She talks about how the ad is taking things that people love and are connected to and destroying them. While the ad is meant to show all the features of the ipad, many people saw it as saying they only need the ipad and the other things don't matter.

This section makes me think social media isn’t just “showing posts”—it’s actively shaping what we believe is important, and even what feels true. The scary part is that the rules can be based on tons of signals we never consented to (like location or contacts), and because the algorithm is hidden, it’s hard to hold anyone accountable when the recommendations go wrong.

This quote shows why it’s so hard to address most issues around social media. It’s almost a necessary evil, as it is an essential part of all of our lives. It is difficult to keep up with real life if you’re not connected online too, so solutions to social media addiction or negative effects must be found on the other end — the developers’ end.

I think this speaks to the divide we often see between empathetic people vs. non-empathetic people. We often see wealthy people who are raised to believe that the world revolves around them, and that breeds apathy. It's important now more than ever to value the wellness of every person, black or white, gay or straight, rich or poor, immigrant or citizen. If people don't understand that everyone getting their needs met leads to a greater outcome for all, the ultra-wealthy will continue to accumulate wealth, and everyone below them will fall further and further into oppression. You don't need firsthand experience to be empathetic to those who are disadvantaged, you just need enough common sense to know it's them today but could be you tomorrow.

It’s really eye-opening to see how social media algorithms are designed to keep us scrolling, even when it’s bad for our mental health. I’ve definitely felt the pressure to keep up with others’ posts, and it’s helpful to understand that this isn’t just my own issue—it’s a feature of the platforms we use.

It's also important to remember that just because a person can see an image doesn't meant that they understand what's going on in the image so keep that in mind when it some to visuals. Given students time to really understand what's in the photo.

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

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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.

This argument can definitely be backed by my own prior experiences. Whether it’s Gone Home or other similar games that I've played and seen–some with horror and mystery aspects–I never truly explored the environments simply for the sake of exploring my surroundings. Rather, I was always driven by a sense of curiosity to unfold the mysteries surrounding my character and the others around me.

I find it interesting that calmer games like walking sims originated from more violent and action-packed games like first-person shooters. Wanting to explore a world usually unavailable due to actions and conflict is common in human beings. It’s like setting a pack of cookies on a table, saying no one can eat it, and then leaving. Surely no one will miss one cookie in the pack. It’s the same concept for these shooter games. Players are busy running around, surviving, and fighting, so they don’t get to actually appreciate the world they are in (by design). It makes a part of their brain curious to experience the world they are already in without the pressures of battle, so a modder will take a cookie form the pack and eat it, opening up the rest of the pack for other people to enjoy. That’s when they realize the game they were praising for graphics and immersion is actually just a rough sketch, raisin cookies when they thought they were chocolate chips. This creates a sense of disappointment. I can see how walking sims were born from it. To cure the disappointment players felt when they realize the game they loved isn’t as polished as they thought. But without the allure of fighting, walking sims need something else, some other temptation. So, they promise ice cream with the cookies, sprinkling lore and stories into their world. Finding out pieces of the story give players their dopamine boost while satisfying their curiosity for adventure. The article then mentioned punishments within the game and how walking sims remove that and instead explore living with the consequences of your actions. This adds more depth to the ice cream and cookies players have been enjoying before, forcing them to either love or hate them more intensely.

SIDE NOTE: Not speaking about learning to write your A,B,C's: Even though there is meaning behind that as well.

!!!

Reviewer #2 (Public review):

Summary:

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

Overall, the study shows some possible functional implications when adding feedback connections in a deep artificial neural network that mimic 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 affects 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 neocortex.

Weaknesses:

Some claims not yet supported.

The problem is that results are phrased quite generally in the abstract and discussion, while the actual results shown in the paper are very specific to certain implementations of top-down feedback and architectures. This could lead to misunderstanding and requires some revisions of the claims in the abstract and discussion (see below).

"Altogether our findings demonstrate that modulatory top-down feedback is a computationally relevant feature of biological brain..."

This claim is not supported, since no performance increase is demonstrated for modulatory feedback. So far, only the second half of the sentence is supported: "...and that incorporating it into ANNs affects their behavior and constrains the solutions it's likely to discover."

"This bias does not impair performance on the audiovisual tasks."

This is only true for the composite top-down feedback that combines driving and modulatory effects, whereas modulatory feedback alone can impair the performance (e.g., in the visual tasks VS1 and VS2). The fact that modulatory feedback alone is insufficient in ANNs to enable effective cross-modal integration and requires some driving component is actually very interesting, but it is not stressed enough in the abstract. This is hinted at in the following sentence, but should be made more explicitly:

"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 and laterally recurrent models."

"Here we develop a deep neural network model that captures the core functional properties of top-down feedback in the neocortex" -> this is too strong, take out "the", because very likely there are other important properties that are not yet incorporated.

"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."

This claim is still not substantiated by evidence provided in the paper. First, the wording is a bit imprecise, because mechanistically, it is not really the feedforward versus feedback (a purely feedforward model is not considered at all in the paper), but modulatory versus driving. Moreover, the second part of the sentence is problematic: The results imply that, computationally/functionally, driving connections are doing the job, while modulatory feedback does not really seem to improve performance (best case, it does not do any harm). It is true that it is a feature that is inspired by biology, but I don't see why the results imply that (modulatory) top-down feedback should be considered in ANN models of the brain. This would require to show that such models either improve performance, or do improve the ability to fit neural data, both which are beyond the scope of the paper.

The same argument holds for the following sentence, which is not supported by the results of the paper:

"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."

Additional supplementary material required

Although the second version checked the influence of processing time, this was not done for the most important figure of the paper, Figure 4. A central claim in the abstract "This bias does not impair performance on the audiovisual tasks" relies on this figure, because only with composite feedback the performance is comparable between the the "drive-only" and "brain-like" models. Thus, the supplementary Figure 3 should also include the composite networks and drive only network to check the robustness of the claim with respect to process time. This robustness analysis should then also be mentioned in the text. For example, it should be mentioned whether results in these networks are robust or not with respect to process time, whether there are differences between network architectures or types of feedback in general etc.

Moreover, the current analysis for networks with modulatory feedback is a bit confusing. Why is the performance so low for the reverse model for a process time of 3 and 10? This is a very strong effect that warrants explanation. More details should be added in the caption as well. For example, are the models separately trained for the output after 3 and 10 processing steps for the comparison, or just evaluated at these times? Not training these networks separately might explain the low performance for some networks, so ideally networks are trained for each choice of processing steps.

Reviewer #2 (Public review):

Summary:

The manuscript reports a cryo-EM structure of TMAO demethylase from Paracoccus sp. This is an important enzyme in the metabolism of trimethylamine oxide (TMAO) and trimethylamine (TMA) in human gut microbiota, so new information about this enzyme would certainly be of interest.

Strengths:

The cryo-EM structure for this enzyme is new and provides new insights into the function of the different protein domains, and a channel for formaldehyde between the two domains.

Weaknesses:

(1) The proposed catalytic mechanism in this manuscript does not make sense. Previous mechanistic studies on the Methylocella silvestris TMAO demethylase (FEBS Journal 2016, 283, 3979-3993, reference 7) reported that, as well as a Zn2+ cofactor, there was a dependence upon non-heme Fe2+, and proposed a catalytic mechanism involving deoxygenation to form TMA and an iron(IV)-oxo species, followed by oxidative demethylation to form DMA and formaldehyde.

