitochondria-like organelles (e.g. mitosomes), which is why these are typically classified separately from canonical mitochondria. When not considering mitochondria-like organelles, energy conversion is the function that the mitochondrion is most well-known for and the one associated with cristae.

Line 56: Unclear what authors mean by "canonical model of mitochondria"

To clarify we changed this to "yeast or human" model of mitochondria.

Lines 75-76: This applies to Mic10 only

We removed the "high degree of conservation in other cristate eukaryotes" statement.

Line 80: Cite DOI: 10.1016/j.cub.2020.02.053

Done

Fig 2D: I find this table difficult to read. If authors keep table format, at least get rid of 'mean' column' as this data is better depicted in 2C. I suggest depicted this data either like in 3B depicting portion of infected vs unaffected flies in all experiments, then move modified Table to supplement. Important to point out experiment 5 appears to be an outlier with reduced infectivity across all cell lines, including WT.

To clarify: the mean reported in the table indicates the mean per replicate while the mean reported in figure 2C is the overall mean for a given genotype that corrects for variability within experiments. We agree that moving the table to the supplementary data is a good idea. We decided to not include a graph for infected and non-infected mosquitoes as this information would be partially misleading, highlighting a phenotype we argue to be influenced by the strong variability.

Fig. 3C-G: I feel like these data repeatedly lead to same conclusions. These are all different ways of showing what is depicted in Fig 2B: mitochondria gross morphology is affected upon ablation of MICOS. I suggest that these graphs be moved to supplement and replaced by the beautiful images.

Thank you for the nice comment on our images. We have now moved part of the graphs to supplementary figure 6 and only kept the Relative Frequency, Sphericity and total mitochondria volume per cell in the main figure.

Line 180: Be more specific with which tubulin isoform is used as a male marker and state why this marker was used in supplemental Fig S6.

We have now specified the exact tubulin isoform used as the male gametocyte marker, both in the main text and in Supplementary Fig. S6. This is a commercial antibody previously known to work as an effective male marker, which is why we selected it for this experiment. This is now clearly stated in the manuscript.

Line 196 and Fig 3C: the word 'intensities' in this context is very ambiguous. Please choose a different term (puncta, elements, parts?). This is related to major point 2i above.

To clarify the biological effect that we can conclude form the measurement, we added an explanation about it in the respective section of the results, and we decided to replace the raw results of the plug-in readout with the deduced relative dispersion.

Line 222: Report male/female crista measurements

We added Supplementary information 2, which contains exact statistical test and outcomes on all presented quantifications as well as a per-sex statistical analysis of the data from figure 4. Correspondingly, we extended supplementary information 2 by a per-sex colour code for the thin section TEM data.

Fig. 4B-E: depict data as violin plots or scatter plots like Fig. 2C to get a better grasp of how the crista coverage is distributed. It seems like the data spread is wider in the double KO. This would also solve the problem with the standard deviation extending beyond 0%.

We changed this accordingly.

Lines 331-333: Please clarify that this applies for some, but not all MICOS subunits. Please also see major point 1 above. Also, the authors should point out that despite their structural divergence, trypanosomal cryptic mitofilins Mic34 and Mic40 are essential for parasite growth, in contrast to their findings with PfMic60 (DOI: https://doi.org/10.1101/2025.01.31.635831).

This has been changed accordingly.

Line 320: incorrect citation. Related to point 1above.

Correct citation is now included in the text.

Lines 333-335. This is related to the above. Again, some subunits appear to affect cell growth under lab conditions, and some do not. This and the previous sentence should be rewritten to reflect this.

This has been changed accordingly.

Line 343-345: The sentence and citation 45 are strange. Regarding the former, it is about CHCHD10, whose status as a bona fide MICOS subunit is very tenuous, so I would omit this. About the phenomenon observed, I think it makes more sense to write that Mic60 ablation results in partially fragmented mitochondria in yeast (Rabl et al., 2009 J Cell Biol. 185: 1047-63). A fragmented mitochondria is often a physiological response to stress. I would just rewrite as not to imply that mitochondrial fission (or fusion) is impaired in these KOs, or at least this could be one of several possibilities.

The sentence has been substituted following the indication of the reviewer. Though we still include the data of the human cells as this has also been shown in Stephens et al. 2020.

Line 373: 'This indicates' is too strong. I would say 'may suggest' as you have no proof that any of the KOs disrupts MICOS. This hypothesis can be tested by other means, but not by penetrance of a phenotype.

Done

Line 376-377; 'deplete functionality' does not make sense, especially in the context of talking about MICOS subunit stability. In my opinion, this paragraph overinterprets the KO effects on MICOS stability. None of the experiments address this phenomenon, and thus the authors should not try to interpret their results in this context. See major point 1. Other suggestions for added value

We removed the sentence. Also, the entire paragraph has been shortened, restructured and wording was changed to address major point 1.

1) Does Plasmodium Sam50 co-fractionate with Mic60 and Mic19 in BN PAGE (Fig. 1E)

While we did identify SAMM50 in our BN PAGE, the protein does not co-migrate with the MICOS components but instead comigrates with other components of a putative sorting and assembly machinery (SAM) complex. As SAMM50, the SAM complex and the overarching putative mitochondrial membrane space bridging (MIB) complex are not mentioned in the manuscript, we decided to not include the information in the figure.

Reviewer #2 (Significance (Required)):

The manuscript by Tassan-Lugrezin is predicated on the idea that Plasmodium represents the only system in which de novo crista formation can be studied. They leverage this system to ask the question whether MICOS is essential for this process. They conclude based on their data that the answer is no, which the authors consider unprecedented. But even if their claim is true that ABS is acristate, this supposed advantage does not really bring any meaningful insight into how MICOS works in Plasmodium.

First the positives of this manuscript. As has been the case with this research team, the manuscript is very sophisticated in the experimental approaches that are made. The highlights are the beautiful and often conclusive microscopy performed by the authors. Only the localization of Mic60 and Mic19 was inconclusive due to their very low expression unfortunately.

The examination of the MICOS mutants during in vitro life cycle of Plasmodium falciparum is extremely impressive and yields convincing results. Mitochondrial deformation is tolerated by life cycle stage differentiation, with a modest but significant reduction of oocyte production, being observed.

However, despite the herculean efforts of the authors, the manuscript as it currently stands represents only a minor advance in our understanding of the evolution of MICOS, which from the title and focus of the manuscript, is the main goal of the authors. In its current form, the manuscript reports some potentially important findings:

1) Mic60 is verified to play a role in crista formation, as is predicted by its orthology to other characterized Mic60 orthologs.

2) The discovery of a novel Mic19 analog (since the authors maintain there is no significant sequence homology), which exhibits a similar (or the same?) complexome profile with Mic60. This protein was upregulated in gametocytes like Mic60 and phenocopies Mic60 KO.

3) Both of these MICOS subunits are essential (not dispensable) for proper crista formation

4) Surprisingly, neither MICOS subunit is essential for in vitro growth or differentiation from ABS to sexual stages, and from the latter to sporozoites. This says more about the biology of plasmodium itself than anything about the essentiality of Mic60, ie plasmodium life cycle progression tolerates defects to mitochondrial morphology. But yes, I agree with the authors that Mic60's apparent insignificance for cell growth in examined conditions does differ with its essentiality in other eukaryotes. But fitness costs were not assayed (eg by competition between mutants and WT in infection of mosquitoes)

5) Decreased fitness of the mutants is implied by a reduction of oocyte formation.

While interesting in their own way, collectively they do not represent a major advance in our understanding of MICOS evolution. Furthermore, the findings bifurcate into categories informing MICOS or Plasmodium biology. Both aspects are somewhat underdeveloped in their current form.

This is unfortunate because there seem to be many missed opportunities in the manuscript that could, with additional experiments, lead to a manuscript with much wider impact. For me, what is remarkable about Plasmodium MICOS that sets it apart from other iterations is the apparent absence of the Mic10 subunit. Purification of plasmodium MICOS via the epitope tagged Mic60 and Mic19 could have verified that MICOS is assembled without this core subunit. Perhaps Mic60 and Mic19 are the vestiges of the complex, and thus operate alone in shaping cristae. Such a reduction may also suggest the declining importance of mitochondria in plasmodium.

Another missed opportunity was to assay the impact of MICOS-depletion of OXPHOS in plasmodium. This is a salient issue as maybe crista morphology is decoupled from OXPHOS capacity in Plasmodium, which links to the apparent tolerance of mitochondrial morphology in cell growth and differentiation. I suggested in section A experiments to address this deficit.

Finally, the authors could assay fitness costs of MICOS-ablation and associated phenotypes by assaying whether mosquito infectivity is reduced in the mutants when they are directly competing with WT plasmodium. Like the authors, I am also surprised that MICOS mutants can pass population bottlenecks represented by differentiation events. Perhaps the apparent robustness of differentiation may contribute plasmodium's remarkable ability to adapt.

I realize that the authors put a lot of efforts into their study and again, I am very impressed by the sophistication of the methods employed. Nevertheless, I think there is still better ways to increase the impact of the study aside from overinterpreting the conclusions from the data. But this would require more experiments along the lines I suggest in Section A and here.

We thank the reviewer for their extensive analysis of the significance of our findings, including the compliments on our microscopy images and the sophisticated experimental approaches. We hope we have convincingly argued why we could or could not include some of the additional analyses suggested by the reviewer in section 1 above.

With regard to the significance statement, we want to point out that our finding that PfMICOS is not needed for initial formation of cristae (as opposed to organization thereof), is a confirmation of something that has been assumed by the field, without being the actual focus of studies. We argue that the distinction between formation and organization of cristae is important and deserves some attention within the manuscript. The result of MICOS not being involved in the initial formation of cristae, we argue to be relevant in Plasmodium biology and beyond. As for the insights into how MICOS works in Plasmodium we have confirmed that the previously annotated PfMIC60 is indeed involved in the organization of cristae. Furthermore, we have identified and characterized PfMIC19. These findings, we argue, are indeed meaningful insights into PfMICOS.

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

Summary:

MICOS is a conserved mitochondrial protein complex responsible for organising the mitochondrial inner membrane and the maintenance of cristae junctions. This study sheds first light on the role of two MICOS subunits (Mic60 and the newly annotated Mic19) in the malaria parasite Plasmodium falciparum, which forms cristae de novo during sexual development, as demonstrated by EM of thin section and electron tomography. By generating knockout lines (including a double knockout), the authors demonstrate that knockout of both MICOS subunits leads to defects in cristae morphology and a partial loss of cristae junctions. With a formidable set of parasitological assays, the authors show that despite the metabolically important role of mitochondria for gametocytes, the knockout lines can progress through the life stages and form sporozoites, albeit with diminished infection efficiency.

We thank the reviewer for their time and compliment.

Major comments:

1) The authors should improve to present their findings in the right context, in particular by:

(i) giving a clearer description in the introduction of what is already known about the role of MICOS. This starts in the introduction, where one main finding is missing: loss of MICOS leads to loss of cristae junctions and the detachment of cristae membranes, which are nevertheless formed, but become membrane vesicles. This needs to be clearly stated in the introduction to allow the reader to understand the consistency of the authors' findings in P. falciparum with previous reports in the literature.

We extended the introduction to include this information.

(ii) at the end to the introduction, the motivating hypothesis is formulated ad hoc "conclusive evidence about its involvement in the initial formation of cristae is still lacking" (line 83). If there is evidence in the literature that MICOS is strictly required for cristae formation in any organism, then this should be explained, because the bona fide role of MICOS is maintenance of cristae junctions (the hypothesis is still plausible and its testing important).

To clarify we rephrased the sentence to: "Although MICOS has been described as an organizer of crista junctions, its role during the initial formation of nascent cristae has not been investigated."

2) Line 96-97: "Interestingly, PfMIC60 is much larger than the human MICOS counterpart, with a large, poorly predicted N-terminal extension." This statement is lacking a reference and presumably refers to annotated ORFs. The authors should clarify if the true N-terminus is definitely known - a 120kDa size is shown for the P. falciparum but this is not compared to the expected length or the size in S. cerevisiae.

To solve the reference issue, we added the uniprot IDs we compared to see that the annotated ORF is bigger in Plasmodium. We also changed the comparison to yeast instead of human, because we realized it is confusing to compare to yeast all throughout the figure, but then talk about human in this specific sentence.

Regarding whether the true N-terminus is known. Short answer: No, not exactly.

However, we do know that the Pf version is about double the size of the yeast protein.

As the reviewer correctly states, we show the size of 120kDa for the tagged protein in Figure 1G. Considering that we tagged the protein C-terminally, and observed a 120kDa product on western blot, it is safe to conclude that the true N-terminus does not deviate massively from the annotated ORF, and hence, that there is a considerable extension of the protein beyond a 60kDa protein. We do not directly compare to yeast MIC60 on our western blots, however, that comparison can be drawn from literature: Tarasenko et al., 2017 showed that purified MIC60 running at ~60kDa on SDS-PAGE actively bends membranes, suggesting that in its active form, the monomer of yeast MIC60 is indeed 60kDa in size.

To clarify, we now emphasize that we ran the Alphafold prediction on the annotated open reading frame (annotated and sequenced by Bohme et al. and Chapell et al. now cited in the manuscript), and revised the wording to make clear what we are comparing in which sentence.

3) lines 244-245: "Furthermore, our data indicates the effect size increases with simultaneous ablation of both proteins?". The authors should explain which data they are referring to, as some of the data in Fig 3 and 4 look similar and all significance tests relate to the wild type, not between the different mutants, so it is not clear if any overserved differences are significant. The authors repeat this claim in the discussion in lines 368-369 without referring to a specific significance test. This needs to be clarified.

As a reply to this and other comments from the reviewers we added the multiple testing within all samples. In addition, to clarify statistics used we included a supplementary dataset with all p-values and statistical tests used.

4) lines 304-306: "Though well established as the cristae organizing system, the role of MICOS in initial formation of cristae remains hidden in model organisms that constitutively display cristae.". This sentence is misleading since even in organisms that display numerous cristae throughout their life cycle, new cristae are being formed as the cells proliferate. Thus, failure to produce cristae in MICOS knockout lines would have been observable but has apparently not been reported in the literature. Thus, the concerted process in P. falciparum makes it a great model organism, but not fundamentally different to what has been studied before in other organisms.

We deleted this statement.

5) lines 373-378. "where ablation of just MIC60 is sufficient to deplete functionality of the entire MICOS (11, 15),". The authors' claim appears to be contrary to what is actually stated in ref 15, which they cite:

"MICOS subunits have non-redundant functions as the absence of both MICOS subcomplexes results in more severe morphological and respiratory growth defects than deletion of single MICOS subunits or subcomplexes."

This seems in line with what the authors show, rather than "different".

This sentence has been removed.

6) lines 380-385: "... thus suggesting that membrane invaginations still arise, but are not properly arranged in these knockout lines. This suggests that MICOS either isn't fully depleted,...". These conclusions are incompatible with findings from ref. 15, which the authors cite. In that study, the authors generated a ∆MICOS line which still forms membrane invaginations, showing that MICOS is not required at all for this process in yeast. Hence the authors' implication that MICOS needs to be fully depleted before membrane invaginations cease to occur is not supported by the literature.

This sentence has been deleted in the revised version of the manuscript.

Minor comments:

7) The authors should consider if the first part of their title could be seen as misleading: It suggests that MICOS is "the architect" in cristae formation, but this is not consistent with the literature nor their own findings.

Title is changed accordingly

Minor comments:

• Line 43, of the three seminal papers describing the discovery of MICOS in 2011, the authors only cite two (refs 6 and 7), but miss the third paper, Hoppins et al, PMID: 21987634, which should probably be corrected.

Done, the paper is now cited

• Page 2, line 58: for a more complete picture the authors should also cite the work of others here which shows that although at very low levels, e.g. complex III (a drug target) and ATP synthase do assemble (Nina et al, 2011, JBC).

Done

• Page 3, line 80: "Irrespective of the shape of an organism's cristae, the crista junctions have been described as tubular channels that connect the cristae membrane to the inner boundary membrane (22, 24)." This omits the slit-shaped cristae junctions found in yeast (Davies et al, 2011, PNAS), which the authors should include.

The paper and concept have been added to the manuscript, though the sentence has been moved up in the introduction, when crista junctions are first introduced.

• Line 97: "poorly predicted N-terminal extension", as there is no experimental structure, we don't know if the prediction is poor. Presumably the authors mean either poorly ordered or the absence of secondary structure elements, or the poor confidence score for that region in the prediction? This should be clarified or corrected.

We were referring to the poor confidence score. To address this comment as well as major point 2, we rewrote the respective paragraph. It now clearly states that confidence of the prediction is low, and we mention the tool that was used to identify conserved domains (Topology-based Evolutionary Domains).

• Line 98: "an antiparallel array of ten β-sheets". They are actually two parallel beta-sheets stacked together. The authors could find out the name of this fold, but the confidence of the prediction is marked a low/very low. So, its existence is unknown, not just its "function".

We adapted the domain description to "a stack of two parallel beta-sheets" and replaced the statement on unknown function by the statement "Because this domain is predicted solely from computational analysis, both its actual existence in the native protein and its biological function remain unknown."

Fig 1B: The authors show two alphafold predictions of S. cerevisiae and P. falciparum Mic60 structures. There is however an experimental Mic60/19 (fragment) structure from the former organism (PMID: 36044574), which should be included if possible

We appreciate the reviewer's suggestion and note that the available structural data indeed provides valuable insight into how MIC60 and MIC19 interact. However, these structures represent fusion constructs of limited protein fragments and therefore capture only a small portion of each protein, specifically the interaction interface. Because our aim in Fig. 1B is to compare the overall domain architecture of the full‑length proteins, we believe that including fragment‑based structures would be less informative in this context.

Line: 318-321: "The same trend was observed for PfMIC19 and PfMIC60. Although transcriptomic data suggested that low-level transcripts of PfMIC19 and PfMIC60 are present in ABS (38), we did not detect either of the proteins in ABS by western blot analysis. While this statement is true, the authors should comment on the sensitivity of the respective methods - how well was the antibody working in their hands and how do they interpret the absence of a WB band compared to transcriptomics data?

The HA antibody used in our experiments is a standard commercial reagent that performs reliably in both WB and IFA, although it shows a low background signal in gametocytes. We agree that the sensitivity of the method and the interpretation of weak or absent bands should be addressed explicitly. Transcript levels for both PfMIC19 and PfMIC60 in asexual blood stages fall within the

• Lines 322-323: would the authors not typically have expected an IFA signal given the strength of the band in Western blot? If possible, the authors should comment if the negative fluorescence outcome can indeed be explained with the low abundance or if technical challenges are an equally good explanation.

Considering the nature of the investigated proteins (embedded in the IMM and spread throughout the mitochondria) difficulties in achieving a clear signal in IFA or U-ExM are not very surprizing. While epitopes may remain buried in IFA, U-ExM usually increases accessibility for the antibodies. However, U-ExM comes at the cost of being prone to dotty background signals, therefore potentially hiding low abundance, naturally dotty signals such as the signal of MICOS proteins that localize to distinct foci (at the CJ) along the mitochondrion. Current literature suggests that, in both human and yeast, STED is the preferred method for accurate spatial resolution of MICOS proteins (https://www.ncbi.nlm.nih.gov/pubmed/32567732,https://www.ncbi.nlm.nih.gov/pubmed/32067344). Unfortunately, we do not have experience with, nor access to, this particular technique/method.

Lines 357-365: the authors describe limitations of the applied methods adequately. Perhaps it would be helpful to make a similar statement about the analysis of 3D objects like mitochondria and cristae from 2D sections. E.g. the apparent cristae length depends on whether cristae are straight (e.g. coiled structures do not display long cross sections despite their true length in 3D).

The limitations of other methods are described in the respective results section.

We added a clarifying sentence in the results section of Figure 4:

"Note that such measurements do not indicate the true total length or width of cristae, as the data is two-dimensional. The recorded values are to be considered indicative of possible trends, rather than absolute dimensions of cristae."

This statement refers to the length/width measurements of cristae.

In the context of Figure 4 D we mention the following (see preprint lines 229 - 230): "We expect this effect to translate into the third dimension and thus conclude that the mean crista volume increases with the loss of either PfMIC19,PfMIC60, or both."

For Figure 5, we included a clarifying statement in the results section of the preprint (lines 269 - 273): "Note that these mitochondrial volumes are not full mitochondria, but large segments thereof. As a result of the incompleteness of the mitochondria within the section, and the tomography specific artefact of the missing wedge, we were unable to confirm whether cristae were in fact fully detached from the boundary membrane, or just too long to fit within the observable z-range. "

Line 404: perhaps undetected or similar would be a better description than "hidden"?

The sentence does not exist in the revised manuscript

Reviewer #3 (Significance (Required)):

The main strength of the study is that it provides the first characterisation of the MICOS complex in P. falciparum, a human parasite in which the mitochondrion has been shown to be a drug target. Mic60 and the newly annotated Mic19 are confirmed to be essential for proper cristae formation and morphology, as well as overall mitochondrial morphology. Furthermore, the mutant lines are characterised for their ability to complete the parasite life cycle and defects in infection effectivity are observed. This work is an important first step for deciphering the role of MICOS in the malaria parasite and the composition and function of this complex in this organism. The limitation of the study stems from what is already known about MICOS and its subunits in

great detail in yeast and humans with similar findings regarding loss of cristae and cristae defects. The findings of this study do not provide dramatic new insight on MICOS function or go substantially beyond the vast existing literature in terms of the extent of the study, which focuses on parasitological assays and morphological analysis. Exploring the role of MICOS in an early-divergent organism and human parasite is however important given the divergence found in mitochondrial biology and P. falciparum is a uniquely suited model system. One aspect that would increase the impact of the paper would be if the authors could mechanistically link the observed morphological defects to the decreased infection efficiency, e.g. by probing effects on mitochondrial function. This will likely be challenging as the morphological defects are diverse and the fitness defects appear moderate/mild.

As suggested by Reviewer 2, we examined mitochondrial membrane potential in gametocytes using MitoTracker staining and did not observe any obvious differences associated with the morphological defects. At present, additional assays to probe mitochondrial function in P. falciparum gametocytes are not sufficiently established, and developing and validating such methods would require substantial work before they could be applied to our mutant lines. For these reasons, a more detailed mechanistic link between the observed morphological changes and the reduced infection efficiency is currently beyond reach.

The advance presented in this study is to pioneer the study of MICOS in P. falciparum, thus widening our understanding of the role of this complex to different model organism. This study will likely be mainly of interest for specialised audiences such as basic research parasitologists and mitochondrial biologists. My own field of expertise is mitochondrial biology and structural biology.

Author response:

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

Reviewer #1 (Public review):

(1) I have to admit that it took a few hours of intense work to understand this paper and to even figure out where the authors were coming from. The problem setting, nomenclature, and simulation methods presented in this paper do not conform to the notation common in the field, are often contradictory, and are usually hard to understand. Most importantly, the problem that the paper is trying to solve seems to me to be quite specific to the particular memory study in question, and is very different from the normal setting of model-comparative RSA that I (and I think other readers) may be more familiar with.

We have revised the paper for clarity at all levels: motivation, application, and parameterization. We clarify that there is a large unmet need for using RSA in a trial-wise manner, and that this approach indeed offers benefits to any team interested in decoding trial-wise representational information linked to a behavioral responses, and as such is not a problem specific to a single memory study.

(2) The definition of "classical RSA" that the authors are using is very narrow. The group around Niko Kriegeskorte has developed RSA over the last 10 years, addressing many of the perceived limitations of the technique. For example, cross-validated distance measures (Walther et al. 2016; Nili et al. 2014; Diedrichsen et al. 2021) effectively deal with an uneven number of trials per condition and unequal amounts of measurement noise across trials. Different RDM comparators (Diedrichsen et al. 2021) and statistical methods for generalization across stimuli (Schütt et al. 2023) have been developed, addressing shortcomings in sensitivity. Finally, both a Bayesian variant of RSA (Pattern component modelling, (Diedrichsen, Yokoi, and Arbuckle 2018) and an encoding model (Naselaris et al. 2011) can effectively deal with continuous variables or features across time points or trials in a framework that is very related to RSA (Diedrichsen and Kriegeskorte 2017). The author may not consider these newer developments to be classical, but they are in common use and certainly provide the solution to the problems raised in this paper in the setting of model-comparative RSA in which there is more than one repetition per stimulus.

We appreciate the summary of relevant literature and have included a revised Introduction to address this bounty of relevant work. While much is owed to these authors, new developments from a diverse array of researchers outside of a single group can aid in new research questions, and should always have a place in our research landscape. We owe much to the work of Kriegeskorte’s group, and in fact, Schutt et al., 2023 served as a very relevant touchpoint in the Discussion and helped to highlight specific needs not addressed by the assessment of the “representational geometry” of an entire presented stimulus set. Principal amongst these needs is the application of trial-wise representational information that can be related to trial-wise behavioral responses and thus used to address specific questions on brain-behavior relationships. We invite the Reviewer to consider the utility of this shift with the following revisions to the Introduction.

Page 3. “Recently, methodological advancements have addressed many known limitations in cRSA. For example, cross-validated distance measures (e.g., Euclidean distance) have improved the reliability of representational dissimilarities in the presence of noise and trial imbalance (Walther et al., 2016; Nili et al., 2014; Diedrichsen et al., 2021). Bayesian approaches such as pattern component modeling (Diedrichsen, Yokoi, & Arbuckle, 2018) have extended representational approaches to accommodate continuous stimulus features or temporal variation. Further, model comparison RSA strategies (Diedrichsen et al., 2021) and generalization techniques across stimuli (Schütt et al., 2023) have improved sensitivity and inference. Nevertheless, a common feature shared across most of improvements is that they require stimuli repetition to examine the representational structure. This requirement limits their ability to probe brain-behavior questions at the level of individual events”.

Page 8. “While several extensions of RSA have addressed key limitations in noise sensitivity, stimulus variance, and modeling (e.g., Diedrichsen et al., 2021; Schütt et al., 2023), our tRSA approach introduces a new methodological step by estimating representational strength at the trial level. This accounts for the multi-level variance structure in the data, affords generalizability beyond the fixed stimulus set, and allows one to test stimulus- or trial-level modulations of neural representations in a straightforward way”.

Page 44. “Despite such prevalent appreciation for the neurocognitive relevance of stimulus properties, cRSA often does not account for the fact that the same stimulus (e.g., “basketball”) is seen by multiple subjects and produces statistically dependent data, an issue addressed by Schütt et al., 2023, who developed cross validation and bootstrap methods that explicitly model dependence across both subjects and stimulus conditions”.

(3) The stated problem of the paper is to estimate "representational strength" in different regions or conditions. With this, the authors define the correlation of the brain RDM with a model RDM. This metric conflates a number of factors, namely the variances of the stimulus-specific patterns, the variance of the noise, the true differences between different dissimilarities, and the match between the assumed model and the data-generating model. It took me a long time to figure out that the authors are trying to solve a quite different problem in a quite different setting from the model-comparative approach to RSA that I would consider "classical" (Diedrichsen et al. 2021; Diedrichsen and Kriegeskorte 2017). In this approach, one is trying to test whether local activity patterns are better explained by representation model A or model B, and to estimate the degree to which the representation can be fully explained. In this framework, it is common practice to measure each stimulus at least 2 times, to be able to estimate the variance of noise patterns and the variance of signal patterns directly. Using this setting, I would define 'representational strength" very differently from the authors. Assume (using LaTeX notation) that the activity patterns $y_j,n$ for stimulus j, measurement n, are composed of a true stimulus-related pattern ($u_j$) and a trial-specific noise pattern ($e_j,n$). As a measure of the strength of representation (or pattern), I would use an unbiased estimate of the variance of the true stimulus-specific patterns across voxels and stimuli ($\sigma^2_{u}$). This estimator can be obtained by correlating patterns of the same stimuli across repeated measures, or equivalently, by averaging the cross-validated Euclidean distances (or with spatial prewhitening, Mahalanobis distances) across all stimulus pairs. In contrast, the current paper addresses a specific problem in a quite specific experimental design in which there is only one repetition per stimulus. This means that the authors have no direct way of distinguishing true stimulus patterns from noise processes. The trick that the authors apply here is to assume that the brain data comes from the assumed model RDM (a somewhat sketchy assumption IMO) and that everything that reduces this correlation must be measurement noise. I can now see why tRSA does make some sense for this particular question in this memory study. However, in the more common model-comparative RSA setting, having only one repetition per stimulus in the experiment would be quite a fatal design flaw. Thus, the paper would do better if the authors could spell the specific problem addressed by their method right in the beginning, rather than trying to set up tRSA as a general alternative to "classical RSA".

At a general level, our approach rests on the premise that there is meaningful information present in a single presentation of a given stimulus. This assumption may have less utility when the research goals are more focused on estimating the fidelity of signal patterns for RSA, as in designs with multiple repetitions. But it is an exaggeration to state that such a trial-wise approach cannot address the difference between “true” stimulus patterns and noise. This trial-wise approach has explicit utility in relating trial-wise brain information to trial-wise behavior, across multiple cognitions (not only memory studies, as applied here). We have added substantial text to the Introduction distinguishing cRSA, which is widely employed, often in cases with a single repetition per stimulus, and model comparative methods that employ multiple repetitions. We clarify that we do not consider tRSA an alternative to the model comparative approach, and discuss that operational definitions of representational strength are constrained by the study design.

Page 3. “In this paper, we present an advancement termed trial-level RSA, or tRSA, which addresses these limitations in cRSA (not model comparison approaches) and may be utilized in paradigms with or without repeated stimuli”.

Page 4. “Representational geometry usually refers to the structure of similarities among repeated presentations of the same stimulus in the neural data (as captured in the brain RSM) and is often estimated utilizing a model comparison approach, whereas representational strength is a derived measure that quantifies how strongly this geometry aligns with a hypothesized model RSM. In other words, geometry characterizes the pattern space itself, while representational strength reflects the degree of correspondence between that space and the theoretical model under test”.

Finally, we clarified that in our simulation methods we assume a true underlying activity pattern and a random error pattern. The model RSM is computed based on the true pattern, whereas the brain RSM comes from the noisy pattern, not the model RSM itself.

Page 9. “Then, we generated two sets of noise patterns, which were controlled by parameters σ_A and σ_B , respectively, one for each condition”.

(4) The notation in the paper is often conflicting and should be clarified. The actual true and measured activity patterns should receive a unique notation that is distinct from the variances of these patterns across voxels. I assume that $\sigma_ijk$ is the noise variances (not standard deviation)? Normally, variances are denoted with $\sigma^2$. Also, if these are variances, they cannot come from a normal distribution as indicated on page 10. Finally, multi-level models are usually defined at the level of means (i.e., patterns) rather than at the level of variances (as they seem to be done here).

We have added notations for true and measured activity patterns to differentiate it from our notation for variance. We agree that multilevel models are usually defined at the level of means rather than at the level of variances and we include a Figure (Fig 1D) that describes the model in terms of the means. We clarify that the σ ($\sigma$) used in the manuscript were not variances/standard deviations themselves; rather, they were meant to denote components of the actual (multilevel) variance parameter. Each component was sampled from normal distributions, and they collectively summed up to comprise the final variance parameter for each trial. We have modified our notation for each component to the lowercase letter s to minimize confusion. We have also made our R code publicly available on our lab github, which should provide more clarity on the exact simulation process.

(5) In the first set of simulations, the authors sampled both model and brain RSM by drawing each cell (similarity) of the matrix from an independent bivariate normal distribution. As the authors note themselves, this way of producing RSMs violates the constraint that correlation matrices need to be positive semi-definite. Likely more seriously, it also ignores the fact that the different elements of the upper triangular part of a correlation matrix are not independent from each other (Diedrichsen et al. 2021). Therefore, it is not clear that this simulation is close enough to reality to provide any valuable insight and should be removed from the paper, along with the extensive discussion about why this simulation setting is plainly wrong (page 21). This would shorten and clarify the paper.

We have added justification of the mixed-effects model given the potential assumption violations. We caution readers to investigate the robustness of their models, and to employ permutation testing that does not make independence assumptions. We have also added checks of the model residuals and an example of permutation testing in the Appendix. Finally, we agree that the first simulation setting does not possess several properties of realistic RDMs/RSMs; however, we believe that there is utility in understanding the mathematical properties of correlations – an essential component of RSA – in a straightforward simulation where the ground truth is known, thus moving the simulation to Appendix 1.

(6) If I understand the second simulation setting correctly, the true pattern for each stimulus was generated as an NxP matrix of i.i.d. standard normal variables. Thus, there is no condition-specific pattern at all, only condition-specific noise/signal variances. It is not clear how the tRSA would be biased if there were a condition-specific pattern (which, in reality, there usually is). Because of the i.i.d. assumption of the true signal, the correlations between all stimulus pairs within conditions are close to zero (and only differ from it by the fact that you are using a finite number of voxels). If you added a condition-specific pattern, the across-condition RSA would lead to much higher "representational strength" estimates than a within-condition RSA, with obvious problems and biases.

The Reviewer is correct that the voxel values in the true pattern are drawn from i.i.d. standard normal distributions. We take the Reviewer’s suggestion of “condition-specific pattern” to mean that there could be a condition-voxel interaction in two non-mutually exclusive ways. The first is additive, essentially some common underlying multi-voxel pattern like [6, 34, -52, …, 8] for all condition A trials, and different one such pattern for condition B trials, etc. The second is multiplicative, essentially a vector of scaling factors [x1.5, x0.5, x0.8, …, x2.7] for all condition A trials, and a different one such vector for condition B trials, etc. Both possibilities could indeed affect tRSA as much as it would cRSA.

Importantly, If such a strong condition-specific pattern is expected, one can build a condition-specific model RDM using one-shot coding of conditions (see example figure; src: https://www.newbi4fmri.com/tutorial-9-mvpa-rsa), to either capture this interesting phenomenon or to remove this out as a confounding factor. This practice has been applied in multiple regression cRSA approaches (e.g., Cichy et al., 2013) and can also be applied to tRSA.

(7) The trial-level brain RDM to model Spearman correlations was analyzed using a mixed effects model. However, given the symmetry of the RDM, the correlations coming from different rows of the matrix are not independent, which is an assumption of the mixed effect model. This does not seem to induce an increase in Type I errors in the conditions studied, but there is no clear justification for this procedure, which needs to be justified.

We appreciate this important warning, and now caution readers to investigate the robustness of their models, and consider employing permutation testing that does not make independence assumptions. We have also added checks of the model residuals and an example of permutation testing in the supplement.

Page 46. “While linear mixed-effects modeling offers a powerful framework for analyzing representational similarity data, it is critical that researchers carefully construct and validate their models. The multilevel structure of RSA data introduces potential dependencies across subjects, stimuli, and trials, which can violate assumptions of independence if not properly modeled. In the present study, we used a model that included random intercepts for both subjects and stimuli, which accounts for variance at these levels and improves the generalizability of fixed-effect estimates. Still, there is a potential for systematic dependence across trials within a subject. To ensure that the model assumptions were satisfied, we conducted a series of diagnostic checks on an exemplar ROI (right LOC; middle occipital gyrus) in the Object Perception dataset, including visual inspection of residual distributions and autocorrelation (Appendix 3, Figure 13). These diagnostics supported the assumptions of normality, homoscedasticity, and conditional independence of residuals. In addition, we conducted permutation-based inference, similar to prior improvements to cRSA (Niliet al. 2014), using a nested model comparison to test whether the mean similarity in this ROI was significantly greater than zero. The observed likelihood ratio test statistic fell in the extreme tail of the null distribution (Appendix 3, Figure 14), providing strong nonparametric evidence for the reliability of the observed effect. We emphasize that this type of model checking and permutation testing is not merely confirmatory but can help validate key assumptions in RSA modeling, especially when applying mixed-effects models to neural similarity data. Researchers are encouraged to adopt similar procedures to ensure the robustness and interpretability of their findings”.

Exemplar Permutation Testing

To test whether the mean representational strength in the ROI right LOC (middle occipital gyrus) was significantly greater than zero, we used a permutation-based likelihood ratio test implemented via the permlmer function. This test compares two nested linear mixed-effects models fit using the lmer function from the lme4 package, both including random intercepts for Participant and Stimulus ID to account for between-subject and between-item variability.

The null model excluded a fixed intercept term, effectively constraining the mean similarity to zero after accounting for random effects:

ROI ~ 0 + (1 | Participant) + (1 | Stimulus)

The full model included the same random effects structure but allowed the intercept to be freely estimated:

ROI ~ 1 + (1 | Participant) + (1 | Stimulus)

By comparing the fit of these two models, we directly tested whether the average similarity in this ROI was significantly different from zero. Permutation testing (1,000 permutations) was used to generate a nonparametric p-value, providing inference without relying on normality assumptions. The full model, which estimated a nonzero mean similarity in the right LOC (middle occipital gyrus), showed a significantly better fit to the data than the null model that fixed the mean at zero (χ²(1) = 17.60, p = 2.72 × 10⁻⁵). The permutation-based p-value obtained from permlmer confirmed this effect as statistically significant (p = 0.0099), indicating that the mean similarity in this ROI was reliably greater than zero. These results support the conclusion that the right LOC contains representational structure consistent with the HMAXc2 RSM. A density plot of the permuted likelihood ratio tests is plotted along with the observed likelihood ratio test in Appendix 3 Figure 14.

(8) For the empirical data, it is not clear to me to what degree the "representational strength" of cRSA and tRSA is actually comparable. In cRSA, the Spearman correlation assesses whether the distances in the data RSM are ranked in the same order as in the model. For tRSA, the comparison is made for every row of the RSM, which introduces a larger degree of flexibility (possibly explaining the higher correlations in the first simulation). Thus, could the gains presented in Figure 7D not simply arise from the fact that you are testing different questions? A clearer theoretical analysis of the difference between the average row-wise Spearman correlation and the matrix-wise Spearman correlation is urgently needed. The behavior will likely vary with the structure of the true model RDM/RSM.

We agree that the comparability between mean row-wise Spearman correlations and the matrix-wise Spearman correlation is needed. We believe that the simulations are the best approach for this comparison, since they are much more robust than the empirical dataset and have the advantage of knowing the true pattern/noise levels. We expand on our comparison of mean tRSA values and matrix-wise Spearman correlations on page 42.

Page 42. “Although tRSA and cRSA both aim to quantify representational strength, they differ in how they operationalize this concept. cRSA summarizes the correspondence between RSMs as a single measure, such as the matrix-wise Spearman correlation. In contrast, tRSA computes such correspondence for each trial, enabling estimates at the level of individual observations. This flexibility allows trial-level variability to be modeled directly, but also introduces subtle differences in what is being measured. Nonetheless, our simulations showed that, although numerical differences occasionally emerged—particularly when comparing between-condition tRSA estimates to within-condition cRSA estimates—the magnitude of divergence was small and did not affect the outcome of downstream statistical tests”.

(9) For the real data, there are a number of additional sources of bias that need to be considered for the analysis. What if there are not only condition-specific differences in noise variance, but also a condition-specific pattern? Given that the stimuli were measured in 3 different imaging runs, you cannot assume that all measurement noise is i.i.d. - stimuli from the same run will likely have a higher correlation with each other.

We recognize the potential of condition-specific patterns and chose to constrain the analyses to those most comparable with cRSA. However, depending on their hypotheses, researchers may consider testing condition RSMs and utilizing a model comparison approach or employ the z-scored approach, as employed in the simulations above. Regarding the potential run confounds, this is always the case in RSA and why we exclude within-run comparisons. We have also added to the Discussion the suggestion to include run as a covariate in their mixed-effects models. However, we do not employ this covariate here as we preferred the most parsimonious model to compare with cRSA.

Page 46 - 47. “Further, while analyses here were largely employed to be comparable with cRSA, researchers should consider taking advantage of the flexibility of the mixed-effects models and include co variates of non-interest (run, trial order etc.)”.

(10) The discussion should be rewritten in light of the fact that the setting considered here is very different from the model-comparative RSA in which one usually has multiple measurements per stimulus per subject. In this setting, existing approaches such as RSA or PCM do indeed allow for the full modelling of differences in the "representational strength" - i.e., pattern variance across subjects, conditions, and stimuli.

We agree that studies advancing designs with multiple repetitions of a given stimulus image are useful in estimating the reliability of concept representations. We would argue however that model comparison in RSA is not restricted to such data. Many extant studies do not in fact have multiple repetitions per stimulus per subject (Wang et al., 2018 https://doi.org/10.1088/1741-2552/abecc3, Gao et al, 2022 https://doi.org/10.1093/cercor/bhac058, Li et al, 2022 https://doi.org/10.1002/hbm.26195, Staples & Graves, 2020 https://doi.org/10.1162/nol_a_00018) that allow for that type of model-comparative approach. While beneficial in terms of noise estimation, having multiple presentations was not a requirement for implementing cRSA (Kriegeskorte, 2008 https://doi.org/10.3389/neuro.06.004.2008). The aim of this manuscript is to introduce the tRSA approach to the broad community of researchers whose research questions and datasets could vary vastly, including but not limited to the number of repeated presentations and the balance of trial counts across conditions.

(11) Cross-validated distances provide a powerful tool to control for differences in measurement noise variances and possible covariances in measurement noise across trials, which has many distinct advantages and is conceptually very different from the approach taken here.

We have added language on the value of cross-validation approaches to RSA in the Discussion:

Page 47. “Additionally, we note that while our proposed tRSA framework provides a flexible and statistically principled approach for modeling trial-level representational strength, we acknowledge that there are alternative methods for addressing trial-level variability in RSA. In particular, the use of cross-validated distance metrics (e.g., crossnobis distance) has become increasingly popular for controlling differences in measurement noise variance and accounting for possible covariance structures across trials (Walther et al., 2016). These metrics offer several advantages, including unbiased estimation of representational dissimilarities under Gaussian noise assumptions and improved generalization to unseen data. However, cross-validated distances are conceptually distinct from the approach taken here: whereas cross-validation aims to correct for noise-related biases in representational dissimilarity matrices, our trial-level RSA method focuses on estimating and modeling the variability in representation strength across individual trials using mixed-effects modeling. Rather than proposing a replacement for cross-validated RSA, tRSA adds a complementary tool to the methodological toolkit—one that supports hypothesis-driven inference about condition effects and trial-level covariates, while leveraging the full structure of the data”.

(12) One of the main limitations of tRSA is the assumption that the model RDM is actually the true brain RDM, which may not be the case. Thus, in theory, there could be a different model RDM, in which representational strength measures would be very different. These differences should be explained more fully, hopefully leading to a more accessible paper.

Indeed, the chosen model RSM may not be the true RSM, but as the noise level increases the correlation between RSMs practically becomes zero. In our simulations we assume this to be true as a straightforward way to manipulate the correspondence between the brain data and the model. However, just like cRSA, tRSA is constrained by the model selections the researchers employ. We encourage researchers to have carefully considered theoretically-motivated models and, if their research questions require, consider multiple and potentially competing models. Furthermore, the trial-wise estimates produced by tRSA encourage testing competing models within the multiple regression framework. We have added this language to the Discussion.

Page 46. ..”choose their model RSMs carefully. In our simulations, we designed our model RSM to be the “true” RSM for demonstration purposes. However, researchers should consider if their models and model alternatives”.

Pages 45-46. “While a number of studies have addressed the validity of measuring representational geometry using designs with multiple repetitions, a conceptual benefit of the tRSA approach is the reliance on a regression framework that engenders the testing of competing conceptual models of stimulus representation (e.g., taxonomic vs. encyclopedic semantic features, as in Davis et al., 2021)”.

Reviewer #2 (Public review):

(1)  While I generally welcome the contribution, I take some issue with the accusatory tone of the manuscript in the Introduction. The text there (using words such as 'ignored variances', 'errouneous inferences', 'one must', 'not well-suited', 'misleading') appears aimed at turning cRSA in a 'straw man' with many limitations that other researchers have not recognized but that the new proposed method supposedly resolves. This can be written in a more nuanced, constructive manner without accusing the numerous users of this popular method of ignorance.

We apologize for the unintended accusatory tone. We have clarified the many robust approaches to RSA and have made our Introduction and Discussion more nuanced throughout (see also 3, 11 and16).

(2) The described limitations are also not entirely correct, in my view: for example, statistical inference in cRSA is not always done using classic parametric statistics such as t-tests (cf Figure 1): the rsatoolbox paper by Nili et al. (2014) outlines non-parametric alternatives based on permutation tests, bootstrapping and sign tests, which are commonly used in the field. Nor has RSA ever been conducted at the row/column level (here referred to by the authors as 'trial level'; cf King et al., 2018).

We agree there are numerous methods that go beyond cRSA addressing these limitations and have added discussion of them into our manuscript as well as an example analysis implementing permutation tests on tRSA data (see response to 7). We thank the reviewer for bringing King et al., 2014 and their temporal generalization method to our attention, we added reference to acknowledge their decoding-based temporal generalization approach.

Page 8. “It is also important to note that some prior work has examined similarly fine-grained representations in time-resolved neuroimaging data, such as the temporal generalization method introduced by King et al. (see King & Dehaene, 2014). Their approach trains classifiers at each time point and tests them across all others, resulting in a temporal generalization matrix that reflects decoding accuracy over time. While such matrices share some structural similarity with RSMs, they do not involve correlating trial-level pattern vectors with model RSMs nor do their second-level models include trial-wise, subject-wise, and item-wise variability simultaneously”.

(3) One of the advantages of cRSA is its simplicity. Adding linear mixed effects modeling to RSA introduces a host of additional 'analysis parameters' pertaining to the choice of the model setup (random effects, fixed effects, interactions, what error terms to use) - how should future users of tRSA navigate this?

We appreciate the opportunity to offer more specific proscriptions for those employing a tRSA technique, and have added them to the Discussion:

Page 46. “While linear mixed-effects modeling offers a powerful framework for analyzing representational similarity data, it is critical that researchers carefully construct and validate their models and choose their model RSMs carefully. In our simulations, we designed our model RSM to be the “true” RSM for demonstration purposes. However, researchers should consider if their models and model alternatives. However, researchers should always consider if their models match the goals of their analysis, including 1) constructing the random effects structure that will converge in their dataset and 2) testing their model fits against alternative structures (Meteyard & Davies, 2020; Park et al., 2020) and 3) considering which effects should be considered random or fixed depending on their research question”.

(4) Here, only a single real fMRI dataset is used with a quite complicated experimental design for the memory part; it's not clear if there is any benefit of using tRSA on a simpler real dataset. What's the benefit of tRSA in classic RSA datasets (e.g., Kriegeskorte et al., 2008), with fixed stimulus conditions and no behavior?

To clarify, our empirical approach uses two different tasks: an Object Perception task more akin to the classic RSA datasets employing passive viewing, and a Conceptual Retrieval task that more directly addresses the benefits of the trialwise approach. We felt that our Object Perception dataset is a simpler empirical fMRI dataset without explicit task conditions or a dichotomous behavioral outcome, whereas the Retrieval dataset is more involved (though old/new recognition is the most common form of memory retrieval testing) and  dependent on behavioral outcomes. However, we recognize the utility of replication from other research groups and do invite researchers to utilize tRSA on their datasets.

(5) The cells of an RDM/RSM reflect pairwise comparisons between response patterns (typically a brain but can be any system; cf Sucholutsky et al., 2023). Because the response patterns are repeatedly compared, the cells of this matrix are not independent of one another. Does this raise issues with the validity of the linear mixed effects model? Does it assume the observations are linearly independent?

We recognize the potential danger for not meeting model assumptions. Though our simulation results and model checks suggest this is not a fatal flaw in the model design, we caution readers to investigate the robustness of their models, and consider employing permutation testing that does not make independence assumptions. We have also added checks of the model residuals and an example of permutation testing in the Appendix. See response to R1.

(6) The manuscript assumes the reader is familiar with technical statistical terms such as Type I/II error, sensitivity, specificity, homoscedasticity assumptions, as well as linear mixed models (fixed effects, random effects, etc). I am concerned that this jargon makes the paper difficult to understand for a broad readership or even researchers currently using cRSA that might be interested in trying tRSA.

We agree this jargon may cause the paper to be difficult to understand. We have expanded/added definitions to these terms throughout the methods and results sections.

Page 12. “Given data generated with 𝑠_{𝑐𝑜𝑛𝑑,𝐴} = 𝑠_{𝑐𝑜𝑛𝑑,B}, the correct inference should be a failure to reject the null hypothesis of ; any significant () result in either direction was considered a false positive (spurious effect, or Type I error). Given data generated with , the inference was considered correct if it rejected the null hypothesis of  and yielded the expected sign of the estimated contrast (b_B-𝐴<0). A significant result with the reverse sign of the estimated contrast (b_B-𝐴<0) was considered a Type I error, and a nonsignificant (𝑝 ≥ 0.05) result was considered a false negative (failure to detect a true effect, or Type II error)”.

Page 2. “Compared to cRSA, the multi-level framework of tRSA was both more theoretically appropriate and significantly sensitive (better able to detect) to true effects”.

Page 25.”The performance of cRSA and tRSA were quantified with their specificity (better avoids false positives, 1 - Type I error rate) and sensitivity (better avoids false negatives 1 - Type II error rate)”.

Page 6. “One of the fundamental assumptions of general linear models (step 4 of cRSA; see Figure 1D) is homoscedasticity or homogeneity of variance — that is, all residuals should have equal variance” .

Page11. “Specifically, a linear mixed-effects model with a fixed effect  of condition (which estimates the average effect across the entire sample, capturing the overall effect of interest) and random effects of both subjects and stimuli (which model variation in responses due to differences between individual subjects and items, allowing generalization beyond the sample) were fitted to tRSA estimates via the `lme4 1.1-35.3` package in R (Bates et al., 2015), and p-values were estimated using Satterthwaites’s method via the `lmerTest 3.1-3` package (Kuznetsova et al., 2017)”.

(7) I could not find any statement on data availability or code availability. Given that the manuscript reuses prior data and proposes a new method, making data and code/tutorials openly available would greatly enhance the potential impact and utility for the community.

We thank the reviewer for raising our oversight here. We have added our code and data availability statements.

Page 9. “Data is available upon request to the corresponding author and our simulations and example tRSA code is available at https://github.com/electricdinolab”.

Reviewer #1 (Recommendations for the authors):

(13) Page 4: The limitations of cRSA seem to be based on the assumption that within each different experimental condition, there are different stimuli, which get combined into the condition. The framework of RSA, however, does not dictate whether you calculate a condition x condition RDM or a larger and more complete stimulus x stimulus RDM. Indeed, in practice we often do the latter? Or are you assuming that each stimulus is only shown once overall? It would be useful at this point to spell out these implicit assumptions.

We agree that stimulus x stimulus RDMs can be constructed and are often used. However, as we mentioned in the Introduction, researchers are often interested in the difference between two (or more) conditions, such as “remembered” vs. “forgotten” (Davis et al., https://doi.org/10.1093/cercor/bhaa269) or “high cognitive load” vs. “low cognitive load” (Beynel et al., https://doi.org/10.1523/JNEUROSCI.0531-20.2020). In those cases, the most common practice with cRSA is to construct condition-specific RDMs, compute cRSA scores separately for each condition, and then compare the scores at the group level. The number of times each stimulus gets presented does not prevent one from creating a model RDM that has the same rows and columns as the brain RDM, either in the same condition (“high load”) or across different conditions.

(14) Page 5: The difference between condition-level and stimulus-level is not clear. Indeed, this definition seems to be a function of the exact experimental design and is certainly up for interpretation. For example, if I conduct a study looking at the activity patterns for 4 different hand actions, each repeated multiple times, are these actions considered stimuli or conditions?

We have added clarifying language about what is considered stimuli vs conditions. Indeed, this will depend on the specific research questions being employed and will affect how researchers construct their models. In this specific example, one would most likely consider each different hand action a condition, treating them as fixed effects rather than random effects, given their very limited number and the lack of need to generalize findings to the broader “hand actions” category.

Page 5. “Critically, the distinction between condition-level and stimulus level is not always clear as researchers may manipulate stimulus-level features themselves. In these cases, what researchers ultimately consider condition-level and stimulus-level will depend on their specific research questions. For example, researchers intending to study generalized object representation may consider object category a stimulus-level feature, while researchers interested in if/how object representation varies by category may consider the same category variable condition-level”.

(15) Page 5: The fact that different numbers of trials / different levels of measurement noise / noise-covariance of different conditions biases non-cross-validated distances is well known and repeatedly expressed in the literature. We have shown that cross-validation of distances effectively removes such biases - of course, it does not remove the increased estimation variability of these distances (for a formal analysis of estimation noise on condition patterns and variance of the cross-nobis estimator, see (Diedrichsen et al. 2021)).

We thank the reviewer for drawing our attention to this literature and have added discussions of these methods.

(16). Page 5: "Most studies present subjects with a fixed set of stimuli, which are supposedly samples representative of some broader category". This may be the case for a certain type of RSA experiments in the visual domain, but it would be unfair to say that this is a feature of RSA studies in general. In most studies I have been involved in, we use a "stimulus" x "stimulus" RDM.

We have edited this sentence to avoid the “most” characterization. We also added substantial text to the introduction and discussion distinguishing cRSA, which is nonetheless widely employed, especially in cases with a single repetition per stimulus (Macklin et al., 2023, Liu et al, 2024) and the model comparative method and explicitly stating that we do not consider tRSA an alternative to the model comparative approach.

(17). Page 5: I agree that "stimuli" should ideally be considered a random effect if "stimuli" can be thought of as sampled from a larger population and one wants to make inferences about that larger population. Sometimes stimuli/conditions are more appropriately considered a fixed effect (for example, when studying the response to stimulation of the 5 fingers of the right hand). Techniques to consider stimuli/conditions as a random effect have been published by the group of Niko Kriegeskorte (Schütt et al. 2023).

Indeed, in some cases what may be thought of as “stimuli” would be more appropriately entered into the model as a fixed effect; such questions are increasingly relevant given the focus on item-wise stimulus properties (Bainbridge et al., Westfall & Yarkoni). We have added text on this issue to the Discussion and caution researchers to employ models that most directly answer their research questions.

Page 46. “However, researchers should always consider if their models match the goals of their analysis, including 1) constructing the random effects structure that will converge in their dataset and 2) testing their model fits against alternative structures (Meteyard & Davies, 2020; Park et al., 2020) and 3) considering which effects should be considered random or fixed depending on their research question. An effect is fixed when the levels represent the specific conditions of theoretical interest (e.g., task condition) and the goal is to estimate and interpret those differences directly. In contrast, an effect is random when the levels are sampled from a broader population (e.g., subjects) and the goal is to account for their variability while generalizing beyond the sample tested. Note that the same variable (e.g., stimuli) may be considered fixed or random depending on the research questions”.

(18) Page 6: It is correct that the "classical" RSA depends on a categorical assignment of different trials to different stimuli/conditions, such that a stimulus x stimulus RDM can be computed. However, both Pattern Component Modelling (PCM) and Encoding models are ideally set up to deal with variables that vary continuously on a trial-by-trial or moment-by-moment basis. tRSA should be compared to these approaches, or - as it should be clarified - that the problem setting is actually quite a different one.

We agree that PCM and encoding models offer a flexible approach and handle continuous trial-by-trial variables. We have clarified the problem setting in cRSA is distinct on page 6, and we have added the robustness of encoding models and their limitations to the Discussion.

Page 6. “While other approaches such as Pattern Component Modeling (PCM) (Diedrichsen et al., 2018) and encoding models (Naselaris et al., 2011) are well-suited to analyzing variables that vary continuously on a trial-by-trial or moment-by-moment basis, these frameworks address different inferential goals. Specifically, PCM and encoding models focus on estimating variance components or predicting activation from features, while cRSA is designed to evaluate representational geometry. Thus, cRSA as well as our proposed approach address a problem setting distinct from PCM and encoding models”.

(19) Page 8: "Then, we generated two noise patterns, which were controlled by parameters 𝜎 𝐴 and 𝜎𝐵, respectively, one for each condition." This makes little sense to me. The noise patterns should be unique to each trial - you should generate n_a + n_b noise patterns, no?

We clarify that the “noise patterns” here are n_voxel x n_trial in size; in other words, all trial-level noise patterns are generated together and each trial has their own unique noise pattern. We have revised our description as “two sets of noise patterns” for clarity starting on page 9.

(20) Page 9: First, I assume if this is supposed to be a hierarchical level model, the "noise parameters" here correspond to variances? Or do these \sigma values mean to signify standard deviations? The latter would make little sense. Or is it the noise pattern itself?

As clarified in 4., the σ values are meant to denote hierarchical components of the composite standard deviation; we have updated our notation to use lower case letter s instead for clarity.

(21) Page 10: your formula states "𝜎_{𝑠𝑢𝑏𝑗}~ 𝙽(0, 0.5^2)". This conflicts with your previous mention that \sigmas are noise "levels" are they the noise patterns themselves now? Variances cannot be normally distributed, as they cannot be negative.

As clarified in 4., the σ values are meant to denote hierarchical components of the composite standard deviation; we have updated our notation to use lower case letter s instead for clarity.

(22) Page 13: What was the task of the subject in the Memory retrieval task? Old/new judgements relative to encoding of object perception?

We apologize for the lack of clarity about the Memory Retrieval task and have added that information and clarified that the old/new judgements were relative to a separate encoding phase, the brain data for which has been reported elsewhere.

Page 14. “Memory Retrieval took place one day after Memory Encoding and involved testing participants’ memory of the objects seen in the Encoding phase. Neural data during the Encoding phase has been reported elsewhere. In the main Memory Retrieval task, participants were presented with 144 labels of real-world objects, of which 114 were labels for previously seen objects and 30 were unrelated novel distractors. Participants performed old/new judgements, as well as their confidence in those judgements on a four-point scale (1 = Definitely New, 2 = Probably New, 3 = Probably Old, 4 = Definitely Old)”.

(23) Page 13: If "Memory Retrieval consisted of three scanning runs", then some of the stimulus x stimulus correlations for the RSM must have been calculated within a run and some between runs, correct? Given that all within-run estimates share a common baseline, they share some dependence. Was there a systematic difference between the within-run and the between-run correlations?

We have clarified in this portion of the methods that within run comparisons were excluded from our analyses. We also double-checked that the within-run exclusion was included in the description of the Neural RSMs.

Page 14. “Retrieval consisted of three scanning runs, each with 38 trials, lasting approximately 9 minutes and 12 seconds (within-run comparisons were later excluded from RSA analyses)”.

Page 18. “This was done by vectorizing the voxel-level activation values within each region and calculating their correlations using Pearson’s r, excluding all within-run comparisons.”

(24) Page 20: It is not clear why the mean estimate of "representational strength" (i.e., model-brain RSM correlations) is important at all. This comes back to Major point #2, namely that you are trying to solve a very different problem from model-comparative RSA.

We have clarified that our approach is not an alternative to model-comparative RSA, and that depending on the task constraints researchers may choose to compare models with tRSA or other approaches requiring stimulus repetition (see 3).

(25) Page 21: I believe the problems of simulating correlation matrices directly in the way that the authors in their first simulation did should be well known and should be moved to an appendix at best. Better yet, the authors could start with the correct simulation right away.

We agree the paper is more concise with these simulations being moved to the appendix and more briefly discussed. We have implemented these changes (Appendix 1). However, we are not certain that this problem is unknown, and have several anecdotes of researchers inquiring about this “alternative” approach in talks with colleagues, thus we do still discuss the issues with this method.

(26) Page 26: Is the "underlying continuous noise variable 𝜎𝑡𝑟𝑖𝑎𝑙 that was measured by 𝑣𝑚𝑒𝑎𝑠𝑢𝑟𝑒𝑑 " the variance of the noise pattern or the noise pattern itself? What does it mean it was "measured" - how?

𝜎𝑡𝑟𝑖𝑎𝑙 is a vector of standard deviations for different trials, and 𝜎𝑡𝑟𝑖𝑎𝑙 i would be used to generate the noise patterns for trial i. v_measured is a hypothetical measurement of trial-level variability, such as “memorability” or “heartbeat variability”. We have revised our description to clarify our methods.

Reviewer #2 (Recommendations for the authors):

(8) It would be helpful to provide more clarity earlier on in the manuscript on what is a 'trial': in my experience, a row or column of the RDM is usually referred to as 'stimulus condition', which is typically estimated on multiple trials (instances or repeats) of that stimulus condition (or exemplars from that stimulus class) being presented to the subject. Here, a 'trial' is both one measurement (i.e., single, individual presentation of a stimulus) and also an entry in the RDM, but is this the most typical scenario for cRSA? There is a section in the Discussion that discusses repetitions, but I would welcome more clarity on this from the get-go.

We have added discussion of stimulus repetition methods and datasets to the Introduction and clarified our use of the terms.

Page 8. “Critically, in single-presentation designs, a “trial” refers to one stimulus presentation, and corresponds to a row or column in the RSM. In studies with repeated stimuli, these rows are often called “conditions” and may reflect aggregated patterns across trials. tRSA is compatible with both cases: whether rows represent individual trials or averaged trials that create “conditions”, tRSA estimates are computed at the row level”.

(9) The quality of the results figures can be improved. For example, axes labels are hard to read in Figure 3A/B, panels 3C/D are hard to read in general. In Figure 7E, it's not possible to identify the 'dark red' brain regions in addition to the light red ones.

We thank the reviewer for raising these and have edited the figures to be more readable in the manner suggested.

(10) I would be interested to see a comparison between tRSA and cRSA in other fMRI (or other modality) datasets that have been extensively reported in the literature. These could be the original Kriegeskorte 96 stimulus monkey/fMRI datasets, commonly used open datasets in visual perception (e.g., THINGS, NSD), or the above-mentioned King et al. dataset, which has been analyzed in various papers.

We recognize the great utility of replication from other research groups and do invite researchers to utilize tRSA on their datasets.

(11) On P39, the authors suggest 'researchers can confidently replace their existing cRSA analysis with tRSA': Please discuss/comment on how researchers should navigate the choice of modeling parameters in tRSA's linear mixed effects setting.

We have added discussion of the mixed-effects parameters and the various and encourage researchers to follow best practices for their model selection.

Page 46. “However, researchers should always consider if their models match the goals of their analysis, including 1) constructing the random effects structure that will converge in their dataset and 2) testing their model fits against alternative structures (Meteyard & Davies, 2020; Park et al., 2020) and 3) considering which effects should be considered random or fixed depending on their research question”.

(12) The final part of the Results section, demonstrating the tRSA results for the continuous memorability factor in the real fMRI data, could benefit from some substantiation/elaboration. It wasn't clear to me, for example, to what extent the observed significant association between representational strength and item memorability in this dataset is to be 'believed'; the Discussion section (p38). Was there any evidence in the original paper for this association? Or do we just assume this is likely true in the brain, based on prior literature by e.g. Bainbridge et al (who probably did not use tRSA but rather classic methods)?

Indeed, memorability effects have been replicated in the literature, but not using the tRSA method. We have expanded our discussion to clarify the relationship of our findings and the relevant literature and methods it has employed.

Page 38. “Critically, memorability is a robust stimulus property that is consistent across participants and paradigms (Bainbridge, 2022). Moreover, object memorability effects have been replicated using a variety of methods aside from tRSA, including univariate analyses and representational analyses of neural activity patterns where trial-level neural activity pattern estimates are correlated directly with object memorability (Slayton et al, 2025).”

(13) The abstract could benefit from more nuance; I'm not sure if RSA can indeed be said to be 'the principal method', and whether it's about assessing 'quality' of representations (more commonly, the term 'geometry' or 'structure' is used).

We have edited the abstract to reflect the true nuisance in the current approaches.

Abstract. Neural representation refers to the brain activity that stands in for one’s cognitive experience, and in cognitive neuroscience, a prominent method of studying neural representations is representational similarity analysis (RSA). While there are several recent advances in RSA, the classic RSA (cRSA) approach examines the structure of representations across numerous items by assessing the correspondence between two representational similarity matrices (RSMs): usually one based on a theoretical model of stimulus similarity and the other based on similarity in measured neural data.

(14) RSA is also not necessarily about models vs. neural data; it can also be between two neural systems (e.g., monkey vs. human as in Kriegeskorte et al., 2008) or model systems (see Sucholutsky et al., 2023). This statement is also repeated in the Introduction paragraph 1 (later on, it is correctly stated that comparing brain vs. model is most likely the 'most common' approach).

We have added these examples in our introduction to RSA.

Page 3.”One of the central approaches for evaluating information represented in the brain is representational similarity analysis (RSA), an analytical approach that queries the representational geometry of the brain in terms of its alignment with the representational geometry of some cognitive model (Kriegeskorte et al., 2008; Kriegeskorte & Kievit, 2013), or, in some cases, compares the representational geometry of two neural systems (e.g., Kriegeskorte et al., 2008) or two model systems (Sucholutsky et al., 2023)”.

(15) 'theoretically appropriate' is an ambiguous statement, appropriate for what theory?

We apologize for the ambiguous wording, and have corrected the text:

Page 11. “Critically, tRSA estimates were submitted to a mixed-effects model which is statistically appropriate for modeling the hierarchical structure of the data, where observations are nested within both subjects and stimuli (Baayen et al., 2008; Chen et al., 2021)”.

(16) I found the statement that cRSA "cannot model representation at the level of individual trials" confusing, as it made me think, what prohibits one from creating an RDM based on single-trial responses? Later on, I understood that what the authors are trying to say here (I think) is that cRSA cannot weigh the contributions of individual rows/columns to the overall representational strength differently.

We thank the reviewer for their clarifying language and have added it to this section of the manuscript.

“Abstract. However, because cRSA cannot weigh the contributions of individual trials (RSM rows/columns), it is fundamentally limited in its ability to assess subject-, stimulus-, and trial-level variances that all influence representation”.

(17) Why use "RSM" instead of "RDM"? If the pairwise comparison metric is distance-based (e..g, 1-correlation as described by the authors), RDM is more appropriate.

We apologize for the error, and have clarified the Methods text:

Page3-4. First, brain activity responses to a series of N trials are compared against each other (typically using Pearson’s r) to form an N×N representational similarity matrix.

(18) Figure 2: please write 'Correlation estimate' in the y-axis label rather than 'Estimate'.

We have edited the label in Figure 2.

(19) Page 6 'leaving uncertain the directionality of any findings' - I do not follow this argument. Obviously one can generate an RDM or RSM from vector v or vector -v. How does that invalidate drawing conclusions where one e.g., partials out the (dis)similarity in e.g., pleasantness ratings out of another RDM/RSM of interest?

We agree such an approach does not invalidate the partial method; we have clarified what we mean by “directionality”.

Page 8. ”For instance, even though a univariate random variable , such as pleasantness ratings, can be conveniently converted to an RSM using pairwise distance metrics (Weaverdyck et al., 2020), the very same RSM would also be derived from the opposite random variable , leaving uncertain of the directionality (or if representation is strongest for pleasant or unpleasant items) of any findings with the RSM (see also Bainbridge & Rissman, 2018)”.

(20) P7 'sampled 19900 pairs of values from a bi-variate normal distribution', but the rows/columns in an RDM are not independent samples - shouldn't this be included in the simulation? I.e., shouldn't you simulate first the n=200 vectors, and then draw samples from those, as in the next analysis?

This section has been moved to Appendix 1 (see responses to Reviewer 1.13).

(21) Under data acquisition, please state explicitly that the paper is re-using data from prior experiments, rather than collecting data anew for validating tRSA.

We have clarified this in the data acquisition section.

Page 13. “A pre-existing dataset was analyzed to evaluate tRSA. Main study findings have been reported elsewhere (S. Huang, Bogdan, et al., 2024)”.

(22) Figure 4 could benefit from some more explanation in-text. It wasn't clear to me, for example, how to interpret the asterisks depicted in the right part of the figure.

We clarified the meaning of the asterisks in the main text in addition to the existent text in the figure caption.

Page 26. “see Figure 4, off-diagonal cells in blue; asterisks indicate where tRSA was statistically more sensitive then cRSA)”.

(23) Page 38 "the outcome of tRSA's improved characterization can be seen in multiple empirical outcomes:" it seems there is one mention of 'outcomes' too many here.

We have revised this sentence.

Page 41. “tRSA's improved characterization can be seen in multiple empirical outcomes”.

(24) Page 38 "model fits became the strongest" it's not clear what aspect of the reported results in the paragraph before this is referring to - the Appendix?

Yes, the model fits are in the Appendix, we have added this in text citation.

Moreover, model-fits became the strongest when the models also incorporated trial-level variables such as fMRI run and reaction time (Appendix 3, Table 6).

References

Diedrichsen, J., Berlot, E., Mur, M., Schütt, H. H., Shahbazi, M., & Kriegeskorte, N. (2021). Comparing representational geometries using whitened unbiased-distance-matrix similarity. Neurons, Behavior, Data and Theory, 5(3). https://arxiv.org/abs/2007.02789

Diedrichsen, J., & Kriegeskorte, N. (2017). Representational models: A common framework for understanding encoding, pattern-component, and representational-similarity analysis. PLoS Computational Biology, 13(4), e1005508.

Diedrichsen, J., Yokoi, A., & Arbuckle, S. A. (2018). Pattern component modeling: A flexible approach for understanding the representational structure of brain activity patterns. NeuroImage, 180, 119-133.

Naselaris, T., Kay, K. N., Nishimoto, S., & Gallant, J. L. (2011). Encoding and decoding in fMRI. NeuroImage, 56(2), 400-410.

Nili, H., Wingfield, C., Walther, A., Su, L., Marslen-Wilson, W., & Kriegeskorte, N. (2014). A toolbox for representational similarity analysis. PLoS Computational Biology, 10(4), e1003553.

Schütt, H. H., Kipnis, A. D., Diedrichsen, J., & Kriegeskorte, N. (2023). Statistical inference on representational geometries. ELife, 12. https://doi.org/10.7554/eLife.82566

Walther, A., Nili, H., Ejaz, N., Alink, A., Kriegeskorte, N., & Diedrichsen, J. (2016). Reliability of dissimilarity measures for multi-voxel pattern analysis. NeuroImage, 137, 188-200.

King, M. L., Groen, I. I., Steel, A., Kravitz, D. J., & Baker, C. I. (2019). Similarity judgments and cortical visual responses reflect different properties of object and scene categories in naturalistic images. NeuroImage, 197, 368-382.

Kriegeskorte, N., Mur, M., Ruff, D. A., Kiani, R., Bodurka, J., Esteky, H., ... & Bandettini, P. A. (2008). Matching categorical object representations in inferior temporal cortex of man and monkey. Neuron, 60(6), 1126-1141.

Nili, H., Wingfield, C., Walther, A., Su, L., Marslen-Wilson, W., & Kriegeskorte, N. (2014). A toolbox for representational similarity analysis. PLoS computational biology, 10(4), e1003553.

Sucholutsky, I., Muttenthaler, L., Weller, A., Peng, A., Bobu, A., Kim, B., ... & Griffiths, T. L. (2023). Getting aligned on representational alignment. arXiv preprint arXiv:2310.13018.

Author response:

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

Reviewer #1 (Public review): 

In this manuscript, Dillard and colleagues integrate cross-species genomic data with a systems approach to identify potential driver genes underlying human GWAS loci and establish the cell type(s) within which these genes act and potentially drive disease. Specifically, they utilize a large single-cell RNA-seq (scRNA-seq) dataset from an osteogenic cell culture model - bone marrow-derived stromal cells cultured under osteogenic conditions (BMSC-OBs) - from a genetically diverse outbred mouse population called the Diversity Outbred (DO) stock to discover network driver genes that likely underlie human bone mineral density (BMD) GWAS loci. The DO mice segregate over 40M single nucleotide variants, many of which affect gene expression levels, therefore making this an ideal population for systems genetic and co-expression analyses. The current study builds on previously published work from the same group that used co-expression analysis to identify co-expressed "modules" of genes that were enriched for BMD GWAS associations. In this study, the authors utilize a much larger scRNA-seq dataset from 80 DO BMSC-OBs, infer co-expression-based and Bayesian networks for each identified mesenchymal cell type, focused on networks with dynamic expression trajectories that are most likely driving differentiation of BMSC-OBs, and then prioritized genes ("differentiation driver genes" or DDGs) in these osteogenic differentiation networks that had known expression or splicing QTLs (eQTL/sQTLs) in any GTEx tissue that colocalized with human BMD GWAS loci. The systems analysis is impressive, the experimental methods are described in detail, and the experiments appear to be carefully done. The computational analysis of the single-cell data is comprehensive and thorough, and the evidence presented in support of the identified DDGs, including Tpx2 and Fgfrl1, is for the most part convincing. Some limitations in the data resources and methods hamper enthusiasm somewhat and are discussed below. Overall, while this study will no doubt be valuable to the BMD community, the cross-species data integration and analytical framework may be more valuable and generally applicable to the study of other diseases, especially for diseases with robust human GWAS data but for which robust human genomic data in relevant cell types is lacking. 

Specific strengths of the study include the large scRNA-seq dataset on BMSC-OBs from 80 DO mice, the clustering analysis to identify specific cell types and sub-types, the comparison of cell type frequencies across the DO mice, and the CELLECT analysis to prioritize cell clusters that are enriched for BMD heritability (Figure 1). The network analysis pipeline outlined in Figure 2 is also a strength, as is the pseudotime trajectory analysis (results in Figure 3). One weakness involves the focus on genes that were previously identified as having an eQTL or sQTL in any GTEx tissue. The authors rightly point out that the GTEx database does not contain data for bone tissue, but the reason that eQTLs can be shared across many tissues - this assumption is valid for many cis-eQTLs, but it could also exclude many genes as potential DDGs with effects that are specific to bone/osteoblasts. Indeed, the authors show that important BMD driver genes have cell-type-specific eQTLs. Furthermore, the mesenchymal cell type-specific co-expression analysis by iterative WGCNA identified an average of 76 co-expression modules per cell cluster (range 26-153). Based on the limited number of genes that are detected as expressed in a given cell due to sparse per-cell read depth (400-6200 reads/cell) and dropouts, it's hard to believe that as many as 153 co-expression modules could be distinguished within any cell cluster. I would suspect some degree of model overfitting here and would expect that many/most of these identified modules have very few gene members, but the methods list a minimum module size of 20 genes. How do the numbers of modules identified in this study compare to other published scRNA-seq studies that use iterative WGCNA? 

In the section "Identification of differentiation driver genes (DDGs)", the authors identified 408 significant DDGs and found that 49 (12%) were reported by the International Mouse Knockout [sic] Consortium (IMPC) as having a significant effect on whole-body BMD when knocked out in mice. Is this enrichment significant? E.g., what is the background percentage of IMPC gene knockouts that show an effect on whole-body BMD? Similarly, they found that 21 of the 408 DDGs were genes that have BMD GWAS associations that colocalize with GTEx eQTLs/sQTLs. Given that there are > 1,000 BMD GWAS associations, is this enrichment (21/408) significant? Recommend performing a hypergeometric test to provide statistical context to the reported overlaps here. 

We thank the reviewer for their constructive feedback and thoughtful questions. In regards to the iterativeWGCNA, a larger number of modules is sometimes an outcome of the analysis, as reported in the iterativeWGCNA preprint (Greenfest-Allen et al., 2017). While we did not make a comparison to other works leveraging this tool for scRNA-seq, it has been used broadly across other published studies, such as PMID: 39640571, 40075303, 33677398, 33653874. While model overfitting, as you mention, may be a cause for more modules, our Bayesian network analysis we perform after iterativeWGCNA highlights smaller aspects of coexpression modules, as opposed to focusing on the entirety of any given module.

We did not perform enrichment or statistical tests as our goal was to simply highlight attributes or unique features of these genes for additional context.

Reviewer #2 (Public review): 

Summary: 

In this manuscript, Farber and colleagues have performed single-cell RNAseq analysis on bone marrow-derived stem cells from DO Mice. By performing network analysis, they look for driver genes that are associated with bone mineral density GWAS associations. They identify two genes as potential candidates to showcase the utility of this approach. 

Strengths: 

The study is very thorough and the approach is innovative and exciting. The manuscript contains some interesting data relating to how cell differentiation is occurring and the effects of genetics on this process. The section looking for genes with eQTLs that differ across the differentiation trajectory (Figure 4) was particularly exciting. 

Weaknesses: 

The manuscript is in parts hard to read due to the use of acronyms and there are some questions about data analysis that need to be addressed. 

We thank the reviewer for their feedback and shared enthusiasm for our work. We tried to minimize the use of technical acronyms as much as we could without compromising readability. Additionally, we addressed questions regarding aspects of data analysis. 

Reviewer #1 (Recommendations for the authors):

(1) For increased transparency and to allow reproducibility, it would be necessary for the scripts used in the analysis to be shared along with the publication of the preprint. Also, where feasible, sharing the processed data in addition to the raw data would allow the community greater access to the results and be highly beneficial. 

Thank you for this suggestion. The raw data will be available via GEO accession codes listed in the data availability statement. We will make available scripts for some analyses on our Github (https://github.com/Farber-Lab/DO80_project) and processed scRNA-seq data in a Seurat object (.rds) on Zenodo (https://zenodo.org/records/15299631)

(2) Lines 55-76: I think the summary of previous work here is too long. I understand that they would like to cover what has been done previously, but this seems like overkill. 

Good suggestion. We have streamlined some of the summary of our previous work.

(3) Did the authors try to map QTL for cell-type proportion differences in their BMSC-OBs? While 80 samples certainly limit mapping power, the data shown in Figs 4C/D suggest that you might identify a large-effect modifier of LMP/OB1 proportions. 

We did try to map QTL for cell type proportion differences, but no significant associations were identified. 

(4) Methods question: Does the read alignment method used in your analysis account for SNPs/indels that segregate among the DO/CC founder strains? If not, the authors may wish to include this in their discussion of study limitations and speculate on how unmapped reads could affect expression results. 

The read alignment method we used does not account for SNPs/indels from the DO founder strains that fall in RNA transcripts captured in the scRNA-seq data. We have included this as a limitation in our discussion (line 422-424). 

(5) Much of the discussion reads as an overview of the methods, while a discussion of the results and their context to the existing BMD literature is relatively lacking in comparison.

We have added additional explanation of the results and context to the discussion (line 381-382, 396-407). 

(6) Figure 1E and lines 146-149: Adjusted p values should be reported in the figure and accompanying text instead of switching between unadjusted and adjusted p values. 

We updated Figure 1e to portray adjusted p-values, listed the adjusted p-values in legend of Figure 1e, and listed them in the main text (line 153-154).

(7) Why do the authors bring the IMPC KO gene list into the analysis so late? This seems like a highly relevant data resource (moreso than the GTEx eQTLs/sQTLs) that could have been used much earlier to help identify DDGs. 

Given that our scRNA-seq data is also from mice, we did choose to integrate information from the IMPC to highlight supplemental features of genes in networks (i.e., genes that have an experimentally-tested and significant effect on BMD in mice). However, our primary goal was to inform human GWAS and leverage our previous work in which we identified colocalizations between human BMD GWAS and eQTL/sQTL in a human GTEx tissue, which is why this information was used to guide our network analysis.

(8) Does Fgfrl1 and/or Tpx2 have a cis-eQTL in your BMSC-OB scRNA-seq dataset? 

We did not identify cis-eQTL effects for Fgfrl1 and Tpx2.

(9) Figure 4B-C: These eQTLs may be real, but based on the diplotype patterns in Figure 4C, I suspect they are artifacts of low mapping power that are driven by rare genotype classes with one or two samples having outlier expression results. For example, if you look at the results in Fig 4C for S100a1 expression, the genotype classes with the highest/lowest expression have lower sample numbers. In the case of Pkm eQTL showing a PWK-low effect, the PWK genome has many SNPs that differ from the reference genome in the 3' UTR of this gene, and I wonder if reads overlapping these SNPs are not aligning correctly (see point 4 above) and resulting (falsely) in lower expression values for samples with a PWK haplotype. 

As mentioned above, our alignment method did not consider DO founder genetic variation that is specifically located in the 3’ end of RNA transcripts in the scRNA-seq data. We have included this as a limitation in our discussion (line 422-424).