In this work, the authors do not mention the previously proposed mechanism, but instead say that elemental analysis "excluded iron". This is alarming, since the previous work has a key role for non-heme iron in the mechanism. The elemental analysis here gives a Zn content of about 0.5 mol/mol protein (and no Fe), whereas the Methylocella TMAO demethylase was reported to contain 0.97 mol Zn/mol protein, and 0.35-0.38 mol Fe/mol protein. It does, therefore, appear that their enzyme is depleted in Zn, and the absence of Fe impacts the mechanism, as explained below.

The proposed catalytic mechanism in this manuscript, I am sorry to say, does not make sense to me, for several reasons:

(i) Demethylation to form formaldehyde is not a hydrolytic process; it is an oxidative process (normally accomplished by either cytochrome P450 or non-heme iron-dependent oxygenase). The authors propose that a zinc (II) hydroxide attacks the methyl group, which is unprecedented, and even if it were possible, would generate methanol, not formaldehyde.

(ii) The amine oxide is then proposed to deoxygenate, with hydroxide appearing on the Zn - unfortunately, amine oxide deoxygenation is a reductive process, for which a reducing agent is needed, and Zn2+ is not a redox-active metal ion;

(iii) The authors say "forming a tetrahedral intermediate, as described for metalloproteinase", but zinc metalloproteases attack an amide carbonyl to form an oxyanion intermediate, whereas in this mechanism, there is no carbonyl to attack, so this statement is just wrong.

So on several counts, the proposed mechanism cannot be correct. Some redox cofactor is needed in order to carry out amine oxide deoxygenation, and Zn2+ cannot fulfil that role. Fe2+ could do, which is why the previously proposed mechanism involving an iron(IV)-oxo intermediate is feasible. But the authors claim that their enzyme has no Fe. If so, then there must be some other redox cofactor present. Therefore, the authors need to re-analyse their enzyme carefully and look either for Fe or for some other redox-active metal ion, and then provide convincing experimental evidence for a feasible catalytic mechanism. As it stands, the proposed catalytic mechanism is unacceptable.

(2) Given the metal content reported here, it is important to be able to compare the specific activity of the enzyme reported here with earlier preparations. The authors do quote a Vmax of 16.52 µM/min/mg; however, these are incorrect units for Vmax, they should be µmol/min/mg. There is a further inconsistency between the text saying µM/min/mg and the Figure saying µM/min/µg.

(3) The consumption of formaldehyde to form methylene-THF is potentially interesting, but the authors say "HCHO levels decreased in the presence of THF", which could potentially be due to enzyme inhibition by THF. Is there evidence that this is a time-dependent and protein-dependent reaction? Also in Figure 1C, HCHO reduction (%) is not very helpful, because we don't know what concentration of formaldehyde is formed under these conditions; it would be better to quote in units of concentration, rather than %.

(4) Has this particular TMAO demethylase been reported before? It's not clear which Paracoccus strain the enzyme is from; the Experimental Section just says "Paracoccus sp.", which is not very precise. There has been published work on the Paracoccus PS1 enzyme; is that the strain used? Details about the strain are needed, and the accession for the protein sequence.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Thach et al. report on the structure and function of trimethylamine N-oxide demethylase (TDM). They identify a novel complex assembly composed of multiple TDM monomers and obtain high-resolution structural information for the catalytic site, including an analysis of its metal composition, which leads them to propose a mechanism for the catalytic reaction.

In addition, the authors describe a novel substrate channel within the TDM complex that connects the N-terminal Zn²-dependent TMAO demethylation domain with the C-terminal tetrahydrofolate (THF)-binding domain. This continuous intramolecular tunnel appears highly optimized for shuttling formaldehyde (HCHO), based on its negative electrostatic properties and restricted width. The authors propose that this channel facilitates the safe transfer of HCHO, enabling its efficient conversion to methylenetetrahydrofolate (MTHF) at the C-terminal domain as a microbial detoxification strategy.

Strengths:

The authors provide convincing high-resolution cryo-EM structural evidence (up to 2 Å) revealing an intriguing complex composed of two full monomers and two half-domains. They further present evidence for the metal ion bound at the active site and articulate a plausible hypothesis for the catalytic cycle. Substantial effort is devoted to optimizing and characterizing enzyme activity, including detailed kinetic analyses across a range of pH values, temperatures, and substrate concentrations. Furthermore, the authors validate their structural insights through functional analysis of active-site point mutants.

In addition, the authors identify a continuous channel for formaldehyde (HCHO) passage within the structure and support this interpretation through molecular dynamics simulations. These analyses suggest an exciting mechanism of specific, dynamic, and gated channeling of HCHO. This finding is particularly appealing, as it implies the existence of a unique, completely enclosed conduit that may be of broad interest, including potential applications in bioengineering.

Weaknesses:

Although the idea of an enclosed channel for HCHO is compelling, the experimental evidence supporting enzymatic assistance in the reaction of HCHO with THF is less convincing. The linear regression analysis shown in Figure 1C demonstrates a THF concentration-dependent decrease in HCHO, but the concentrations used for THF greatly exceed its reported KD (enzyme concentration used in this assay is not reported). It has previously been shown that HCHO and THF can couple spontaneously in a non-enzymatic manner, raising the possibility that the observed effect does not require enzymatic channeling. An additional control that can rule out this possibility would help to strengthen the evidence. For example, mutating the THF binding site to prevent THF binding to the protein complex could clarify whether the observed decrease in HCHO depends on enzyme-mediated proximity effects. A mutation which would specifically disable channeling could be even more convincing (maybe at the narrowest bottleneck).

We agree with the reviewer that HCHO and THF can react spontaneously in a non-enzymatic manner, and our experiments were not intended to demonstrate enzymatic channeling. The linear regression analysis in Figure 1C was designed solely to confirm that HCHO reacts with THF under our assay conditions. Accordingly, THF was titrated over a broad concentration range starting from zero, and the observed THF concentration–dependent decrease in HCHO reflects this chemical reactivity.

We do not interpret these data as evidence that the enzyme catalyzes or is required for the HCHO–THF coupling reaction. Instead, the structural observation of an enclosed channel is presented as a separate finding. We have clarified this point in the revised text to avoid overinterpretation of the biochemical data (page 2, line 16).

Another concern is that the observed decrease in HCHO could alternatively arise from a reduced production of HCHO due to a negative allosteric effect of THF binding on the active site. From this perspective, the interpretation would be more convincing if a clear coupled effect could be demonstrated, specifically, that removal of the product (HCHO) from the reaction equilibrium leads to an increase in the catalytic efficiency of the demethylation reaction.

We agree that, in principle, a decrease in detectable HCHO could also arise from an indirect effect of THF binding on enzyme activity. However, in our study the experiment was not designed to assess catalytic coupling or allosteric regulation. The assay in question monitors HCHO levels under defined conditions and does not distinguish between changes in HCHO production and downstream consumption.

Additionally, we do not interpret the observed decrease in HCHO as evidence that THF binding enhances catalytic efficiency, or that removal of HCHO shifts the reaction equilibrium. Instead, the data are presented to establish that HCHO can react with THF under the assay conditions. Any potential allosteric effects of THF on the demethylation reaction, or kinetic coupling between HCHO removal and catalysis, are beyond the scope of the current study, and are not claimed.

While the enzyme kinetics appear to have been performed thoroughly, the description of the kinetic assays in the Methods section is very brief. Important details such as reaction buffer composition, cofactor identity and concentration (Zn²⁺), enzyme concentration, defined temperature, and precise pH are not clearly stated. Moreover, a detailed methodological description could not be found in the cited reference (6), if I am not mistaken.