In future studies, we intend to include larger populations of mice to potentially overcome, as you mention, any artifacts that may be attributable to low statistical power, rare genotype classes, or outlier expression.

Reviewer #2 (Recommendations for the authors):

Major Points 

(1) The authors hypothesize "that many genes impacting BMD do so by influencing osteogenic differentiation or possibly bone marrow adipogenic differentiation". However, cell type itself does not correlate with any bone trait. Does this indicate that the hypothesis is not entirely correct, as genes that drive these phenotypes would not be enriched in one particular cell type? The authors have previously identified "high-priority target genes". So, are there any cell types that are enriched for these target genes? If not, this would indicate that all these genes are more ubiquitously expressed and this is probably why they would have a greater effect on the overall bone traits. Furthermore, are the 73 eGenes (so genes with eQTLs in a particular cell type that change around cell type boundaries) or the DDGs (Table 1) enriched for these high-priority target genes? 

The bone traits measured in the DO mice are complex and impacted by many factors, including the differentiation propensity and abundance of certain cell types, both within and outside of bone. Though we did not identify correlations between cell type abundance and the bone traits we measured, we tailored our investigations to focus on cellular differentiation using the scRNA-seq data. However, future studies would need to be performed to investigate any connections between cellular differentiation, cell type abundance, and bone traits.

We did not perform enrichment analyses of either the target genes identified from our other work or eGenes identified here, but instead used the target gene list to center our network analysis and the eGenes to showcase the utility of the DO mouse population.

(2) The readability of the paper could be improved by minimising the use of acronyms and there are several instances of confusing wording throughout the paper. In many cases, this can be solved by re-organising sentences and adding a bit more detail. For example, it was unclear how you arrived at Fgfrl1 or Tpx2.

One of the goals of our study was to identify genes that have (to our knowledge) little to no known connection to BMD. We chose to highlight Fgfrl1 and Tpx2 because there is minimal literature characterizing these genes in the context of bone, which we speak to in the results (line 296-297). Additionally, we prioritized these genes in our previous work and they were identified in this study by using our network analyses using the scRNA-seq data, which we mention in the results (line 276-279).

(3) Technical aspects of the assay. In Figure 1d you show that the cell populations vary considerably between different DO mice. It would be useful to give some sense of the technical variance of this assay given that the assay involves culturing the cells in an exogenous environment. This could take the form of tests between mice within the same inbred strain, or even between different legs of the same DO mice to show that results are technically very consistent. It might also be prudent to identify that this is a potential limitation of the approach as in vitro culturing has the potential to substantially change the cell populations that are present. 

We agree that in vitro culturing, in addition to the preparation of single cells for scRNA-seq, are unavoidable sources of technical variation in this study. However, the total number of cells contributed by each of the 80 DO mice after data processing does not appear to be skewed and the distribution appears normal (see added figures, now included as Supplemental Figure 3). Therefore, technical variation is at least consistent across all samples. Nevertheless, we have mentioned the potential for technical variation artifacts in our study in the discussion (line 414-416).

(4) Need for permutation testing. "We identified 563 genes regulated by a significant eQTL in specific cell types. In total, 73 genes with eQTLs were also tradeSeq-identified genes in one or more cell type boundaries". These types of statements are fine but they need to be backed up with permutation testing to show that this level of enrichment is greater than one would expect by chance. 

We did not perform enrichment tests as our only goal was to 1. determine if eQTL could be resolved in the DO mouse population using our scRNA-seq data and 2. predict in what cell type the associated eQTL and associated eGene may have an effect.

(5) The main novelty of the paper seems to be that you have used single-cell RNA seq (given that you appear to have already detailed the candidates at the end). I don't think this makes the paper less interesting, but I think you need to reframe the paper more about the approach, and not the specific results. How you landed on these candidates is also not clear. So the paper might be improved by more robustly establishing the workflow and providing guidelines for how studies like this should be conducted in the future. 

We sought to not only devise a rigorous approach to analyze our single cell data, but also showcase the utility of the approach in practice by highlighting targets for future research (i.e., Fgfrl1 and Tpx2).

Our goal was to identify novel genes and we landed on these candidate genes (Fgfrl1 and Tpx2) because they had substantial data supporting their causality and they have yet to be fully characterized in the context of bone and BMD (line 295-297).

In regards to establishing the workflow, we have included rationale for specific aspects of our approach throughout the paper. For example, Figure 2 itemizes each step of our network analysis and we explain why each step is utilized throughout various parts results (e.g., lines 168-170, 179-181, 191-193, 202-203, 257-260, 276-277).

We have added a statement advocating for large-scale scRNA-seq from genetically diverse samples and network analyses for future studies (line 436-438).

Minor Points 

(1) In the summary you use the word "trajectory". Trajectories for what? I assume the transition between cell types, but this is not clear. 

We added text to clarify the use of trajectory in the summary (line 34).

(2) This sentence: "By 60 identifying networks enriched for genes implicated in GWAS we predicted putatively causal genes 61 for hundreds of BMD associations based on their membership in enriched modules." is also not clear. Do you mean: we predicted putatively causal genes by identifying clusters of co-expressed genes that were enriched for GWAS genes?" It is not clear how you identify the causal gene in the network. Is this just based on the hub gene? 

The aforementioned sentence has since been removed to streamline the introduction, as suggested by Reviewer 1.

In regards to causal gene identification, it is not based on whether it is hub gene. We prioritized a DDG (and their associated networks) if it was a causal gene that we identified in our previous work as having eQTL/sQTL in a GTEx tissue that colocalizes with human BMD GWAS.

(3) Figure 3C. This is good but the labels are quite small. Would be good to make all the font sizes larger. 

We have enlarged Figure 3C.

(4) Line 341 in the Discussion should be "pseudotemporal". 

We have edited “temporal” to “pseduotemporal”.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #2

Evidence, reproducibility and clarity

In their study, Haghighi et al. seek to build upon prior literature linking alterations in mitochondrial network distribution with various kinds of psychosis. Correlations between subcellular mitochondrial localization and different psychological states is an interesting and potentially fruitful frontier and should be explored; however, despite their ambitious strategy to screen 168 skin fibroblasts from patients experiencing psychosis, and examine various online image databases, there is a concerning number of issues related to the image-analysis approach. The foremost of these is a lack of direct measures of mitochondrial distribution, which might serve to validate their proposed MITO-SLOPE protocol. There is also a worrisome lack of robust controls, which are critical in light of how admittedly subtle some of the distribution phenotypes may be. Overall, the aim to screen differences in mitochondrial distribution is a laudable goal and, in the context of psychological disorders, could be helpful in identifying new therapeutic targets; but the methodology employed in this study does not seem to be sufficiently rigorous to be able to leverage this approach for screening purposes.

I have extensive experience investigating mitochondria with advanced imaging technologies, including super-resolution microscopy as well as high-throughput and 4D imaging modalities. I am also familiar with standard as well as machine-learning approaches for quantifying mitochondrial morphology as well as distribution or trafficking. In my opinion, this study requires substantial revision, both in terms of the indirect and often opaque image-analysis pipeline as well as the inclusion of orthogonal experiments, which could serve to lessen concerns regarding purported differences in mitochondrial distribution, which are so difficult to discern as to be imperceptible. It is worth noting, too, that this study appears to be predicated, in many ways, upon a 2010 study (Cataldo et al.) of mitochondria in patients with bipolar disorder, which appears to reflect its own lack of critical controls for cell size.

Major comments:

The authors state, in the first paragraph of the results section: "By eye, we observed that samples from patients in the control and MDD categories show a more fine-grained, dispersed mitochondrial network extending to the edges of the cell, whereas patients in the categories experiencing psychosis tend to show an agglomerated, thicker network more concentrated around the nucleus. The pattern is subtle and heterogeneous across a cell population." The pattern is indeed subtle. I am concerned that it is so subtle as to be imperceptible. Firstly, it is important to note that the mitochondrial reticulum in BP, SZ, and SZA is more difficult to differentiate, by eye, because the signal appears to be saturated in places, such that the boundaries of individual mitochondria are indistinguishable due to differences in contrast or possibly from the fluorescence intensity itself. Although the authors indicate in the legend that the intensity of the mitochondrial fluorescence was adjusted "for visual clarity," it appears that the contrast needs to be decreased in the BP, SZ, and SZA conditions. It is also important to note that MitoTrackers load into mitochondria in a membrane-potential-dependent fashion. Did the authors detect differences in membrane potential between these groups? While imaging, was the same laser power and gain utilized from condition to condition? With this being said, it is not clear that mitochondria in control and MDD categories have different morphologies from the other conditions. It is also not clear what "fine-grained" means in this context. Is this a comment on aspect ratio? If so, it would be better to use standard terminology. (Why are there large red circular structures in the nucleus? These are likely not mitochondria, so why are they showing up in the channel with MitoTracker?) It is also not evident that one condition has more dispersed mitochondria than another. Given that the authors appear to be making this a central claim of their manuscript, it would seem appropriate to highlight specifically the regions of the different cells that they believe exhibit meaningful differences. If I attempt to look at the merged image, which is important because it is really the only way that one can gauge the relative distance of the mitochondrial network from the edge of the cell, there would seem to be no obvious differences between the conditions. Another key point that I think important to mention, given that it is frequently referenced in this manuscript, Cataldo et al., 2010 indicate that mitochondria in patient fibroblasts with bipolar disorder (BD) are more perinuclear than those in control. However, a cursory inspection of the images from this study (e.g., Figure 2A-B; Figure 4A-D; and Figure 6A-H) unambiguously demonstrate that the BD cells are smaller than the control cells. Of course, if the cells are smaller, the distance from the nucleus will tend to be shorter. In Cataldo et al., 2010, the authors state, "We also measured cell area, cell length, cell width, and cell perimeter of the fibroblasts used in this analysis to verify that the observed mitochondrial distributional differences were not simply a result of BD cells being smaller, shorter, or fatter. No significant differences in any of these measurements were seen based on diagnosis after two sample t tests." Notably, the data is not shown, so it is difficult to appreciate what the variance of the population of cells from control and BD would look like, but it must be said, nevertheless, that the representative images in this paper all point to the BD cells being smaller. In light of this, it would be helpful if Haghighi et al. could add scale bars to all the images (e.g., in Figure 2), so readers can ascertain whether all the cells are portrayed at the same scale and are of similar areas.

As the authors indicate, interpretable measures of mitochondrial morphology include values like size and shape. It is concerning, therefore, that Figure 3 purports to identify a number of significantly different mitochondrial "features" in the patient groups experiencing psychosis, but they do not appear to make an effort to clarify how any of these features might reflect ground truths of mitochondrial architecture, which can be understood directly by values such as aspect ratio, circularity, area, number organelles, number of nodes or branching points in a network, etc. Unless the authors can specifically tie their machine-learning classifications to standard mitochondrial shape descriptors, their classifications will remain opaque and therefore of limited credibility or value. One way to improve the validation of their machine-learning classification methods would be to use empirically sound methods for manipulating a mitochondrial morphology and distribution, which could serve as positive or negative controls. For example, treatment of cells with the uncoupler FCCP would induce mitochondrial fragmentation, treatment with cycloheximide results in stress-induced mitochondrial hyperfusion (SIMH), or treatment with Nocodazole would block mitochondrial trafficking. Treating control cells with these chemicals would help to establish baseline measurements for how far the patient cells are deviating from untreated controls, in one direction or another. Such considerations, I think, are especially important when the mitochondrial phenotypes are so subtle. I agree with the authors' argument that, for the purposes of screening, it is best to focus on a single metric. Based on their apparent discernment of the subtle differences in mitochondrial distribution in patients experiencing psychosis, they opted to examine possible differences in network density. To this end, they developed "MITO-SLOPE." Out of multiple categories of features, they highlight the following as the most powerful for establishing differences in mitochondrial network density:

"(a) A subset of texture measures in the nuclei and cytoplasm area of the mito channel. (b) A subset of features measuring the intensity of the mitochondria area across the cell."

Within the concentric bins around the cell nuclei, they measure:

• FracAtD: Fraction of total stain in an object at a given radius.
• MeanFrac: Mean fractional intensity at a given radius, calculated as the fraction of total intensity normalized by the fraction of pixels at a given radius.
• RadialCV: Coefficient of variation of intensity within a ring, calculated across 8 slices."

While the authors have recommended the use of a single metric for purposes of screening, MITO-SLOPE appears to represent a bundle of metrics, which, in the end, do not amount to a clear readout of what is being measured. From my point of view, if one were interested in measuring mitochondrial distribution, then, in an ideal situation, one would measure the average distance of all the mitochondria from the center of the nucleus. And, since the size of the cell is critical for establishing relative distances to the boundaries or periphery of the cell, one would normalize this metric by cellular area. Thus, the readout would be: [average mitochondrial distance from the nuclear center (µm)]/[cellular area (µm2)]. An even simpler metric could be: [average mitochondrial distance from nuclear center (µm)]/[average cytoplasmic radius (µm)]. When talking about mitochondrial distribution, we typically think in terms of where is the mitochondrial network, on average, in relation to the nucleus (perinuclear) or to the edge of the cell (peripheral). By quantifying the actual mean distance of the mitochondrial network in relation to both the nucleus and the bona fide cell extremities, via the metrics I described above, one can obtain direct measurements of the truly meaningful values related to mitochondrial distribution. It seems deviating from these approaches introduces more and more opportunities for confounding variables.

However, the MITO-SLOPE analysis does not seem to consider this metric. Is this, or a similar variation, not the most direct way to establish differences in the mitochondrial network distribution? I would, of course, at least want to see a discussion of why the authors have not chosen to use the most direct form of quantification for this purely spatial value. Why opt for a multifaceted measurement of a relatively straightforward quantity, when a simpler form of quantification would not only suffice but arguably be more likely to capture the ground truth? With this being said, it is not clear to me why, within MITO-SLOPE there seems to be a reliance on measuring the "intensity" of the mitochondria. (And what intensity is it? Mean intensity per ROI?) Of course, particularly if MitoTrackers were used for staining mitochondria, there will be heterogeneity in fluorescence intensity from organelle to organelle, which introduces potential confounders into the workflow. Furthermore, as indicated above, to know if the subcellular distribution of mitochondria is truly altered, it is essential to know if the cell size has likewise changed. Therefore, any unbiased measure of mitochondrial distribution must take into consideration the size of the cell; however, based on the information provided about MITO-SLOPE, it does not appear that the authors are accounting for possible variations in cell size that might account for alterations in mitochondrial network distribution - i.e., a smaller cell will have a more constrained area in which mitochondria will be able to disperse - thus, not accounting for cell size (area) will yield ambiguous results. For example, how can we know if mitochondrial motility is impaired or if the cell is simply smaller and there is less space in which to move? Another complexity, here, is if the cell boundaries were not accounted for via staining of actin, etc., then establishing a true cell boundary will be very challenging. How many bins are sufficient to capture the whole cell? Just 12? Furthermore, human fibroblasts have a tendency to be quite large (sometimes several hundred microns from end to end); how can the authors account for the whole cell, particularly in cases where part of the cell is beyond the field of view or cells are growing on top of each other, as is often the case?

In Figure 6, there is no control image that could be used as a frame of reference. I have extensive experience imaging A549 cells. The mitochondria in these images appear to be highly fragmented. The staining patterns, particularly of the cells treated with divalproex-sodium, are quite dim, indicating mitochondrial depolarization. Of course, depolarization affects the fluorescence intensity of mitochondria stained with vital dyes, such as MitoTrackers, which will, in turn, presumably affect the values obtained from MITO-SLOPE, which appear to rely on intensity gradients, rather than more concrete spatial coordinates. Also, as indicated above, it is unclear how the authors are establishing the edges of cells without a marker of the plasma membrane or cytoskeleton.

The authors note that "Divalproex-sodium is a benzodiazepine receptor agonist and HDAC inhibitor (Rahman et al. 2025) used to manage a variety of seizure disorders (Willmore 2003) and bipolar disorder(Bond et al. 2010; Cipriani et al. 2013); it shows a positive MITO-SLOPE which is the direction expected to normalize the centralized mitochondrial localization associated with psychosis." Insofar as this recommends the drug for use in "normalizing" perinuclear mitochondria within neurons, it would seem only prudent to mention that this drug also appears to induce mitochondrial depolarization and fragmentation, which are both associated with a range of severe human pathologies. I would caution the authors to not highlight one potential benefit while omitting an obvious side effect involving what appears to be significant perturbation of mitochondrial structure and function. What is the point of normalizing mitochondrial distribution if the mitochondria being redistributed are dysfunctional?

The authors note, in Figure 7, that their MITO-SLOPE analysis was unable to discern a statistically significant difference in cells with specific knockouts of genes associated with mitochondrial trafficking. If the MITO-SLOPE cannot discern a difference in the context of a substantial abrogation of mitochondrial transport capacity, how is it that it could detect meaningful differences where there is only a "subtle" change in distribution? This result would seem to militate strongly against the efficacy of this analysis pipeline and would not recommend its use for unbiased screening and discovery.

Minor comments:

For Figure 6 b and c, "µm" should be "µM."

The introduction and discussion could be more concise.

Significance

This study attempts to fill an important gap in knowledge relating to mitochondrial distribution and psychological disorders. It aims to perform an initial screen to try to validate a novel analysis pipeline called MITO-SLOPE, however, the study appears to lack analytical rigor, both in terms of the underlying cell biology together with the approach for quantification, itself. Conceptually, this study has great promise, but the authors will need to improve their pipeline prior to publication, which will likely require fundamental revisions, including an array of orthogonal measures (largely lacking here) as well as detailed demonstrations of how the segmentation actually works and ultimately yields data reflecting demonstrable mitochondrial trafficking/distribution defects.

Author response:

eLife Assessment

This study provides a valuable contribution to understanding how negative affect influences food-choice decision making in bulimia nervosa, using a mechanistic approach with a drift diffusion model (DDM) to examine the weighting of tastiness and healthiness attributes. The solid evidence is supported by a robust crossover design and rigorous statistical methods, although concerns about the interpretation of group differences across neutral and negative conditions limit the interpretability of the results.

We are grateful for this improved assessment. Below, we provide detailed responses that we believe address the noted concerns about interpreting group differences across conditions. If these clarifications resolve the interpretability concerns, we would be grateful if the editors would consider updating the eLife assessment accordingly.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Using a computational modeling approach based on the Drift and Diffusion Model (DDM) introduced by Ratcliff and McKoon in 2008, the article by Shevlin and colleagues investigates whether there are differences between neutral and negative emotional states in:

(1) The timings of the integration in food choices of the perceived healthiness and tastiness of food options in individuals with bulimia nervosa (BN) and healthy participants

(2)The weighting of the perceived healthiness and tastiness of these options.

Strengths:

By looking at the mechanistic part of the decision process, the approach has potential to improve the understanding of pathological food choices.

Weaknesses:

I thank the author for reviewing their manuscript.

However, I still have major concerns.

The authors say that they removed any causal claims in their revised version of the manuscript. The sentence before the last one of the abstract still says "bias for high-fat foods predicted more frequent subjective binge episodes over three months". This is a causal claim that I already highlighted in my previous review, specifically for that sentence (see my second sentence of my major point 2 of my previous review).

We appreciate the Reviewer's continued attention to causal language. We acknowledge that our use of the term 'predicted', though intended to refer to statistical prediction in a regression model, could be misinterpreted as implying causation. We have therefore revised this sentence to read: 'bias for high-fat foods was associated with more frequent subjective binge episodes over three months’.

I also noticed that a comment that I added was not sent to the authors. In this comment I was highlighting that in Figure 2 of Galibri et al., I was uncertain about a difference between neutral and negative inductions of the average negative rating after the induction in the BN group (i.e. comparing the negative rating after negative induction in BN to the negative rating after neutral induction in BN). Figure 2 of Galibri et al. looks to me that:

(1) The BN participants were more negative before the induction when they came to the neutral session than when they came to the negative session.

(2) The BN participants looked almost negatively similar (taking into account the error bars reported) after the induction in both sessions

These observations are of high importance because they may support the fact that BN patients were likely in a similar negative state to run the food decision task in both conditions (negative and neutral). Therefore, the lack of difference in food choices in BN patients is unsurprising and nothing could be concluded from the DDM analyses. Moreover, the strong negative ratings of BN patients in the neutral condition as compared to healthy participants together with almost similar negative ratings after the two inductions contradict the authors' last sentence of their abstract.

I appreciate that the authors reproduced an analysis of their initial paper regarding the negative ratings (i.e. Table S1). It partly answers my aforementioned point but does not address the fact that BN may have been in a similar negative state in both conditions (neutral and negative) when running the food decision task: if BN patients were similarly negative after both induction (neutral and negative), nothing can be concluded from their differences in their results obtained from the DDM. As the authors put it, "not all loss-ofcontrol eating occurs in the context of negative state", I add that far from all negative states lead to a loss-of-control eating in BN patients. This grounds all my aforementioned remarks and my remarks of my first review.

A solution for that is to run a paired t-test in BN patients only comparing the score after the induction in the two conditions (neutral and negative) reported in Figure 2 of their initial article.

We appreciate the reviewer’s concern. We understand how the visual representation in Figure 2, which displays between-subject error bars, might suggest similar post-induction affect levels. However, the within-subject paired comparison (which appropriately accounts for individual differences in baseline affect) reveals a significant difference, which we detail below.

While BN participants did report higher baseline negative affect than the HC group prior to the mood inductions, this does not negate the effectiveness of the manipulation. The critical comparison is the within-subject change from pre- to post-induction (detailed below) which shows that negative affect was significantly higher after the negative induction than the neutral induction.

As we reported in the Supplementary Information (Table S1), our initial analyses of self-reported affect ratings used a linear mixed-effects model with group (HC = 0, BN = 1), condition (Neutral = 0, Negative = 1), and time (pre-induction = 0, post-induction = 1) as fixed effects, including all interactions, and random intercepts for participants. This approach accounts for individual differences in baseline affect.

However, to address the reviewer's concerns, we conducted two simple effects analyses using estimated marginal means. As the reviewer suggested, we directly compared post-induction affect between conditions within the BN group (described in the second analysis below). In the first analysis, we examined the diagnosis × time interaction within each condition separately. In the Negative condition, individuals with BN demonstrated a substantial increase in negative affect from pre- to post-induction (mean difference = 20.36, t = 4.84, p < 0.0001, Cohen’s d = 0.97). In the second analysis, we examined the condition × time interaction within each group separately. Among the BN group, we found that reported affect was significantly higher following the negative mood induction than after the neutral affect induction (mean difference = -17.40, t = -4.13, p = 0.0003, Cohen’s d = 0.83). This difference in post-induction negative affect between conditions within the BN group represents a meaningful and statistically robust difference in affective states. These within-group effects confirm that the negative mood induction was (1) effective in the BN group and (2) produced significantly greater negative affect than the neutral mood induction.

These findings confirm that participants completed the food decision task under meaningfully different affective states, supporting the interpretability of the subsequent DDM analyses. We now report these analyses in the Supplementary Information.

I appreciate the analysis that the authors added with the restrictive subscale of the EDE-Q.

That this analysis does not show any association with the parameters of interest does not show that there is a difference in the link between self reported restrictions and self reported binges. Only such a difference would allow us to claim that the results the authors report may be related to binges.

We thank the reviewer for raising this important point about specificity. To address this concern, we examined the correlation between self-reported binge frequency (both subjective binge episodes and objective binge episodes over the past three months) and EDE-Q Restraint subscale in our BN sample.

The correlation between these measures were modest and non-significant (subjective binge frequency: Spearman’s p = 0.21, p = 0.306; objective binge frequency: Spearman’s p = 0.05, p = 0.806), indicating that both binge frequency measures and dietary restraint were relatively independent dimensions of eating pathology in our sample. This dissociation supports the specificity of our findings: the fact that our DDM parameters were associated with binge frequency but not with dietary restraint suggests that the affect-induced changes in decisionmaking we observed are specifically related to binge-eating behavior rather than reflecting a correlate of dietary restraint. We now report this analysis in the Supplementary Information.

I appreciate the wording of the answer of the authors to my third point: "the results suggest that individuals whose task behavior is more reactive to negative affect tend to be the most symptomatic, but the results do not allow us to determine whether this reactivity causes the symptoms". This sentence is crystal clear and sums very well the limits of the associations the authors report with binge eating frequency. However, I do not see this sentence in the manuscript. I think the manuscript would benefit substantially from adding it.

We thank the reviewer for the suggestion. We have added the following sentences that convey this information to the end of the third paragraph of the discussion:

“These results suggest that individuals whose task behavior is more reactive to negative affect tend to be the most symptomatic. However, our correlational design does not allow us to determine whether this reactivity causes the symptoms.”

Statistical analyses:

If I understood well the mixed models performed, analyses of supplementary tables S1 and S27 to S32 are considering all measures as independent which means that the considered score of each condition (neutral vs negative) and each time (before vs after induction) which have been rated by the same participants are independent. Such type of analyses does not take into account the potential correlation between the 4 scores of a given participant. As a consequence, results may lead to false positives that a linear mixed model does not address. The appropriate analysis would be to run adapted statistical tests pairing the data without running any mixed model.

We appreciate the reviewer's attention to the statistical approach. However, we respectfully note that mixed-effects models do account for within-subject correlations, contrary to the reviewer’s interpretation.

The linear mixed-effects model we employed explicitly accounts for the correlation among repeated measures from the same participant through the random intercept term. This random effect structure models the non-independence of observations within participants, allowing for correlated errors within individuals while assuming independence between individuals. This is a standard and appropriate approach for analyzing repeated-measures data (Bates et al., 2015).

The mixed-effects model is, in fact, more appropriate than separate paired t-tests for our design because it:

(1) Simultaneously models all fixed effects (group, condition, time) and their interactions in a single unified framework;

(2) Properly partitions variance into within-subject and between-subject components;

(3) Provides greater statistical power and more precise estimates by using all available data simultaneously; and

(4) Allows for direct testing of three-way interactions that cannot be assessed through pairwise comparisons alone.

Paired tests (e.g., t-tests), as the reviewer suggests, would require multiple separate analyses and would not allow us to test our primary hypotheses about group × condition × time interactions. The mixed-effects approach provides a more comprehensive and statistically rigorous analysis of our repeated-measures design. To clarify this even further in the manuscript, we have added the following in our methods when describing our model, “participant-level random intercepts were included to account for within-subject correlations across repeated measurements.”

Notes:

It is not because specific methods like correlating self reported measures over long periods with almost instantaneous behaviors (like tasks) have been used extensively in studies that these methods are adapted to answer a given scientific question. Measures aggregated over long periods miss the variations in instantaneous behaviors over these periods.

We acknowledge the reviewer’s concern about the temporal mismatch between our session-level task measures and the 3-month aggregated symptom reports. This is a valid limitation of crosssectional designs, and we agree that examining how task performance fluctuates in relation to real-time symptom variation would provide richer insights into the potential dynamics of these relationships.

We agree that we cannot capture how daily changes in task performance relate to momentary symptom occurrence. In response to previous rounds of helpful reviews, we added this limitation to the Discussion section, noting that future research employing ecological momentary assessment (EMA) or daily diary methods could examine whether the decision-making processes we identified also fluctuate in relation to real-time symptom occurrence.

We note that our finding that affect-induced changes in decision-making parameters were associated with subjective binge frequency suggests that this laboratory-measured reactivity may reflect a stable individual difference that manifests across contexts and time periods. While our current study provides initial evidence that individual differences in affect-related decisionmaking are associated with symptom severity, we acknowledge that longitudinal designs with repeated assessments would strengthen causal and temporal inferences.

Reviewer #2 (Public review):

Summary:

Binge eating is often preceded by heightened negative affect, but the specific processes underlying this link are not well-understood. The purpose of this manuscript was to examine whether affect state (neutral or negative mood) impacts food choice decisionmaking processes that may increase the likelihood of binge eating in individuals with bulimia nervosa (BN). The researchers used a randomized crossover design in women with BN (n=25) and controls (n=21), in which participants underwent a negative or neutral mood induction prior to completing a food-choice task. The researchers found that despite no differences in food choices in the negative and neutral conditions, women with BN demonstrated a stronger bias toward considering the 'tastiness' before the 'healthiness' of the food after the negative mood induction.

Strengths:

The topic is important and clinically relevant, and the methods are sound. The use of computational modeling to understand nuances in decision-making processes and how that might relate to eating disorder symptom severity is a strength of the study.

Weaknesses:

Sample size was relatively small, and participants were all women with BN, which limits generalizability of findings to the larger population of individuals who engage in binge eating. It is likely that the negative affect manipulation was weak and may not have been potent enough to change behavior. These limitations are adequately noted in the discussion.

We are grateful to Reviewer #2 for their careful and supportive review of our manuscript. We appreciate their recognition that computational modeling can reveal nuanced alterations in decision-making processes that may not be apparent in overt behavioral choices. Their balanced assessment of both the strengths and limitations of our work has been helpful in contextualizing our findings appropriately. We have carefully considered their comments regarding sample size and the potential limitations of our mood induction procedure, both of which we discuss in detail in the manuscript's limitations section.

Reviewer #3 (Public review):

Summary:

The study uses the food choice task, a well-established method in eating disorder research, particularly in anorexia nervosa. However, it introduces a novel analytical approach-the diffusion decision model-to deconstruct food choices and assess the influence of negative affect on how and when tastiness and healthiness are considered in decision-making among individuals with bulimia nervosa and healthy controls.

Strengths:

The introduction provides a comprehensive review of the literature, and the study design appears robust. It incorporates separate sessions for neutral and negative affect conditions and counterbalances tastiness and healthiness ratings. The statistical methods are rigorous, employing multiple testing corrections.

A key finding-that negative affect induction biases individuals with bulimia nervosa toward prioritizing tastiness over healthiness-offers an intriguing perspective on how negative affect may drive binge eating behaviors.

Weaknesses:

A notable limitation is the absence of a sample size calculation, which, combined with the relatively small sample, may have contributed to null findings. Additionally, while the affect induction method is validated, it is less effective than alternatives such as image or film-based stimuli (Dana et al., 2020), potentially influencing the results.

We are grateful to Reviewer #3 for their thoughtful evaluation of our work. We appreciate their recognition that the diffusion decision model provides a novel analytical lens for understanding how negative affect influences the dynamics of food-related decision-making in bulimia nervosa. Their balanced assessment of both the methodological strengths of our design (counterbalancing, rigorous statistical corrections) and its limitations (sample size, mood induction efficacy) has been valuable in ensuring we appropriately contextualize our findings and their implications. Specifically, we have taken their comments regarding sample size and the relative efficacy of different mood induction methods seriously, and we address these important methodological considerations in our discussion of the study's limitations.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

The authors have addressed my previous comments, and I do not have any additional suggestions for improvement.

We thank the reviewer for their time, effort, and insightful feedback.

Reviewer #3 (Recommendations for the authors):

The authors have adequately addressed my feedback. I have no further comments.

We thank the reviewer for their time, effort, and insightful feedback.

Author response:

eLife Assessment

Hoverflies are known for their sexually dimorphic visual systems and exquisite flight behaviors. This valuable study reports how two types of visual descending neurons differ between males and females in their motion- and speed-dependent responses, yet surprisingly, the behavior they control lacks any sexual dimorphism. The results convincingly support these findings, which will be of interest for studies of visuomotor transformations and network-level brain organization.

This statement perfectly recapitulates our findings.

Public Reviews:

Reviewer #1 (Public review):  

Summary: 

Hoverflies are known for a striking sexual dimorphism in eye morphology and early visual system physiology. Surprisingly, the male and female flight behaviors show only subtle differences. Nicholas et al. investigate the sensori-motor transformation of sexually dimorphic visual information to flight steering commands via descending neurons. The authors combined intra- and extracellular recordings, neuroanatomy, and behavioral analysis. They convincingly demonstrate that descending neurons show sexual dimorphisms - in particular at high optic flow velocities - while wing steering responses seem relatively monomorphic. The study highlights a very interesting discrepancy between neuronal and behavioral response properties.

Thank you for this summary. Most of the statement perfectly recapitulates the main findings of our paper. However, we want to emphasize that some hoverfly flight behaviors are strongly sexually dimorphic, especially those related to courtship and mating. Indeed, only male hoverflies pursue targets at high speed, chase away territorial intruders, and pursue females for mating. However, other flight behaviours, such as those related to optomotor responses and flights between flowers when feeding, are not sexually dimorphic. We will amend the Introduction to make the difference between flight behaviors clear.

More specifically, the authors focused on two types of descending neurons that receive inputs from well-characterized wide-field sensitive tangential cells: OFS DN1, which receives inputs from so-called HS cells, and OFS DN2, which receives input from a set of VS cells. Their likely counterparts in Drosophila connect to the neck, wing, and haltere neuropils. The authors characterized the visual response properties of these two neuronal classes in both male and female hoverflies and identified several interesting differences. They then presented the same set of stimuli, tracked wing beat amplitude, and analyzed the sum and the difference of right and left wing beat amplitude as a readout of lift or thrust, and yaw turning, respectively. Behavioral responses showed little to no sexual dimorphism, despite the observed neuronal differences.

Thank you for this very nice summary of our work. We want to clarify that LPTC input to DN1 and DN2 has not been shown directly in hoverflies using e.g. dye coupling, or dual recordings. Instead, the presumed HS and VS input is inferred from morphological and physiological DN evidence, and comparisons to similar data in Drosophila and blowflies. We will amend the Introduction to clarify this. The rest of the paragraph perfectly recapitulates the main findings of our paper.

Strengths:

I find the question very interesting and the results both convincing and intriguing. A fundamental goal in neuroscience is to link neuronal responses and behavior. The current study highlights that the transformations - even at the level of descending neurons to motoneurons - are complex and less straightforward than one might expect.

Thank you.

Weaknesses:

The authors investigated two types of descending neurons, but it was not clear to me how many other descending neurons are thought to be involved in wing steering responses to wide-field motion. I would suggest providing a more in-depth overview of what is known about hoverflies and Drosophila, since the conclusions drawn from the study would be different if these two types were the only descending neurons involved, as opposed to representing a subset of the neurons conveying visual information to the wing neuropil.

This is a great point. There are around 1000 fly DNs, of which many could respond to widefield motion, without being specifically tuned to widefield motion. For example, many looming sensitive neurons also respond to widefield motion, and could therefore be involved in the WBA movements that we measured here. In addition, there are many multimodal neurons that could be involved in optomotor responses in free flight, but these may not have been stimulated when we only provided visual input. Furthermore, many visual neurons are modulated by proprioceptive feedback, which is lacking in immobilized physiology preps. Finally, in blowflies, up to 5 optic flow sensitive DNs have been identified morphologically, and in Drosophila 3 have been identified morphologically and physiologically. In summary, it is more than likely that other neurons project visual widefield motion information to the wing neuropil. We will amend our Introduction and Discussion to make this important point clear to the readers.

Both neuronal classes have counterparts in Drosophila that also innervate neck motor regions. The authors filled the hoverfly DNs in intracellular recordings to characterize their arborization in the ventral nerve cord. In my opinion, these anatomical data could be further exploited and discussed a bit more: is the innervation in hoverflies also consistent with connecting to the neck and haltere motor regions? Are there any obvious differences and similarities to the Drosophila neurons mentioned by the authors? If the arborization also supports a role in neck movements, the authors could discuss whether they would expect any sexual dimorphism in head movements.

These are all great points. We did not see any clear arborizations to the frontal nerve, where we would expect to find the neck motor neurons (NMNs). In addition, while we did see fine arborizations throughout the length of the thoracic ganglion, we saw no strong outputs projecting directly to the haltere nerve (HN). In the revised version of the MS we will modify figure 4 (morphological characterization) to clarify.

There are important differences between the morphology of DN1 and DN2 in hoverflies and DNHS1 and DNOVS2 in Drosophila, in terms of their projections in the thoracic ganglion. For example, In Drosophila DNOVS2, there are several fine branches along the length of the neuron in the thoracic ganglia. Similarly, we found fine branches in Eristalis tenax DN2, however, in addition, we found a wide branch projecting to the area of the thoracic ganglion where the prothoracic and pterothoracic nerves likely get their inputs (Figure 4), suggesting that the neuron could contribute to controlling the wings and/or the forelegs (which is why we quantified the WBA). In Drosophila DNHS1, there is a similar fat branch to the prothoracic and pterothoracic nerves, which we also found in Eristalis tenax OFS DN1 (Figure 4). Indeed, while Drosophila DNHS1 and DNOVS2 have quite strikingly different morphology, DN1 and DN2 in Eristalis looked quite similar. We will modify the Results section to make this clear.

In addition, to investigate this further, in the revised version of the MS we will include analysis of the movement of different body parts (including the head) to investigate the presence of any potential sexual dimorphism. Unfortunately, however, this will not include the halteres, as they cannot be seen well in the videos.

Reviewer #2 (Public review):

Summary:

Many fly species exhibit male-specific visual behaviors during courtship, while little is known about the circuit underlying the dimorphic visuomotor transformations. Nicholas et al focus on two types of visual descending neurons (DNs) in hoverflies, a species in which only males exhibit high-speed pursuit of conspecifics. They combined electrophysiology and behavior analysis to identify these DNs and characterize their response to a variety of visual stimuli in both male and female flies. The results show that the neurons in both sexes have similar receptive fields but exhibit speed-dependent dimorphic responses to different optic flow stimuli.

This statement perfectly recapitulates the main findings of our paper. However, as mentioned above, while hoverfly flight behaviors related to courtship and mating are strongly sexually dimorphic, other flight behaviours, such as those related to optomotor responses and flights between flowers when feeding, are not. We will amend the Introduction to make the difference between flight behaviors clear.

Strengths:

Hoverflies, though not a common model system, show very interesting dimorphic behaviors and provide a unique and valuable entry point to explore the brain organization behind sexual dimorphism. The findings here are not only interesting on their own right but will also likely inspire those working in other systems, particularly Drosophila.

Thank you.

The authors employed rigorous morphology, electrophysiology, and behavior methods to deliver a comprehensive characterization of the neurons in question. The precision of the measurements allowed for identifying a subtle and nuanced neuronal dimorphism and set a standard for future work in this area.

Thank you.

Weaknesses:

Cell-typing using receptive field preferred directions (RFPDs): if I understood correctly, this classification method mostly relies on the LPDs near the center of the receptive field (median within the contour in Fig.1). I have two concerns here. First, this method is great if we are certain there are only two types of visual DNs as described in the manuscript. But how certain is this? Given the importance of vision in flight control, I would expect many DNs that transmit optic flow information to the motor center. I'd also like to point out that there are other lobula plate tangential cells (LPTCs) than HS and VS cells, which are much less studied and could potentially contribute to dimorphic behaviors.

This is very true, and an important point. As mentioned above, in blowflies, up to 5 optic flow sensitive DNs have been identified morphologically, however, if these correspond to 5 different physiological types remain unclear. In both blowflies and Drosophila 3 have been identified morphologically and physiologically (DNHS1, DNOVS1, DNOVS2). Importantly, in both blowflies and fruitflies DNOVS1 gives graded responses, and no action potentials, meaning that we would not be able to record from it using extracellular electrophysiology.

We previously used clustering techniques to show that in Eristalis, we can reliably distinguish two types of optic flow sensitive DNs from extracellular electrophysiological data, based on a range of receptive field parameters, and we think that these correspond to DNHS1 and DNOVS2 in Drosophila (Nicholas et al, J Comp Physiol A, 2020, cited in paper). As mentioned above in response to Reviewer 1, this does not mean that there are no other neurons that could respond to widefield optic flow, and which might be involved in the WBA we recorded in the paper. However, the point of this paper was not to conclusively show that there are only two optic flow sensitive descending neurons. The point was to say that there are two quite distinct optic flow sensitive neurons that have similar receptive fields in males and females, while the responses to widefield motion show differences between males and females.

We will modify the Introduction and Discussion to make these important points clear to the Reader, including the discussion of the 45-60 LPTCs that exist in the lobula plate, and what their role might be.

Second, this method feels somewhat impoverished given the richness of the data. The authors have nicely mapped out the directional tuning for almost the entire visual field. Instead of reducing this measurement to 2 values (center and direction), I was wondering if there is a better method to fully utilize the data at hand to get a better characterization of these DNs. As the authors are aware, local features alone can be ambiguous in characterizing optic flows. What's more, taking into account more global features can be useful for discovering potentially new cell types.

This is a great point, and we did an extensive analysis of other receptive field properties in this study (shown in supp fig 1). In addition, and as mentioned above, we have published a clustering analysis across receptive field properties of these neurons (Nicholas et al, J Comp Physiol A, 2020, cited in paper). The point that we attempted to make in this paper was that by using two strikingly simple metrics, we can reliably distinguish which of the two neuron types we are recording from (if we accept that there are two main types that we are likely to record from) simply based on location and overall directional preference. This makes automated analysis very easy and straightforward. Indeed, we now use this routinely to ID what neuron we are recording from, rather than making a human-based assumption.

However, we agree that further in depth analysis is warranted. Therefore, to address this, we will provide additional receptive field analysis and clustering in the revised version of the MS. In addition, we want to highlight that all data is uploaded to DataDryad for anyone interested in doing additional in-depth analyses.

Line 131, it wasn't clear to me why full-screen stimuli were used for comparison here, instead of the full receptive field maps. Male flies exhibit sexual dimorphic behaviors only during courtship, which would suggest that small-sized visual stimuli (mimicking an intruder or female conspecific) would be better suited to elicit dimorphic neuronal responses. A similar comment applies to the later results as well. Based on the receptive field mapping in Figure 1, I'm under the impression that these 2 DN types are more suited to detect wide-field optic flows, those induced by self-motion as mentioned in the manuscript. The results are still very interesting, but it's good to make this point clear early on to help set appropriate expectations. Conversely, this would also suggest that there are other visual DN types that are responsible for the courtship-related sexually dimorphic behaviors.

Thank you for mentioning these important points. Our reasoning for using full-screen stimuli for the analysis on line 131 was that since we used the small sinusoidal gratings for mapping the receptive fields, and to subsequently classify the neurons, it would be unfair to use the same data to investigate potential sexual dimorphism. I.e., we selected neurons that fulfilled certain criteria, and then we cannot rightfully use the same criteria to determine differences. This was not explicitly mentioned in the paper, so we will modify the text to make this clear to the Reader.

However, in Supp Figure 1d/e we show that there are no striking receptive field differences between males and females in terms of receptive field center nor directional preference. In Supp Figure 1f we show that there is no difference between male and female receptive field height and width. We will modify the text to draw the Reader’s attention to this figure, and also mention the additional analysis done in response to the comment above.

As a side note, I personally expected at least DNHS1 to have a smaller receptive field in males, as the hoverfly HSN is strikingly sexually dimorphic (Nordström et al, Curr Biol 2008), and also very sensitive to small objects. However, while optic flow sensitive DNs do respond to small objects (see e.g. the J Comp Physiol paper mentioned above) we did not detect any obvious sexual dimorphism in receptive field properties. Indeed, we think that a different subset of DNs control target pursuit behavior (target selective DNs (TSDNs)). This will be addressed in the modified version of the paper.

This section clearly shows that virality isn’t neutral and always involves tradeoffs between different groups. I liked how the examples highlight that what benefits platforms or audiences can still harm individuals, especially through misinformation or loss of privacy. It also made me think more about how recommendation systems should reflect ethical values, not just engagement metrics

This section does a great job showing how recommendation algorithms can unintentionally amplify polarization and even contribute to radicalization. The examples (Facebook reactions, Twitter quote-tweet dynamics, and the flat earth → QAnon pipeline) clearly illustrate how engagement-based systems can reward negativity and extreme content. I also appreciate the nuance at the end that polarization itself isn’t always bad, which keeps the discussion balanced rather than alarmist. Overall, this is a clear, well-supported explanation of why algorithmic design choices have serious social consequences beyond individual user intent.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #2 (Public review):

In this valuable manuscript, Lin et al attempt to examine the role of long non coding RNAs (lncRNAs) in human evolution, through a set of population genetics and functional genomics analyses that leverage existing datasets and tools. Although the methods are incomplete and at times inadequate, the results nonetheless point towards a possible contribution of long non coding RNAs to shaping humans, and suggest clear directions for future, more rigorous study.

Comments on revisions:

I thank the authors for their revision and changes in response to previous rounds of comments. As before, I appreciate the changes made in response to my comments, and I think everyone is approaching this in the spirit of arriving at the best possible manuscript, but we still have some deep disagreements on the nature of the relevant statistical approach and defining adequate controls. I highlight a couple of places that I think are particularly relevant, but note that given the authors disagree with my interpretation, they should feel free to not respond!

(1) On the subject of the 0.034 threshold, I had previously stated: "I do not agree with the rationale for this claim, and do not agree that it supports the cutoff of 0.034 used below."

In their reply to me, the authors state:

"What we need is a gene number, which (a) indicates genes that effectively differentiate humans from chimpanzees, (b) can be used to set a DBS sequence distance cutoff. Since this study is the first to systematically examine DBSs in humans and chimpanzees, we must estimate this gene number based on studies that identify differentially expressed genes in humans and chimpanzees. We choose Song et al. 2021 (Song et al. Genetic studies of human-chimpanzee divergence using stem cell fusions. PNAS 2021), which identified 5984 differentially expressed genes, including 4377 genes whose differential expression is due to trans-acting differences between humans and chimpanzees. To the best of our knowledge, this is the only published data on trans-acting differences between humans and chimpanzees, and most HS lncRNAs and their DBSs/targets have trans-acting relationships (see Supplementary Table 2). Based on these numbers, we chose a DBS sequence distance cutoff of 0.034, which corresponds to 4248 genes (the top 20%), slightly fewer than 4377."

I have some notes here. First, Agoglia et al, Nature, 2021, also examined the nature of cis vs trans regulatory differences between human and chimps using a very similar set up to Song et al; their Supplementary Table 4 enables the discovery of genes with cis vs trans effects although admittedly this is less straightforward than the Song et al data. Second, I can't actually tell how the 4377 number is arrived at. From Song et al, "Of 4,671 genes with regulatory changes between human-only and chimpanzee-only iPSC lines, 44.4% (2,073 genes) were regulated primarily in cis, 31.4% (1,465 genes) were regulated primarily in trans, and the remaining 1,133 genes were regulated both in cis and in trans (Fig. 2C). This final category was further broken down into a cis+trans category (cis- and transregulatory changes acting in the same direction) and a cis-trans category (cis- and trans-regulatory changes acting in opposite directions)." Even when combining trans-only and cis&trans genes that gives 2,598 genes with evidence for some trans regulation. I cannot find 4,377 in the main text of the Song et al paper.

Elsewhere in their response, the authors respond to my comment that 0.034 is an arbitrary threshold by repeating the analyses using a cutoff of 0.035. I appreciate the sentiment here, but I would not expect this to make any great difference, given how similar those numbers are! A better approach, and what I had in mind when I mentioned this, would be to test multiple thresholds, ranging from, eg,0.05 to 0.01 <DBS dist =0.01 -> 0.034 -> 0.05> at some well-defined step size.

(1) We sincerely thank the reviewer for this critical point. Our initial purpose, based on DBS distances from the human genome to chimpanzee genome and archaic genomes, was that genes with large DBS distances may have contributed more to human evolution. However, our ORA (overrepresentation analysis) explored only genes with large DBS distances (the legend of old Figure 2 was “1256 target genes whose DBSs have the largest distances from modern humans to chimpanzees and Altai Neanderthals are enriched in different Biological Processes GO terms”), with the use of the cutoff (threshold) of 0.034 for defining large distance. The cutoff is not totally unreasonable (as our new results and the following sensitivity analysis indicate), but this approach was indirect and flawed.

(2) We have now performed ORA using two methods. The first uses only DBS distances. Instead of using a cutoff, we now sort genes by DBS distance (human-chimpanzee distances and human-Altai Neanderthal distance, respectively, see Supplementary Table 5) and use the top 25% and bottom 25% of genes to perform ORA. This directly examines whether DBS distances along indicate that genes with large DBS distances contribute more to human evolution than genes with small DBS distances. The second also explores the ASE genes (allele-specific expression, genes undergoing human/chimpanzee-specific regulation in the tetraploid human–chimpanzee hybrid iPS) reported by Agoglia et al. 2021. We select the top 50% and bottom 50% of genes with large and small DBS distances, intersect them with ASE genes from Agoglia et al. 2021 (their Supplementary Table 4), and apply ORA to the intersections. Both the results are that: (a) more GO terms are obtained from genes with large DBS distances, (b) more human evolution-related GO terms are obtained from genes with large DBS distances (Supplementary Table 5,6,7; Figure 2; Supplementary Fig. 15). These results directly suggest that genes with large DBS distances contribute more to human evolution than genes with small DBS distances, which is a key theme of the study.

(3) Regarding Song et al 2021, the statement of “we differentiated…allotetraploid (H1C1a, H1C1b, H2C2a, H2C2b) lines into ectoderm, mesoderm, and endoderm” made us assume that their differentiated hybrid cell lines cover more tissue types than those of Agoglia et al. 2021. Now, upon re-examining Supplementary Table 5 of Song et al. and Supplementary Table 4 of Agoglia et al. 2021, we find that the latter more clearly indicates significant ASE genes (p-adj<0.01 and |LFC>0.5| in GRCh38 and PanTro5).

(4) We have also performed two additional analyses in response to the suggestion of “test multiple thresholds, ranging from, eg, 0.05 to 0.01 <DBS dist =0.01 -> 0.034 -> 0.05> at some well-defined step size”. First, we performed a multi-threshold sensitivity analysis using a spectrum of cutoffs (0.03, 0.034, 0.04, 0.05), and tracked the number of genes identified and the enrichment significance of key GO terms (e.g., "neuron projection development," "behavior") across these thresholds. The result confirms that while the absolute number of genes varies with the cutoffs, the core biological conclusion (specifically, the significant enrichment of target genes in neurodevelopmental and cognitive functions) remains stable and significant. For instance, "behavior" maintains strong statistical significance (FDR<0.01) in both the human-chimpanzee and human-Altai Neanderthal comparisons across all tested cutoffs, and "Neuron projection development" also remains significant across three (0.03, 0.034, 0.04) of the four cutoffs in the Altai comparison. This pattern suggests that our core findings regarding neurodevelopmental functions are robust across a range of cutoffs. Nevertheless, we did not extend the analysis to smaller cutoffs (e.g., 0.01 or 0.02) because such values would identify an excessively large number of genes (>10000) for ORA, which would render the GOterm enrichment analysis less meaningful due to a loss of specificity.

Second, we have performed an additional validation to directly evaluate whether the 0.034 cutoff itself represents a stringent and biologically meaningful value. We sought to empirically determine how often a DBS sequence distance of 0.034 or greater might occur by chance in promoter regions, thereby testing its significance as a marker of potential evolutionary divergence. We randomly sampled 10,000 windows from annotated promoter regions across the hg38 genome, each with a size matching the average length of DBSs (147 bp). We then calculated the per-base sequence distances for these random windows between modern humans and chimpanzees, as well as between modern humans and the three archaic humans (Altai, Denisovan, Vindija). The analysis reveals that a distance of ≥0.034 is a rare event in random promoter sequences: for Human-Chimp, Human-Altai, HumanDenisovan, and Human-Vindija, 5.49% (549/10000), 0.31% (31/10000), 4.47% (447/10000), and0.03% (3/10000) of random windows reach this distance. This empirical evidence suggests that 0.034 is a sufficiently strong cutoff for defining large DBS distance, it would occur very unlikely in a random genomic background (P<0.1 for Chimpanzee and P<0.05 for the archaic humans), and DBSs exceeding this cutoff are significantly enriched for sequences that have undergone substantial evolutionary change instead of being random neutral variations.  

(5) We present new Figure 2, Supplementary Table 5,6,7, and Supplementary Fig. 15. We have substantially revised section 2.3, related sections in Results, Supplementary Note 3, and Supplementary Table 8. We have removed related descriptions and explanations in the main text and Supplementary Notes. The results of the above two analyses are presented here as two Author response images.

Author response table 1.

Sensitivity analysis of GO-term enrichment across different DBS sequence distance cutoffs. The table shows the numbers of target genes identified and the false discovery rates (FDR) for the enrichment of three selected GO terms at four different distance cutoffs. Note that, unlike in the old Figure 2, the results for chimpanzees and Altai Neanderthals are not directly comparable here, as the numbers of target genes used for the enrichment analysis differ between them at each cutoff.

Author response image 1.

Distribution of per-base sequence distances for DBS size-matched random genomic windows in Ensembl-annotated promoter regions, calculated between modern humans and (A) chimpanzee, (B) Altai Neanderthal, (C) Denisovan, and (D) Vindija Neanderthal genomes.

(2) The authors have introduced a new TFBS section, as a control for their lncRNAs - this is welcome, though again I would ask for caution when interpreting results. For instance, in their reply to me the authors state: "The number of HS TFs and HS lncRNAs (5 vs 66) <HS TF vs all HS lncRNAs> alone lends strong evidence suggesting that HS lncRNAs have contributed more significantly to human evolution than HS TFs (note that 5 is the union of three intersections between <many2zero + one2zero> and the three <human TF list>)."

But this assumes the denominator is the same! There are 35899 lncRNAs according to the current GENCOVE build; 66/35899 = 0.0018, so, 0.18% of lncRNAs are HS. The authors compare this to 5 TFs. There are 19433 protein coding genes in the current GENCOVE build, which naively (5/19433) gives a big depletion (0.026%) relative to the lnc number. However, this assumes all protein coding genes are TFs, which is not the case. A quick search suggests that ~2000 protein coding genes are TFs (see, eg, https://pubmed.ncbi.nlm.nih.gov/34755879/); which gives an enrichment (although I doubt it is a statistically significant one!) of HS TFs over HS lncRNAs (5/2000 = 0.0025). Hence my emphasis on needing to be sure the controls are robust and valid throughout!

We thank the reviewer for this comment. While 5 vs 66 reveals a difference, a direct comparison is too simplified. The real take-home message of the new TFBS section is not the numbers but the distributions of HS TFs’ targets and HS lncRNAs’ targets across GTEx organs and tissues (Figure 3 and Supplementary Figures 24, 25) - correlated HS lncRNA-target transcript pairs are highly enriched in brain regions, but correlated HS TF-target transcript pairs are distributed broadly across GTEx tissues and organs. We have now removed the simple comparison of “5 vs 66” and more carefully explained our comparison in section 2.6.

(3) In my original review I said: line 187: "Notably, 97.81% of the 105141 strong DBSs have counterparts in chimpanzees, suggesting that these DBSs are similar to HARs in evolution and have undergone human-specific evolution." I do not see any support for the inference here. Identifying HARs and acceleration relies on a far more thorough methodology than what's being presented here. Even generously, pairwise comparison between two taxa only cannot polarise the direction of differences; inferring human-specific change requires outgroups beyond chimpanzee.

In their reply to me, the authors state:

Here, we actually made an analogy but not an inference; therefore, we used such words as "suggesting" and "similar" instead of using more confirmatory words. We have revised the latter half sentence, saying "raising the possibility that these sequences have evolved considerably during human evolution".

Is the aim here to draw attention to the ~2.2% of DBS that do not have a counterpart? In that case, it would be better to rewrite the sentence to emphasise those, not the ones that are shared between the two species? I do appreciate the revised wording, though.

(1) Our original phrasing may be misleading, and we agree entirely that “pairwise comparison between two taxa only cannot polarise the direction of differences; inferring human-specific change requires outgroups beyond chimpanzee”. As explained in that reply, we know and think that DBSs and HARs are two different classes of sequences, and indeed, identifying HARs and acceleration relies on a far more thorough methodology. Yet, three factors prompted us to compare them. First, both suggest the importance of sequences outside genes. Second, both are quite “old” sequences and have undergone considerable evolution recently (although the references are different). Third, both have contributed greatly to human brain evolution.  

(2) Here, our stress is 97.81% but not 2.2%, and we have made this analogy more clearly and cautiously. Relevant revisions have been made in the Results, Discussion, and Methods sections.   

(3) We also have further determined whether the 2.2% DBSs are human-specific gains by analyzing them using the UCSC Multiz Alignments of 100 Vertebrates. The result confirms that all 2248 DBSs are present in the human genome but are absent from the chimpanzee genome and all other aligned vertebrate genomes. We add this result into the manuscript.

(4) Finally, Line 408: "Ensembl-annotated transcripts (release 79)" Release 79 is dated to March 2015, which is quite a few releases and genome builds ago. Is this a typo? Both the human and the chimpanzee genome have been significantly improved since then!

(1) We thank the reviewer for this comment, which prompts us to provide further explanation and additional data. First, we began predicting HS lncRNAs’ DBSs when Ensembl release 79 was available, but did not re-predict DBSs when new Ensembl releases were published because (a) these new Ensembl releases are based also on hg38, (b) we did not find any fault in the LongTarget program during our use, nor received any one from users, (c) predicting lncRNAs’ DBSs using the LongTarget program is highly time-consuming.  

(2) Second, to assess the influence of newer Ensembl releases, we compared the promoters annotated in release 79 and in release 115. We found that the vast majority (87.3%) of promoters newly annotated in release 115 belong to non-coding genes. Thus, using release 115 may predict more DBSs in non-coding genes, but downstream analyses based on protein-coding genes would be essentially the same (meaning that all figures and tables would be the same).

(3) Third, a key element of this study is GTEx data analysis, and these data were also published years ago.  

(4) Finally, some lncRNA genes have new gene symbols in new Ensembl releases. To allow researchers to use our data conveniently, we have added a new column titled "Gene symbol (Ensembl release115)" to Supplementary Tables 2A and 2B.  

Summary:

Major changes based on Reviewer’s comments:

(1) The following revisions are made to address the comment on “the 0.034 threshold”: (a) Section 2.3, section 2.4, Supplementary Note 3, and related contents in Discussion and Methods are revised, (b) new Figure 2, Supplementary Figure 15, new Supplementary Table 5,6,7, (c) Table 2 and Supplementary Table 8 are revised.

(2) To address the comment on “new TFBS section”, section 2.6 and section 4.13 are revised.  

(3) To address the comment on “97.81% and 2.2% of DBSs”, section 2.3 is revised.

(4) The following revisions are made to address the comment on “release 79”: (a) the old Supplementary Table 2, 3 are merged to Supplementary Table 2AB, and the new column "Gene symbol (Ensembl release115)" is added to Supplementary Table 2AB, (b) accordingly, Supplementary Table 4,5 are renamed to Supplementary Table 3,4.

Additional revisions:

(1) Section 2.5 “Young weak DBSs may have greatly promoted recent human evolution” is moved into Supplementary Note 3 (which now has the subtitle “Target genes with specific DBS features are enriched in specific functions”), because this section is short and lacking sufficient cross-validation.

(2) Considerable minor revisions of sentences have been made.

(3) Since there are many supplementary figures, the main text now cites only Supplementary Notes, as the reader can easily access supplementary figures in Supplementary Notes.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

This article deals with the chemotactic behavior of E coli bacteria in thin channels (a situation close to 2D). It combines experiments and simulations.

The authors show experimentally that, in 2D, bacteria swim up a chemotactic gradient much more effectively when they are in the presence of lateral walls. Systematic experiments identify an optimum for chemotaxis for a channel width of ~8µm, close to the average radius of the circle trajectories of the unconfined bacteria in 2D. It is known that these circles are chiral and impose that the bacteria swim preferentially along the right-side wall when there is no chemotactic gradient. In the presence of a chemotactic gradient, this larger proportion of bacteria swimming on the right wall yields chemotaxis. This effect is backed by numerical simulations and a geometrical analysis.

If the conclusions drawn from the experiments presented in this article seem clear and interesting, I find that the key elements of the mechanism of this wall-directed chemotaxis are not sufficiently emphasized. Moreover, the paper would be clearer with more details on the hypotheses and the essential ingredients of the analyses.

We thank the reviewer for these constructive suggestions. We agree that emphasizing the underlying mechanism is crucial for the clarity of our findings. In the revised manuscript, we have now explicitly highlighted the critical roles of chiral circular motion and the alignment effect following side-wall collisions in both the Abstract (lines 25-27) and the Discussion (lines 391-393). Furthermore, we have added a new analysis of bacterial trajectories post-collision (Fig. S2), which demonstrates that cells predominantly align with and swim along the sidewalls. We have also clarified the assumptions in our numerical simulations, specifically how the radius of circular trajectories and the alignment effect are incorporated into the equations of motion. Please refer to our detailed responses in the "Recommendations for the authors" section for further specifics.

Reviewer #2 (Public review):

Summary:

In this study, the authors investigated the chemotaxis of E. coli swimming close to the bottom surface in gradients of attractant in channels of increasingly smaller width but fixed height = 30 µm and length ~160 µm. In relatively large channels, they find that on average the cells drift in response to the gradient, despite cells close to the surface away from the walls being known to not be chemotactic because they swim in circles.

They find that this average drift is due to the cell localization close to the side walls, where they slide along the wall. Whereas the bacteria away from the walls have no chemotaxis (as shown before), the ones on the left side wall go down-gradient on average, but the ones on the right-side wall go up-gradient faster, hence the average drift. They then study the effect of reducing channel width. They find that chemotaxis is higher in channels with a width of about 8 µm, which approximately corresponds to the radius of the circular swimming R. This higher chemotactic drift is concomitant to an increased density of cells on the RSW. They do simulations and modeling to suggest that the disruption of circular swimming upon collision with the wall increases the density of cells on the RSW, with a maximal effect at w = ~ 2/3 R, which is a good match for their experiments.

Strengths:

The overall result that confinement at the edge stabilises bacterial motion and allows chemotaxis is very interesting although not entirely unexpected. It is also important for understanding bacterial motility and chemotaxis under ecologically relevant conditions, where bacteria frequently swim under confinement (although its relevance for controlling infections could be questioned). The experimental part of the study is nicely supported by the model.

Weaknesses:

Several points of this study, in particular the interpretation of the width effect, need better clarification:

(1) Context:

There are a number of highly relevant previous publications that should have been acknowledged and discussed in relation to the current work:

https://pubs.rsc.org/en/content/articlehtml/2023/sm/d3sm00286a

https://link.springer.com/article/10.1140/epje/s10189-024-00450-7

https://doi.org/10.1016/j.bpj.2022.04.008

https://doi.org/10.1073/pnas.1816315116

https://www.pnas.org/doi/full/10.1073/pnas.0907542106

https://doi.org/10.1038/s41467-020-15711-0

http://doi.org/10.1038/s41467-020-15711-0

http://doi.org/10.1039/c5sm00939a

We appreciate the reviewer bringing these important publications to our attention. We have now cited and discussed these works in the Introduction (lines 55-62 and 76-85) to better contextualize our study regarding bacterial motility and chemotaxis in confined geometries.

(2) Experimental setup:

a) The channels are built with asymmetric entrances (Figure 1), which could trigger a ratchet effect (because bacteria swim in circle) that could bias the rate at which cells enter into the channel, and which side they follow preferentially, especially for the narrow channel. Since the channel is short (160 µm), that would reflect on the statistics of cell distribution. Controls with straight entrances or with a reversed symmetry of the channel need to be performed to ensure that the reported results are not affected by this asymmetry.

We appreciate the reviewer's insight regarding the potential ratchet effect caused by asymmetric entrances. To rule this out, we fabricated a control device with straight entrances and repeated the measurements. As shown in Figure S3, the chemotactic drift velocity follows the same trend as observed in the original setup, confirming an optimal width of ~9 mm. These results demonstrate that the entrance geometry does not bias the reported statistics. We have updated the manuscript text at lines 233-235.

b) The authors say the motile bacteria accumulate mostly at the bottom surface. This is strange, for a small height of 30 µm, the bacteria should be more-or-less evenly spread between the top and bottom surface. How can this be explained?

We apologize for not explaining this clearly in the text. As shown by Wei et al., Phys. Rev. Lett. 135, 188401 (2025), significant surface accumulation occurs in channels with heights exceeding 20 µm. In our specific experimental setup, we did not use Percoll to counteract gravity. Therefore, the bacteria accumulated mostly at the bottom surface under the combined influence of gravity and hydrodynamic attraction. This bottom-surface localization is supported by our observation that the bacterial trajectories were predominantly clockwise (characteristic of the bottom surface) rather than counter-clockwise (characteristic of the top surface). We have added this explanation to Line 141.

c) At the edge, some of the bacteria could escape up in the third dimension (http://doi.org/10.1039/c5sm00939a). What is the magnitude of this phenomenon in the current setup? Does it have an effect?

We thank the reviewer for raising this important point regarding 3D escape. We have quantified this phenomenon and found the escape rate from the edge into the third dimension to be 0.127 s^-1. This corresponds to a mean residence time that allows a cell moving at 20 mm/s to travel approximately 157.5 mm along the edge. Since this distance is comparable to the full length of our lanes (~160 mm), most cells traverse the entire edge without escaping. Furthermore, our analysis is based on the average drift of the surface trajectories per unit of time; this metric is independent of the absolute number of cells present. Therefore, the escape phenomenon does not significantly impact our conclusions. We have added a statement clarifying this at line 154.

d) What is the cell density in the device? Should we expect cell-cell interactions to play a role here? If not, I would suggest to de-emphasize the connection to chemotaxis in the swarming paper in the introduction and discussion, which doesn't feel very relevant here, and rather focus on the other papers mentioned in point 1.

The cell density in our experiments was approximately 1.3×10^-3 μm^-2. Given this low density, we do not expect cell-cell interactions to play a role in the observed behaviors.

Regarding the connection to swarming chemotaxis: We agree that our low-density setup differs from a high-density swarm; however, we believe the comparison remains relevant for two reasons. First, it provides a necessary contrast to studies showing surface inhibition of chemotaxis. Second, while we eliminate cell-cell interactions, we isolate the geometric aspect of swarming. In a swarm, cells move within narrow lanes created by their neighbors. Our device mimics this specific physical confinement by replacing neighboring cells with PDMS sidewalls. This allows us to decouple the effects of physical confinement from cell-cell interactions. We have added the text (Line 370) to clarify this rationale and have incorporated the additional references in introduction as suggested in point 1.

e) We are not entirely convinced by the interpretation of the results in narrow channels. What is the causal relationship between the increased density on the RSW and the higher chemotactic drift? The authors seem to attribute higher drift to this increased RSW density, which emerges due to the geometric reasons. But if there is no initial bias, the same geometric argument would induce the same increased density of down-gradient swimmers on the LSW, and so, no imbalance between RSW and LSW density. Could it be the opposite that the increased RSW density results from chemotaxis (and maybe reinforces it), not the other way around? Confinement could then deplete one wall due to the proximity of the other, and/or modify the swimming pattern - 8 µm is very close to the size of the body + flagellum. To clarify this point, we suggest measuring the bacterial distributions in the absence of a gradient for all channel widths as a control.

We thank the reviewer for this insightful comment regarding the causal relationship between cell density and chemotactic drift. We apologize if the initial explanation was unclear.

Regarding the no-gradient control: Without an attractant gradient (and no initial bias), there is no breaking of symmetry and the labels of "LSW" and "RSW" are arbitrary. Therefore, there will be no asymmetry in the bacterial distributions on both sides (within experimental fluctuations) in the absence of a gradient for any channel width.

Regarding the causality and density imbalance: We agree that the increased RSW density is a result of chemotaxis, which is then reinforced by the lane geometry especially at narrow lane width. The mechanism relies on the coupling of chemotactic bias with surface circularity. The angle ranges that lead to RSW-UG accumulation (Fig. 6A-C) coincide with the up-gradient direction. Because these cells experience suppressed tumbling (longer runs), they can maintain the steady circular trajectories required to reach and align with the RSW. Conversely, while pure geometric analysis suggests a similar potential for LSW-DG accumulation, these trajectories coincide with the down-gradient direction. These cells experience enhanced tumbling, which distorts the circular trajectories. This prevents them from effectively reaching the LSW and also increases the probability of them leaving the wall. Therefore, the causality is indeed a positive feedback loop: the attractant gradient creates an initial bias that allows the RSW-UG fraction to form stable trajectories; the optimal lane width (matching the swimming radius) then maximizes this capture efficiency, further enriching the RSW fraction and enhancing the overall drift.

We have added clarifications regarding these points in the revised manuscript (the last paragraph of “Results”).

(3) Simulations:

The simulations treat the wall interaction very crudely. We would suggest treating it as a mechanical object that exerts elastic or "hard sphere" forces and torques on the bacteria for more realistic modeling.

We appreciate the reviewer's suggestion to incorporate more detailed mechanical interactions, such as elastic or hard-sphere forces, for the wall collisions. While we agree that a full hydrodynamic or mechanical model would offer higher fidelity, our experimental observations suggest that a simplified kinematic approach is sufficient for the specific phenomena studied here.

As shown in the new Fig. S2, our analysis of cell trajectories in the 44-µm-wide channels reveals that cells colliding with the sidewalls tend to align with the surface almost instantaneously. The timescale required for this alignment is negligible compared to the typical wall residence time (see also Ref. 6). Consequently, to maintain computational efficiency without sacrificing the essential physics of the accumulation effect, we employed a coarse-grained phenomenological model where a bacterium immediately aligns parallel to the wall upon contact, similar to approaches used previously (Ref. 43). We have added relevant text to the manuscript on lines 168-171.

Notably, the simulations have a constant (chemotaxis independent) rate of wall escape by tumbling. We would expect that reduced tumbling due to up-gradient motility induces a longer dwell time at the wall.

We apologize for the confusion. The chemotaxis effect is indeed fully integrated into our simulation. Specifically, the simulated cells sense the chemical gradient and adjust their motor CW bias (B) accordingly. This adjustment directly modulates the tumble rate (k), calculated as k \= B/0.31 s^-1. Consequently, the wall escape rate is not constant but varies with the chemotactic response. We also imposed a maximum detention time limit which, when combined with the variable tumble rate, results in an average wall residence time of approximately 2 s, consistent with our experimental observations (Fig. S6B). We have clarified these details in the final section of 'Materials and Methods'.

Reviewer #3 (Public review):

This paper addresses through experiment and simulation the combined effects of bacterial circular swimming near no-slip surfaces and chemotaxis in simple linear gradients. The authors have constructed a microfluidic device in which a gradient of L-aspartate is established to which bacteria respond while swimming while confined in channels of different widths. There is a clear effect that the chemotactic drift velocity reaches a maximum in channel widths of about 8 microns, similar in size to the circular orbits that would prevail in the absence of side walls. Numerical studies of simplified models confirm this connection.

The experimental aspects of this study are well executed. The design of the microfluidic system is clever in that it allows a kind of "multiplexing" in which all the different channel widths are available to a given sample of bacteria.

While the data analysis is reasonably convincing, I think that the authors could make much better use of what must be voluminous data on the trajectories of cells by formulating the mathematical problem in terms of a suitable Fokker-Planck equation for the probability distribution of swimming directions. In particular, I would like to see much more analysis of how incipient circular trajectories are interrupted by collisions with the walls and how this relates to enhanced chemotaxis. In essence, there needs to be a much clearer control analysis of trajectories without sidewalls to understand the mechanism in their presence.

We thank the reviewer for this insightful suggestion. We agree that understanding how circular trajectories are interrupted by wall collisions is central to explaining the enhanced chemotaxis. While we did not explicitly formulate a Fokker-Planck equation, we have addressed the reviewer's core point by employing two complementary mathematical approaches that model the probability distribution of swimming directions and wall interactions:

(1) Stochastic simulations (Langevin approach): As detailed in the "Simulation of E. coli chemotaxis within lane confinements" subsection of “Results” and Figure 5, we modeled cells as self-propelled particles performing random walks. This model explicitly accounts for the "interruption" of circular trajectories by incorporating a constant angular velocity (circular swimming) and an alignment effect upon collision with sidewalls. These simulations successfully reproduced the experimental trends, confirming that the interplay between circular radius and lane width determines the optimal drift velocity.

(2) Geometric probability analysis: To provide the "intuitive understanding", we included a specific Geometrical Analysis section (the last subsection of “Results”) and Figure 6. This analysis mathematically formulates the problem by calculating the exact proportion of swimming angles that allow a cell to transition from a circular trajectory in the bulk to an up-gradient trajectory along the Right Sidewall (RSW). By integrating over the possible swimming directions, we derived the probability of wall interception as a function of lane width (w) and swimming radius (r). This analysis reveals that the interruption of circular paths is most favorable for chemotaxis when w » (0.7-0.8)´r.

(3) Control analysis: regarding the "control analysis of trajectories without sidewalls," we utilized the cells in the Middle Area (MA) of the wide lanes as an internal control. As shown in Fig. 2B and 4A, these cells exhibit typical surface-associated circular swimming (Fig. 3B) but generate zero net drift. This serves as the baseline "no sidewall" condition, demonstrating that the chemotactic enhancement is strictly driven by the rectification of circular swimming into wall-aligned motion at the boundaries.

The authors argue that these findings may have relevance to a number of physiological and ecological contexts. Yet, each of these would be characterized by significant heterogeneity in pore sizes and geometries, and thus it is very unclear whether or how the findings in this work would carry over to those situations.

We thank the reviewer for this important observation regarding environmental heterogeneity. We agree that we should be cautious about directly extrapolating to complex ecological contexts without qualification. We have revised the last sentence of the abstract to adopt a more measured tone: "Our results may offer insights into bacterial navigation in complex biological environments such as host tissues and biofilms, providing a preliminary step toward exploring microbial ecology in confined habitats and potential strategies for controlling bacterial infections."

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Key elements of the mechanism of wall-directed chemotaxis are not sufficiently emphasized:

For instance, the chirality of the trajectories is an essential part of the analysis but is mentioned only briefly in the introduction. In the geometrical analysis, I understand that one of the critical parameters is the angle at which bacteria "collide" with the walls. But, again, this remains largely implicit in the discussion. This comes to the point that these ideas are not even mentioned in the abstract which doesn't provide any hint of a mechanism. An analysis of the actual trajectories of the cells after they hit the walls, as a function of their initial angle would be helpful in comparison with the simulations and the geometrical analysis.

We appreciate the reviewer's insightful comment regarding the need to better emphasize the mechanism of wall-directed chemotaxis. We agree that the chirality of trajectories and the geometry of wall collisions are central to our analysis and were previously under-emphasized.

To address this, we have made the following revisions:

(1) We have revised the Abstract (lines 25-27) and the Discussion (lines 391-393) to explicitly highlight the crucial role of chiral circular motion and the alignment effect following sidewall collisions.

(2) We further analyzed bacterial trajectories at different collision angles. Typical examples are shown in Supplementary Fig. S2. We observed that cells tend to align with and swim along the sidewalls regardless of their initial collision angles. This finding is now described in the main text at lines 168-171.

The motion of the bacteria is modelled as run-and-tumble at several places in the manuscript, and in particular in the simulations. Yet, the trajectories of the bacteria seem to be smooth in this almost 2D geometry, except of course when they directly interact with the walls (I hardly see tumbles in the MA region in Figure 1B). Can the authors elaborate on the assumptions made in the numerical simulations? In particular, how is the radius of the trajectories included in these equations of motion (line 514)?

We apologize for the lack of clarity regarding the bacterial motion model. It has been established that while bacteria do tumble near solid surfaces, they exhibit a smaller reorientation angle compared to bulk fluids; in fact, the most probable reorientation angle on a surface is zero (Ref. 41). Consequently, tumbles are often difficult to distinguish from runs with the naked eye. Additionally, the trajectories in Figure 1B are plotted on a 44 mm ´ 150 mm canvas with unequal coordinate scales, which may further obscure the visual distinctness of tumbling events.

Regarding the equations of motion: We modeled the bacteria as self-propelled particles governed by the internal chemotaxis pathway, alternating between run and tumble states. As noted in the equations on lines 286 & 578, we incorporated the circular motion by introducing a constant angular velocity, −ν₀/r, during the run state. Here, ν₀ represents the swimming speed, r denotes the radius of circular swimming, and the negative sign indicates clockwise chirality. Furthermore, to model the hydrodynamic interaction with the boundaries, we assumed that when a cell collides with a sidewall, its velocity vector instantly aligns parallel to that wall.

The comparison of Figure 5B (simulations) with Figure 4B (experiments) does not strike me as so "similar". Why are the points at small widths so noisy (Figure 5AB)? Figure 5C is cut at these widths, it should be plotted over the entire scale.

We acknowledge that the agreement between simulation and experiment is less robust in the narrowest channels. The discrepancy and "noise" at small widths in Figure 5 arise from the limitations of the self-propelled particle model in highly confined geometries. Specifically, our simulation treats bacteria as point particles and does not explicitly calculate the physical exclusion (steric effects) caused by the finite size of the flagella and cell body.

In the experimental setup, steric constraints within narrow channels (comparable to the cell size) restrict the cells' ability to turn freely, effectively stabilizing their motion. However, because our model allows particles to reorient more freely than actual cells would in such confined spaces, it produces fluctuations and an overestimation of the drift velocity at small widths. If these confinement effects were fully incorporated, the cell density mismatch between the left and right sidewalls would be reduced, leading to lower drift velocities that match the experimental data more closely.

Regarding Figure 5C: Since the "active particle" assumption loses physical validity in channels narrower than the scale of the bacterium, the simulation results in this regime are not representative of biological reality. Plotting these non-physical points would distort the analysis. Therefore, we have maintained the truncation of Figure 5C at 4 mm to ensure the data presented is physically meaningful. We have added a clear discussion of these model limitations to the manuscript at lines 310-314.

These important precisions should be added to the text or in a supplementary section. A validated mechanism describing in detail the impact of the walls on the cell trajectories would greatly improve the conclusions.

We thank the reviewer for the suggestions. As noted in the responses above, we have incorporated the details concerning the simulation assumptions and the model limitations at narrow widths into the revised manuscript. We have performed further analysis of the collision trajectories between bacteria and the sidewalls. As illustrated in the new Fig. S2, the data confirms that cells tend to align with and swim along the sidewalls following a collision, regardless of the initial impact angle.

Reviewer #2 (Recommendations for the authors):

Minor points

(1) Related to swimming in 3D: The authors should specify the depth of field of the objective in their setup.

We thank the reviewer for pointing this out. We have calculated the depth of field (DOF) of our objective to be approximately 3.7 µm. This estimate is based on the standard formula:

where l = 610 nm (emission wavelength), n = 1.0 (refractive index), NA = 0.45 (numeric aperture), M = 20 (magnification), and e = 6.5 µm (camera resolution). We have added this specification to the "Microscopy and Data Acquisition" section of “Materials and Methods”.

(2) Related to the interpretation of the width effect: We think plotting the cell enrichment, ie the probabilities P in Figure 4B normalized to the expected value if cells were homogeneously distributed ((3µm)/w for the side walls, (w - 6µm)/w for the middle) would help understand the strength of the wall 'siphoning' effect.

We thank the reviewer for the suggestion. We have calculated the cell enrichment by normalizing the observed probabilities against the expected values for a homogeneous distribution, as suggested. The resulting relationship between cell enrichment and lane width is presented in Figure S4.

Related to simulations:

(1) Showing vd for the 3 regions in Figure S5 would be helpful also to understand the underlying mechanism.

We thank the reviewer for the suggestion. The V_d values for the three regions are shown in Fig. S5.

(2) Figure 5B vs 4B: There is a mismatch in the right vs left side density at w=6µm in the simulations that is not here in the experiments. What could explain this difference?

We appreciate the reviewer pointing this out. The mismatch in the simulations is due to the simplified treatment of cells as self-propelled particles, which overlooks the physical volume of the cell body and flagella. In narrow channels (w\=6 mm), these physical constraints would restrict the cells' ability to change direction freely - a factor not fully captured in the simulation. Accounting for these steric effects would trap cells more effectively against the walls, reducing the density asymmetry between the LSW and RSW and lowering the drift velocity. This would bring the simulation results closer to the experimental observations. We have added a discussion of these limitations and effects to the revised manuscript (lines 310-314).

(3) The simulations essentially assume that the density of motile cells is homogeneous and equal at both x=0 and x=L open ends of the channel. Is it the case in the experiments, even with the gradient, and the walls creating some cell transport?