Thank you for the suggestion. We have added reference [24] to the methodological description on page 8. The Methods section has been revised accordingly on page 8 under “TDM Activity Assay,” without altering the Zn²⁺ concentration.

The composition of the complex is intriguing but raises some questions. Based on SDS-PAGE analysis, the purified protein appears to be predominantly full-length TDM, and size-exclusion chromatography suggests an apparent molecular weight below 100 kDa. However, the cryo-EM structure reveals a substantially larger complex composed of two full-length monomers and two half-domains.

We appreciate the reviewer’s careful analysis of the apparent discrepancy between the biochemical characterization and the cryo-EM structure. This issue is addressed in Figure S1, which may have been overlooked.

As shown in Figure S1, the stability of TDM is highly dependent on protein and salt conditions. At 150 mM NaCl, SEC reveals a dominant peak eluting between 10.5 and 12 mL, corresponding to an estimated molecular weight of ~170–305 kDa (blue dot, Author response image 1). This fraction was explicitly selected for cryo-EM analysis and yields the larger complex observed in the reconstruction. At lower salt concentrations (50 mM) or higher (>150 mM NaCl), the protein either aggregates or elutes near the void volume (~8 mL).

SDS–PAGE analysis detects full-length TDM together with smaller fragments (~40–50 kDa and ~22–25 kDa). The apparent predominance of full-length protein on SDS–PAGE likely reflects its greater staining intensity per molecule and/or a higher population, rather than the absence of truncated species.

Author response image 1.

Given the lack of clear evidence for proteolytic fragments on the SDS-PAGE gel, it is unclear how the observed stoichiometry arises. This raises the possibility of higher-order assemblies or alternative oligomeric states. Did the authors attempt to pick or analyze larger particles during cryo-EM processing? Additional biophysical characterization of particle size distribution - for example, using interferometric scattering microscopy (iSCAT)-could help clarify the oligomeric state of the complex in solution.

Cryo-EM data were collected exclusively from the size-exclusion chromatography fraction eluting between 10.5 and 12 mL. This fraction was selected to isolate the dominant assembly in solution. Extensive 2D and 3D particle classification did not reveal distinct classes corresponding to smaller species or higher-order oligomeric assemblies. Instead, the vast majority of particles converged to a single, well-defined structure consistent with the 2 full-length + 2 half-domain stoichiometry.

A minor subpopulation (~2%) exhibited increased flexibility in the N-terminal region of the two full-length subunits, but these particles did not form a separate oligomeric class, indicating conformational heterogeneity rather than alternative assembly states (Author response image 2). Together, these data support the 2+2½ architecture as the predominant and stable complex under the conditions used for cryo-EM. Additional techniques, such as iSCAT, would provide complementary information, but are not required to support the conclusions drawn from the SEC and cryo-EM analyses presented here.

Author response image 2.

The authors mention strict symmetry in the complex, yet C2 symmetry was enforced during refinement. While this is reasonable as an initial approach, it would strengthen the structural interpretation to relax the symmetry to C1 using the C2-refined map as a reference. This could reveal subtle asymmetries or domain-specific differences without sacrificing the overall quality of the reconstruction.

We thank the reviewer for this thoughtful suggestion. In standard cryo-EM data processing, symmetry is typically not imposed initially to minimize potential model bias; accordingly, we first performed C1 refinement before applying C2 symmetry. The resulting C1 reconstructions revealed no detectable asymmetry or domain-specific differences relative to the C2 map. In addition, relaxing the symmetry consistently reduced overall resolution, indicating lower alignment accuracy and further supporting the presence of a predominantly symmetric assembly.

In this context, the proposed catalytic role of Zn²⁺ raises additional questions. Why is a 2:1 enzyme-to-metal stoichiometry observed, and how does this reconcile with previous reports? This point warrants discussion. Does this imply asymmetric catalysis within the complex? Would the stoichiometry change under Zn²⁺-saturating conditions, as no Zn²⁺ appears to be added to the buffers? It would be helpful to clarify whether Zn²⁺ occupancy is equivalent in both active sites when symmetry is not imposed, or whether partial occupancy is observed.

The observed ~2:1 enzyme-to-Zn²⁺ stoichiometry likely reflects the composition of the 2 full-length + 2 half-domain (2+2½) complex. In this assembly, only the core domains that are fully present in the complex contribute to metal binding. The truncated or half-domains lack the Zn²⁺ binding domain. As a result, only two metal-binding sites are occupied per assembled complex, consistent with the measured stoichiometry.

We note that Zn²⁺ was not deliberately added to the buffers, so occupancy may not reflect full saturation. Based on our cryo-EM and biochemical data, both metal-binding sites in the full-length subunits appear to be occupied to an equivalent extent, and no clear evidence of asymmetric catalysis is observed under these current experimental conditions. Full Zn²⁺ saturation could potentially increase occupancy, but was not explored in these experiments.

The divalent ion Zn²⁺ is suggested to activate water for the catalytic reaction. I am not sure if there is a need for a water molecule to explain this catalytic mechanism. Can you please elaborate on this more? As one aspect, it might be helpful to explain in more detail how Zn-OH and D220 are recovered in the last step before a new water molecule comes in.

Thank you for your suggestion. We revised our text in page 2 as bellow.

Based on our structural and biochemical data, we propose a structurally informed working model for TMAO turnover by TDM (Scheme 1). In this model, Zn²⁺ plays a non-redox role by polarizing the O–H bond of the bound hydroxyl, thereby lowering its pK_a. The D220 carboxylate functions as a general base, abstracting the proton to generate a hydroxide nucleophile. This hydroxide then attacks the electrophilic N-methyl carbon of TMAO, forming a tetrahedral carbinolamine (hemiaminal) intermediate. Subsequent heterolytic cleavage of the C–N bond leads to the release of HCHO. D220 then switches roles to act as a general acid, donating a proton to the departing nitrogen, which facilitates product release and regenerates the active site. This sequence allows a new water molecule to rebind Zn²⁺, enabling subsequent catalytic turnovers. This proposed pathway is consistent with prior mechanistic studies, in which water addition to the azomethine carbon of a cationic Schiff base generates a carbinolamine intermediate, followed by a rate-limiting breakdown to yield an amino alcohol and a carbonyl compound, in the published case, an aldehyde (Pihlaja et al., J. Chem. Soc. Perkin Trans. 2, 1983, 8, 1223–1226).

Overall, the authors were successful in advancing our structural and functional understanding of the TDM complex. They suggest an interesting oligomeric complex composition which should be investigated with additional biophysical techniques.

Additionally, they provide an intriguing hypothesis for a new type of substrate channeling. Additional kinetic experiments focusing on HCHO and THF turnover by enzymatic proximity effects would strengthen this potentially fundamental finding. If this channeling mechanism can be supported by stronger experimental evidence, it would substantially advance our understanding and knowledge of biologic conduits and enable future efforts in the design of artificial cascade catalysis systems with high conversion rate and efficiency, as well as detoxification pathways.

Reviewer #2 (Public review):

Summary:

The manuscript reports a cryo-EM structure of TMAO demethylase from Paracoccus sp. This is an important enzyme in the metabolism of trimethylamine oxide (TMAO) and trimethylamine (TMA) in human gut microbiota, so new information about this enzyme would certainly be of interest.

Strengths:

The cryo-EM structure for this enzyme is new and provides new insights into the function of the different protein domains, and a channel for formaldehyde between the two domains.