We thank the reviewer for pointing this out. The simulation assumption is consistent with our experimental observations. Our data were recorded within 160-μm-long lanes located in the center of the wider (400 μm) cell channel. In this central region, the cells maintain a continuous flux. Furthermore, experiments were performed within 8 min of flow, limiting the time for significant cell density gradients to establish. As illustrated in Author response image 11, the inhomogeneity in the measured cell density distribution is insignificant across the length of the observation window, indicating that the walls and gradient do not create significant heterogeneity at the boundaries of the region of interest.

Author response image 1.

The cell density distribution along the gradient field from the data of 44-μm-wide lane.

(4) Line 506: There is something strange with the definition of the bias. B cannot be the tumbling bias if k=B/0.31 s^-1 and the tumble-to-run rate is 5/s, because then the tumbling bias is B/0.31 / (B/0.31 + 5). Please clarify.

We apologize for the confusion caused by the notation. In our model, B represents the CW bias of the individual flagellar motor, not the macroscopic tumbling bias of the cell. We assume the run-to-tumble rate is equivalent to the motor CCW-to-CW switching rate (k). Previous studies have shown that this rate increases linearly with the motor CW bias according to k=B/t, where t is a characteristic time (Ref. 50).

Based on experimental data for wildtype cells, the average run time in the near-surface region is ~2.0 s (corresponding to a run-to-tumble rate of ~0.5 s^-1) (Ref. 11), and the steady-state wildtype CW bias is ~0.15. Using these values, we determined t ~ 0.31 s. Consequently, the switching rate is defined as k=B/0.31 s^-1. Since the tumble duration is constant (0.2 s) (Ref. 51), the tumble-to-run rate is fixed at 5 s^-1. We have clarified these definitions and parameter values in lines 569-573.

Other minor comments:

(1) Line 20 and lines 34-35: We think that the connection to infection is questionable here and should be toned down.

Thank you for the suggestion. We have revised Line 20 to read: “Understanding bacterial behavior in confined environments is helpful to elucidating microbial ecology and developing strategies to manage bacterial infections.” Additionally, we modified lines 34-35 to state: “Our results may offer insights into bacterial navigation in complex biological environments such as host tissues and biofilms, providing a preliminary step toward exploring microbial ecology in confined habitats and potential strategies for controlling bacterial infections.”

(2) Line 49: Consider highlighting the change in the sense of rotation at the air-liquid interface.

Thank you for the suggestion. We have now highlighted the difference in chirality between trajectories at the air-liquid interface and those at the liquid-solid interface. The text has been updated to read: “For example, E. coli swim clockwise when observed from above a solid surface, whereas Caulobacter crescentus move in tight, counter-clockwise circles when viewed from the liquid side.”

(3) Lines 58-59: The sentence should be better formulated, explaining what is CheY-P and that its concentration changes because of a change in phosphorylation (P).

Thank you for the suggestion. We have reformulated this section to explicitly define CheY-P and explain how its concentration is regulated through phosphorylation. The revised text reads: “The transmembrane chemoreceptors detect attractants or repellents and transmit signals into the cell by modulating the autophosphorylation of the histidine kinase CheA. Attractant binding suppresses CheA autophosphorylation, while repellent binding promotes it. This modulation alters the concentration of the phosphorylated response regulator protein, CheY-P.”

(4) Lines 63-64: CheR CheB do a bit more than "facilitating" adaptation, they mediate it. The notation CheB(p) may be confusing, since "-P" was used above for CheY.

Thank you for pointing this out. We have corrected the notation and strengthened the description of the enzymes' roles. The revised text is: “The adaptation enzymes CheR and CheB methylate and demethylate the receptors, respectively, mediating sensory adaptation.”

(5) Line 130: there must be a typo in the formula.

We have replaced the ambiguous lag time variable in Fig. 1C with _n_Δt to ensure mathematical consistency.

(6) Additionally, \Delta t is both the time between the frame here and the lag time in Figure 1.

Thank you for highlighting this ambiguity. We have updated the notation to distinguish these two values. The lag time in Figure 1 is now explicitly denoted as _n_Δt, while Δt remains the time interval between individual frames.

(7) Line 162: "Consistent with previous reports," a reference to said reports is missing.

Thank you for pointing this out. We have now added the reference (Ref. 41) to support this statement.

(8) Figure 1B: Are these tracks in the presence of a gradient? Same as used in panel C? This needs to be explained.

Response: Thank you for this question. We confirm that the tracks shown in Figure 1B were indeed recorded in the presence of a gradient and represent a subset of the data used in Figure 1C. We have clarified this in the figure legend as follows: "Thirty bacterial trajectories selected from the data of the 44-mm-wide lane in gradient assays. These represent a subset of the trajectories analyzed in panel C."

(9) Simulations: the equation for x(t) should also be given for completeness.

Thank you for the suggestion. For completeness, we have added the position updating equations for the run state to the Materials and Methods section (lines 579-580). The equations are defined as:

(10) Figure S2: For the swimming directions that are more unstable due to the surface friction torque, RSW-DG, and LSW-UG, one would have expected that the Up-gradient motion is more persistent than the down gradient one. It seems to be the opposite. Is it significant, and what could be the reason for this?

We apologize for the lack of clarity in our original explanation. While we would generally expect up-gradient motion to be more persistent than down-gradient motion in bulk fluid, our measurements near the surface show a different trend due to the specific contributions of run and tumble states to the escape rate. Cells swimming up-gradient (UG) in the LSW experience higher probability of running. Consequently, they are subjected to the destabilizing surface friction torque for a greater proportion of time compared to cells swimming down-gradient (DG) in the RSW. This can be explained mathematically. The escape rates for RSW-DG and LSW-UG can be expressed as:

Where B⁺ and B⁻ represent the tumble bias (probability of tumbling) when swimming up-gradient and down-gradient, respectively, and k_T and k_R denote the escape rates during a tumble and a run, respectively. Due to the chemotactic response, 0≤ B⁺< B⁻ ≤1. Crucially, our system is characterized by k_R>k_T (the escape rate is higher during a run than a tumble). Therefore, the lower tumble bias during up-gradient swimming (B⁺< B⁻) increases the weight of the run-state escape term((1−B⁺)k_R), leading to a higher overall escape rate for LSW-UG compared to RSW-DG. We have added an intuitive understanding of k_R>k_T in the Supplemental text.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Reviewer #1

Evidence, reproducibility and clarity

Authors should be commended for the availability of data/code and detailed methods. Clarity is good. Authors have clearly spent a lot of time thinking about the challenges of metabolomics data analysis.

Significance

Schmidt et al. present MetaProViz, a comprehensive and modular platform for metabolomics data analysis. The tool provides a full suite of processing capabilities spanning metabolite annotation, quality control, normalization, differential analysis, integration of prior knowledge, functional enrichment, and visualization. The authors also include example datasets, primarily from renal cancer studies, to demonstrate the functionality of the pipeline. The MetaProViz framework addresses several long-standing challenges in metabolomics data analysis, particularly issues of reproducibility, ambiguous metabolite annotation, and the integration of metabolite features with pathway knowledge. The platform is likely to be a valuable addition for the community, but the reviewer has some comments that need to be addressed prior to publication.

We thank the reviewer for this positive feedback.

Comments:

(1) (Planned)

The section "Improving the connection between prior knowledge and metabolomics features" could benefit from additional clarification. It is not entirely clear to the reader what specific steps were taken beyond using RaMP-DB to translate metabolite identifiers. For example, how exactly were ambiguous mappings ("different scenarios") handled in practice, and to what extent does this process "fix" or merely flag inconsistencies? A more explicit description or example of how MetaProViz resolves these cases would help readers better understand the improvements claimed.

We thank the reviewer for pointing this out and we agree that this section requires extension to ensure clarity. Beyond using RaMP-DB, we are characterising the mapping ambiguity (one-to-none, one-to-many, many-to-one, many-to-many) within and across metabolite-sets (i.e. pathways) and return this information to the user together with the translated identifiers. This is important to understand potential inflation/deflation of metabolite-sets that occur due to the translation. Moreover, we also offer the manually curated amino-acid collection to ensure L-, D- and zwitterion without chirality IDs are assigned for aminoacids (Fig. 2b). Ambiguous mappings are handled based on the measured data (Fig. 2e). Indeed, many translation cases that deflate (many-to-one mapping) or inflate (one-to-many mapping) the metabolite-sets are resolved when merging the prior knowledge with actual measured data (i.e. Fig. 2e, one-to-many in scenario 1, which becomes obsolete as only one/none of the many potential metabolite IDs is detected). By sorting each mapping into one of those scenarios, we only flag those cases. The reason for this decision has been that in many cases multiple decisions are valid (i.e. Fig. 2e, Scenario 5: Here the values of the two detected metabolites could be summed or the metabolite value with the larger Log2FC could be kept) and it should really be up to the user to make those dependent on their knowledge of the biological system and the analytical LC-MS method used.

Since these points have not been clear enough, we will add a more explicit description to the results section by showcasing more details on how we exactly tackled this problem in the ccRCC example data. This has also been suggested by Reviewer 3 (Minor Comment 7 and 8), so feel free to also see the responses below.

(2) (Planned)

The introduction of MetSigDB is intriguing, but its construction and added value are not sufficiently described. It would be helpful to clarify what specific advantages MetSigDB provides over directly using existing pathway resources such as KEGG, Reactome, or WikiPathways. For example, how many features, interactions, or metabolite-set relationships are included, and in what way are these pathways improved or extended compared to those already available in public databases?

We thank the reviewer for this valuable comment and we apologise that this was not described sufficiently. One of the major advantages is that all the resources are available in one place following the same table format without the need to visit the different original resources and perform data wrangling prior to enrichment analysis. In addition, where applicable, we have removed metabolites that are not detectable by LC-MS (i.e. ions, H2O, CO2) to circumvent pathway inflation with features that are never within the data and hence impacting the statistical testing in enrichment analysis workflows.

During the revision, we will compile an Extended Data Table listing all the resources present in MetSigDB, their number of features and interactions. We will also extend the methods section "Prior Knowledge access" about MetSigDB and how we removed metabolites.

(3)

Figure 1D/1E: The reviewer appreciates the inclusion of the visualizations illustrating the different mapping scenarios, as these effectively convey the complexity of metabolite ID translation. However, it took some time to interpret what each scenario represented. It would be helpful to include brief annotations or explanatory text directly on the figures to clarify what each scenario depicts and how it relates to the underlying issue being addressed.

*We think the reviewer refers to Fig. 2D/E and we acknowledge that this is a complex problem we try to convey. We received a similar comment from Reviewer 2 (Minor Comment 1), who asked to extend the figure legend description of what the different scenarios display. *

We have extended the figure legend and specifically explained each displayed case and its meaning (Line 222-242):

"d-e) Schematics of possible mapping cases between metabolite IDs (= each circle corresponds to one ID) of a pathway-metabolite set (e.g. KEGG) to metabolites IDs of a different database (e.g. HMDB) with (d) showing many-to-many mappings that can occur within and across pathway-metabolite sets and (e) additionally showing the mapping to metabolite IDs that were assigned to the detected peaks within and across pathway-metabolite sets. (d) __Translating the metabolite IDs of a pathway-metabolite set can lead to special cases such as many-to-one mappings (Pathway 1), where for example the original resource used the ID for L-Alanine (Pathway 1, green) and D-Alanine (Pathway 1, yellow) in the amino-acid pathway, whilst the translated resources only has an entry for Alanine zwitterion (Pathway 1, blue). Additionally, many-to-one mappings can also occur across pathways (Pathway 2-4), where this mapping is only detected when mappings are analysed taking all pathways into account. Both of these cases deflate the pathways, which can also happen for one-to-none mappings (Pathway 1, white). There are also cases that inflate the pathway such as one-to-many mappings (e.g. Pathway 2-4, orange mapping to pink and violet). (e)__ Showcasing the different scenarios when merging measured data (detected) based on the translated metabolites within pathways (scenario 1-5) and across pathways (scenario 6-8) highlighting problematic scenarios (4-7) that require further actions. Unproblematic scenarios (1-3 and 8) can include special cases between original and translated (i.e. one-to-many in scenario 1), which become obsolete as only one/none of the many potential metabolite IDs is detected. Yet, if multiple metabolites are detected action is required (scenario 5), which can include building the sum of the multiple detected features or only keeping the one with the highest Log2FC between two conditions. Other special cases between original and translated (i.e. many-to-one in scenario 4 and 6) also depend on what has been mapped to the measured features. If features have been measured in those scenarios, pathway deflation (i.e. only one original entry remains) or measured feature duplication (the same measurement is mapped to many features in the prior knowledge) are the possible results within and across pathways. Those scenarios should be addressed on a case-by-case basis as they also require biological information to be taken into account."

We have also rearranged the Scenarios in Fig. 2e. We hope that together with the extended figure legend this is now clear.

(4) (Planned)

"By assigning other potential metabolite IDs and by translating between the present ID types, we not only increase the number of features within all ID types but also increase the feature space with HMDB and KEGG IDs (Fig. 2a, right, SFig. 2 and Supplementary Table 1)". The reviewer would appreciate additional clarification on how this was done. It is not clear what specific steps or criteria were used to assign additional metabolite IDs or to translate between identifier types. The reviewer also appreciates the inclusion of the UpSet plots. However, simply having the plots side-by-side makes it difficult to determine the specific differences. An alternative visualization, such as stacked bar plots, scatter plots summarizing the changes in feature counts, or other representation that more clearly highlights the deltas, might make these results easier to interpret.

The main Fig. 2a shows the original (left) metabolite ID availability per detected metabolite feature in the ccRCC data and the adapted (right) metabolite IDs. The individual steps taken to extend the metabolite ID coverage of the measured features and obtain Fig 2a (right), are shown in SFig. 2 for HMDB (SFig. 2a) and KEGG (SFig. 2b). We did not include the plots for the pubchem IDs as they follow the same principle. The individual steps we are showcasing with SFig. 2 are (I) How many of the detected features (577) have a HMDB ID (341, red bar + grey bar), (II) How this distribution changed after equivalent amino-acid IDs are added, which does not change the number of features with an HMDB ID, but the number of features with a single HMDB ID, and (III) How this distribution changed after translating from the other available ID types (KEGG and PubChem) to HMDB IDs using RaMP-DBs knowledge, which leads to 430 detected features with one or multiple HMDB IDs. The exact numbers can be extracted from Supplementary Table 1, Sheet "Feature metadata", where for example N-methylglutamate had no HMDB ID assigned in the original publication (see column HMDB_Original), yet by translating HMDB from KEGG (hmdb_from_kegg) and PubChem (see column hmdb_from_pubchem) we obtain in both cases the same HMDB ID "HMDB0062660". In order to clarify this in the manuscript, we have extended the figure legend of SFig. 2: "a-b) Bargraphs showing the frequency at which a certain number of metabolite IDs per integrated peak are available as per ccRCC patients feature metadata provided in the original publication (left), after potential equivalent IDs for amino-acid and amnio-acid-related features were assigned (middle), which increases the number of features with multiple (middle: grey bars) and after IDs were translated from the other available ID types (right). for a) Of 577 detected features, 341 had at least one HMDB IDs assigned (left graph, red + grey bar) according to the original publication (left). Translating from KEGG-to-HMDB and from PubChem-to-HMDB increased the number of features with an HMDB ID from 341 to 430 (left). and __b) __Of 577 detected features, 306 had at least one KEGG IDs assigned (left graph, red + grey bar) according to the original publication (left). Translating from HMDB-to-KEGG and from PubChem-to-KEGG did not increase the total number of features with an KEGG ID (left)."

We like the suggestion of the reviewer to provide representations of the deltas and will add additional plots to SFig. 2 as part of our planned revision.

(5) (Planned)

MetaboAnalyst is mentioned several times in the manuscript. The reviewer is familiar with some of the limitations and practical challenges associated with using MetaboAnalyst and its R package. Given that MetaboAnalyst already offers some overlapping functionality with MetaProViz (and offers it in the form of an interactive website and a sometimes functional R package), a more explicit comparison between the two tools would help readers fully understand the unique advantages and improvements provided by MetaProViz.

This is a good point the reviewer raises. As part of the revisions, we plan to create a supplementary data table that includes both tools and their respective features. We will refer to this table within the manuscript text.

(6)

Page 11: The authors state that they used limma for statistical testing, including for the analysis of exometabolomics data, where the values appear to represent log2-transformed distances or ratios rather than normally distributed intensities. Since limma assumes approximately normal residuals, please provide evidence or justification that this assumption holds for these data types. If the distributions deviate substantially from normality, a non-parametric alternative might be more appropriate.

For exometabolomics data we use data normalised to media blank and growth factor (formula (1)). Limma is performed on those data, not on the log2-transformed distances. The Log2(Distance) is calculated separately to the statistical results using the normalised exometabolomics data. In addition, we always perform the Shapiro-Wilk test as part of MetaProViz differential analysis function on each metabolite to understand the distribution. In this particular case we have the following distributions:

Cell line

Metabolites normal distribution [%]

Metabolites not-normal distribution [%]

HK2

82.35

17.65

786-O

95.71

4.29

786-M1A

97.14

2.86

786-M2A

88.57

11.43

OSRC2

92.86

7.14

OSLM1B

85.71

14.29

RFX631

97.14

2.86

If a user would have distributions that deviate substantially from normality, non-parametric alternatives are also available in MetaProViz (see methods section for all options).

7)

Page 13: why were young and old defined this way? Authors should provide their reasoning and/or citations for this grouping.

We thank the reviewer for pointing this out. The explanation of our choices of the age groups is purely based on the literature:

First, ccRCC can be sporadic (>96%) or familial (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3308682/pdf/nihms362390.pdf). This was also observed in other cohorts, where of 1233 patients only 93 were under 40 years of age (%, whilst 1140 (%) were older than 40 years (https://www.europeanurology.com/article/S0302-2838(06)01316-9/fulltext). Second, given the high frequency of sporadic cases it is unsurprising that ccRCC incidences were found to peak in patients aged 60 to 79 years with more male than female incidences (https://journals.lww.com/md-journal/Fulltext/2019/08020/Frequency,_incidence_and_survival_outcomes_of.49.aspx). Third, it was shown that sex impacts on the renal cancer-specific mortality and is modified by age, which is a proxy for hormonal status with premenopausal period below 42 years and postmenopausal period above 58 years (https://www.ncbi.nlm.nih.gov/pmc/articles/PMC4361860/pdf/srep09160.pdf). Putting all of this information together, we decided on our age groups of young (58years) following the hormonal period in order to account for sex impact. Additionally, our young age group is representative of the age of familial ccRCC, whilst our old age group summarises the age group where incidences were found to peak.

To make this clear in the manuscript we have extended the method section of the manuscript (Line 547-548):

"For the patient's ccRCC data, we compared tumour versus normal of two patient subset, "young" (58years)."

(8)

Figure 4e: It may help with interpretation to have these Sankey-like graph edges be proportional to the number of metabolites.

We thank the reviewer for this suggestion, which we also pondered. When we tested this visualisation, the plot became convoluted, hard to interpret and not all potential flows exist in the data. This is why we have opted to create an overview graph of each potential flow, with each edge representing a potentially existing flow. The number of times a flow exists is shown in Fig. 4f.

(9)

Figure 4h: The values appear to be on an intensity scale (e.g., on the order of 3e10), yet some of them are negative, which would not be expected for raw or log-transformed mass spectrometry intensities. It is unclear whether these represent normalized abundance values, distances, or some other transformation. In addition, for the comparison of tumour versus normal tissue, it is not specified what statistical test was applied. Since mass spectrometry data are typically log2-transformed to approximate a log-normal distribution before performing t-tests or similar parametric methods, clarification is needed on how these data were processed.

Thanks for pointing this out, it made us realize that we need to extend our figure legend for clarity for Fig. 4h (Line 343-345). In both cases we show normalized intensities following the workflow described in Fig. 3a. In case of the left graph labelled "CoRe", we are plotting an exometabolomics experiment, were additionally normalised using both media blanks (samples where no cells were cultured in) and growth factor (accounts for cell growth during experiment) as growth rate (accounts for variations in cell proliferation) has not been available (see also formula (1) in methods section). A result has a negative value if the metabolite has been consumed from the media, or a positive value if the metabolite has been released from the cell into the culture media.

In addition, the reviewer refers to the comparison of tumour versus normal (Fig. 4a __and 4d__) and the missing description of the chosen statistical test. We have added the details to the figure legend (Lines 334 and 345).

Adapted legend Fig. 4: "a) Differential metabolite analysis results for exometabolomics data comparing 786-O versus HK2 cells using Annova and false discovery rate (FDR) for p-value adjustment. b) __Heatmap of mean consumption-release of the measured metabolites across cell lines. c) Heatmap of normalised ccRCC cell line exometabolomics data for the selected metabolites of amino acid metabolism for a sample subset. __d) __Differential metabolite analysis results for intracellular data comparing 786-O versus HK2 cells using Annova and false discovery rate (FDR) for p-value adjustment. __e) __Schematics of bioRCM process to integrate exometabolomics with intracellular metabolomics and __f) __number of metabolites by their combined change patterns in intracellular- and exometabolomics in 786-M1A versus HK2. g)__ Heatmap of the metabolite abundances in the "Both_DOWN (Released/Comsumed)" cluster. __h) __Bar graphs of normalised methionine intensity for exometabolomics (CoRe: negative value, if the metabolite has been consumed from the media, or a positive value, if the metabolite has been released from the cell into the culture media) and intracellular metabolomics (Intra)."

(10)

Figure 5: "Tukey's p.adj We thank the reviewer for pointing this out. We have used the TukeyHSD (Tukey's Honestly Significant Difference) test in R on the Anova results. We have added more details into the figure legend (Line 384): "(Tukey's post-doc test after anova p.adj<br /> (11)

The potential for multi-omics is mentioned. Please clarify how generalizable this framework is. Can it readily accommodate transcriptomics, proteomics, or fluxomics data, or does it require custom logic or formatting for each new data type?

Thanks for raising this question. MetaProViz can readily accommodate transcriptomics and proteomics data for combined enrichment analysis using for example MetalinksDB metabolite-receptor pairs. Yet, MetaProViz does not support modelling fluxomics data into metabolic networks. We state in the discussion that this could be future development ("Beyond current capabilities, future developments could also incorporate mechanistic modeling to capture metabolic fluxes, subcellular compartmentalization, enzyme kinetics, regulatory feedback loops, and thermodynamic constraints to dissect metabolic response under perturbations."). To clarify on the availability of multi-omics integration for combined enrichment analysis, we have added some more details into the discussion section.

Line 467-469: "In addition, providing knowledge of receptor-, transporter- and enzyme-metabolite pairs, MetaProViz can readily accommodate transcriptomics and proteomics data for combined enrichment analysis."

(12)

Please clarify if/how enrichment analyses account for varying set sizes and redundant metabolite memberships across pathways, which can bias over-representation analysis results.

This is a very relevant point, which we have already been working on. Indeed, we agree that enrichment results from enrichment analyses can be biased due to varying set sizes and redundant metabolite memberships across pathways. MetaProViz explicitly accounts for varying set sizes when running over representation analysis (functions standard_ora()and cluster_ora()), which uses a model that computes the p-value under a hypergeometric distribution. Thereby, larger pathways are penalized unless the overlap is proportionally large, while smaller pathways can be significant with fewer overlaps. Hence, the test quantifies whether the observed overlap between the query set and a pathway is larger than would be expected under random sampling. In addition, we explicitly filter by gene‑set size using min_gssize/max_gssize, which further controls for extreme small or large sets. So both the statistical test itself and the size filters incorporate gene‑set size variation.

Regarding the redundant metabolite-set (i.e. pathways) memberships, we have now implemented a new function (cluster_pk()) to cluster metabolite-sets like pathways based on overlapping metabolites. Thereby we allow investigation of enrichment results in regard to redundancy and similarity. For given metabolite-sets, the function calculates pathway similarities via either overlap- or correlation-based metrics. After optional thresholding to remove weak similarities, we implemented three clustering algorithms (connected-components clustering, Louvain community detection and hierarchical clustering) to group similar pathways. We then visualize the clustering results as a network graph using the new function viz_graph based on igraph. We have added all information into our methods section "Metabolite-set clustering" (Lines 656-671). In addition, we have also added the results of the clustering into Fig. 5f.

New Fig. 5f:"f) *Network graph of top enriched pathways (p.adjusted

Reviewer #2

Evidence, reproducibility and clarity

Schmidt et al report the development of MetaProViz, an integrated R package to process, analyze and visualize metabolomics data, including integration with prior knowledge. The authors then go on to demonstrate utility by analyzing several metabolomes of cell lines, media and patient samples from kidney cancer. The manuscript provides a concise description of key challenges in metabolomics that the authors identify and address in their software. The examples are helpful and illustrative, although I should point out that I lack the expertise to evaluate the R package itself. I only have a few very minor comments.

Significance

This is a very significant advance from one of the leading groups in the field that is likely to enhance metabolomics data analysis in the wider community.

We thank the reviewer for this positive feedback on our package. We appreciate that there are no major comments from the reviewer.

Minor comments:

(1)

Figure 2D, E: While the schematics are fairly intuitive, a brief figure legend description of what the different scenarios etc. represent would make this easier to grasp.

We thank the reviewer for pointing this out and we acknowledge that this is a complex problem we try to convey. We received a similar comment from Reviewer 1 (Comment 3), so please see the extensive response there. In brief, we have extended the figure legend and specifically explained each displayed case and its meaning (Line 222-242) and extended the Figure itself by adding additional categories to Fig. 2e.

Extended legend Fig.2 d-e: "d-e) Schematics of possible mapping cases between metabolite IDs (= each circle corresponds to one ID) of a pathway-metabolite set (e.g. KEGG) to metabolites IDs of a different database (e.g. HMDB) with (d) showing many-to-many mappings that can occur within and across pathway-metabolite sets and (e) additionally showing the mapping to metabolite IDs that were assigned to the detected peaks within and across pathway-metabolite sets. (d) __Translating the metabolite IDs of a pathway-metabolite set can lead to special cases such as many-to-one mappings (Pathway 1), where for example the original resource used the ID for L-Alanine (Pathway 1, green) and D-Alanine (Pathway 1, yellow) in the amino-acid pathway, whilst the translated resources only has an entry for Alanine zwitterion (Pathway 1, blue). Additionally, many-to-one mappings can also occur across pathways (Pathway 2-4), where this mapping is only detected when mappings are analysed taking all pathways into account. Both of these cases deflate the pathways, which can also happen for one-to-none mappings (Pathway 1, white). There are also cases that inflate the pathway such as one-to-many mappings (e.g. Pathway 2-4, orange mapping to pink and violet). (e)__ Showcasing the different scenarios when merging measured data (detected) based on the translated metabolites within pathways (scenario 1-5) and across pathways (scenario 6-8) highlighting problematic scenarios (4-7) that require further actions. Unproblematic scenarios (1-3 and 8) can include special cases between original and translated (i.e. one-to-many in scenario 1), which become obsolete as only one/none of the many potential metabolite IDs is detected. Yet, if multiple metabolites are detected action is required (scenario 5), which can include building the sum of the multiple detected features or only keeping the one with the highest Log2FC between two conditions. Other special cases between original and translated (i.e. many-to-one in scenario 4 and 6) also depend on what has been mapped to the measured features. If features have been measured in those scenarios, pathway deflation (i.e. only one original entry remains) or measured feature duplication (the same measurement is mapped to many features in the prior knowledge) are the possible results within and across pathways. Those scenarios should be addressed on a case-by-case basis as they also require biological information to be taken into account."

(2) Fig. 4: The authors briefly state that they integrate prior knowledge to identify the changes in methionine metabolism in kidney cancer, but it is not clear how exactly they contribute to this conclusion. It could be helpful to expand a bit on this to better illustrate how MetaProViz can be used to integrate prior knowledge into the analysis workflow.

We think the reviewer refers to this section in the text (Line 363-370):

"Next, we focused on the cluster "Both_DOWN (Released-Consumed)" and found that several amino acids are consumed by the ccRCC cell line 786-M1A but released by healthy HK2 cells. At the same time, intracellular levels are significantly lower than in HK2 (Log2FC = -0.9, p.adj = 4.4e-5) (Fig. 4g). To explore the role of these metabolites in signaling, we queried the prior knowledge resource MetalinksDB, which includes metabolite-receptor, metabolite-transporter and metabolite-enzyme relationships, for their known upstream and downstream protein interactors for the measured metabolites (Supplementary Table 5). This approach is especially valuable for exometabolomics, as it allows us to generate hypotheses about cell-cell communication. Notably, we identified links involving methionine (Fig. 4h), enzymes such as BHMT, and transporters such as SLC43A2 that were previously shown to be important in ccRCC25,42 (Supplementary Table 5)."

We have now extended this part to clearly state that here MetalinkDB is the prior knowledge resource we used to identify the links for methionine (Line 363-364). In addition we have extended our summary statement to ensure clarity for the reader that we combine the biological clustering, which revealed the amino acid changes, with prior knowledge for the mechanistic insight (Line 380-381):

"In summary, calculating consumption-release and combining it with intracellular metabolomics via biological regulated clustering reveals metabolites of interest. Further combining these results with prior knowledge using the MetaproViz toolkit facilitates biological interpretation of the data."

(3)

Given the functional diversity among metabolites -central to diverse pathways, are key signaling molecules, restricted functions, co-variation within a pathway - I wonder how informative approaches such as PCA or enrichment analyses are for identifying metabolic drivers of a (patho)physiological state. To some extent, this can be addressed by integrating prior knowledge, and it would be helpful if the authors could comment on (and if applicable explain) whether/how this is integrated into MetaProViz.

The reviewer is correct in stating the functional diversity of metabolites, which is also why prior knowledge is needed to add mechanistic interpretation to the finding from the metadata analysis (as we showcased by focusing on the separation of age (Fig. 5c-d)). We think that approaches such as PCA or enrichment can be helpful, even if admittedly limited. For example, in the metadata analysis presented in Fig. 5b and the subsequent enrichment analysis presented in Fig. 5, we used PCA to extract the eigenvector and the loading, which act as weights indicating the contribution of each original metabolite to that specific principal components separation. Hence, the eigenvector of PCA shows the metabolite drivers of the separation. This does not necessarily mean that those metabolites are drivers of a (patho)physiological state - the (patho)physiological state can equally be the reason for those metabolites driving the separation on the Eigenvectors. Thus, the metadata analysis presented in Fig. 5b enables us to extract the metadata variables (patho)physiological states separated on a PC with the explained variance. This can also lead to co-variation, when multiple (patho)physiological states are separated on the same PC, as the reviewer correctly points out. Regarding the enrichment analysis, we provide different types of prior knowledge for classical mapping, but also the prior knowledge we used to create the biological regulated clustering, which together help to identify key metabolic groups as we can first cluster the metabolites and afterwards perform functional enrichment. Yet, this does not account for the technical issues of enrichment analysis. In this context multi-omics integration building metabolic-centric networks could further elucidate the diversity of metabolic pathways and connection to signalling and co-variation, yet this is not the scope of MetaProViz. To sum up, we are aware of the limitations of this analysis and the constraints on the downstream interpretation.

To capture the functional diversity amongst metabolites, which leads to metabolites being present in multiple pathways of metabolite-pathways sets, we have implemented a new function to cluster metabolite-sets like pathways based on overlapping metabolites and visualize redundant metabolite-set (i.e. pathways) memberships (Fig.5f). For more details also see our response to Reviewer 1, Comment 12. We hope this will circumvent miss- and over-interpretation of the enrichment results.

In addition, we have extended the text to include the analysis pitfalls explicitly (Line 416-419): "Another variable explaining the same amount of variance in PC1 is the tumour stage, which could point to adjacent normal tissue metabolic rewiring that happens in relation to stage and showcases that biological data harbour co-variations, which can not be disentangled by this method."

Reviewer #3

Evidence, reproducibility and clarity

This manuscript introduces an R package MetaProViz for metabolomics data analysis (post anotation), aiming to solve a poor-analysis-choices problem and enable more people to do the analysis. MetaProViz not only guides people to select the best statistical method, but also enables to solve previously unsolved problems: e.g. multiple and variable metabolite names in different databases and their connections to prior knowledge. They also created exometabolomics analysis and the needed steps to visualise intra-cell / media processes. The authors demonstrated their new package via kidney cancer (clear-cell renal cell carcinoma dataset, steping one step closer to improve biological interpretability of omics data analysis.

Significance

This is a great tool and I can't wait to use it on many upcoming metabolomics projects! Authors tackle multiple ongoing issues within the field: from poor selection of statistical methods (they provide guidance or have default safer options) to the messiness of data annotation between databases and improving data interpretability. The field is still evolving quickly, and it's impossible to solve all problems with one package; thus some limitations within the package could be seen as a bit rigid. Nonetheless, this fully steps toward filling an existing methodological gap. All bioinformaticians doing metabolomic analysis, or those learning how to do it, will greatly benefit from this knowledge.

I myself lead a team of 6 bioinformaticians, and we do analysis for researchers, clinicians, drug discovery, and various companies. We run internal metabolomics pipelines every day and fully sympathise with the problems addressed by the authors.

Major comments affecting conclusions

none.

We thank the reviewer for this positive feedback on evidence, reproducibility and clarity as well as significance of our work given the reviewers experience with metabolomics data analysis mentioned. We appreciate that there are no major comments from the reviewer.

Minor comments

Minor comments, important issues that could be addressed and possibly improve the clarity or generally presentation of the tool. Please see all below.

(1)

1- You start with separating and talking about metabolomics and lipidomics, but lipidomics quickly dissapears (especially beyond abstract/intro) - no real need to discuss lipidomics.

Thanks, that's a good note and we have removed it from the abstract and introduction.

(2)

2- You refer to the MetImp4 imputation web tool, but I cannot find an active website, manuscript, or R package for it, and the cited link does not load. This raises doubts about whether the tool is currently usable. Additionally, imputation choice should be guided by biological context and study design, not just by testing a few methods and selecting the one that performs best.

We fully agree with the reviewer on imputation handling. The manuscript we cite from Wei et. al. (https://doi.org/10.1038/s41598-017-19120-0) compared a multitude of missing value imputation methods and made this comparison strategy available as a web-based tool not as any code-based package such as an R-package. Yet, the reviewer is right, the web-tool is no longer reachable. Hence, we have adapted the statement in our introduction (Line 61-62): "Moreover, there are tools that focus on specific steps of the pre-processing of feature intensities, which encompasses feature selection, missing value imputation (MVI)9 and data normalisation. For example, MetImp4 is a web-tool that includes and compares multiple MVI methods9. "

(3)

3- The authors address key metabolomics issues such as ambiguous metabolite names and isoforms, and their focus on resolving mapping ambiguities and translating between database identifiers is highly valuable. However, the larger challenge of de novo identification and the "dark matter" of unannotated metabolites remains unresolved (initiatives as MassIVE might help in the future https://massive.ucsd.edu/ProteoSAFe/ ), and readers may benefit from clearer acknowledgement that MetaProViz does not operate on raw spectral data. The introduction currently emphasizes annotation, but since MetaProViz requires already annotated metabolite tables (and then deals with all the messiness), this space might be better used to frame the interpretability and pathway-analysis challenges that the tool directly addresses.

We appreciate the comment and have highlighted this in the abstract and introduction: "MetaProViz operates on annotated intensity values..." (Line 29 and 88).

Given the newest advancements in metabolite identification using AI-based methods, MetaProViz toolkit with a focus on connecting metabolite IDs to prior knowledge becomes increasingly valuable. We added this to our discussion (Line 484-488): "Given the imminent shift in metabolite identification through AI-based approaches, including language model-guided48 methods and self-supervised learning49, the growing number of identified metabolites will make the MetaProViz toolkit increasingly valuable for the community to gain functional insights."

In regards to the introduction, where we mention some tools for peak annotation: The reason why we have this paragraph where peak annotation are named is that we wanted to set the basis by (I) listing the different steps of metabolomics data analysis and (II) pointing to well-known tools of those steps. We also have a dedicated paragraph for pathway-analysis challenges.

(4)

4- I also really enjoyed you touching on the point of user-friendly but then inflexible and problem of reproducibility. We truly need well working packages for other bioinformaticians, rather than expecting wet-lab scientists to do all the analysis within the user interface.

We thank the reviewer for this positive feedback.

(5)

5- It would be helpful to explain why the authors chose cancer/RCC samples for the demonstration. Was it because the dataset included both media and cell measurements? Does the tool perform best when multiple layers of information are available from the same experiment?

We specifically chose the ccRCC cell line data as example since, for a multitude of cell lines, both media (exometabolomics) and intracellular metabolomics had been performed. The combination of both data types is only used in the biological regulated clustering (Fig. 5e-g), all other analyses do not require additional data modalities. We have not specifically tested how performance differs for this particular case as it would require multiple paired data (exometabolomics and intracellular metabolomics) taken at the same time and at different times.

(6)

6- Figure 2B: The upset plots effectively show increased overlap after adaptation, but it would be easier to compare changes if the order of the intersection bars in the "adapted" plot matched the original. For example, while total intersections increased (251→285), the PubChem+KEGG overlap decreased (24→5), likely due to reallocation to the full intersection.

Thanks for raising this point. We initially had ordered the bars based on their intersection size, but we agree with the reviewers that for our point it makes sense to fix the order in the adapted plot to match the order of the original plot. We have done this (Fig 2a) and also extended the figure legend text of SFig. 2, which shows the individually performed adaptations summarized in Fig 2a.

(7) (Planned)

7- In your example of D-alanine and L-alanine - you mention how chirality is important biological feature, but up to this point it's not clear how do you do translation exactly and in which situations this would be treated just as "alanine" and when the more precise information would be retained? You mention RaMP-DB knowledge and one to X mappings as well as your general guidance in the "methods" part, but it would be useful to describe in this publication how you exactly tackled this problem in the ccRCC case.

We thank the reviewer for this suggestion. Since this is a complex problem, we will add a more explicit description to the results section by showcasing more details on how we exactly tackled this problem in the ccRCC example data.

In regards to D- and L-alanine, even though chirality is an important biological feature, in a standard experiment we can not distinguish if we detect the L- or D-aminoacid. This is why we try to assign all possible IDs to increase the overlap with the prior knowledge. In Fig. 2b we showcase that this can potentially lead to multiple mappings of the same measured feature to multiple pathways. For example, if we measure alanine and assign the pubchem ID for L-Alanine, D-Alanine and Alanine and try to map to metabolite-sets that include both L-Alanine and D-Alanine. In turn this could fall into Scenario 6 (Fig. 2e), where across pathways there is a D-Alanine specific one (Pathway 1) and a L-Alanine specific one (Pathway 2). Now we can decide, if we want to allow both mapping (many-to-one) or if we decide to exclude D-Alanine because we know our biological system is human and should primarily have L-Alanine.

(8) (Planned)

8- In one to many mappings, it would be interesting to see quantification how frequently it was happening within a pathway or across pathways. I.e. Would going into pathway analysis "solve" the issue of "lost in translation" or not really?

We have quantified the frequency for the example of translating the KEGG metabolite-set into HMDB IDs (Fig. 2c, left panel). Yet, we are not showcasing the quantification across the KEGG metabolite-sets with this plot. During the revision we will add the full results available to the Extended Data Table 2, which currently only includes the results displayed in Fig.2c.

(9)

9- QC: the coefficient of variation (CV) helps identify features with high variability and thus low detection accuracy. Here it's important to acknowledge that if the feature is very variable between groups it can be extremely important, but if the feature is very variable within the group - only then one would have low trust in the accuracy.

Yes, we totally agree with the reviewer on this. For this reason, we have applied CV only in instances where this is not leading to any condition-driven CV differences, but is truly feature-focused: (1) Function pool_estimation performs CV on the pool samples only, which are a homogeneous mixture of all samples, and hence can be used to assess feature variability. (2) Function processing performs CV on exometabolomics media samples (=blanks), which are also not impacted by different conditions.

(10)

10- Missing value imputation - while missing not at random is a great way to deal with missingness, it would be great to have options for others (not just MNAR), as missingness is of a complex nature. If a pretty strong decision has been made, it would be good to support this by some supplementary data (i.e. how results change while applying various combinations of missingness and why choosing MNAR seems to be the most robust).

We have decided to only offer support for MNAR, since we would recommend MVI only if there is a biological basis for it.

As mentioned in the response to your minor comment 2, Wei et. al. (https://doi.org/10.1038/s41598-017-19120-0) compared a multitude of missing value imputation methods. They compared six imputation methods (i.e., QRILC, Half-minimum, Zero, RF, kNN, SVD) for MNAR and systematically measured the performance of those imputation methods. They showed that QRILC and Half-Minimum produced much smaller SOR values, showing consistent good performances on data with different numbers of missing variables. This was the reason for us to only provide Half-minimum.

(11) (Planned)

11- In the pre-processing and imputation stages - it would be interesting to see a summary table of how many features are left after each stage.

This is a good suggestion and refers to the steps described in Fig. 3a. We will create an overview table for this, add it into the Extended Data Table and refer to it in the results section.

(12)

12- Is there a reason not to do UMAP or PSL-DA graphs for outlier detection? Doing more than PCA would help to have more confidence in removing or retaining outliers in the cases where biological relevance is borderline.

The reason we decided to use PCA was the standardly used combination with the Hotelling T2 outlier testing. Since PCA is a linear dimensionality reduction technique that preserves the overall variance in the data and has a clear mathematical foundation linked to the covariance structure, it specifically fits the required assumptions of the Hotelling T2 outlier testing. Indeed, Hotelling T2 relies on the properties of the covariance matrix and the assumption of a multivariate Gaussian distribution. UMAP is a non-linear dimensionality reduction technique, which prioritizes preserving local and global structures in a way that often results in good clustering visualization, but it distorts distances between clusters and does not have the same rigorous statistical underpinnings as PCA. In terms of PLS-DA, which focuses on maximizing the covariance between variables and the class labels, even though not commonly done, one could use the optimal latent variables for discrimination and apply Hotelling's T² to those latent variables. Yet, PLS-DA is supervised and actively tries to separate data points in the latent space, which can be misleading for outlier detection where methods like PCA that are unbiased, unsupervised and preserve global variance are advantageous.

(13)

13- Metadata vs metabolite features - can this be used beyond metabolomics (i.e. proteomics, transcriptomics, etc)? It can be always very useful when there are many metadata features and it's hard to pre-select beforehand which ones are the most biologically relevant.

Yes, definitely. In fact, we have used the metadata analysis strategy also with proteomics data and it will work equally with any omics data type.

(14)

14- While authors discussed what KEGG pathways were significantly deregulated, it would be interesting to see all the pathways that were affected (e.g. aPEAR "bubble" graphs can show this (https://github.com/kerseviciute/aPEAR) , or something similar to NES scores). I appreciate the trickiness of it, but it would be quite interesting to see how authors e.g. Figure5e narrowed it down to the two pathways and how all the others looked like.

We thank the reviewer for the suggestion of the aPEAR graphs. Following this suggestion, we have implemented a new function to enable clustering of the pathways based on overlapping metabolites (cluster_pk()). For more details regarding the method see also our response to Reviewer 1 (Comment 12) and our extended method section "Metabolite-set clustering" (Lines 656-671). We visualize the clustering results as a network graph, which we also included into Fig. 5f.

The complete result of the KEGG enrichment can be found in Extended Data Table 1, Sheet 13 (Pathway enrichment analysis using KEGG on Young patient subset). The pathways are ranked by p.adjusted value and also include a score (FoldEnrichment) from the fishers exact test (similar to NES scores in GSEA). Here one can find a total of seven pathways with a p.adjusted value For Fig. 5e we narrowed down to these two pathways based on the previous findings of dysregulated dipeptides (Fig. 5d), as we searched for a potential explanation of this observation.

(15)

15- Could you comment on the runtime of the pipeline? In particular, do the additional translation steps and use of multiple databases substantially affect computational speed?

Downloading and parsing databases takes significant time, especially large ones like RaMP or HMDB might take minutes on a standard laptop. Our local cache speeds up the process by eliminating the need for repeated downloads. In the future, database access will be even faster: according to our plans, all prior knowledge will be accessible in an already parsed format by our own API (omnipathdb.org). The ambiguity analysis, which is a complex data transformation pipeline, and plotting by ggplot2, another key component of MetaProViz, are the slowest parts, especially when performing analysis for the first time when no cache can be used. This means there are a few slow operations which complete in maximum a few dozens of seconds. However, the implementation and speed of these solutions doesn't fall behind what we commonly find in bioinformatics packages, and most importantly, the speed of MetaProViz doesn't pose an obstacle or difficulty regarding an efficient use of it in analysis pipelines.

(16)

16- I clap to the authors for automated checks if selected methods are appropriate!

Thank you, this is something we think is important to ensure correct analysis and circumvent misinterpretation.

(17)

17- My suggestion would be to also look into power calculation or p-value histogram. In your example you saw some clear signal, but very frequently research studies are under-sampled and while effect can be clearly seen, there are just not enough samples to have statistically significant hits.

We fully agree that power calculations are very important. Yet, this should ideally happen prior to the user's experiment. MetaProViz analysis starts at a later time-point and power calculations should have been done before. In regards to p-value histogram, we have implemented a similar measure, namely a density plot, which is plotted as a quality control measure within MetaProViz differential analysis function. The density plot is a smoothed version of a histogram that represents the distribution as a continuous probability density function and can be used to assess whether the p-values follow a uniform distribution.

(18)

18- Overall functional parts are novel and next step in helping with data interpretability, but I still found it hard to read into functionally clear insights (re to pathways / functional groupings of metabolites) - especially as you have e.g. enzyme-metabolite databases etc. I think clarity there could be improved and would help to get your message more widely across.

Regarding the clarity to the pathway enrichment and their functional insights, we have extended the Figure legends of Fig. 4 and 5, clearly state that for the functional interpretation MetalinkDB is the prior knowledge resource we used to identify the links for methionine (Line 367-368), and we have extended our summary statement to highlight that we combine the biological clustering with prior knowledge for the mechanistic insight (Line 380-381).

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

This manuscript introduces an R package MetaProViz for metabolomics data analysis (post anotation), aiming to solve a poor-analysis-choices problem and enable more people to do the analysis. MetaProViz not only guides people to select the best statistical method, but also enables to solve previously unsolved problems: e.g. multiple and variable metabolite names in different databases and their connections to prior knowledge. They also created exometabolomics analysis and the needed steps to visualise intra-cell / media processes. The authors demonstrated their new package via kidney cancer (clear-cell renal cell carcinoma dataset, steping one step closer to improve biological interpretability of omics data analysis.

Major comments affecting conclusions: none.

Minor comments, important issues that could be addressed and possibly improve the clarity or generally presentation of the tool. Please see all below.

1. You start with separating and talking about metabolomics and lipidomics, but lipidomics quickly dissapears (especially beyond abstract/intro) - no real need to discuss lipidomics.
2. You refer to the MetImp4 imputation web tool, but I cannot find an active website, manuscript, or R package for it, and the cited link does not load. This raises doubts about whether the tool is currently usable. Additionally, imputation choice should be guided by biological context and study design, not just by testing a few methods and selecting the one that performs best.
3. The authors address key metabolomics issues such as ambiguous metabolite names and isoforms, and their focus on resolving mapping ambiguities and translating between database identifiers is highly valuable. However, the larger challenge of de novo identification and the "dark matter" of unannotated metabolites remains unresolved (initiatives as MassIVE might help in the future https://massive.ucsd.edu/ProteoSAFe/ ), and readers may benefit from clearer acknowledgement that MetaProViz does not operate on raw spectral data. The introduction currently emphasizes annotation, but since MetaProViz requires already annotated metabolite tables (and then deals with all the messiness), this space might be better used to frame the interpretability and pathway-analysis challenges that the tool directly addresses.
4. I also really enjoyed you touching on the point of user-friendly but then inflexible and problem of reproducibility. We truly need well working packages for other bioinformaticians, rather than expecting wet-lab scientists to do all the analysis within the user interface.
5. It would be helpful to explain why the authors chose cancer/RCC samples for the demonstration. Was it because the dataset included both media and cell measurements? Does the tool perform best when multiple layers of information are available from the same experiment?
6. Figure 2B: The upset plots effectively show increased overlap after adaptation, but it would be easier to compare changes if the order of the intersection bars in the "adapted" plot matched the original. For example, while total intersections increased (251→285), the PubChem+KEGG overlap decreased (24→5), likely due to reallocation to the full intersection.
7. In your example of D-alanine and L-alanine - you mention how chirality is important biological feature, but up to this point it's not clear how do you do translation exactly and in which situations this would be treated just as "alanine" and when the more precise information would be retained? You mention RaMP-DB knowledge and one to X mappings as well as your general guidance in the "methods" part, but it would be useful to describe in this publication how you exactly tackled this problem in the ccRCC case.
8. In one to many mappings, it would be interesting to see quantification how frequently it was happening within a pathway or across pathways. I.e. Would going into pathway analysis "solve" the issue of "lost in translation" or not really?
9. QC: the coefficient of variation (CV) helps identify features with high variability and thus low detection accuracy. Here it's important to acknowledge that if the feature is very variable between groups it can be extremely important, but if the feature is very variable within the group - only then one would have low trust in the accuracy.
10. Missing value imputation - while missing not at random is a great way to deal with missingness, it would be great to have options for others (not just MNAR), as missingness is of a complex nature. If a pretty strong decision has been made, it would be good to support this by some supplementary data (i.e. how results change while applying various combinations of missingness and why choosing MNAR seems to be the most robust).
11. In the pre-processing and imputation stages - it would be interesting to see a summary table of how many features are left after each stage.
12. Is there a reason not to do UMAP or PSL-DA graphs for outlier detection? Doing more than PCA would help to have more confidence in removing or retaining outliers in the cases where biological relevance is borderline.
13. Metadata vs metabolite features - can this be used beyond metabolomics (i.e. proteomics, transcriptomics, etc)? It can be always very useful when there are many metadata features and it's hard to pre-select beforehand which ones are the most biologically relevant.
14. While authors discussed what KEGG pathways were significantly deregulated, it would be interesting to see all the pathways that were affected (e.g. aPEAR "bubble" graphs can show this (https://github.com/kerseviciute/aPEAR) , or something similar to NES scores). I appreciate the trickiness of it, but it would be quite interesting to see how authors e.g. Figure5e narrowed it down to the two pathways and how all the others looked like.
15. Could you comment on the runtime of the pipeline? In particular, do the additional translation steps and use of multiple databases substantially affect computational speed?
16. I clap to the authors for automated checks if selected methods are appropriate!
17. My suggestion would be to also look into power calculation or p-value histogram. In your example you saw some clear signal, but very frequently research studies are under-sampled and while effect can be clearly seen, there are just not enough samples to have statistically significant hits.
18. Overall functional parts are novel and next step in helping with data interpretability, but I still found it hard to read into functionally clear insights (re to pathways / functional groupings of metabolites) - especially as you have e.g. enzyme-metabolite databases etc. I think clarity there could be improved and would help to get your message more widely across.

Significance

This is a great tool and I can't wait to use it on many upcoming metabolomics projects! Authors tackle multiple ongoing issues within the field: from poor selection of statistical methods (they provide guidance or have default safer options) to the messiness of data annotation between databases and improving data interpretability. The field is still evolving quickly, and it's impossible to solve all problems with one package; thus some limitations within the package could be seen as a bit rigid. Nonetheless, this fully steps toward filling an existing methodological gap. All bioinformaticians doing metabolomic analysis, or those learning how to do it, will greatly benefit from this knowledge.

I myself lead a team of 6 bioinformaticians, and we do analysis for researchers, clinicians, drug discovery, and various companies. We run internal metabolomics pipelines every day and fully sympathise with the problems addressed by the authors.

Author response:

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

Reviewer #1 (Public review):

Thank you so much for your comprehensive and insightful assessment of our manuscript. We appreciate your recognition of the novelty of our experimental design and the utility of our computational framework for interpreting visual remapping across the lifespan and in clinical populations. We are very grateful for your suggestions regarding the narrative flow, which have helped us to improve the manuscript's focus and coherence. Our responses to your specific concerns are detailed below.

(1) Relevance of the figure-copy results (pp. 13-15). Is it necessary to include the figure-copy task results within the main text? The manuscript already presents a clear and coherent narrative without this section. The figure-copy task represents a substantial shift from the LOCUS paradigm to an entirely different task that does not measure the same construct. Moreover, the ROCF findings are not fully consistent with the LOCUS results, which introduces confusion and weakens the manuscript's coherence. While I understand the authors' intention to assess the ecological validity of their model, this section does not effectively strengthen the manuscript and may be better removed or placed in the Supplementary Materials.

We thank the reviewer  for their perspective regarding the narrative flow and the transition between the LOCUS paradigm and the ROCF results. However, we remain keen to retain these findings in the main text, as they provide critical ecological and clinical validation for the computational mechanisms identified in our study.

We think these results strengthen the manuscript for the following main reasons:

(1) The ROCF we used is a standard neuropsychological tool for identifying constructional apraxia. Our results bridge the gap between basic cognitive neuroscience and clinical application by demonstrating that specific remapping parameters—rather than general memory precision—predict real-world deficits in patients.

(2) The finding that our winning model explains approximately 62% of the variance in ROCF copy scores across all diagnostic groups further indicates that these parameters from the LOCUS task represent core computational phenotypes that underpin complex, real-life visuospatial construction (copying drawings).

(3) Previous research has often observed only a weak or indirect link between drawing ability and traditional working memory measures, such as digit span (Senese et al., 2020). This was previously attributed to “deictic” strategies—like frequent eye and hand movements—that minimise the need to hold large amounts of information in memory (Ballard et al., 1995; Cohen, 2005; Draschkow et al., 2021). While our study was not exclusively designed to catalogue all cognitive contributions to drawing, the findings provide significant and novel evidence indicating that transsaccadic integration is a critical driver of constructional (copying drawing) ability. By demonstrating this link, the results provide evidence to stimulate a new direction for future research, shifting the focus from general memory capacity toward the precision of spatial updating across eye movements.

In summary, by including the ROCF results in the main text, we provide evidence for a functional role for spatial remapping that extends beyond perceptual stability into the domain of complex visuomotor control. We have expanded on these points throughout the revised manuscript:

In the Introduction: p.2:

“The clinical relevance of these spatial mechanisms is underscored by significant disruptions to visuospatial processing and constructional apraxia—a deficit in copying and drawing figures—observed in neurodegenerative conditions such as Alzheimer's disease (AD) and Parkinson's disease (PD).[20,21] This raises a crucial question: do clinical impairments in complex visuomotor tasks stem from specific failures in transsaccadic remapping? If so, the computational parameters that define normal spatial updating should also provide a mechanistic account of these clinical deficits, differentiating them from general age-related decline.”

p.3: "Finally, by linking these mechanistic parameters to a standard clinical measure of constructional ability (the Rey-Osterrieth Complex Figure task), we demonstrate that transsaccadic updating represents a core computational phenotype underpinning real-world visuospatial construction in both health and neurodegeneration.

In the Results:

“To assess whether the mechanistic parameters derived from the LOCUS task represent core phenotypes of real-world visuospatial abilities, we also instructed all participants to complete the Rey-Osterrieth Complex Figure copy task (ROCF; Figure 7A) on an Android tablet using a digital pen (see examples in Figure 7B; all Copy data are available in the open dataset: https://osf.io/95ecp/). The ROCF is a gold-standard neuropsychological tool for identifying constructional apraxia.[29] Historically, drawing performance has shown only weak or indirect correlations with traditional working memory measures.[30] This disconnect has been attributed to active visual-sampling strategies—frequent eye movements that treat the environment as an external memory buffer, minimising the necessity of holding large volumes of information in internal working memory.[3–5]

We hypothesised that drawing accuracy is primarily constrained by the precision of spatial updating across frequent saccades rather than raw memory capacity. To evaluate the ecological validity of the identified saccade-updating mechanism, we modelled individual ROCF copy scores across all four groups using the estimated (maximum a posteriori) parameters from the winning “Dual (Saccade) + Interference” model (Model 7; Figure 8) as regressors in a Bayesian linear model. Prior to inclusion, each regressor was normalised by dividing by the square root of its variance.

This model successfully explained 61.99% of the variance in ROCF copy scores, indicating that these computational parameters are strong predictors of real-word constructional ability (Figure 8A). … This highlights the critical role of accurate remapping based on saccadic information; even if the core saccadic update mechanism is preserved across groups (as shown in previous analyses), the precision of this updating process is crucial for complex visuospatial tasks. Moreover, worse ROCF copy performance is associated particularly with higher initial angular encoding error. This indicates that imprecision in the initial registration of angular spatial information contributes to difficulties in accurately reproducing complex visual stimuli.”

In the Discussion:

“Importantly, our computational framework establishes a direct mechanistic link between trassaccadic updating and real-world constructional ability. Specifically, higher saccade and angular encoding errors contribute to poorer ROCF copy scores. By mapping these mechanistic estimates onto clinical scores, we found that the parameters derived from our winning model explain approximately 62% of the variance in constructional performance across groups. These findings suggest that the computational parameters identified in the LOCUS task represent core phenotypes of visuospatial ability, providing a mechanistic bridge between basic cognitive theory and clinical presentation.

This relationship provides novel insights into the cognitive processes underlying drawing, specifically highlighting the role of transsaccadic working memoty.ry. Previous research has primarily focused on the roles of fine motor control and eye-hand coordination in this skill.[4,50–55] This is partly because of consistent failure to find a strong relation between traditional memory measures and copying abili [4,31] For instance, common measures of working memory, such as digit span and Corsi block tasks, do not directly predict ROCF copying performance.[31,56] Furthermore, in patients with constructional apraxia, these memory performance measures often remain relatively preserved despite significant drawing impairments.[56–58] In the literature, this lack of association has often been attributed to “deictic” visual-sampling strategies, characterised by frequent eye movements that treat the environment as an external memory buffer, thereby minimising the need to maintain a detailed internal representation.[4,59] In a real-world copying task, the ROCF requires a high volume of saccades, making it uniquely sensitive to the precision of the dynamic remapping signals identified here. Recent eye-tracking evidence confirms that patients with AD exhibit significantly more saccades and longer fixations during figure copying compared to controls, potentially as a compensatory response to trassaccadic working memory constraints.[56] This high-frequency sampling—averaging between 150 and 260 saccades for AD patients compared to approximately 100 for healthy controls—renders the task highly dependent on the precision of dynamic remapping signals.[56] To ensure this relationship was not driven by a general "g-factor" or non-spatial memory impairment, we further investigated the role of broader cognitive performance using the ACE-III Memory subscale. We found that the relationship between transsaccadic working memory and ROCF performance remains highly significant, even after controlling for age, education, and ACE-III Memory subscore. This suggests that transsaccadic updating may represent a discrete computational phenotype required for visuomotor control, rather than a non-specific proxy for global cognitive decline.

In other words, even when visual information is readily available in the world, the act of copying depends critically on working memory across saccades. This reveals a fundamental computational trade-off: while active sampling strategies (characterised with frequent eye-hand movements) effectively reduce the load on capacity-limited working memory, they simultaneously increase the demand for precise spatial updating across eye movements. By treating the external world as an "outside" memory buffer, the brain minimises the volume of information it must hold internally, but it becomes entirely dependent on the reliability with which that information is remapped after each eye movement. This perspective aligns with, rather contradicts, the traditional view of active sampling, which posits that individuals adapt their gaze and memory strategies based on specific task demands.[3,60] Furthermore, this perspective provides a mechanistic framework for understanding constructional apraxia; in these clinical populations, the impairment may not lie in a reduced memory "span," but rather in the cumulative noise introduced by the constant spatial remapping required during the copying process.[58,61]

Beyond constructional ability, these findings suggest that the primary evolutionary utility of high-resolution spatial remapping lies in the service of action rather than perception. While spatial remapping is often invoked to explain perceptual stability,[11–13,15] the necessity of high-resolution transsaccadic memory for basic visual perception is debated.[13,62–64] A prevailing view suggests that detailed internal models are unnecessary for perception, given the continuous availability of visual information in the external world.[13,44] Our findings support an alternative perspective, aligning with the proposal that high-resolution transsaccadic memory primarily serves action rather than perception.[13] This is consistent with the need for precise localisation in eye-hand coordination tasks such as pointing or grasping.[65] Even when unaware of intrasaccadic target displacements, individuals rapidly adjust their reaching movements, suggesting direct access of the motor system to remapping signals.66 Further support comes from evidence that pointing to remembered locations is biased by changes in eye position,[67] and that remapping neurons reside within the dorsal “action” visual pathway, rather than the ventral “perception” visual pathway.[13,68,69] By demonstrating a strong link between transsaccadic working memory and drawing (a complex fine motor skill), our findings suggest that precise visual working memory across eye movements plays an important role in complex fine motor control.”

(2) Model fitting across age groups (p. 9).

It is unclear whether it is appropriate to fit healthy young and healthy elderly participants' data to the same model simultaneously. If the goal of the model fitting is to account for behavioral performance across all conditions, combining these groups may be problematic, as the groups differ significantly in overall performance despite showing similar remapping costs. This suggests that model performance might differ meaningfully between age groups. For example, in Figure 4A, participants 22-42 (presumably the elderly group) show the best fit for the Dual (Saccade) model, implying that the Interference component may contribute less to explaining elderly performance.

Furthermore, although the most complex model emerges as the best-fitting model, the manuscript should explain how model complexity is penalized or balanced in the model comparison procedure. Additionally, are Fixation Decay and Saccade Update necessarily alternative mechanisms? Could both contribute simultaneously to spatial memory representation? A model that includes both mechanisms-e.g., Dual (Fixation) + Dual (Saccade) + Interference-could be tested to determine whether it outperforms Model 7 to rule out the sole contribution of complexity.

We thank you for the opportunity to expand upon and clarify our modelling approach. Our decision to use a common generative model for both young and older adults was grounded in the empirical finding that there was no significant interaction between age group and saccade condition for either location or colour memory. While older adults demonstrated lower baseline precision, the specific "saccade cost" remained remarkably consistent across cohorts. This was the justification we proceeded on to use of a common model to assess quantitative differences in parameter estimates while maintaining a consistent mechanistic framework for comparison.

Moreover, our winning model nests simpler models as special cases, providing the flexibility to naturally accommodate groups where certain components—such as interference—might play a reduced role. This ultimately confirms that the mechanisms for age-related memory deficits in this task reflect more general decline rather than a qualitative failure of the saccadic remapping process.

This approach is further supported by the properties of the Bayesian model selection (BMS) procedure we used, which inherently penalises the inclusion of unnecessary parameters. Unlike maximum likelihood methods, BMS compares marginal likelihoods, representing the evidence for a model integrated over its entire parameter space. This follows the principle of Bayesian Occam’s Razor, where a model is only favoured if the improvement in fit justifies the additional parameter space; redundant parameters instead "dilute" the probability mass and lower the model evidence.

Consequently, we contend that a hybrid model combining fixation and saccade mechanisms is unnecessary, as we have already adjudicated between alternative mechanisms of equal complexity. Specifically, Model 6 (Dual Fixation + Interference) and Model 7 (Dual Saccade + Interference) possess an identical number of parameters. The fact that Model 7 emerged as the clear winner—providing substantial evidence against Model 6 with a Bayes Factor of 6.11—demonstrates that our model selection is driven by the specific mechanistic account of the data rather than a simple preference for complexity.

We have revised the Results and Discussion sections of the manuscript to state these points more explicitly for readers and have included references to established literature regarding the robustness of marginal likelihoods in guarding against overfitting.

In the Results,

“By fitting these models to the trial-by-trial response data from all healthy participants (N=42), we adjudicated between competing mechanisms to determine which best explained participant performance (Figure 4). We used random-effects Bayesian model selection to identify the most plausible generative model. This process relies on the marginal likelihood (model evidence), which inherently balances model fit against complexity—a principle often referred to as Occam’s razor.[25–27] The analysis yielded a strong result: the “Dual (Saccade) + Interference” model (Model 7 in Table 1) emerged as the winning model, providing substantial evidence against the next best alternative with a Bayes Factor of 6.11.”

In the Discussion:

“Our framework employs Variational Laplace, a method used to recover computational phenotypes in clinical populations like those with substance use disorders,[34,35] and the models we fit using this procedure feature time-dependent parameterisation of variance—conceptually similar to the widely-used Hierarchical Gaussian Filter.[36–39] Importantly, the risk of overfitting is mitigated by the Bayesian Model Selection framework; by utilising the marginal likelihood for model comparison, the procedure inherently penalises excessive model complexity and promotes generalisability.[25–27,40] This generalisability was further evidenced by the model's ability to predict performance on the independent ROCF task, confirming that these parameters represent robust mechanistic phenotypes rather than idiosyncratic fits to the initial dataset.”

Minor point: On p. 9, line 336, Figure 4A does not appear to include the red dashed vertical line that is mentioned as separating the age groups.

Thank you for pointing out this inconsistency. We apologise for the oversight; upon further review, we concluded that the red dashed vertical line was unnecessary for the clear presentation of the data. We have therefore removed the line from Figure 4A and deleted the corresponding sentence in the figure caption.

(3) Clarification of conceptual terminology.

Some conceptual distinctions are unclear. For example, the relationship between "retinal memory" and "transsaccadic memory," as well as between "allocentric map" and "retinotopic representation," is not fully explained. Are these constructs related or distinct? Additionally, the manuscript uses terms such as "allocentric map," "retinotopic representation," and "reference frame" interchangeably, which creates ambiguity. It would be helpful for the authors to clarify the relationships among these terms and apply them consistently.

Thank you for pointing this out. We have revised the manuscript to ensure that these terms are applied with greater precision and consistency. Our revisions standardise the terminology based on the following distinctions:

Reference frames: We distinguish between the eye-centred reference frame (coordinate systems that shift with gaze) and the world-centred reference frame (coordinate systems anchored to the environment).

Retinotopic representation vs. allocentric map: We clarify that retinotopic representations are encoded within an eye-centred reference frame and are updated with every ocular movement. Conversely, the allocentric map is anchored to stable environmental features, remaining invariant to the observer’s gaze direction or position.

Retinotopic memory vs. transsaccadic memory: We have removed the term "retinal memory" to avoid ambiguity. We now consistently use retinotopic memory to describe the persistence of visual information in eye-centred coordinates within a single fixation. In contrast, transsaccadic memory refers to the higher-level integration of visual information across saccades, which involves the active updating or remapping of representations to maintain stability.

To incorporate these clarifications, we have implemented the following changes:

In the Introduction, the second paragraph has been entirely rewritten to establish these definitions at the outset, providing a clearer theoretical framework for the study.

“Central to this enquiry is the nature of the coordinate system used for the brain's internal spatial representation. Does the brain maintain a single, world-centred (allocentric) map, or does it rely on a dynamic, eye-centred (retinotopic) representation?[11,13,15,16] In the latter system, retinotopic memory preserves spatial information within a fixation, whereas transsaccadic memory describes the active process of updating these representations across eye movements to achieve spatiotopic stability—the perception of a stable world despite eye movements.[11,16–18] If spatial stability is indeed reconstructed through such remapping, the mechanism remains unresolved: do we retain memories of absolute fixation locations, or do we reconstruct these positions from noisy memories of the intervening saccade vectors? We can test these hypotheses by analysing when and where memory errors occur. Assuming that memory precision declines over time,[19] the resulting error distributions should reveal the specific variables that are represented and updated across each saccade.”

In the Results, the opening section of the Results has been reorganised to align with this terminology. We have ensured that the hypotheses and behavioural data—specifically the definition of "saccade cost"—are introduced using this consistent conceptual vocabulary to improve the overall coherence of the narrative.

(4) Rationale for the selective disruption hypothesis (p. 4, lines 153-154). The authors hypothesize that "saccades would selectively disrupt location memory while leaving colour memory intact." Providing theoretical or empirical justification for this prediction would strengthen the argument.

We have revised the Results to state the hypothesis more explicitly and expanded the Discussion to provide a robust theoretical and empirical rationale:

In the Results,

“This design allowed us to isolate and quantify the unique impact of saccades on spatial memory, enabling us to test competing hypotheses regarding spatial representation. If spatial memory were solely underpinned by an allocentric mechanism, precision should remain comparable across all conditions as the representation would be world-centred and unaffected by eye movements. Thus, performance in the no-saccade condition should be comparable to the two-saccade condition. Conversely, if spatial memory relies on a retinotopic representation requiring active updating across eye movements, the two-saccade condition was anticipated to be the most challenging due to cumulative decay in the memory traces used for stimulus reconstruction after each saccade.[22] Critically, we hypothesised that this saccade cost would be specific to the spatial domain; while location requires active remapping via noisy oculomotor signals, non-spatial features like colour are not inherently tied to coordinate transformations and should therefore remain stable (see more in Discussion below).

Meanwhile, the no-saccade condition was expected to yield the most accurate localisation, relying solely on retinotopic information (retinotopic working memory). These predictions were confirmed in young healthy adults (N = 21, mean age = 24.1 years, ranged between 19 and 34). A repeated measures ANOVA revealed a significant main effect of saccades on location memory (F(2.2,43.9)=33.2, p<0.001, partial η²=0.62), indicating substantial impairment after eye movements (Figure 2A). In contrast, colour memory remained remarkably stable across all saccade conditions (Figure 2B; F(2.2, 44.7) = 0.68, p=0.53, partial η² =0.03).

This “saccade cost”—the loss of memory precision following an eye movement—indicates that spatial representations require active updating across saccades rather than being maintained in a static, world-centred reference frame.

Critically, our comparison between spatial and colour memory does not rely on the absolute magnitude of errors, which are measured in different units (degrees of visual angle vs. radians). Instead, we assessed the relative impact of the same saccadic demand on each feature within the same trial. While location recall showed a robust saccade cost, colour recall remained statistically unchanged. To ensure this null effect was not due to a lack of measurement sensitivity, we examined the recency effect; recall performance for the second item was predicted to be better than for the first stimulus in each condition.[23,24] As expected, colour memory for Item 2 was significantly more accurate than for Item 1 (F(1,20) = 6.52, p = 0.02, partial η² = 0.25), demonstrating that the task was sufficiently sensitive to detect standard working memory fluctuations despite the absence of a saccade-induced deficit.”

In the Discussion, we now write that on p.18:

“A clear finding was the specificity of the saccade cost to spatial features; it was not observed for non-spatial features like colour, even in neurodegenerative conditions. This discrepancy challenges notions of fixed visual working memory capacity unaffected by saccades.16,44–46 The differential impact on spatial versus non-spatial features in transsaccadic memory aligns with the established "what" and "where" pathways in visual processing.32,33 For objects to remain unified, object features must be bound to stable representations of location across saccades.19 One possibility is that remapping updates both features and location through a shared mechanism, predicting equal saccadic interference for both colour and location in the present study.

However, our findings suggest otherwise. One potential concern is whether this dissociation simply reflects the inherent spatial noise introduced by fixational eye movements (FEMs), such as microssacades and drifts.47 Because locations are stored in a retinotopic frame, fixational instability necessarily shifts retinal coordinates over time. However, the "saccade cost" here was defined as the error increase relative to a no-saccade baseline of equal duration; because both conditions are subject to the same fixational drift, any FEM-induced noise is effectively subtracted out. Thus, despite the ballistic and non-Gaussian nature of FEMs,48 they cannot account for the fact the saccade cost in the spatial memory, but total absence in the colour domain. Another possibility is that this dissociation reflects differences in baseline task difficulty or dynamic range. Yet, the presence of a robust recency effect in colour memory (Figure 2B) confirms that our paradigm was sensitive to memory-dependent variance and was not limited by floor or ceiling effects.

The fact that identical eye movements—executed simultaneously and with identical vectors—systematically degraded spatial precision while sparing colour suggests a feature-specific susceptibility to transsaccadic remapping. This supports the view that the computational process of updating an object’s location involves a vector-subtraction mechanism—incorporating noisy oculomotor commands (efference copies)—that introduces specific spatial variance. Because this remapping is a coordinate transformation, the resulting sensorimotor noise does not functionally propagate to non-spatial feature representations. Consequently, features like colour may be preserved or automatically remapped without the precision loss associated with spatial updating.11,49 Our paradigm thus provides a refined tool to investigate the architecture of transsaccadic working memory across distinct object features.”

(5) Relationship between saccade cost and individual memory performance (p. 4, last paragraph).

The authors report that larger saccades were associated with greater spatial memory disruption. It would be informative to examine whether individual differences in the magnitude of saccade cost correlate with participants' overall/baseline memory performance (e.g. their memory precision in the no-saccade condition). Such analyses might offer insights into how memory capacity/ability relates to resilience against saccade-induced updating.

We have now conducted the correlation analysis to determine whether baseline memory capacity (no-saccade condition) predicts resilience to saccade-induced updating. The results indicate that these two factors are independent.

To clarify the nature of the saccade-induced impairment, we have updated the text as follows:

p.4: “This “saccade cost”—the loss of memory precision following an eye movement—indicates that spatial representations require active updating across saccades rather than being maintained in a static, world-centred reference frame.”

p.5: “Further analysis examined whether individual differences in baseline memory precision (no-saccade condition) predicted resilience to saccadic disruption. Crucially, individual saccade costs (defined as the precision loss relative to baseline) did not correlate with baseline precision (rho = 0.20, p = 0.20). This suggests that the noise introduced by transsaccadic remapping acts as an independent, additive source of variance that is not modulated by an individual’s underlying memory capacity. These findings imply a functional dissociation between the mechanisms responsible for maintaining a representation and those involved in its coordinate transformation.”

(6) Model fitting for the healthy elderly group to reveal memory-deficit factors (pp. 11-12). The manuscript discusses model-based insights into components that contribute to spatial memory deficits in AD and PD, but does not discuss components that contribute to spatial memory deficits in the healthy elderly group. Given that the EC group also shows impairments in certain parameters, explaining and discussing these outcomes of the EC group could provide additional insights into age-related memory decline, which would strengthen the study's broader conclusions.

This is a very good point. We rewrote the corresponding results section (p.12-13):

“Modelling reveals the sources of spatial memory deficits in healthy aging and neurodegeneration - To understand the source of the observed deficits, we applied the winning ‘Dual (Saccade) + Interference’ model the data from all participants (YC, EC, AD, and PD). By fitting the model to the entire dataset, we obtained estimates of the parameters for each individual, which then formed the basis for our group-level analysis. To formally test for group differences, we used Parametric Empirical Bayes (PEB), a hierarchical Bayesian approach that compares parameter estimates across groups while accounting for the uncertainty of each estimate [28]. This allowed us to identify which specific cognitive mechanisms, as formalised by the model parameters, were affected by age and disease.

The Bayesian inversion used here allows us to quantify the posterior mode and variance for each parameter and the covariance for each parameter. From these, we can compute the probabilities that pairs of parameters differ from one another, which we report as P(A>B)—meaning the posterior probability that the parameter for group A was greater than that for group B.

We first examined the specific parameters differentiating healthy elderly (EC) from young controls (YC) to isolate the factors contributing to non-pathological, age-related decline. The analysis revealed that healthy ageing is primarily characterised by a significant increase in Radial Decay (P(EC > YC) = 0.995), a heightened susceptibility to Interference (P(EC > YC) = 1.000), and a reduction in initial Angular Encoding precision (P(YC < EC) = 0.002; Figure 6). These results suggest that normal ageing degrades the fidelity of the initial memory trace and its resilience over time, while the core computational process of updating information across saccades remains intact.

Beyond these baseline ageing effects, our clinical cohorts exhibited more severe and condition-dependent impairments. Radial decay showed a clear, graded impairment: AD patients had a greater decay rate than PD patients (P(AD > PD) = 1.000), who in turn were more impaired than the EC group (P(PD > EC) = 0.996). A similar graded pattern was observed for Interference, where AD patients were most susceptible (P(AD > PD) = 0.999), while the PD and EC groups did not significantly differ (P(PD > EC) = 0.532).

Patients with AD also showed a tendency towards greater angular decay than controls (P(AD > EC) = 0.772), although this fell below the 95% probability threshold. This effect was influenced by a lower decay rate in the PD group compared to the EC group (P(PD < EC) = 0.037). In contrast, group differences in encoding were less pronounced. While YC exhibited significantly higher precision than all other groups, AD patients showed significantly higher angular encoding error than PD patients (P(AD > PD) = 0.985), though neither group differed significantly from the EC group.

Crucially, parameters related to the saccade itself—saccade encoding and saccade decay—did not differentiate the groups. This indicates that neither healthy ageing nor the early stages of AD and PD significantly impair the fundamental machinery for transsaccadic remapping. Instead, the visuospatial deficits in these conditions arise from specific mechanistic failures: a faster decay of radial position information and increased susceptibility to interference, both of which are present in healthy ageing but significantly amplified by neurodegeneration.”

In the Discussion, we added:

“Although saccade updating was an essential component of the winning model, its two key parameters—initial encoding error and decay rate during maintenance—did not significantly differ across groups. This indicates that the core computational process of updating spatial information based on eye movements is largely preserved in healthy aging and neurodegeneration.

Instead, group differences were driven by deficits in angular encoding error (precision of initial angle from fixation), angular decay, radial decay (decay in memory of distance from fixation), and interference susceptibility. This implies a functional and neuroanatomical dissociation: while the ventral stream (the “what” pathway) shows an age-related decline in the quality and stability of stored representations, the dorsal-stream (the “where” pathway) parietal-frontal circuits responsible for coordinate transformations remain functionally robust.[31–34] These spatial updating mechanisms appear resilient to the normal ageing trajectory and only break down when challenged by the specific pathological processes seen in Alzheimer’s or Parkinson’s disease.”

(7) Presentation of saccade conditions in Figure 5 (p. 11). In Figure 5, it may be clearer to group the four saccade conditions together within each patient group. Since the main point is that saccadic interference on spatial memory remains robust across patient groups, grouping conditions by patient type rather than intermixing conditions would emphasize this interpretation.

There are several valid ways to present these plots, but we chose this format because it allows for a direct visual comparison of the post-hoc group differences within each specific task demand. This arrangement clearly illustrates the graded impairment from young controls through to patients with Alzheimer’s disease across every condition. This structure also directly mirrors our two-way ANOVA, which identified significant main effects for both Group and Condition, but crucially, no significant Group x Condition interaction. We felt that grouping the data by participant group would force readers to look across four separate clusters to compare the slopes, making the stability of the saccadic remapping mechanism much harder to grasp at a glance.

Reviewer #1 (Recommendations for the authors):

(1) Formatting of statistical parameters.

The formatting of statistical symbols should be consistent throughout the manuscript. Some instances of F, p, and t are italicized, while others are not. All statistical symbols should be italicized.

Thank you for pointing this out. We have audited the manuscript. While we have revised the text to address these instances throughout the Results and Methods sections, any remaining minor formatting inconsistencies will be corrected during the final typesetting stage.

(2) Minor typographical issues.

(a) Line 532: "are" should be "be."

(b) Line 654: "cantered" should be "centered."

(c) Line 213: In "(p(bonf) < 0.001, |t| {greater than or equal to} 5.94)," the t value should be reported with its degrees of freedom, and t should be reported before p. The same applies to line 215.

Thank you for your careful reading. All corrected.

Reviewer #2 (Public review):

We thank you for your positive feedback regarding our eye-tracking methodology and computational approach. We appreciate your critical insights into the feature-specific disruption hypothesis and the task structure. We have substantially revised the results and discussion about the saccadic interference on colour memory. Below we will answer your suggestions point-by-point:

Reviewer #2 (Recommendations for the authors):

(1) The study treats colour and location errors as comparable when arguing that saccades selectively disrupt spatial but not colour memory. However, these measures are defined in entirely different units (degrees of visual angle vs radians on a colour wheel) and are not psychophysically or statistically calibrated. Baseline task difficulty, noise level, or dynamic range do not appear to be calibrated or matched across features. As a result, the null effect of saccades on colour could reflect lower sensitivity or ceiling effects rather than implicit feature-specific robustness.