Weaknesses:

(1) The proposed catalytic mechanism in this manuscript does not make sense. Previous mechanistic studies on the Methylocella silvestris TMAO demethylase (FEBS Journal 2016, 283, 3979-3993, reference 7) reported that, as well as a Zn2+ cofactor, there was a dependence upon non-heme Fe²⁺, and proposed a catalytic mechanism involving deoxygenation to form TMA and an iron(IV)-oxo species, followed by oxidative demethylation to form DMA and formaldehyde.

In this work, the authors do not mention the previously proposed mechanism, but instead say that elemental analysis "excluded iron". This is alarming, since the previous work has a key role for non-heme iron in the mechanism. The elemental analysis here gives a Zn content of about 0.5 mol/mol protein (and no Fe), whereas the Methylocella TMAO demethylase was reported to contain 0.97 mol Zn/mol protein, and 0.35-0.38 mol Fe/mol protein. It does, therefore, appear that their enzyme is depleted in Zn, and the absence of Fe impacts the mechanism, as explained below.

The proposed catalytic mechanism in this manuscript, I am sorry to say, does not make sense to me, for several reasons:

(i) Demethylation to form formaldehyde is not a hydrolytic process; it is an oxidative process (normally accomplished by either cytochrome P450 or non-heme iron-dependent oxygenase). The authors propose that a zinc (II) hydroxide attacks the methyl group, which is unprecedented, and even if it were possible, would generate methanol, not formaldehyde.

(ii) The amine oxide is then proposed to deoxygenate, with hydroxide appearing on the Zn - unfortunately, amine oxide deoxygenation is a reductive process, for which a reducing agent is needed, and Zn2+ is not a redox-active metal ion;

(iii) The authors say "forming a tetrahedral intermediate, as described for metalloproteinase", but zinc metalloproteases attack an amide carbonyl to form an oxyanion intermediate, whereas in this mechanism, there is no carbonyl to attack, so this statement is just wrong.

So on several counts, the proposed mechanism cannot be correct. Some redox cofactor is needed in order to carry out amine oxide deoxygenation, and Zn²⁺cannot fulfil that role. Fe²⁺ could do, which is why the previously proposed mechanism involving an iron(IV)-oxo intermediate is feasible. But the authors claim that their enzyme has no Fe. If so, then there must be some other redox cofactor present. Therefore, the authors need to re-analyse their enzyme carefully and look either for Fe or for some other redox-active metal ion, and then provide convincing experimental evidence for a feasible catalytic mechanism. As it stands, the proposed catalytic mechanism is unacceptable.

We thank the reviewer for the detailed and thoughtful mechanistic critique. We fully agree that Zn²⁺ is not redox-active, and cannot directly mediate oxidative demethylation or amine oxide deoxygenation. We acknowledge that the oxidative step required for the conversion of TMAO to HCHO is not explicitly resolved in the present study. Accordingly, we have revised the manuscript to remove any implication of Zn²⁺-mediated redox chemistry, and have eliminated the previously imprecise analogy to zinc metalloproteases.

We recognize and now discuss prior biochemical work on TMAO demethylase from Methylocella silvestris (MsTDM), which proposed an iron-dependent oxidative mechanism (Zhu et al., FEBS 2016, 3979–3993). That study reported approximately one Zn²⁺ and one non-heme Fe²⁺ per active enzyme, implicated iron in catalysis through homology modeling and mutagenesis, and used crossover experiments suggesting a trimethylamine-like intermediate and oxygen transfer from TMAO, consistent with an Fe-dependent redox process. However, that system lacked experimental structural information, and did not define discrete metal-binding sites.

In contrast,

(1) Our high-resolution cryo-EM structures and metal analyses of TDM consistently reveal only a single, well-defined Zn²⁺-binding site, with no structural evidence for an additional iron-binding site as in the previous report (Zhu et al., FEBS 2016, 3979–3993).

(2) To investigate the potential involvement of iron, we expressed TDM in LB medium supplemented with Fe(NH₄)₂SO₄ and determined its cryo-EM structure. This structure is identical to the original one, and no EM density corresponding to a second iron ion was observed. Moreover, the previously proposed Fe²⁺-binding residues are spatially distant (Figure S6).

(3) ICP-MS analysis shows undetectable Iron, and only Zinc ion (Figure S5).

(4) Our enzyme kinetics analysis with the TDM without Iron is comparable to that of from MsTDM (Figure 1A). The differences in Km and Vmax we propose is due to the difference in the overall sequence of the enzymes. Please also see comment at the end on a new published paper on MsTDM.

While we cannot comment on the MsTDM results, our ‘experimental’ results do not support the presence of an iron-binding site. Our data indicate that this chemistry is unlikely to be mediated by a canonical non-heme iron center as proposed for MsTDM. We therefore revised our model as a structural framework that rationalizes substrate binding, metal coordination, and product stabilization, while clearly delineating the limits of mechanistic inference supported by the current data.

The scheme 1 and proposal mechanism section were revised in page 4. Figure S6 was added.

(2) Given the metal content reported here, it is important to be able to compare the specific activity of the enzyme reported here with earlier preparations. The authors do quote a Vmax of 16.52 µM/min/mg; however, these are incorrect units for Vmax, they should be µmol/min/mg. There is a further inconsistency between the text saying µM/min/mg and the Figure saying µM/min/µg.

Thank you for the correction. We converted the V_max unit to nmol/min/mg. and revised the text in page 2. We also compared with the value of the previous report in the TDM enzyme by revising the text on page 2. See also the note on a newly published manuscript and its comparison.

(3) The consumption of formaldehyde to form methylene-THF is potentially interesting, but the authors say "HCHO levels decreased in the presence of THF", which could potentially be due to enzyme inhibition by THF. Is there evidence that this is a time-dependent and protein-dependent reaction? Also in Figure 1C, HCHO reduction (%) is not very helpful, because we don't know what concentration of formaldehyde is formed under these conditions; it would be better to quote in units of concentration, rather than %.

We appreciate this important point. We have revised Figure 1C to present HCHO levels in absolute concentration units. While the current data demonstrate reduced detectable HCHO in the presence of THF, we agree that distinguishing between HCHO consumption and potential THF-mediated enzyme inhibition would require dedicated time-course and protein-dependence experiments. We have therefore revised the description to avoid overinterpretation and limit our conclusions to the observed changes in HCHO concentration in page 2, line 18-19.

(4) Has this particular TMAO demethylase been reported before? It's not clear which Paracoccus strain the enzyme is from; the Experimental Section just says "Paracoccus sp.", which is not very precise. There has been published work on the Paracoccus PS1 enzyme; is that the strain used? Details about the strain are needed, and the accession for the protein sequence.

Thank you for this comment. We now indicate that the enzyme is derived from Paracoccus sp. DMF and provide the accession number for the protein sequence (WP_263566861) in the Experimental Section (page 8, line 4).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) The ITC experiment requires a ligand-into-buffer titration as an additional control. Also, maybe I misunderstood the molar ratio or the concentrations you used, but if you indeed added a total of 4.75 μL of 20 μM THF into 250 μL of 5 μM TDM, it is not clear to me how this leads to a final molar ratio of 3.

We thank the reviewer for this suggestion. A ligand-into-buffer control ITC experiment was performed and is now included in Figure S8C, which shows no realizable signal.

Regarding the molar ratio, it is our mistake. The experiment used 2.45 μL injections of 80 μM THF into 250 μL of 5 μM TDM. This corresponds to a final ligand concentration of ~12.8 μM, giving a ligand-to-protein molar ratio of ~2.6. We revised our text in page 9, ITC section.

(2) Characterization/quality check of all mutant enzymes should be performed by NanoDSF, CD spectroscopy or similar techniques to confirm that proteins are properly folded and fit for kinetic testing.

We appreciate the reviewer’s suggestion. All mutant proteins, including D220A, D367A, and F327A, were purified with yields similar to the wild-type enzyme. Additionally, cryo-EM maps of the mutants show well-defined density and overall structural integrity consistent with the wild-type. These findings indicate that the introduced mutations do not significantly affect protein folding, supporting their use for kinetic analysis. While NanoDSF might reveal differences in thermal stability due to mutations, it does not provide structural information. Our conclusions are not based on minor differences in thermostability. Our cryo-EM structures of the mutants offer much more reliable structural data than CD spectroscopy.

(3) Best practice would suggest overlapping pH ranges between different buffer systems in the pH-dependence experiments to rule out buffer-specific effects independent of pH.

We thank the reviewer for this helpful suggestion. We agree that overlapping pH ranges between different buffer systems can be valuable for excluding buffer-specific effects. In this study, the pH-dependence experiments were intended to provide a qualitative assessment of pH sensitivity rather than a detailed analysis of buffer-independent pKa values. While we cannot fully exclude minor buffer-specific contributions, the overall trends observed were reproducible and sufficient to support the conclusions drawn. We have added a clarifying statement to the revised manuscript to reflect this consideration, page 2, line 12.

(4) Structural comparison revealed high similarity to a THF-binding protein, with superposition onto a T protein.": It would be nice to show this as an additional figure, as resolution and occupancy for THF are low.

We thank the reviewer for this suggestion. To address this point, we have revised Figure S6 by adding an additional panel (C, now is Figure S7C) showing the structural superposition of TDM with the THF-binding T protein. This comparison is included to better illustrate the structural similarity, despite the limited resolution and partial occupancy of THF density in our map.

(5) Editing could have been done more thoroughly. Some spelling mistakes, e.g. "RESEULTS", "redius", "complec"; kinetic rate constants should be written in italic (not uniform between text and figures); Prism version is missing; Vmax of 16.52 µM/min/mg - doublecheck units; Figure S1B: The "arrow on the right" might have gone missing.

We corrected the spelling in page 2 ~ line 10, page 5 ~ line 34, page 6 ~ line40. Prism version was added. The arrow was added into figure S1B. The Vmax unit is corrected to nmol/min/mg.

Reviewer #2 (Recommendations for the authors):

(1) The authors must re-examine the metal content of their purified enzyme, looking in particular for Fe or another redox-active metal ion, which could be involved in a reasonable catalytic mechanism.

We thank the reviewer for this suggestion and have carefully re-examined the metal content of TDM. Elemental analyses by EDX and ICP-MS consistently detected Zn²⁺ in purified TDM (Zn:protein ≈ 1:2), whereas Fe was below the detection limit across multiple independent preparations (Fig. S5A,B). To assess whether iron could be incorporated or play a functional role, we expressed TDM in E. coli grown in LB medium supplemented with Fe(NH₄SO₄)₂ and performed activity assays in the presence of exogenous Fe²⁺. Neither condition resulted in enhanced enzymatic activity.

Consistent with these biochemical data, all cryo-EM structures reveal a single, well-defined metal-binding site coordinated by three conserved cysteine residues and occupied by Zn²⁺, with no evidence for an additional iron species or other redox-active metal site.

(2) The specific activity of the enzyme should be quoted in the same units as other literature papers, so that the enzyme activity can be compared. It could be, for example, that the content of Fe (or other redox-active metal) is low, and that could then give rise to a low specific activity.

Thank you for the suggestion, we quoted the enzyme units as similar with previous report. and revised the text in in page 2.

Since the submission of our paper a new report on MsTDM has been published (Cappa et al., Protein Science 33(11), e70364). It further supports our findings. First, the reported kinetic parameters using ITC (Vmax = 0.309 μmol/s, approximately 240 nmol/min/mg; Km = 0.866 mM) are comparable to our observed (156 nmol/min/mg and 1.33 mM, respectively) in the absence of exogenous iron. Second, the optimal pH for enzymatic activity similar to that observed in our paraTDM. Third, the reported two-state unfolding behavior is consistent with our cryo-EM structural observations, in which the more dynamic subunits appear to destabilize prior to unfolding of the core domains. Based on these findings, we now propose that Zn²⁺ appears to function primarily as an organizational cofactor at the core catalytic domain (revised Scheme 1).

I would make this bolder - on first read I'm thinking that I would maybe even make this the header because it's very striking and head-nod-y

First phishing. Fishing with an F. There's a way to catch fish using bait like worms. It's fun, except for the worms. Fishing with a Ph isn't fun. It's scary internet stuff. Phishing is a way for bad people to catch your private details, like your bank account number or passwords. The bait they use is lies. Here's how phishing works, say you get an email. It looks like it's from someone you trust, like your bank, but it's not. It tells you to confirm your bank details or your account may be closed. Scary. You click on the link and go to a website. It looks like a real Bank website. But it's not. You enter your details and someone uses them to steal your identity and buy things with your money. Which is not nice. Here's how to be safe from fishing. Number one, your bank will never ask you to confirm your details via an email, like ever. This is the most obvious way to spot a fishing attempt if you receive an email like this, suspecting. Don't click it. Number two, look for your name. Phishing messages say things like, um, dear valued customer. If it doesn't say your name, don't click it. Number three. Look at the URL in your browser browser window if the URL looks like a different name from the name of the company. Don't click it. Number four. Rest your mouse pointer on the link that will show the real web address. If it doesn't look like the proper company name, don't click it. Number five, look for spelling mistakes. If there are any spelling mistakes or the email doesn't look professional? Don't click it. Number six, get security software that includes anti-phishing and identity protection features like Norton 360 or Symantec. Best of all, just don't use links in emails to get to websites like ever. Always type the URL instead. Thank you for looking at our quick guide to scary internet stuff to allow to be safe.

That's why Innovative startups are popping up around the world, solving the security problem with Biometrics. We actually use the vein patterns in your eye. Eye verify discovered that the blood vessels in the whites of your eyes are as unique as the worlds on the tips of your fingers. So the iris, many people know the iris. They expect that to be a good biometric, and it is but actually takes infrared light and an infrared camera. Which phones don't have? We use just an ordinary phone, enter my name. Gosh, this is fast. Done. Eye Verified caught the attention of Samsung Sprint and Wells Fargo. They all invested now. The Kansas City-based company is using that backing to crack two markets where security is Paramount. Number one is Enterprises. The companies want to protect access to their networks. There's a breach like every day, the second one is, you know, broadly, mobile banking or mobile financial Services. According to one forecast by 2019, five, and a half billion people will use Biometric authentication on mobile and wearable devices. MasterCard has been experimenting with biometrics, too, and recently tested an app using voice and facial recognition for 14, 000 e-commerce transactions. MasterCard also invested in Bionam. This Toronto-based startup has developed a wristband, the 79 Nymi that harnesses what may be the most secure Biometric of all your heartbeat. You look at all of the little Peaks and valleys in the shape of that waveform that's unique to you. We've now tied this to you. It's in an active State because it's no, it's still on your rest, right? And now, we can have it do stuff. For example, we can have it unlock a phone. That's the beauty of persistent identity. Imagine how seamless life would be if logging onto your email, unlocking your car, or checking into a flight where as easy as strapping on a wristband and verifying your ECG. The device does the rest is binary to kill the password. I don't know if you use that word too much, but probably.