We agree that direct comparisons of absolute error magnitudes across different dimensions are not appropriate. Our argument for feature-specific disruption relies not on the scale of errors, but on the presence or absence of a saccade cost within identical trials. In our within-subject design, the same saccade vectors produced a systematic increase in location error while leaving colour error statistically unchanged. To address sensitivity, we observed that colour memory was sufficiently precise to show a significant recency effect (p = 0.02). To further quantify the evidence for the null effect, we performed Bayesian repeated measures ANOVAs, which yielded a BF10 = 0.22. This provides substantial evidence that saccades do not disrupt colour precision, regardless of baseline sensitivity.

We have substantially revised this in Results, Methods and Discussion:

In the Results:

“This design allowed us to isolate and quantify the unique impact of saccades on spatial memory, enabling us to test competing hypotheses regarding spatial representation. If spatial memory were solely underpinned by an allocentric mechanism, precision should remain comparable across all conditions as the representation would be world-centred and unaffected by eye movements. Thus, performance in the no-saccade condition should be comparable to the two-saccade condition. Conversely, if spatial memory relies on a retinotopic representation requiring active updating across eye movements, the two-saccade condition was anticipated to be the most challenging due to cumulative decay in the memory traces used for stimulus reconstruction after each saccade.[22] Critically, we hypothesised that this saccade cost would be specific to the spatial domain; while location requires active remapping via noisy oculomotor signals, non-spatial features like colour are not inherently tied to coordinate transformations and should therefore remain stable (see more in Discussion below).

Meanwhile, the no-saccade condition was expected to yield the most accurate localisation, relying solely on retinotopic information (retinotopic working memory). These predictions were confirmed in young healthy adults (N = 21, mean age = 24.1 years, ranged between 19 and 34). A repeated measures ANOVA revealed a significant main effect of saccades on location memory (F(2.2,43.9)=33.2, p<0.001, partial η²=0.62), indicating substantial impairment after eye movements (Figure 2A). In contrast, colour memory remained remarkably stable across all saccade conditions (Figure 2B; F(2.2, 44.7) = 0.68, p=0.53, partial η² =0.03).

This “saccade cost”—the loss of memory precision following an eye movement—indicates that spatial representations require active updating across saccades rather than being maintained in a static, world-centred reference frame.

Critically, our comparison between spatial and colour memory does not rely on the absolute magnitude of errors, which are measured in different units (degrees of visual angle vs. radians). Instead, we assessed the relative impact of the same saccadic demand on each feature within the same trial. While location recall showed a robust saccade cost, colour recall remained statistically unchanged. To ensure this null effect was not due to a lack of measurement sensitivity, we examined the recency effect; recall performance for the second item was predicted to be better than for the first stimulus in each condition.[23,24] As expected, colour memory for Item 2 was significantly more accurate than for Item 1 (F(1,20) = 6.52, p = 0.02, partial η² = 0.25), demonstrating that the task was sufficiently sensitive to detect standard working memory fluctuations despite the absence of a saccade-induced deficit.”

In the Methods, at the beginning of “Statistical Analysis”, we added

“Because location and colour recall involve different scales and units, all analyses were performed independently for each feature to avoid cross-dimensional magnitude comparisons.” (p25)

In the Discussion, we added:

“A potential concern is whether the observed dissociation between colour and location reflects differences in baseline task difficulty or dynamic range. Yet, the presence of a robust recency effect in colour memory (Figure 2B) confirms that our paradigm was sensitive to memory-dependent variance and was not limited by floor or ceiling effects.”

(2) Colour and then location are probed serially, without a counter-balanced order. This fixed response order could introduce a systematic bias because location recall is consistently subject to longer memory retention intervals and cognitive interference from the colour decision. The observed dissociation-saccades impair location but not colour, and may therefore reflect task structure rather than implicit feature-specific differences in trans-saccadic memory.

Thank you for the insightful observation regarding our fixed response order. We acknowledge that that a counterbalanced design is typically preferred to mitigate potential order effects. However, we chose this consistent sequence to ensure the task remained accessible for cognitively impaired patients (i.e., the Alzheimer’s disease (AD) and Parkinson’s disease (PD) cohorts). Conducting an eye-tracking memory task with cognitively impaired patients is challenging, as they may struggle with task engagement or forget complex instructions. During the design phase, we prioritised a consistent structure to reduce the cognitive load and task-switching demands that typically challenge these cohorts.

Critically, because the saccade cost is a relative measure calculated by comparing conditions with identical timings, any bias from the fixed order is present in both the baseline and saccade trials. The disruption we report is therefore a specific effect of eye movements that goes beyond the noise introduced by the retention interval or the preceding colour report.

We added the following text in the Methods – experimental procedure (p.22):

“Recall was performed in a fixed order, with colour reported before location. This sequence was primarily chosen to minimise cognitive load and task-switching demands for the two neurological patient cohorts, ensuring the paradigm remained accessible for individuals with AD and PD. While this order results in a slightly longer retention interval for location recall, the saccade cost was identified by comparing location error across experimental conditions with similar timings but varying saccadic demands.”

(3) Relatedly, because spatial representations are retinotopic, fixational eye movements (FEMs - microsaccades and drift) displace the retinal coordinates of encoded positions, increasing apparent spatial noise with time delays. Colour memory, however, is feature-based and unaffected by small retinal translations. Thus, any between-condition or between-group differences in FEMs could selectively inflate location error and the associated model parameters (encoding noise, decay, interference), while leaving colour error unchanged. Note that FEMs tend to be slightly ballistic [1,2], hence not well modelled with a Gaussian blur.

This is a very insightful point. We have now addressed this in detail within the discussion:

“However, our findings suggest otherwise. One potential concern is whether this dissociation simply reflects the inherent spatial noise introduced by fixational eye movements (FEMs), such as microssacades and drifts.[46] Because locations are stored in a retinotopic frame, fixational instability necessarily shifts retinal coordinates over time. However, the "saccade cost" here was defined as the error increase relative to a no-saccade baseline of equal duration; because both conditions are subject to the same fixational drift, any FEM-induced noise is effectively subtracted out. Thus, despite the ballistic and non-Gaussian nature of FEMs,n [47] they cannot account for the fact the saccade cost in the spatial memory, but total absence in the colour domain. Another possibility is that this dissociation reflects differences in baseline task difficulty or dynamic range. Yet, the presence of a robust recency effect in colour memory (Figure 2B) confirms that our paradigm was sensitive to memory-dependent variance and was not limited by floor or ceiling effects.”

(4) There is no in silico demonstration that the modelling framework can recover the true generating model from synthetic data or recover accurate parameters under realistic noise levels, which can be challenging in generative models with a hierarchical structure (as per [3], for example). Figure 8b shows that the parameters possess substantial posterior covariance, which raises concerns as to whether they can be reliably disambiguate.

Many thanks for this comment. We have added a simple recovery analysis as detailed below but are also keen to ensure we fully answer your question—which has more to do with empirical rather than simulated data—and make clear the rationale for this analysis in this instance.

We added this in Supplementary Materials:

“Model validation and recovery analysis

The following section provides a detailed technical assessment of the model inversion scheme, focusing on the discriminability of the model space and the identifiability of individual parameters.

Recovery analyses of this sort are typically used prior to collecting data to allow one to determine whether, in principle, the data are useful in disambiguating between hypotheses. In this sense, they have a role analogous to a classical power calculation. However, their utility is limited when used post-hoc when data have already been collected, as the question of whether the models can be disambiguated becomes one of whether non-trivial Bayes factors can be identified from those data.

The reason for including a recovery analysis here is not to identify whether the model inversion scheme identifies a ‘true’ model. The concept of ‘true generative models’ commits to a strong philosophical position which is at odds with the ‘all models are wrong, but some are useful’ perspective held by many in statistics, e.g., (So, 2017). Of note, one can always confound a model recovery scheme by generating the same data in a simple way, and in (one of an infinite number of) more complex ways. A good model inversion scheme will always recover the simple model and therefore would appear to select the ‘wrong’ model in a recovery analysis. However, it is still the best explanation for the data. For these reasons, we do not necessarily expect ‘good’ recoverability in all parameter ranges. This is further confounded by the relationship between the models we have proposed—e.g., an interference model with very low interference will look almost identical to a model with no interference. The important question here is whether they can be disambiguated with real data.

Instead, the value of a post-hoc recovery analysis here is to evaluate whether there was a sensible choice of model space—i.e., that it was not a priori guaranteed that a single model (and, specifically, the model we found to be the best explanation for the data) would explain the results of all others. To address this, for each model, we simulated 16 datasets, each of which relied upon parameters sampled from the model priors, which included examples of each of the experimental conditions. We then fit each of these datasets to each of the 7 models to construct the confusion matrix shown in the lower panel of Supplementary Figure 3, by accumulating evidence over each of the 16 participants generated according to each ‘true’ model (columns) for each of the possible explanatory models (rows). This shows that no one model, for the parameter ranges sampled here, explains all other datasets. Interestingly, our ‘winning’ model in the empirical analysis is not the best explanation for any of the datasets simulated (including its own). This is reassuring, in that it implies this model winning was not a foregone conclusion and is driven by the data—not just the choice of model space.”

Your point about the posterior covariance is well founded. As we describe in Supplementary Materials, this is an inherent feature of inverse problems (analogous to EEG source localisation). However, the fact that our posterior densities move significantly away from the prior expectations demonstrates that the data are indeed informative. By adopting a Bayesian framework, we are able to explicitly quantify this uncertainty rather than ignoring it, providing a more transparent account of parameter identifiability. We have added the following in the same section of Supplementary Materials:

“This problem is an inverse problem—inferring parameters from a non-linear model. We therefore expect a degree of posterior covariance between parameters and, consequently, that they cannot be disambiguated with complete certainty. While some degree of posterior covariance is inherent to inverse models—including established methods like EEG source localisation—the fact that many of the parameters are estimated with posterior densities that do not include their prior expectations implies the data are informative about these.

The advantage of the Bayesian approach we have adopted here is that we can explicitly quantify posterior covariance between these parameters, and therefore the degree to which they can be disambiguated. While the posterior covariance matrices from empirical data are the relevant measure here, we can better understand the behaviour of the model inversion scheme in relation to the specific models used using the model recovery analysis reported in Supplementary figure 3.

The middle panel of the figure is key, along with the correlation coefficients reported in the figure caption. Here, we see at least a weak positive correlation (in some cases much stronger) for almost all parameters and limited movement from prior expectations for those parameters that are less convincingly recovered. This reinforces that the ability of the scheme to recover parameters is best assessed in terms of the degree of movement of posterior from prior values following fitting to empirical data.”

(5) The authors employ Bayes factors (BFs) to disambiguate models, but BFs would also strengthen the claims that location, but not colour, is impacted by saccades. Despite colour being a circular variable, colour error is analysed using ANOVA on linearised differences (radians). The authors should also arguably use circular statistics, such as the von Mises distribution, for the analysis of colour.

Regarding the use of circular statistics, you are correct that such error distributions are not suitable for ANOVA, and it is better to use circular statistics. However, for the present dataset, we used the mean absolute angular error per condition (ranging from 0 to π radians), which represents the shortest distance on the colour wheel between the target and the response.

This approach effectively linearises the measure by removing the 2π wrap-around boundary. because the observed errors were relatively small and did not cluster near the π boundary—even in the patient cohorts (Figure 5B)—the "wrap-around" effect of circular space is negligible. Moreover, by analysing the mean error across trials for each condition, rather than trial-wise data, we invoke the Central Limit Theorem. This ensures that the distribution of these means is approximately normal, satisfying the fundamental assumptions of ANOVA. Due to these reasons, we adopted simpler linear models. We confirmed that the data did not violate the assumptions of linear statistics. In this low-noise regime, linear and circular models converge on the same conclusions. This has been revised in Methods:

“For colour memory, we calculated the absolute angular error, defined as the shortest distance on the colour wheel between the target and the reported colour (range 0 to π radians). For the primary statistical analyses, we utilised the mean absolute error per condition for each participant. By analysing these condition-wise means rather than trial-wise raw data, we invoke the Central Limit Theorem, which ensures that the sampling distribution of these means approximates normality. Because the absolute errors in this paradigm were relatively small and did not approach the π boundary (Figure 5B) even in the clinical cohorts, the data were treated as a continuous measure in our linear ANOVAs and regression models. Moreover, because location and colour recall involve different scales and units, all analyses were performed independently for each feature to avoid cross-dimensional magnitude comparisons.”

We have also now integrated Bayesian repeated measures ANOVA throughout the manuscript. The Results section for the young healthy adults now reads (p. 4):

“A repeated measures ANOVA revealed a significant main effect of saccades on location memory (F(3, 20) = 51.52, p < 0.001, partial η²=0.72), with Bayesian analysis providing decisive evidence for the inclusion of the saccade factor (BF_incl = 3.52 x 10^13, P(incl|data) = 1.00). In contrast, colour memory remained remarkably stable across all saccade conditions (F(3, 20) = 0.57, p = 0.64, partial η² =0.03). This null effect was supported by Bayesian analysis, which provided moderate evidence in favour of the null hypothesis (BF₀₁ = 8.46, P(excl|data) = 0.89), indicating that the data were more than eight times more likely under the null model than a model including saccade-related impairment.”

For elderly healthy adults:

“In contrast, colour memory remained unaffected by saccade demands (F(3, 20) = 0.57, p = 0.65, partial η² =0.03), again supported by the Bayesian analysis: BF₀₁ = 8.68, P(excl|data) = 0.90.”

For patient cohorts:

“Bayesian repeated measures ANOVAs further supported this dissociation, providing moderate evidence for the null hypothesis in the AD group (BF₀₁ = 3.35, P(excl|data) = 0.77) and weak evidence in the PD group (BF₀₁ = 2.23, P(excl|data) = 0.69). This indicates that even in populations with established neurodegeneration, the detrimental impact of eye movements is specific to the spatial domain.”

Related description is also updated in Methods – Statistical Analysis.

Minor:

(1) The modelling is described as computational but is arguably better characterised as a heuristic generative model at Marr's algorithmic level. It does not derive from normative computational principles or describe an implementation in neural circuits.

We appreciate your perspective on the classification of our model within Marr’s hierarchy. We agree that our framework is best characterised as an algorithmic-level generative model. Our objective was to identify the mechanistic principles governing transsaccadic updating rather than to provide a normative derivation or a specific circuit-level implementation.

To ensure readers do not over-interpret the term ‘computational’, we have added a clarifying statement in the Discussion acknowledging the algorithmic nature of the model. Interestingly, we note that a model predicated on this form of spatial diffusion implies a neural field representation with a spatial connectivity kernel whose limit approximates the second derivative of a Dirac delta function. While a formal neural field implementation is beyond the scope of the present work, our algorithmic results provide the necessary constraints for such future biophysical models.

p.20: “While we describe the present framework as 'computational', it is more precisely characterised as an algorithmic-level generative model within Marr’s hierarchy. Our focus was on defining the rules of spatial integration and the sources of eye-movement-induced noise, rather than deriving these processes from normative principles or defining their specific neural implementation.”

(2) I did not find a description of the recruitment and characterization of the AD and PD patients.

Apologies for this omission. We have now included a detailed description of participant recruitment and clinical characterisation in the Methods section and also updated Table 2:

“A total of 87 participants completed the study: 21 young healthy adults (YC), 21 older healthy adults (EC), 23 patients with Parkinson’s disease (PD), and 22 patients with Alzheimer’s disease (AD). Their demographic and clinical details are summarised in Table 2. Initially, 90 participants were recruited (22 YC, 21 EC, 25 PD, 22 AD); however, three individuals (1 YC and 2 PD) were excluded from all analyses due to technical issues during data acquisition.

All participants were recruited locally in Oxford, UK. None were professional artists, had a history of psychiatric illness, or were taking psychoactive medications (excluding standard dopamine replacement therapy for PD patients). Young participants were recruited via the University of Oxford Department of Experimental Psychology recruitment system. Older healthy volunteers (all >50 years of age) were recruited from the Oxford Dementia and Ageing Research (OxDARE) database.

Patients with PD were recruited from specialist clinics in Oxfordshire. All had a clinical diagnosis of idiopathic Parkinson's disease and no history of other major neurological or psychiatric conditions. While specific dosages of dopamine replacement therapy (e.g., levodopa equivalent doses) were not systematically recorded, all patients were tested while on their regular medication regimen ('ON' state).

Patients with PD were recruited from clinics in the Oxfordshire area. All had a clinical diagnosis of idiopathic Parkinson’s disease and no history of other major neurological or psychiatric illnesses. While all patients were tested in their regular medication ‘ON’ state, the specific pharmacological profiles—including the exact types of medication (e.g., levodopa, dopamine agonists, or combinations) and dosages—were not systematically recorded. The disease duration and PD severity were also un-recorded for this study.

Patients with AD were recruited from the Cognitive Disorders Clinic at the John Radcliffe Hospital, Oxford, UK. All AD participants presented with a progressive, multidomain, predominantly amnestic cognitive impairment. Clinical diagnoses were supported by structural MRI and FDG-PET imaging consistent with a clinical diagnosis of AD dementia (e.g., temporo-parietal atrophy and hypometabolism).69 All neuroimaging was reviewed independently by two senior neurologists (S.T. and M.H.).

Global cognitive function was assessed using the Addenbrooke’s Cognitive Examination-III (ACE-III).70 All healthy participants scored above the standard cut-off of 88, with the exception of one elderly participant who scored 85. In the PD group, two participants scored below the cut-off (85 and 79). In the AD group, six participants scored above 88; these individuals were included based on robust clinical and radiological evidence of AD pathology rather than their ACE-III score alone.”

(3) YA and OA patients appear to differ in gender distribution.

We acknowledge the difference in gender distribution between the young (71.4% female) and older adult (57.1% female) cohorts. However, we do not anticipate that gender influences the fundamental computational mechanisms of retinotopic maintenance or transsaccadic remapping. These processes represent low-level visuospatial functions for which there is no established evidence of gender-specific differences in precision or coordinate transformation. We have ensured that the gender distribution for each cohort is clearly listed in the demographics table (Table 2) for full transparency.

Thank you very much for very insightful feedback!

Reviewer #3 (Public review):

Thank you for the positive feedback regarding our inclusion of clinical groups and the identification of computational phenotypes that differentiate these cohorts.

To address your concerns about the model, we have clarified our use of Bayesian Model Selection, which inherently penalises model complexity to ensure that our results are not driven solely by the number of parameters. We will also provide further evidence regarding model generalisability to address the concern of overfitting.

Regarding the link with the ROCF, we have revised the manuscript to better highlight the specific relationship between our transsaccadic parameters and the ROCF data and better motivate the inclusion of these results in the main text.

Below is our response to your suggestions point-by-point:

(1) The models tested differ in terms of the number of parameters. In general, a larger number of parameters leads to a better goodness of fit. It is not clear how the difference in the number of parameters between the models was taken into account. It is not clear whether the modelling results could be influenced by overfitting (it is not clear how well the model can generalize to new observations).

To ensure our results were not driven by the number of parameters, we utilised random-effects Bayesian Model Selection (BMS) to adjudicate between our candidate models. Unlike maximum likelihood methods, BMS relies on the marginal likelihood (model evidence), which inherently balances model fit against parsimony—a principle known as the Occam’s Razor (Rasmussen and Ghahramani, 2000). In this framework, a model is only preferred if the improvement in fit justifies the additional parameter space; redundant parameters actually lower model evidence by diluting the probability mass. We would be happy to point toward literature that discusses how these marginal likelihood approximations provide a more robust guard against overfitting than standard metrics like BIC or AIC (MacKay, 2003; Murray and Ghahramani, 2005; Penny, 2012).

The fact that the "Dual (Saccade) + Interference" model (Model 7) emerged as the winner—with a Bayes Factor of 6.11 against the next best alternative—demonstrates that its complexity was statistically justified by its superior account of the trial-by-trial data.

Furthermore, to address the risk of overfitting, we established the generalisability of these parameters by using them to predict performance on an independent clinical task. These parameters successfully explained ~62% of the variance in ROCF copy scores—a very distinct, real-world task--confirming that they represent robust computational phenotypes rather than idiosyncratic fits to the initial dataset.

In the Results (p10):

“We used random-effects Bayesian model selection to identify the most plausible generative model. This process relies on the marginal likelihood (model evidence), which inherently balances model fit against complexity—a principle often referred to as Occam’s razor.[25–27]”

In the Discussion (p17):

“Importantly, the risk of overfitting is mitigated by the Bayesian Model Selection framework; by utilising the marginal likelihood for model comparison, the procedure inherently penalises excessive model complexity and promotes generalisability.[25–27,42] This generalisability was further evidenced by the model's ability to predict performance on the independent ROCF task, confirming that these parameters represent robust mechanistic phenotypes rather than idiosyncratic fits to the initial dataset.”

(2) Results specificity: it is not clear how specific the modelling results are with respect to constructional ability (measured via the Rey-Osterrieth Complex Figure test). As with any cognitive test, performance can also be influenced by general, non-specific abilities that contribute broadly to test success.

We agree that constructional performance is influenced by both specific mechanistic constraints and general cognitive abilities. To isolate the unique contribution of transsaccadic updating, we therefore performed a partial correlation analysis across the entire sample. We examined the relationship between location error in the two-saccades condition (our primary behavioural measure of transsaccadic memory) and ROCF copy scores. Even after partialling out the effects of global cognitive status (ACE-III total score), age, and years of education, the correlation remained highly significant (rho = -0.39, p < 0.001).

This suggests that our model captures a specific computational phenotype—the precision of spatial updating during active visual sampling—rather than acting as a proxy for non-specific cognitive decline. This mechanistic link explains why traditional working memory measures (e.g., digit span or Corsi blocks) frequently fail to predict drawing performance; unlike those tasks, figure copying requires thousands of saccades, making it uniquely sensitive to the precision of the dynamic remapping signals identified by our modelling framework.

We added the following text in the Discussion (p19):

“We also found that the relationship between transsaccadic working memory and ROCF performance remains highly significant (rho = -0.39, p < 0.001), even after controlling for age, education, and global cognitive status (ACE-III total score). Consequently, transsaccadic updating may represent a discrete computational phenotype required for visuomotor control, rather than a non-specific proxy for global cognitive decline.[57]”

Reviewer #3 (Recommendations for the authors):

(1) The authors mention in the introduction the following: "One key hypothesis is that we use working memory across visual fixations to update perception dynamically", citing the following manuscript:

Harrison, W. J., Stead, I., Wallis, T. S. A., Bex, P. J. & Mattingley, J. B. A computational 906 account of transsaccadic attentional allocation based on visual gain fields. Proc. Natl. 907 Acad. Sci. U.S.A. 121, e2316608121 (2024).

However, the manuscript above does not refer explicitly to the involvement of working memory in transaccadic integration of object location in space. Rather, it takes advantage of recent evidence showing how the true location of a visual object is represented in the activity of neurons in primary visual cortex ( A. P. Morris, B. Krekelberg, A stable visual world in primate primary visual cortex. Curr. Biol. 29, 1471-1480.e6 (2019) ). The model hypothesizes that true locations of objects are readily available, and then allocates attention in real-world coordinates, allowing efficient coordination of attention and saccadic eye movements.

Thank you for clarification. As suggested, we have now included the citation of Morris & Krekelberg (2019) to acknowledge the evidence for stable object locations within the primary visual cortex.

(2) The authors in the introduction and the title use the terms 'transaccadic memory' and 'spatial working memory'. However, it is not clear whether these can be used interchangeably or are reflecting different constructs.

Classical measures of visuo-spatial working memory are derived from the Corsi task (or similar), where the location of multiple objects is displayed and subsequently remembered. In such tasks, eye movements and saccades are not generally considered, only memory performance, representing the visuo-spatial span.

Transaccadic memory tasks are instead explicitly measuring the performance on remembered object locations of features across explicit eye movements, usually using a very limited number of objects (1 or 2, as is the case for the current manuscript).

While the two constructs share some features, it is not clear whether they represent the same underlying ability or not, especially because in transaccadic tasks, participants are required to perform one or more saccades, thus representing a dual-task case.

I think the relationship between 'transaccadic memory' and 'spatial working memory' should be clarified in the manuscript.

Thank you. Yes, we have added this within the Methods - Measurement of saccade cost to clarify that spatial working memory is the broad cognitive construct responsible for short-term maintenance, whereas transsaccadic memory is the specific, dynamic process of remapping representations to maintain stability across eye movements.

In Methods (p.22):

“Within this framework, it is important to distinguish between the broad construct of spatial working memory and the specific process of transsaccadic memory. While spatial working memory refers to the general ability to maintain spatial information over short intervals, transsaccadic memory describes the dynamic updating of these representations—termed remapping—to ensure stability across eye movements. Unlike classical 'static' measures of spatial working memory, such as the Corsi block task which focuses on memory span, transsaccadic memory tasks explicitly require the integration of stored visual information with motor signals from intervening saccades. Our paradigm treats transsaccadic updating as a core computational process within spatial working memory, where eye-centred representations are actively reconstructed based on noisy memories of the intervening saccade vectors.”

(3) In Figure 1, the second row indicates the presentation of item 2. Indeed, in the condition 'saccade-after-item-1', the target in the second row of Figure 1 is displaced, as expected. This clarifies the direction and amplitude of the first saccade requested. However, from Figure 1, it is hard to understand the amplitude and direction of the second requested saccade. I think the figure should be updated, giving a full description of the direction and amplitude of the second saccade as well ('saccade-after-item-2' and 'two-saccades' conditions).

We agree that making the figure legend more self-contained is beneficial for the reader. While the specific physical parameters and the trial sequence for each condition are detailed in the Results and Methods sections, we have now updated the legend for Figure 1 to explicitly define these details. Specifically, we have clarified that the colour wheel itself served as the target for the second instructed saccade (i.e., the movement from the second fixation cross to the colour wheel location). We have also included the quantitative constraint that all saccade vectors were at least 8.5 degrees of visual angle in amplitude. Given the limited space within a figure legend, we hope these concise additions provide the transparency requested without interrupting the conceptual flow of the diagram.

Updated Figure 1 legend:

“Participants were asked to fixate a white cross, wherever it appeared. They had to remember the colour and location of a sequence of two briefly presented coloured squares (Item 1 and 2), each appearing within a white square frame. They then fixated a colour wheel wherever it appeared on the screen, which served as the target for the second instructed saccade (i.e., a movement from the second fixation cross to the colour wheel location). This cued recall of a specific square (Item 1 or Item 2 labelled within the colour wheel). Participants selected the remembered colour on the colour wheel which led to a square of that colour appearing on the screen. They then dragged this square to its remembered location on the screen. Saccadic demands were manipulated by varying the locations of the second frame and the colour wheel, resulting in four conditions in their reliance on retinotopic versus transsaccadic memory: (1) No-Saccade condition providing a baseline measure of within-fixation precision as no eye movements were required. (2) Saccade After Item 1; (3) Saccade After Item 2; (4) Saccades after both items (Two Saccades condition). In all conditions requiring eye movements, saccade vectors were constrained to a minimum amplitude of 8.5° (degrees of visual angle). While the No-Saccade condition isolates retinotopic working memory, conditions (2) to (4) collectively quantify the impact of varying saccadic demands and timings on the maintenance of spatial information, thereby assessing the efficacy of the transsaccadic updating process.”

(4) The authors write: "Eye tracking analysis confirmed high compliance: participants correctly maintained fixation or executed saccades as instructed on the vast majority of trials (83% {plus minus} 14%). Non-compliant trials were excluded 136 from further analysis." 14% of excluded trials are a substantial fraction of trials, given the task requirements. Is this proportion of excluded trials different between experimental groups, and are experimental groups contributing equally to this proportion?

We thank the reviewer for pointing this out, and we apologise for the confusion. The 83% trial number was actually across all four cohorts, and all conditions, and it was actually above 90% for YC, EC and even AD, but dropped to 60 ish in PD group.

We now have conducted a full analysis of compliant trial counts using a mixed ANOVA (4 saccade conditions x 4 cohorts). This analysis revealed a main effect of group (F(3, 80) = 8.06, p < 0.001), which was driven by lower compliance in the PD cohort (mean approx. 25.4 trials per condition) compared to the AD, EC, and YC cohorts (means ranging from 35.8 to 38.9 trials per condition). Crucially, however, the interaction between group and condition was not statistically significant (p = 0.151). This indicates that the relative impact of saccade demands on trial retention was consistent across all four groups.

Because our primary behavioural measure—the saccade cost—is a within-subject comparison of impairment across conditions, these differences in absolute trial numbers do not introduce a systematic bias into our findings. Furthermore, even with the higher attrition in the PD group, we retained a sufficient number of high-quality trials (minimum mean of ~23 trials in the most demanding condition) to support robust trial-by-trial parameter estimation and valid statistical inference. We have updated the Results and Methods to reflect these details.

In Results (p4):

“To mitigate potential confounds, we monitored eye position throughout the experiment. Eye-tracking analysis confirmed high compliance in healthy adults, who followed instructions on the vast majority of trials (Younger Adults: 97.2 ± 5.2 %; Older Adults: 91.3 ± 20.4 %). The mean difference between these groups was negligible, representing just 1.25 trials per condition, and was not statistically significant (t(80) = 0.16, p = 1.000; see more in Methods – Eyetracking data analysis). Non-compliant trials were excluded from all further analyses.”

In Methods (p27):

“Eye-tracking analysis confirmed high compliance overall, with participants correctly maintaining fixation or executing saccades on the vast majority of trials (83% across all participants). A mixed ANOVA revealed a main effect of group on trial retention (F(3, 80) = 8.06, p < 0.001, partial η² = 0.23), primarily due to lower compliance in the PD cohort (YC: 97±4%; EC: 91±10%; AD: 95±5%; PD: 63±38%). Importantly, there was no significant interaction between group and saccade condition (F(3.36, 80) = 1.78, p = 0.15, partial η² = 0.008), suggesting that trial attrition was not disproportionately affected by specific task demands in any group.

We acknowledge that this reduced trial count in the PD group represents a limitation for across-cohort comparison. However, the absolute number of compliant trials in PD group (mean approx. 25 per condition) remained sufficient for robust trial-by-trial parameter estimation. Furthermore, the lack of a significant group-by-condition interaction confirms that the results reported for this cohort remain valid and that our primary finding of a selective spatial memory deficit is robust to these differences in data retention.”

(5) Modelling

(a) Degrees of freedom, cross-validation, number of parameters.

I appreciate the effort in introducing and testing different models. Models of increase in complexity and are based on different assumptions about the main drivers and mechanisms underlying the dependent variable. The models differ in the number of parameters. How are the differences in the number of parameters between models taken into account in the modelling analysis? Is there a cost associated with the extra parameters included in the more complex models?

(b) Cross-validation and overfitting.

Overfitting can occur when a model learns the training data but cannot generalize to novel datasets. Cross-validation is one approach that can be used to avoid overfitting. Was cross-validation (or other approaches) implemented in the fitting procedure against overfitting? Otherwise, the inference that can be derived from the modelled parameters can be limited.

To address your concerns regarding model complexity and overfitting, we would like to clarify our use of Bayesian Model Selection (BMS). Unlike frequentist methods that often rely on cross-validation to assess generalisability, we used random-effects BMS based on the marginal likelihood (model evidence). This approach inherently implements Bayesian Occam’s Razor by integrating out the parameters. Under this framework, the use of the marginal likelihood for model selection provides a mathematically equivalent safeguard to frequentist cross-validation, as it evaluates the model's ability to generalise across the entire parameter space rather than just finding a maximum likelihood fit for the training data. Thus, models are penalised not just for the absolute number of parameters, but for their overall functional flexibility. A more complex model is only preferred if the improvement in model fit is substantial enough to outweigh this inherent penalty. The emergence of Model 7 as the winner (Bayes Factor = 6.11 against the next best alternative) confirms that its additional complexity is statistically justified.

Furthermore, in this study we provided an external validation of these recovered parameters by demonstrating that they explain 62% of the variance in an independent, real-world, clinical task (ROCF copy). This empirical evidence confirms that our model captures robust mechanistic phenotypes rather than idiosyncratic noise. We have updated the Results and Discussion to explicitly state these.

In Results: (p10)

“We used random-effects Bayesian model selection to identify the most plausible generative model. This process relies on the marginal likelihood (model evidence), which inherently balances model fit against complexity—a principle often referred to as Occam’s razor.[26–28]”

In Discussion: (p17)

“Importantly, the risk of overfitting is mitigated by the Bayesian Model Selection framework; by utilising the marginal likelihood for model comparison, the procedure inherently penalises excessive model complexity and promotes generalisability.[26–28,43] This generalisability was further evidenced by the model's ability to predict performance on the independent ROCF task, confirming that these parameters represent robust mechanistic phenotypes rather than idiosyncratic fits to the initial dataset.”

(6) n. of participants.

(a) The authors write the following: "A total of healthy volunteers (21 young adults, mean age = 24.1 years; 21 older adults, mean age = 72.4 years) participated in this study. Their demographics are shown in Table 1. All participants were recruited locally in Oxford." However, Table 1 reports the data from more than 80 participants, divided into 4 groups. Details about the PD and AD groups are missing. Please clarify.

We apologize for this lack of clarity in the text. We have rewrote and expand the “Participants” section and corrected Table 2 in the Methods section to reflect the correct number of participants.

In Methods (p20):

“A total of 87 participants completed the study: 21 young healthy adults (YC), 21 older healthy adults (EC), 23 patients with Parkinson’s disease (PD), and 22 patients with Alzheimer’s disease (AD). Their demographic and clinical details are summarised in Table 2. Initially, 90 participants were recruited (22 YC, 21 EC, 25 PD, 22 AD); however, three individuals (1 YC and 2 PD) were excluded from all analyses due to technical issues during data acquisition.

All participants were recruited locally in Oxford, UK. None were professional artists, had a history of psychiatric illness, or were taking psychoactive medications (excluding standard dopamine replacement therapy for PD patients). Young participants were recruited via the University of Oxford Department of Experimental Psychology recruitment system. Older healthy volunteers (all >50 years of age) were recruited from the Oxford Dementia and Ageing Research (OxDARE) database.

Patients with PD were recruited from specialist clinics in Oxfordshire. All had a clinical diagnosis of idiopathic Parkinson's disease and no history of other major neurological or psychiatric conditions. While specific dosages of dopamine replacement therapy (e.g., levodopa equivalent doses) were not systematically recorded, all patients were tested while on their regular medication regimen ('ON' state).

Patients with PD were recruited from clinics in the Oxfordshire area. All had a clinical diagnosis of idiopathic Parkinson’s disease and no history of other major neurological or psychiatric illnesses. While all patients were tested in their regular medication ‘ON’ state, the specific pharmacological profiles—including the exact types of medication (e.g., levodopa, dopamine agonists, or combinations) and dosages—were not systematically recorded. The disease duration and PD severity were also un-recorded for this study.

Patients with AD were recruited from the Cognitive Disorders Clinic at the John Radcliffe Hospital, Oxford, UK. All AD participants presented with a progressive, multidomain, predominantly amnestic cognitive impairment. Clinical diagnoses were supported by structural MRI and FDG-PET imaging consistent with a clinical diagnosis of AD dementia (e.g., temporo-parietal atrophy and hypometabolism).[70] All neuroimaging was reviewed independently by two senior neurologists (S.T. and M.H.).

Global cognitive function was assessed using the Addenbrooke’s Cognitive Examination-III (ACE-III).[71] All healthy participants scored above the standard cut-off of 88, with the exception of one elderly participant who scored 85. In the PD group, two participants scored below the cut-off (85 and 79). In the AD group, six participants scored above 88; these individuals were included based on robust clinical and radiological evidence of AD pathology rather than their ACE-III score alone.”

(b) As modelling results rely heavily on the quality of eye movements and eye traces, I believe it is necessary to report details about eye movement calibration quality and eye traces quality for the 4 experimental groups, as noisier data could be expected from naïve and possibly older participants, especially in case of clinical conditions. Potential differences in quality between groups should be discussed in light of the results obtained and whether these could contribute to the observed patterns.

Thank you for pointing this out. We have revised the Methods about how calibration was done:

(p27) “Prior to the experiment, a standard nine-point calibration and validation procedure was performed. Participants were instructed to fixate a small black circle with a white centre (0.5 degrees) as it appeared sequentially at nine points forming a 3 x 3 grid across the screen. Calibration was accepted only if the mean validation error was below 0.5 degrees and the maximum error at any single point was below 1.0 degree. If these criteria were not met, or if the experimenter noticed significant gaze drift between blocks, the calibration procedure was repeated. This calibration ensured high spatial accuracy across the entire display area, facilitating the precise monitoring of fixations on item frames and saccadic movements to the response colour wheel.”

Moreover, as detailed in our response to Point 4, while the PD group exhibited lower compliance, there was no interaction between group and saccade condition for compliance (p = 0.151). This confirms that any noise or trial attrition was distributed evenly across experimental conditions. Consequently, the observed "saccade cost" (the difference in error between conditions) is not an artefact of unequal noise but represents a genuine mechanistic impairment in spatial updating. We have updated the Methods to clarify this distinction.

Furthermore, our Bayesian framework explicitly estimates precision (random noise) as a distinct parameter from updating cost (saccade cost). This allows the model to partition the variance: even if a clinical group is "noisier" overall, this is captured by the precision parameter, ensuring it does not inflate the specific estimate of saccade-driven memory impairment.

(7) Figure 5. I suggest reporting these results using boxplots instead of barplots, as the former gives a better overview of the distributions.

We appreciate the suggestion to use boxplots to better illustrate data distributions. However, we have chosen to retain the current bar plot format due to the visual and statistical complexity of our 4 x 4 x 2 experimental design. Figure 5 represents 16 distinct distributions across four groups and four conditions for both location and colour measures; employing boxplots/violins for this density of data would significantly increase visual clutter and make the figure difficult to parse.

Furthermore, the primary objective of this figure is to reflect the statistical analysis and illustrate group differences in overall performance and highlight the specific finding that patients with AD were significantly more impaired across all conditions compared to YC, EC, and PD groups. Our statistical focus remains on the mean effects—specifically the significant main effect of group (F(3, 318) = 59.71, p < 0.001) and the critical null-interaction between group and condition (p = 0.90). The error measure most relevant to these comparisons is the standard error of the mean (SEM), rather than the interquartile range (IQR). We think that bar plots provide the most straightforward and scannable representation of these mean differences and the consistent pattern of decay across cohorts for the final manuscript layout.

To address the reviewer’s request for distributional transparency, we have provided a version of Figure 5 using grouped boxplots in the supplementary material (Supplementary figure 2). We note, however, that the spread of raw data points in these plots does not directly reflect the variance associated with our within-subject statistical comparisons.

(8) Results specificity, trans-saccadic integration and ROCF. The authors demonstrate that the derived model parameters account for a significant amount of variability in ROCF performance across the experimental groups tested (Figure 8A). However, it remains unclear how specific the modelling results are with respect to the ROCF.

The ROCF is generally interpreted as a measure of constructional ability. Nevertheless, as with any cognitive test, performance can also be influenced by more general, non-specific abilities that contribute broadly to test success. To more clearly link the specificity between modelling results and constructional ability, it would be helpful to include a test measure for which the model parameters would not be expected to explain performance, for example, a verbal working memory task.

I am not necessarily suggesting that new data should be collected. However, I believe that the issue of specificity should be acknowledged and discussed as a potential limitation in the current context.

We appreciate this important point regarding the discriminant validity of our findings. We agree that cognitive performance in clinical populations is often influenced by a general "g-factor" or non-specific executive decline. However, we chose the ROCF Copy task specifically because it is a hallmark clinical measure of constructional ability that effectively serves as a real-world transsaccadic task, requiring participants to integrate spatial information across hundreds of saccades between the model figure and the drawing surface.

To address the reviewer’s concern regarding specificity, we leveraged the fact that all participants completed the ACE-III, which includes a dedicated verbal memory component (the ACE Memory subscale). We conducted a partial correlation analysis and found that the relationship between transsaccadic working memory and ROCF copy performance remains highly significant (rho = -0.46, p < 0.001), even after controlling for age, education, and the ACE-III Memory subscale score. This suggests that the link between transsaccadic updating and constructional ability is mechanistically specific rather than a byproduct of global cognitive impairment. We have substantially revised the Discussion to highlight this link and the supporting statistical evidence.