I think it's a bit of an exaggeration demonizing AI but I think we already know it's not alive and it says its happy to see us. It's like dora the explora saying how's your day going its just a cartoon and behind it is a voice actor that will never know you and your struggles in life.

I've heard that they got there data to train the AI illegally, but I don't think that's our problem I think that's between them and the person they stole from. As long as you inspect sources they use and credit them then that's not your issue. I think sometimes we dig deep into stuff thats none of our buisness. There are a lot of sketchy things going in the world and if we focus too much on its orgin we would die from boycotting everything. It's like if your boss does something illegally to get his money but your just working a normal job as long you don't use that money in a bad way then its none of your buisness what he does because your not directly assisting his act.

I guess there are details that you can find is profound that you won't find AI doing since it's mostly taking whats common but whose to say that It wont in the future make the small decisions we do. At the end of the day when we draw its from our in expereince in life and Ai just observing our observations

while there are relatively more trans people in tech (a clear pattern yes), it does not explain the overall presence of dysphoria in tech.

describes dysphoria as directionlessness, as long as you don't know its cause, mimicking the desires and motions others go through and society suggest. Leading to detachment and withdrawal.

I hadn't thought about it that way, but I think It's right. Instead of just using the product, it would be much more interesting to create something myself

I don't see it exactly the same way, but I agree with part of it. I think writing is different from other talents. For example, being good at math comes from practice ,just repeating things over and over. But with writing, I believe people are born with that imagination; it’s a special gift you’re born with it

It’s so interesting that such a seemingly regular aspect of our modern day society seems to be so disorienting for those in the center of it. It just seems like something people aren’t meant to experience and yet it increasingly because a outcome more people want to achieve

And that's what's dark(ening), I'd say! It naturalises conservatism. By matching mainstream culture to individualistic desire, it establishes A Brave New World's premise: "I am giving you what you want". But desire is manufactured AND HISTORICAL (inherited, slightly molded through Overton window and Creeping normality), there was no choice, there is no choice, we have no free will, we are interdependent!

Matthew effect. Survivors survive, rich get richer. Of course, spotlight bias would have us imagine otherwise it's possible, and actually rich people make sure to create that image by buying news outlets, marketing, philantropies or even social media sites, to shout how many people went from zero to hero. Actually, just check the 1%, and see how monopolistic aristocrats relate and feed on to monopolistic aristocrats.

Trump, Elon, Bezos, Gates, Zuckerberg, are white, straight, cis, men BORN IN RICH FAMILIES.

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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.

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• our egos personalize our life experience
• transformation is what's constant in the universe
• the only way to grieve is to cry
• pain opens your heart
• "if you inquire into the hurt, you know what you're experiencing is love"
• living and dying consciously and simultaneously

This statement is strong because it clearly connects social annotation to active participation. By comparing it to class discussions, it helps readers understand that annotation is not just marking up a text—it’s a form of engagement and conversation.

I think doomscrolling can be really damaging on mental health, but I also think that in the recent time it's become more than just bad news, it's when you're on a social media platform (and say to yourself: just 5 more minutes) and then end up scrolling for another hour or so, without being able to stop. This loss of self control can be really hard to grasp, and take a toll on ones mental health.

This makes me realize that social annotation isn’t just highlighting... it’s contributing to an ongoing conversation about the reading.

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

The authors assess the effectiveness of electroporating mRNA into male germ cells to rescue the expression of proteins required for spermatogenesis progression in individuals where these proteins are mutated or depleted. To set up the methodology, they first evaluated the expression of reporter proteins in wild-type mice, which showed expression in germ cells for over two weeks. Then, they attempted to recover fertility in a model of late spermatogenesis arrest that produces immotile sperm. By electroporating the mutated protein, the authors recovered the motility of ~5% of the sperm; although the sperm regenerated was not able to produce offspring using IVF, the embryos reached the 2-cell state (in contrast to controls that did not progress past the zygote state).

This is a comprehensive evaluation of the mRNA methodology with multiple strengths. First, the authors show that naked synthetic RNA, purchased from a commercial source or generated in the laboratory with simple methods, is enough to express exogenous proteins in testicular germ cells. The authors compared RNA to DNA electroporation and found that germ cells are efficiently electroporated with RNA, but not DNA. The differences between these constructs were evaluated using in vivo imaging to track the reporter signal in individual animals through time. To understand how the reporter proteins affect the results of the experiments, the authors used different reporters: two fluorescent (eGFP and mCherry) and one bioluminescent (Luciferase). Although they observed differences among reporters, in every case expression lasted for at least two weeks. The authors used a relevant system to study the therapeutic potential of RNA electroporation. The ARMC2-deficient animals have impaired sperm motility phenotype that affects only the later stages of spermatogenesis. The authors showed that sperm motility was recovered to ~5%, which is remarkable due to the small fraction of germ cells electroporated with RNA with the current protocol. The sperm motility parameters were thoroughly assessed by CASA. The 3D reconstruction of an electroporated testis using state-of-the-art methods to show the electroporated regions is compelling.

The main weakness of the manuscript is that although the authors manage to recover motility in a small fraction of the sperm population, it is unclear whether the increased sperm quality is substantial to improve assisted reproduction outcomes. The authors found that the rescued sperm could be used to obtain 2-cell embryos via IVF, but no evidence for more advanced stages of embryo differentiation was provided. The motile rescued sperm was also successfully used to generate blastocyst by ICSI, but the statistical significance of the rate of blastocyst production compared to non-rescued sperm remains unclear. The title is thus an overstatement since fertility was never restored for IVF, and the mutant sperm was already able to produce blastocysts without the electroporation intervention.

Overall, the authors clearly show that electroporating mRNA can improve spermatogenesis as demonstrated by the generation of motile sperm in the ARMC2 KO mouse model.

We thank the reviewer for this thoughtful and constructive comment. We agree that our study demonstrates a partial functional recovery of spermatogenesis rather than a complete restoration of fertility. Our main objective was to establish and validate a proof-of-concept approach showing that mRNA electroporation can rescue the expression of a missing or mutated protein in post-meiotic germ cells and result in the production of motile sperm.

To address the reviewer’s concern, we have the title and discussion to more accurately reflect the scope of our findings. The new title reads:

“Sperm motility in mice with oligo-astheno-teratozoospermia restored by in vivo injection and electroporation of naked mRNA”

In the manuscript, we now emphasize that while motility recovery was significant, complete fertility restoration was not achieved. We have also clarified that:

The 5% recovery in motile sperm represents a substantial improvement considering the small population of germ cells reached by the current electroporation method.

The 2-cell embryo formation observed after IVF serves as a strong indication of partial functional recovery

Finally, we now explicitly state in the Discussion that this approach should be considered a therapeutic proof-of-concept, demonstrating feasibility and potential, rather than a fully curative intervention.

Reviewer #2 (Public review):

The authors inject, into the rete testes, mRNA and plasmids encoding mRNAs for GFP and then ARMC2 (into infertile Armc2 KO mice) in a gene therapy approach to express exogenous proteins in male germ cells. They do show GFP epifluorescence and ARMC2 protein in KO tissues, although the evidence presented is weak. Overall, the data do not necessarily make sense given the biology of spermatogenesis and more rigorous testing of this model is required to fully support the conclusions, that gene therapy can be used to rescue male infertility.

In this revision, the authors attempt to respond to the critiques from the first round of reviews. While they did address many of the minor concerns, there are still a number to be addressed. With that said, the data still do not support the conclusions of the manuscript.

We thank the reviewer for their careful and detailed assessment of our manuscript. We appreciate the concerns raised regarding mRNA stability, GFP localization, and the interpretation of spermatogenesis stages, and we have addressed these points in the manuscript and in the responses below.

(1) The authors have not satisfactorily provided an explanation for how a naked mRNA can persist and direct expression of GFP or luciferase for ~3 weeks. The most stable mRNAs in mammalian cells have half-lives of ~24-60 hours. The stability of the injected mRNAs should be evaluated and reported using cell lines. GFP protein's half-life is ~26 hours, and luciferase protein's half-life is ~2 hours.

We thank the reviewer for this important comment. The stability of mRNA-GFP was assessed by RT-QPCR in HEK cells and seminiferous tubule cells (Fig. 5). mRNA-GFP was detected for up to 60 hours in HEK cells and for up to two weeks in seminiferous tubule cells (Fig. 5A). Together, these results suggest that the long-lasting fluorescence observed in our experiments reflects a combination of transcript stability, efficient translation within germ cells and the slow protein turnover that is typical of the spermatogenic lineage.

(2) There is no convincing data shown in Figs. 1-8 that the GFP is even expressed in germ cells, which is obviously a prerequisite for the Armc2 KO rescue experiment shown in the later figures! In fact, to this reviewer the GFP appears to be in Sertoli cell cytoplasm, which spans the epithelium and surrounds germ cells - thus, it can be oft-confused with germ cells. In addition, if it is in germ cells, then the authors should be able to show, on subsequent days, that it is present in clones of germ cells that are maturing. Due to intracellular bridges, a molecule like GFP has been shown to diffuse readily and rapidly (in a matter of minutes) between adjacent germ cells. To clarify, the authors must generate single cell suspensions and immunostain for GFP using any of a number of excellent commercially-available antibodies to verify it is present in germ cells. It should also be present in sperm, if it is indeed in the germline.

We thank the reviewer for this insightful comment. To directly address the concern, we performed additional experiments to assess GFP expression in germ cells following in vivo mRNA delivery. GFP-encoding mRNA was injected and electroporated into the testes on day 0. On day 1, testes were collected, enzymatically dissociated, and the resulting seminiferous tubule cell suspensions were cultured for 12 hours. Live cells were then analyzed by fluorescence microscopy (Fig. 10).

We observed GFP expression in various germ cell types, including pachytene spermatocytes (53,4 %) (Fig 10 A-), round spermatids (25 %) (Fig 10B-E) and in elongated spermatids (11,4%) (Fig 10 C-E). The identification of these cell types was based on DAPI nuclear staining patterns, cell size fig 10 F, non-adherent characteristics, and the use of an enzymatic dissociation protocol.

Fluorescence imaging revealed strong cytoplasmic GFP signals in each of these populations, confirming efficient transfection and translation of the delivered mRNA. These results demonstrate that the in vivo injection and electroporation protocol enables effective mRNA transfection across multiple stages of spermatogenesis. These results confirm that the injected mRNA is efficiently translated in germ cells at various stages of spermatogenesis. Together, these data validate the germ cell-specific nature of the GFP signal, supporting the Armc2 KO rescue experiments.

As mentioned previously, we assessed the stability of mRNA-GFP using RT-QPCR in HEK cells and seminiferous tubule cells (see Fig. 5). mRNA-GFP was detected for up to 60 hours in HEK cells and for up to two weeks in seminiferous tubule cells. Together, these results suggest that the long-lasting fluorescence observed in our experiments reflects a combination of transcript stability and local translation within germ cells, as well as the slow protein turnover typical of the spermatogenic lineage.

Other comments:

70-1 This is an incorrect interpretation of the findings from Ref 5 - that review stated there were ~2,000 testis-enriched genes, but that does not mean "the whole process involves around two thousand of genes"

We thank the reviewer for this helpful comment. We agree that our previous phrasing was imprecise. We have revised the sentence to clarify that approximately 2,000 genes show testis-enriched expression, rather than implying that the entire spermatogenic process is limited to these genes. The corrected sentence now reads:

“Spermatogenesis involves the coordinated expression of a large number of genes, with approximately 2,000 showing testis-enriched expression, about 60% of which are expressed exclusively in the testes”

74 would specify 'male':

we have now specified it as you suggested.

79-84 Are the concerns with ICSI due to the procedure itself, or the fact that it's often used when there is likely to be a genetic issue with the male whose sperm was used? This should be clarified if possible, using references from the literature, as this reviewer imagines this could be a rather contentious issue with clinicians who routinely use this procedure, even in cases where IVF would very likely have worked:

We thank the reviewer for this important comment. Concerns about ICSI outcomes indeed reflect two partly overlapping causes: the procedure itself (direct sperm injection and associated laboratory manipulations) and the clinical/genetic background of couples undergoing ICSI (especially men with severe male-factor infertility). Large reviews and meta-analyses report a small increase in some perinatal and congenital risks after ART/ICSI, but these studies conclude that it is difficult to fully disentangle procedural effects from parental factors. Importantly, genetic or epigenetic abnormalities in the male (which motivate use of ICSI) likely contribute to adverse outcomes in offspring, while some studies also suggest that ICSI-specific manipulations may alter epigenetic marks in embryos. For these reasons professional bodies recommend reserving ICSI for appropriate male-factor indications rather than as routine insemination for non-male-factor cases

We have revised the text accordingly to clarify this distinction:

“ICSI can efficiently overcome the problems faced.  Nevertheless, concerns persist regarding the potential risks associated with this technique, including blastogenesis defect, cardiovascular defect, gastrointestinal defect, musculoskeletal defect, orofacial defect, leukemia, central nervous system tumors, and solid tumors [1-4]. Statistical analyses of birth records have demonstrated an elevated risk of birth defects, with a 30-40 % increased  likelihood in cases involving ICSI [1-4], and a prevalence of birth defects between 1 % and 4 % [3]. It is important to note, however, that the origin of these risks remains debated. Several large epidemiological and mechanistic studies indicate that both the procedure itself (direct microinjection and in vitro manipulation) and the underlying genetic or epigenetic abnormalities often present in men requiring ICSI contribute to the observed outcomes [1, 3] [5, 6] . To overcome these drawbacks, a number of experimental strategies have been proposed to bypass ARTs and restore spermatogenesis and fertility, including gene therapy [7-10].”

199 Codon optimization improvement of mRNA stability needs a reference;

We have added the references accordingly: [11-15]

In one study using yeast transcripts, optimization improved RNA stability on the order of minutes (e.g., from ~5 minutes to ~17 minutes); is there some evidence that it could be increased dramatically to days or weeks?

We agree with the reviewer that codon optimization can enhance mRNA stability, but available evidence indicates that this effect is moderate. In Saccharomyces cerevisiae, Presnyak et al. (2015) [16] showed that codon optimization increased mRNA half-life from approximately 5 minutes to ~17 minutes, representing a several-fold improvement rather than a shift to days or weeks. Similar codon-dependent stabilization has been observed in mammalian systems, where transcripts enriched in optimal codons exhibit longer half-lives and enhanced translation efficiency [11]; [17]). However, these studies consistently report effects on the scale of minutes to hours. In mammalian cells, the prolonged stability of therapeutic or vaccine mRNAs—lasting for days—is primarily achieved through additional features such as optimized untranslated regions, chemical nucleotide modifications (e.g., N¹-methylpseudouridine), and protective delivery systems, rather than codon usage alone ([18]; [19]).