We first updated the last paragraph of Introduction:

“Finally, by linking these mechanistic parameters to a standard clinical measure of constructional ability (the Rey-Osterrieth Complex Figure task), we demonstrate that transsaccadic updating represents a core computational phenotype underpinning real-world visuospatial construction in both health and neurodegeneration.”

The new section in Discussion highlighting the ROCF copy link:

“Importantly, our computational framework establishes a direct mechanistic link between trassaccadic updating and real-world constructional ability. Specifically, higher saccade and angular encoding errors contribute to poorer ROCF copy scores. By mapping these mechanistic estimates onto clinical scores, we found that the parameters derived from our winning model explain approximately 62% of the variance in constructional performance across groups. These findings suggest that the computational parameters identified in the LOCUS task represent core phenotypes of visuospatial ability, providing a mechanistic bridge between basic cognitive theory and clinical presentation.

This relationship provides novel insights into the cognitive processes underlying drawing, specifically highlighting the role of transsaccadic working memory. Previous research has primarily focused on the roles of fine motor control and eye-hand coordination in this skill.[4,50–55] This is partly because of consistent failure to find a strong relation between traditional memory measures and copying ability.[4,31] For instance, common measures of working memory, such as digit span and Corsi block tasks, do not directly predict ROCF copying performance.[31,56] Furthermore, in patients with constructional apraxia, these memory performance often remain relatively preserved despite significant drawing impairments.[56–58] In literature, this lack of association has often been attributed to “deictic” visual-sampling strategies, characterised by frequent eye movements that treat the environment as an external memory buffer, thereby minimising the need to maintain a detailed internal representation.[4,59] In a real-world copying task, the ROCF requires a high volume of saccades, making it uniquely sensitive to the precision of the dynamic remapping signals identified here. Recent eye-tracking evidence confirms that patients with AD exhibit significantly more saccades and longer fixations during figure copying compared to controls, potentially as a compensatory response to trassaccadic working memory constraints.[56] This high-frequency sampling—averaging between 150 and 260 saccades for AD patients compared to approximately 100 for healthy controls—renders the task highly dependent on the precision of dynamic remapping signals.[56] We also found that the relationship between transsaccadic working memory and ROCF performance remains highly significant (rho = -0.46, p < 0.001), even after controlling for age, education, and ACE-III Memory subscore. Consequently, transsaccadic updating may represent a discrete computational phenotype required for visuomotor control, rather than a non-specific proxy for global cognitive decline.[58]

In other words, even when visual information is readily available in the world, the act of drawing performance depends critically on working memory across saccades. This reveals a fundamental computational trade-off: while active sampling strategies (characterised with frequent eye-hand movements) effectively reduce the load on capacity-limited working memory, they simultaneously increase the demand for precise spatial updating across eye movements. By treating the external world as an "outside" memory buffer, the brain minimises the volume of information it must hold internally, but it becomes entirely dependent on the reliability with which that information is remapped after each eye movement. This perspective aligns with, rather contradicts, the traditional view of active sampling, which posits that individuals adapt their gaze and memory strategies based on specific task demands.[3,60] Furthermore, this perspective provides a mechanistic framework for understanding constructional apraxia; in these clinical populations, the impairment may not lie in a reduced memory "span," but rather in the cumulative noise introduced by the constant spatial remapping required during the copying process.[58,61]

Beyond constructional ability, these findings suggest that the primary evolutionary utility of high-resolution spatial remapping lies in the service of action rather than perception. While spatial remapping is often invoked to explain perceptual stability,[11–13,15] the necessity of high-resolution transsaccadic memory for basic visual perception is debated.[13,62–64] A prevailing view suggests that detailed internal models are unnecessary for perception, given the continuous availability of visual information in the external world.[13,44] Our findings support an alternative perspective, aligning with the proposal that high-resolution transsaccadic memory primarily serves action rather than perception.[13] This is consistent with the need for precise localisation in eye-hand coordination tasks such as pointing or grasping.[65] Even when unaware of intrasaccadic target displacements, individuals rapidly adjust their reaching movements, suggesting direct access of the motor system to remapping signals.[66] Further support comes from evidence that pointing to remembered locations is biased by changes in eye position,[67] and that remapping neurons reside within the dorsal “action” visual pathway, rather than the ventral “perception” visual pathway.[13,68,69] By demonstrating a strong link between transsaccadic working memory and drawing (a complex fine motor skill), our findings suggest that precise visual working memory across eye movements plays an important role in complex fine motor control.”

We are deeply grateful to the reviewers for their meticulous reading of our manuscript and for the constructive feedback provided throughout this process. Your insights have significantly enhanced the clarity and rigour of our work.

In addition to the changes requested by the reviewers, we wish to acknowledge a reporting error identified during the revision process. In the original Results section, the repeated measures ANOVA statistics for YC included Greenhouse-Geisser corrections, and the between-subjects degrees of freedom were incorrectly reported as within-subjects residuals. Upon re-evaluation of the data, we confirmed that the assumption of sphericity was not violated; therefore, we have removed the unnecessary Greenhouse-Geisser corrections and corrected the degrees of freedom throughout the Results and Methods sections. We have ensured that these statistical updates are reflected accurately in the revised manuscript and that they do not alter the significance or interpretation of any of our primary findings.

We hope that these revisions address all the concerns raised and provide a more robust account of our findings. We look forward to your further assessment of our work.

This activity is a really effective way to make accessibility feel concrete instead of abstract. By starting with critique and assumptions, it highlights how many “default” design choices silently exclude users before accessibility settings are even considered. I especially like how the Imagine and Design steps force you to think through a specific user’s experience and then brainstorm multiple solutions, rather than jumping straight to a single fix. Ending with exploring existing accessibility settings also reinforces that accessibility is often an afterthought in design, even though it should be part of the core system from the beginning.

This section does a great job comparing different ways of managing disability and, more importantly, showing how each approach places responsibility on different people. Coping strategies and modifying the person often shift the burden onto disabled individuals, asking them to adapt or appear “normal” in environments that were not designed for them. In contrast, universal design and ability-based design move that responsibility to designers and programmers, emphasizing systems that work for a wider range of users. I also appreciated the final point that accessibility is not a linear story of progress—new technologies can improve access for some people while creating new barriers for others, making accessibility an ongoing design challenge rather than a solved problem.

Okay, now that we've seen how some of the modern cryptographic techniques work. Let's see how they work together to make our internet secure. Securing the internet involves making the https protocol and the secure socket level protocol (ssl) secure. You've all familiar with https. This is the protocol you use when, for example, you want to give Amazon your credit card number so that you can buy a book or a movie. The secure socket level is a transport level protocol that is used when the client and server want to communicate through encrypted messages. So, both of these need be made secure And what does that mean? It means two things: that the messages can be sent securely, meaning encrypted and secondly, that the identity of the server can be trusted. When we think we're communicating with Amazon, we want to make sure we're communicating with Amazon and not some rogue site. All browsers and web servers come with a suite of both symmetric and asymmetric ciphers (public key). They also use what are known as digital certificates provided by certificate authorities that enable them to confirm the identity to confirm the identity of (trusted sites, such as Google, Amazon, etc.) servers and other computers on the internet? We're going to see how all this works together.

Let's begin with a handshake that takes place whenever you request, or whenever your browser requests a secure session with a server. So, this is your browser on the left running on your laptop or your desktop computer (or even a mobile device: phones, tablets, etc. since they are smaller, confined computers). It makes a secure request to some server, using the https protocol to this server. The first thing the server does is it responds to the client by sending an x509 certificate, that's a standard certificate containing its public key. The client takes this certificate and uses one of its digital certificates that it has built into it to authenticate that the server really is who it says it is, that the server is Amazon. It also uses the certificate authorities information to confirm that the public key that was sent does belong to Amazon. So, in other words, it can be assured that when it sends an encrypted message, now back to the server that it's sending it to Amazon, and then only Amazon can read the the message. Given that once the client authenticates the server's identity and public key, it uses the publicly key to encrypt a randomly generated symmetric key. The client generates this internally encrypts it in the servers publicly and sends it back to the server. The server, of course, then uses its private key to decrypt the symmetric key. Now, at this point, both the client and server are sharing a symmetric key. And from then on, they can communicate in encrypted messages using that shared symmetric key. All the rest of the traffic between them during this session is done encrypted using that symmetric key. Now, why do they use both public key and symmetric keys in this handshake? Well, the reason is that they use the public key for exchanging the symmetric key. And they use the symmetric key for the actual encryption of the data that they're sending back and forth. And the reason for is, this is simply that symmetric key cryptography is much more efficient than public key cryptography. So, this saves time in terms of the traffic that goes on back and forth between the client and the server. Slide 87

Now, what role do the certificate authorities play? Well, first of all, a Certificate Authority is an entity like a corporation or a foundation that issues digital certificates. These certify the ownership of the public keys, so these certificate authorities need to do whatever it takes including maybe visiting the mem, visiting the organizations that say that may that create these public keys to determine that the public key really is what it says, (example) it is the public key of Google or the public key of Amazon. And the fact that they are trusted third parties, these authorities is what enables the browsers and the servers to trust them. They don't have any stake in the game other than authenticating that these public keys really do belong to who they say they belong to. So, commercial certificate authorities charge money to organizations to create browsers and so forth, and they will automatically provide a set of these certificates that are built into the browsers. For example, Mozilla maintains a list of at least 57 different trusted certificate authority corresponding certificates built right into its software.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

Learn more at Review Commons

Reply to the reviewers

Reply to the reviewers

We are grateful for the reviewers' constructive comments and suggestions, which contributed to improving our manuscript. We are pleased to see that our work was described as an "interesting manuscript in which a lot of work has been undertaken". We are also encouraged by the fact that the experiments were considered "on the whole well done, carefully documented, and support most of the conclusions drawn," and that our findings were viewed as providing "mechanistic insight into how HNRNPK modulates prion propagation" and potentially offering "new mechanical insight of hnRNPK function and its interaction with TFAP2C."

We conducted several new experiments and revised specific sections of the manuscript, as detailed below in the point-by-point response in this letter.

Referee #1

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

The paper by Sellitto describes studies to determine the mechanism by which hnRNPK modulates the propagation of prion. The authors use cell models lacking HNRNPK, which is lethal, in a CRISPR screen to identify genes that suppress lethality. Based on this screen to 2 different cell lines, gene termed Tfap2C emerged as a candidate for interaction with HNRNPK. The show that Tfap2C counteracts the actions of HNRNPK with respect to prion propagation. Cells lacking HNRNPK show increased PrPSc levels. Overexpression of Tfap2C suppesses PrPSc levels. These effects on PrPSc are independent of PrPC levels. By RNAseq analysis, the authors hone in on metabolic pathways regulated by HNRPNK and Tfap2C, then follow the data to autophagy regulation by mTor. Ultimately, the authors show that short-term treatments of these cell models with mTor inhibitors causes increased accumulation of PrPSc. The authors conclude that the loss of HNRNPK leads to a reduced energy metabolism causing mTor inhibition, which is reduces translation by dephosphorylation of S6

Major comments:

1) Fig H and I, Fig 3L. The interaction between Tfap2C and HNRNPK is pretty weak. The interaction may not be consequential. The experiment seems to be well controlled, yielding limited interaction. The co-ip was done in PBS with no detergent. The authors indicate that the cells were mechanically disrupted. Since both of these are DNA binding proteins, is it possible that the observed interaction is due to the proximity on DNA that is linking the 2 proteins, including a DNAase treatment would clarify.

Response: We agree that the observed co-IP between Tfap2c and hnRNP K is weak (previous Fig. 2H-I, Supp. Fig. 3L now shifted in Supp. Fig. 4C-E), and we have now highlighted this in the relevant section of the manuscript to reflect this observation better.

Importantly, the co-IP was performed using endogenous proteins without overexpression or tagging, which can sometimes artificially enhance protein-protein interactions. However, we acknowledge that the use of a detergent-free lysis buffer and mechanical disruption alone may have limited nuclear protein extraction and solubilization, potentially contributing to the low co-IP signal.

To address the reviewer's concerns and clarify whether the observed interaction could be DNA-mediated, we repeated the co-IP experiments under low-detergent conditions and included benzonase nuclease treatment to digest nucleic acids (Fig. 2H-I). DNA digestion was confirmed by agarose gel electrophoresis (Supp. Fig. 4F-G). Additionally, we performed the reciprocal IPs using both hnRNP K and Tfap2c antibodies (Fig. 2H-I). Although the level of co-immunoprecipitation remains modest, these updated experiments continue to demonstrate a specific co-immunoprecipitation between Tfap2c and hnRNP K, independent of DNA bridging. These additional controls and experimental refinements strengthen the validity of our findings. These results are also attached here for your convenience.

2) Supplemental Fig 5B - The western blot images for pAMPK don't really look like a 2 fold increase in phosphorylation in HNRNPK deletion.

Response: We thank the reviewer for raising this point. We re-examined the original pAMPK western blot (previously Supp. Fig. 5B; now presented as Supp. Fig. 6B) and confirmed the reported results. We note that the overall loading is not perfectly uniform across lanes (as suggested by the actin signal), which may affect the visual impression of band intensity. However, the phosphorylation change reported in the manuscript is based on the pAMPK/total AMPK ratio, which accounts for differences in AMPK expression and accurately reflects relative phosphorylation levels. To further address this concern, we performed three additional independent experiments. These new data reproduce the increase in pAMPK/AMPK upon HNRNPK deletion and are now included in the revised Supplementary Fig. 6B, together with the updated quantification. The new blot and the quantification are also attached here for your convenience.

3) Fig. 5A - I don't think it is proper to do statistics on an of 2.

Response: We believe the reviewer's comment refers to Fig. 5B, as Fig. 5A already has sufficient replication. We have now added two additional replicates, bringing the total to four. The updated statistical analysis corroborates our initial results. The new quantification is provided in the revised manuscript (Fig. 5B) along with the new blot (Supp. Fig. 6C). Both data are also attached here for your convenience.

4) Fig 6D. The data look a bit more complicated than described in the text. At 7 days, compared to 2 days, it looks like there is a decrease in % cells positive for 6D11. Is there clearance of PrPSc or proliferation of un-infected cells?

Response: We have now reworded our text in the results paragraph as follows:

"These data show that TFAP2C overexpression and HNRNPK downregulation bidirectionally regulate prion levels in cell culture."

We have now also included the following comments in the discussion section:

"However, prion propagation relies on a combination of intracellular PrPSc seeding and amplification, as well as intercellular spread, which together contribute to the maintenance and expansion of infected cells within the cultured population. In this study, we were limited in our ability to dissect which specific steps of the prion life cycle are affected by TFAP2C. We also cannot fully exclude the possibility that TFAP2C overexpression influenced the relative proliferation of prion-infected versus uninfected cells in the PG127-infected HovL culture, thereby contributing to the observed reduction in the percentage of 6D11+ cells and overall 6D11+ fluorescence. However, we did not observe any signs of cell death, growth impairment, or increased proliferation under TFAP2C overexpression in PG127-infected HovL cells compared to NBH controls (data not shown). This suggests that a negative selective pressure on infected cells or a proliferative advantage of uninfected cells is unlikely in this context".

5) The authors might consider a different order of presenting the data. Fig 6 could follow Fig. 2 before the mechanistic studies in Figs 3-5.

Response: We believe that the current order of presenting the data is more appropriate. The first part of the manuscript focuses on the genetic and functional interactions between hnRNP K and its partners, particularly TFAP2C, which is a critical point for understanding the broader context before delving into the mechanistic studies involving prion-infected cells.

6) The authors use SEM throughout the paper and while this is often used, there has been some interest in using StdDev to show the full scope of variability.

Response: We chose to use SEM as it reflects the precision of the mean, which is central to our statistical comparisons. As the reviewer notes, this is a common and appropriate practice. To address variability, almost all graphs already include individual data points, which provide a direct visual representation of data spread. To further enhance clarity, we have now included StdDev in the Supplementary Source Data table of the revised manuscript.

Discussion:

The discrepancy between short-term and long-term treatments with mTor inhibitors is only briefly mentioned with a bit of a hand-waving explanation. The authors may need a better explanation.

Response: We have now integrated a more detailed explanation in the discussion section of the revised manuscript as follows:

"Previous studies showed that mTORC1/2 inhibition and autophagy activation generally reduce, rather than increase, PrPSc aggregation (79, 80). The reason for this discrepancy remains unclear and may be multifactorial. First, most prior studies were based on long-term mTOR inhibition, whereas our work examined acute inhibition, mimicking the time frame of HNRNPK and TFAP2C manipulation. Acute inhibition may trigger transient metabolic or signaling shifts that differ from adaptive changes associated with mTOR chronic inhibition, potentially overriding autophagy's effects on prion propagation. Additionally, while previous works were primarily conducted in murine in vivo models, our study focused on a human cell system propagating ovine prions. Differences in species background, model complexity (e.g., interactions between different cell types), and prion strain variability, as certain strains exhibit distinct responses to autophagy and mTOR modulation (https://doi.org/10.1371/journal.pone.0137958), likely contributed to the observed differences".

Minor comments:

Page 12 - no mention of chloroquine in the text or related data.

Page 12 - Supp. Fig. E - should be 5E

Response: We thank the reviewer for pointing this out. We have now better highlighted the use of chloroquine in Fig. 5B (see reviewer #1 - Point 3 - Major comments) and in the text as follows:

"Furthermore, in the presence of chloroquine, LC3-II levels rose almost proportionally across all conditions (Fig. 5B), suggesting that the effects of HNRNPK and TFAP2C on autophagy occur at the level of autophagosome formation, rather than autophagosome-lysosome fusion and degradation."

We have corrected the reference to Supp. Fig. 5E.

Reviewer #1 (Significance (Required)):

The study provides mechanistic insight into how HNRNPK modulates prion propagation. The paper is limited to cell models, and the authors note that long term treatment with mTor inhibitors reduced PrPSc levels in an in vivo model.

The primary audience will be other prion researchers. There may be some broader interest in the mTor pathway and the role of HNRNPK in other neurodegenerative diseases.

Referee #2

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

The manuscript "Prion propagation is controlled by a hierarchical network involving the nuclear Tfap2c and hnRNP K factors and the cytosolic mTORC1 complex" by Sellitto et al aims to examine how heterogenous nuclear ribonucleoprotein K (hnRNPK), limits pion propagation. They perform a synthetic - viability CRISPR- ablation screen to identify epistatic interactors of HNRNPK. They found that deletion of Transcription factor AP-2g (TFAP2C) suppressed the death of hnRNP-K depleted LN-229 and U-251 MG cells whereas its overexpression hypersensitized them to hnRNP K loss. Moreover, HNRNPK ablation decreased cellular ATP, downregulated genes related to lipid and glucose metabolism and enhanced autophagy. Simultaneous deletion of TFAP2C reversed these effects, restored transcription and alleviated energy deficiency. They state that HNRNPK and TFAP2C are linked to mTOR signalling and observe that HNRNPK ablation inhibits mTORC1 activity through downregulation of mTOR and Rptor while TFAP2C overexpression enhances mTORC1 downstream functions. In prion infected cells, TFAP2C activation reduced prion levels and countered the increased prion propagation due to HNRNPK suppression. Pharmacological inhibition of mTOR also elevated prion levels and partially mimicked the effects of HNRNPK silencing. They state their study identifies TFAP2C as a genetic interactor of HNRNPK and implicates their roles in mTOR metabolic regulation and establishes a causative link between these activities and prion propagation.

This is an interesting manuscript in which a lot of work has been undertaken. The experiments are on the whole well done, carefully documented and support most of the conclusions drawn. However, there are places where it was quite difficult to read as some of the important results are in the supplementary Figures and it was necessary to go back and forth between the Figs in the main body of the paper and the supplementary Figs. There are also Figures in the supplementary which should have been presented in the main body of the paper. These are indicated in our comments below.

We have the following questions /points:

Major comments:

1) A plasmid harbouring four guide RNAs driven by four distinct constitutive promoters is used for targetting HNRNPK- is there a reason for using 4 guides- is it simply to obtain maximal editing - in their experience is this required for all genes or specific to HNRNPK?

Response: The use of four guide RNAs driven by distinct promoters is chosen to maximize editing efficiency for HNRNPK. As previously demonstrated by J. A. Yin et al. (Ref. 32), this system provides better efficiency for gene knockout (or activation). For HNRNPK, achieving full knockout was crucial for observing a complete lethal phenotype, which made the four guide RNAs approach fundamental. However, other knockout systems, while potentially less efficient, have been shown to work well in other circumstances. We have now included this explanation in the revised manuscript as follows:

"We employed a plasmid harboring quadruple non-overlapping single-guide RNAs (qgRNAs), driven by four distinct constitutive promoters, to target the human HNRNPK gene and maximize editing efficiency in polyclonal LN-229 and U-251 MG cells stably expressing Cas9 (32)."

2) Is there a minimal amount of Cas9 required for editing?

Response: We did not observe a correlation between Cas9 levels and activity, yet the C3 clone was the one with higher Cas9 expression and higher activity (Supp. Fig. 1A-B). We agree that comments about the amount of Cas9 expression may be misleading here. Thus, in the first result paragraph of the revised manuscript, we have now modified the text "we isolated by limiting dilutions LN-229 clones expressing high Cas9 levels" to "we isolated by limiting dilutions LN-229 single-cell clones expressing Cas9".

3) It is stated that cell death is delayed in U251-MG cells compared to LN-229-C3 cells- why? Also, why use glioblastoma cells other than that they have high levels of HNRNPK? Would neuroblastoma cells be more appropriate if they are aiming to test for prion propagation?

Response: As shown in Fig. 1A, U251-MG cells reached complete cell death at day 13, while LN-229 C3 reached it already at day 10. The percentage of viable U251-MG cells is higher (statistically significant) than LN-229 C3 cells at all time points before day 13, when both lines show complete death. The underlying reasons for this partial and relative resistance are probably multiple, but we clearly showed in Fig. 2 that TFAP2C differential expression is one modulator of cell sensitivity to HNRNPK ablation.

We selected glioblastoma cells because their high expression of HNRNPK was essential for developing our synthetic lethality screen strategy, and we have now clarified it in the revised manuscript as follows:

"As model systems, we chose the human glioblastoma-derived LN-229 and U-251 MG cell lines, which express high levels of HNRNPK (2, 3), a key factor for optimizing our synthetic lethality screen."

While neuroblastoma cells might be more relevant in terms of prion neurotoxicity, glial cells, despite their resistance to prion toxicity, are fully capable of propagating prions. Prion propagation in glial cells has been shown to play crucial roles in mediating prion-dependent neuronal loss in a non-autonomous manner (see 10.1111/bpa.13056). This makes glioblastoma cells a valuable model for studying prion propagation (that is the focus of our study), despite the lack of direct toxicity (which is not the focus of our study). We have now added this explanation to the revised manuscript as follows:

"Therefore, we continued our experiments using LN-229 cells, which provide a relevant model for studying prions, as glial cells can propagate prions and contribute to prion-induced neuronal loss through non-cell-autonomous mechanisms."

4) Human CRISPR Brunello pooled library- does the Brunello library use constructs which have four independent guide RNAs as used for the silencing of HNRPNK?

Response: No, the Human CRISPR Brunello pooled library does not use constructs with four independent guide RNAs (qgRNAs). Instead, each gene is targeted by 4 different single-guide RNAs (sgRNAs), each expressed on a separate plasmid. We have now clarified this in the main text of the revised manuscript as follows:

"To identify functionally relevant epistatic interactors of HNRNPK, we conducted a whole-genome ablation screen in LN-229 C3 cells using the Human CRISPR Brunello pooled library (33), which targets 19,114 genes with an average of four distinct sgRNAs per gene, each expressed by a separate plasmid (total = 76,441 sgRNA plasmids)."

5) To rank the 763 enriched genes, they multiply the -log10FDR with their effect size - is this a standard step that is normally undertaken?

Response: The approach of ranking hits using the product of effect size and statistical significance is a well-established method in CRISPR screening studies. This strategy has been explicitly used in high-impact work by Martin Kampmann and others (see https://doi.org/10.1371/journal.pgen.1009103 and https://doi.org/10.1016/j.neuron.2019.07.014 as references). We have now added both references to the revised manuscript.

6) The 32 genes selected- they were ablated individually using constructs with one guide RNA or four guide RNAs?

Response: The 32 genes selected were ablated individually using constructs with quadruple-guide RNAs (qgRNAs), as this approach was intended to maximize editing efficiency for each gene. We have now clarified this in the main text of the revised manuscript as follows:

"We ablated each gene individually using qgRNAs and then deleted HNRNPK."

7) The identified targets were also tested in U251-MG cells and nine were confirmed but the percent viability was variable - is the variability simply a reflection of the different cell line?

Response: The variability in percent viability observed in U251-MG cells likely reflects the inherent differences between cell lines, which can contribute to varying levels of susceptibility to gene ablation, even for the same targets. We have now highlighted these small differences in the main text of the revised manuscript as follows:

"We confirmed a total of 9 hits (Fig. 1H), including the ELPs gene IKBAKP and the transcription factor TFAP2C, the two strongest hits identified in LN-229 C3 cells. However, in the U251-Cas9 the rescue effect did not always fall within the exact range observed in LN-229 C3 cells, likely due to intrinsic differences between the two cell lines."

8) The two strongest hits were IKBAKP and TFAP2C. As TFAP2C is a transcription factor - is it known to modulate expression of any of the genes that were identified to be perturbed in the screen? Moreover, it is stated that it regulates expression of several lncRNAs- have the authors looked at expression of these lncRNAs- is the expression affected- can modulation of expression of these lncRNAs modulate the observed phenotypic effects and also some of the targets they have identified in the screen?

Response: While TFAP2C is a transcription factor known to regulate the expression of several genes and lncRNAs, we did not identify any of its known target genes among the hits of our screen. However, our RNA-seq data and RT-qPCR (data not shown) indicate that the expression of lncRNA MALAT1 and NEAT1 (reported to interact with both HNRNPK and TFAP2C; ref 37, 41, 47) is strongly affected by HNRNPK ablation and to a lesser extent by TFAP2C deletion. However, the double deletion condition does not appear to change these lncRNA levels beyond what is observed with HNRNPK ablation alone. Therefore, we concluded that these changes do not play a primary role in the phenotypic effects observed in our study. Thus, although interesting, we believe that the description of such observations goes beyond the scope of this manuscript and the relevance of this work.

9) As both HNRNPK and TFAP2C modulate glucose metabolism, the authors have chosen to explore the epistatic interaction. This is most reasonable.

Response: We do not have further comments on this point.

10) The orthogonal assay to confirm that deletion of TFAP2C supresses cell death upon removing HNRNPK- was this done using a single guide RNA or multiple guides - is there a level of suppression required to observe rescue? Interestingly ablation of HNRNPK increases TFAP2C expression in LN-229-C3 whereas in U251-Cas9 cells HNRNPK ablation has the opposite effect- both RNA and protein levels of TFAP2C are decreased - is this the cause of the smaller protective effect of TFAP2C deletion in this cell line?

Response: TFAP2C deletion was performed using quadruple-guide RNAs (gqRNAs). We have clarified this point by addressing the reviewer #2's point 6 in "Major comments".

We did not directly test the threshold of TFAP2C inhibition required to suppress HNRNPK ablation-induced cell death. We did not exclude that other effectors may take a role in the smaller protective effect of TFAP2C deletion in the U251-Cas9 cells, however, multiple lines of evidence from our study suggest that TFAP2C expression levels influence cellular sensitivity to HNRNPK loss:

1) Both LN-229 C3 and U251-Cas9 cells are less sensitive to HNRNPK ablation upon TFAP2C deletion (Fig. 1G-H, Fig. 2A-B, Supp. Fig.3A-B).

2) We observed a correlation between endogenous TFAP2C levels and HNRNPK ablation sensitivity. U251-Cas9 cells, where TFAP2C expression is reduced upon HNRNPK ablation (in contrast to LN-229 C3 cells, where HNRNPK ablation leads to an increase in TFAP2C expression) (Fig. 2C-F), are a) less sensitive to HNRNPK deletion than LN-229 C3 (Fig. 1A, 2A-B) and b) the protective effect of TFAP2C deletion is less pronounced than in LN-229 C3 (Fig. 1G-H, Fig. 2A-B, Supp. Fig.3A-B).

3) TFAP2C overexpression experiments (Fig. 2G) establish a causal relationship to the former correlation: TFAP2C overexpression increased U251-Cas9 sensitivity to HNRNPK ablation.

As clearly mentioned in the manuscript, we believe that, taken together, these findings strongly demonstrate a causal role for TFAP2C in modulating sensitivity to HNRNPK loss. Thus, despite the differences in the expression, the proposed viability interaction between TFAP2C and HNRNPK is conserved across cell lines.

To further strengthen our conclusions, we have now added LN-229 C3 TFAP2C overexpression in Fig. 2G (also attached below for your convenience). As for the U251-Cas9, LN-229 C3 cells show increased sensitivity to HNRNPK ablation upon TFAP2C overexpression.

11) Nuclear localisation studies indicate that the HNRNPK and TFAP2C proteins colocalise in the nucleus however the co-IP data is not convincing- although appropriate controls are present, the level of interaction is very low - the amount of HNRNPK pulled down by TFAP2C is really very low in the LN-229C3 cells and even lower in the U251-Cas9 cells. Have they undertaken the reciprocal co-IP expt?

Response: We rephrased our text to better highlight this as also mentioned in our response to reviewer #1 (Point 1 - Major comments). However, as also noted by the reviewer, the experiments included all the relevant controls. Thus, the results are solid and confirm a degree of co-immunoprecipitation (although weak). As detailed in our response to reviewer #1 (Point 1 - Major comments), to strengthen our conclusion, we have now repeated the experiment in low-detergent conditions and used benzonase nuclease for DNA digestion. We also have performed the reciprocal experiment as suggested by the reviewer, confirming the initial results. In our opinion, these additional experiments support the conclusion that Tfap2c and hnRNP K co-immunoprecipitate through a weak, but direct, interaction.

12) They state that LN-229 C3 ∆TFAP2C and U251-Cas9 ∆TFAP2C were only mildly resistant to the apoptotic action of staurosporin Fig 3E and F - I accept they have undertaken the stats which support their statement that at high concentrations of staurosporin the LN-229 C3 ∆TFAP2C cells are less sensitive but the U251-Cas9 ∆TFAP2C decreased sensitivity is hard to believe. Has this been replicated? I agree that HNRNPK deletion causes apoptosis in both LN-229 C3 and U251-Cas9 cells and this is blocked by Z-VAD-FMK - however the block is not complete- the max viability for HNRNPK deletion in LN-229 C3 cells is about 40% whereas for U251-Cas9 cells it is about 30% - does this suggest that cells are being lost by another pathway. Have they tested concentrations higher than 10nM?

Response: The experiments in FIG. 3E-F have been replicated four times, as stated in the figure legend. We agree that TFAP2C plays a limited role in response to staurosporine-induced apoptosis, particularly in U251-Cas9 cells. To ensure clarity, we have now modified our previous sentence as follows:

"LN-229 C3ΔTFAP2C cells were only mildly resistant to the apoptotic action of staurosporine, and U251-Cas9ΔTFAP2C showed even lower and minimal recovery (Fig. 3E-F). These results indicate that TFAP2C plays a limited role in apoptosis regulation and suggest that its suppressive effect on HNRNPK essentiality is not mediated through direct modulation of apoptosis but rather through upstream processes that eventually converge on it."

The incomplete blockade of apoptosis by Z-VAD-FMK suggests that HNRNPK ablation may activate alternative, non-caspase-mediated cell death pathways. Regarding this point, we decided to not test Z-VAD-FMK above 10 nM as we noted that the rescue effect at the lowest concentration (2nM) was not proportionally increasing at higher concentrations, suggesting we already reached saturation. We have now added and clarified these observations in the revised manuscript as follows:

"Z-VAD-FMK decreased cell death consistently and significantly in LN-229 C3 and U251-Cas9 cells transduced with HNRNPK ablation qgRNAs (Fig. 3C‑D), confirming that HNRNPK deletion promotes cell apoptosis. However, we observed that viability recovery plateaued already at the lowest concentration (2 nM) without further increase at higher doses, suggesting a saturation effect. This indicates that while caspase inhibition alleviates part of the cell death, HNRNPK loss triggers additional mechanisms beyond apoptosis".

Following the suggestion of the reviewer, we have now also tested two higher concentrations of Z-VAD (20 and 50nM) in LN-229 cells. At these concentrations, we observed a slight decrease in cell viability in the NT condition, with a rescue effect in the HNRNPK-ablated cells comparable to what was observed at 2-10nM Z-VAD. For this reason, we did not include these data in the revised manuscript, and we attached them here for transparency.

13) The RNA-seq comparisons- the authors use log2 FC Response: We used a log2 FC threshold of >0.5 and 0.25) is commonly used in RNA-seq studies to capture biologically relevant shifts (e.g.,https://doi.org/10.1371/journal.ppat.1012552; https://doi.org/10.1371/journal.ppat.1008653; https://doi.org/10.1016/j.neuron.2025.03.008; https://doi.org/10.15252/embj.2022112338). We complemented this analysis with Gene Set Enrichment Analysis (GSEA) to assess coordinated changes in biological/genetic pathways, ensuring that our conclusions are not based on isolated, minor expression changes nor on arbitrary thresholds. Finally, to enhance our result robustness, we applied False Discovery Rate (FDR) statistics, which is more stringent than a p-value cutoff. We hope this clarification strengthens the reviewer's confidence in the significance of the observed changes.

14) It is stated" Accordingly, we observed increased AMPK phosphorylation (pAMPK) upon ablation of HNRNPK, which was consistently reduced in LN-229 C3ΔTFAP2C cells (Supp. Fig. 5B). LN-229 C3ΔTFAP2C; ΔHNRNPK cells also showed a partial reduction of pAMPK relative to LN-229 C3ΔHNRNPK cells (Supp. Fig. 5B). These results suggest that hnRNP K depletion causes an energy shortfall, leading to cell death.

Response: I am not totally convinced by the data presented in this Fig. The authors have quantified the band intensity and present the ratio of pAMPK to AMPK. Please note that the actin levels are variable across the samples - did they normalise the data using the actin level before undertaking the comparisons? Also, if the authors think this is an important point which supports their conclusion, then it should be in the main body of the paper rather than the supplementary. If AMPK is being phosphorylated, this should lead to activation of the metabolic check point which involves p53 activation by phosphorylation. Activated p53 would turn on p21CIP1 which is a very sensitive indicator of p53 activation.

We also refer the reviewer to our response to reviewer #1 (Point 2 - Major comments). We understand the point of the reviewer as pAMPK/Actin (absolute AMPK phosphorylation) may provide additional context regarding the downstream effects of AMPK activation, which, however, is not the primary scope of our experiment. We believe that in our specific case, a) the pAMPK/AMPK ratio is the most appropriate metric, as it reflects the energy status of the cell (ATP/AMP levels), which was our main point to assess in this experiment, and b) phospho-protein/total protein is the standard approach for quantifying phosphorylation ratio. For completeness, we have now included pAMPK/Actin quantifications in Supp. Fig. 6B of the revised manuscript (also attached below). pAMPK/Actin levels follow the same trend of pAMPK/AMPK in HNRNPK and TFAP2C single ablations. The pAMPK/AMPK partial rescue in HNRNPK;TFAP2C double ablation relative to HNRNPK single deletion is instead not observed at pAMPK/Actin level. We have now added the pAMPK/Actin quantification and this observation to the revised manuscript as follows:

"Accordingly, we observed increased AMPK phosphorylation (pAMPK/AMPK ratio and pAMPK/Actin) upon ablation of HNRNPK, with a trend toward reduction in LN-229 C3ΔTFAP2C cells (Supp. Fig. 6B). LN-229 C3ΔTFAP2C;ΔHNRNPK cells also showed a reduction of pAMPK/AMPK ratio relative to LN-229 C3ΔHNRNPK cells, although absolute AMPK phosphorylation (pAMPK/Actin) remained high (Supp. Fig. 6B)."

We prefer to keep the AMPK blots in Supplementary Fig. 6B, as we believe the main take-home message of the manuscript should remain centered on mTORC1 activity.

15) We also do not understand why the mTOR Suppl. Fig. 5E is not in the main body of the paper. It's clear that RNA and protein levels of mTOR were downregulated in LN-229 C3ΔHNRNPK cells but were partially rebalanced by the ΔTFAP2C- however the ΔTFAP2C;ΔHNRNPK double deletion levels are only slightly higher than the ΔHNRNPK - they are not at the level NT or even ΔTFAP2C (Fig. 4C, Supp. Fig. 5E).

Response: We moved the mTOR blot to Fig.5D of the revised manuscript. About the low rescue effect, this is in line with all the other observations where a full rescue of the effects of HNRNPK ablation is never achieved, but is only partial. As suggested by reviewer #3 (Figure 5 - Point 2), we have now added RT-qPCR in Fig.5C, which corroborates these data.

16) The authors state: "Deletion of HNRNPK diminished the highly phosphorylated forms of 4EBP1, which instead were preserved in both LN-229 C3ΔTFAP2C and LN-229 C3ΔTFAP2C;ΔHNRNPK cells (Fig. 5C). Similarly, the S6 phosphorylation ratio was reduced in LN-229 C3ΔHNRNPK cells and was restored in the ΔTFAP2C;ΔHNRNPK double-ablated cells (Fig. 5C)."

WE are not convinced that p4EBP1 is preserved in the LN-229 C3ΔTFAP2C cells - there is a very faint band which is at a lower level than the band in the LN-229 C3ΔHNRNPK cells. However, when both HNRNPK and TFAP2C were ablated, the p4EBP1 band is clear cut. I agree with the quantitation that deletion of HNRNPK and TFAP2C both reduce the level of 4EBP1 - the reduction is greater with TFAP2 but when both are deleted together the levels of 4EBP1 are higher and p4EBP1 is clearly present. In quantifying the S6 and pS6 levels, did the authors consider the actin levels- they present a ratio of the pS6 to S6. I may be lacking some understanding but why is the ratio of pS6/S6 being calculated. Is the level of pS6 not what is important - phosphorylation of S6 should lead it to being activated and thus it's the actual level of pS6 that is important, not the ratio to the non-phosphorylated protein.

Response: In Fig. 5C, the three-band pattern of 4EBP1 is clearly visible in the NT+NT or WT condition, with the top band representing the highest phosphorylation state. Upon HNRNPK deletion, this top band almost completely disappears, mimicking the effect of our starvation control (Starv.). This top band remains clearly visible in both TFAP2C-ablated and double-ablated cells, supporting our conclusion. In our original text, we referred to the "highly phosphorylated forms" of 4EBP1, which might have caused some confusion, suggesting we were evaluating the two top bands. We are specifically referring only to the very top band (high p4EBP1), which represents the most highly phosphorylated form of 4EBP1. This is the relevant phosphorylated form to focus on, as it is the only one that disappears in the starvation control (Starv.) or upon mTORC1/2 inhibition with Torin-1 (Fig. 7B).

To better clarify these points, we have now more clearly indicated the "high p4EBP1" band with an asterisk in Fig. 5E, added quantification of high p4EBP1/4EBP1, and rephrased the text as follows:

"Deletion of HNRNPK diminished the highest phosphorylated form of 4EBP1 (high p4EBP1, marked with an asterisk), mimicking the effect observed in starved cells (Starv.). This high p4EBP1 band was preserved in both LN-229 C3ΔTFAP2C and LN-229 C3ΔTFAP2C;ΔHNRNPK cells (Fig. 5C).".

Regarding pS6 quantification, we added pS6/Actin quantification in Supp. Fig. 6E and F of the revised manuscript, also attached here for your convenience.

17) When determining ATP levels, do they control for cell number? HNRNPK depletion results in lower ATP levels, co-deletion of TFAP2C rescues this. But this could be because there is less cell-death? So, more cells express ATP. Have they controlled for relative numbers of cells.

Response: As described in the Materials and Methods , we normalized ATP levels to total protein content, which is a standard approach for this type of quantification (see DOI:10.1038/nature19312).

18) The construction of the HovL cell line that propagate ovine prions - very few details are provided of the susceptibility of the cell line to PG127 prions.