Other molecular optimizations that improve in vivo mRNA stability and translation include a poly(A) tail, which binds poly(A)-binding proteins to protect the transcript from 3′ exonuclease degradation and promotes ribosome recycling, and a CleanCap structure at the 5′ end, which mimics the natural Cap 1 configuration, protects against 5′ exonuclease attack, and enhances translational initiation [11-15]. Together, these modifications act synergistically to stabilize the transcript and support efficient translation.

472-3 The reported half-life of EGFP is ~36 hours - so, if the mRNA is unstable (and not measured, but certainly could be estimated by qRT-PCR detection of the transcript on subsequent days after injection) and EGFP is comparatively more stable (but still hours), how does EGFP persist for 21 days after injection of naked mRNA??

We thank the reviewer for this important comment. The stability of mRNA-GFP was assessed by RT-QPCR in HEK cells and seminiferous tubule cells (Fig. 5). mRNA-GFP was detected for up to 60 hours in HEK cells and for up to two weeks in seminiferous tubule cells (Fig. 5). Together, these results suggest that the long-lasting fluorescence observed in our experiments reflects a combination of transcript stability, efficient translation within germ cells and the slow protein turnover that is typical of the spermatogenic lineage.

Curious why the authors were unable to get anti-GFP to work in immunostaining?

We appreciate the reviewer’s question. We attempted to detect GFP using several commercially available anti-GFP antibodies under various standard immunostaining conditions. However, in our hands, these antibodies consistently produced either no signal or high background staining, making the results unreliable. We therefore relied on direct detection of GFP fluorescence, which provides a more accurate and specific readout of protein expression in our system.

In Fig. 3-4, the GFP signals are unremarkable, in that they cannot be fairly attributed to any structure or cell type - they just look like blobs; and why, in Fig. 4D-E, why does the GFP signal appear stronger at 21 days than 15 days? And why is it completely gone by 28 days? This data is unconvincing.

We would like to thank the reviewer for their comments. Figure 3–4 provides a global overview of GFP expression on the surface of the testis. The entire testis was imaged using an inverted epifluorescence microscope, and the GFP signal represents a composite of multiple seminiferous tubules across the tissue surface. Due to this whole-organ imaging approach, it is not possible to resolve individual structures such as the basement membrane or lumen, which is why the signals may appear as diffuse “blobs.”

Regarding the time-course in Figure 4D–E, the apparent increase in GFP signal at 21 days compared with 15 days likely reflects accumulation and translation of the delivered mRNA in germ cells over time, whereas the absence of signal at 28 days corresponds to the natural turnover and degradation of GFP protein and mRNA in the tissue. We hope this explanation clarifies the observed patterns of fluorescence.

If the authors did a single cell suspension, what types or percentage of cells would be GFP+? Since germ cells are not adherent in culture, a simple experiment could be done whereby a single cell suspension could be made, cultured for 4-6 hours, and non-adherent cells "shaken off" and imaged vs adherent cells. Cells could also be fixed and immunostained for GFP, which has worked in many other labs using anti-GFP.

We thank the reviewer for this insightful comment. To directly address the concern, we performed additional experiments to assess GFP expression in germ cells following in vivo mRNA delivery. GFP-encoding mRNA was injected and electroporated into the testes on day 0. On day 1, testes were collected, enzymatically dissociated, and the resulting seminiferous tubule cell suspensions were cultured for 12 hours. Live cells were then analyzed by fluorescence microscopy (Fig. 10).

We observed GFP expression in various germ cell types, including pachytene spermatocytes (53,4 %) (Fig 10 A-), round spermatids (25 %) (Fig 10B-E) and in elongated spermatids (11,4%) (Fig 10 C-E). The identification of these cell types was based on DAPI nuclear staining patterns, cell size fig 10 F, non-adherent characteristics, and the use of an enzymatic dissociation protocol.

Fluorescence imaging revealed strong cytoplasmic GFP signals in each of these populations, confirming efficient transfection and translation of the delivered mRNA. These results demonstrate that the in vivo injection and electroporation protocol enables effective mRNA transfection across multiple stages of spermatogenesis.

These results confirm that the injected mRNA is efficiently translated in germ cells at various stages of spermatogenesis. Together, these data validate the germ cell-specific nature of the GFP signal, supporting the Armc2 KO rescue experiments.

As mentioned previously, we assessed the stability of mRNA-GFP using RT-QPCR in HEK cells and seminiferous tubule cells (see Fig. 5). mRNA-GFP was detected for up to 60 hours in HEK cells and for up to two weeks in seminiferous tubule cells. Together, these results suggest that the long-lasting fluorescence observed in our experiments reflects a combination of transcript stability and local translation within germ cells, as well as the slow protein turnover typical of the spermatogenic lineage.

In Fig. 5, what is the half-life of luciferase? From this reviewer's search of the literature, it appears to be ~2-3 h in mammalian cells. With this said, how do the authors envision detectable protein for up to 20 days from a naked mRNA? The stability of the injected mRNAs should be shown in a mammalian cell line - perhaps this mRNA has an incredibly long half-life, which might help explain these results. However, even the most stable endogenous mRNAs (e.g., globin) are ~24-60 hrs.

We did not directly assess the stability of luciferase mRNA, but we evaluated the persistence of GFP mRNA, which was synthesized and optimized using the same sequence optimization and chemical modification strategy as the luciferase mRNA. In these experiments, mRNA-GFP was detectable in seminiferous tubule cells for up to two weeks after injection. We therefore expect a similar stability profile for the luciferase mRNA. These findings suggest that the prolonged fluorescence or bioluminescence observed in our study likely reflects a combination of factors, including enhanced transcript stability, local translation within germ cells, and the inherently slow protein turnover characteristic of the spermatogenic lineage.

527-8 The Sertoli cell cytoplasm is not just present along the basement membrane as stated, but also projects all the way to the lumina:

we clarified the sentence " Sertoli cells have an oval to elongated nucleus and the cytoplasm presents a complex shape (“tombstone” pattern) along the basement membrane, with long projections that extend toward the lumen."

529-30 This is incorrect, as round spermatids are never "localized between the spermatocytes and elongated spermatids" - if elongated spermatids are present, rounds are not - they are never coincident in the same testis section:

We thank the reviewer for this important comment and for drawing attention to the detailed staging of the seminiferous epithelium. We agree that the spatial organization of germ cells varies depending on the stage of spermatogenesis. While round spermatids (steps 1–8) and elongated spermatids (steps 9–16) are typically associated with distinct stages, transitional stages of the seminiferous epithelium can contain both cell types in close proximity, reflecting the continuous and overlapping nature of spermatid differentiation (Meistrich, 2013, Methods Mol. Biol. 927:299–307). We have revised the text to clarify this point, indicating that the relative positioning of germ cell types depends on the stage of the seminiferous cycle rather than implying their constant coexistence within the same tubule section.

Fig. 7. To this reviewer, all of the GFP appears to be in Sertoli cell cytoplasm In Figs 1-8 there is no convincing evidence presented that GFP is expressed in germ cells! In fact, it appears to be in Sertoli cells.

We thank the reviewer for their observation. As previously mentioned, we have included an additional experiment specifically demonstrating GFP expression in germ cells (fig 10). This new data provides clear evidence that the GFP signal is not restricted to Sertoli cells and confirms successful uptake and translation of GFP mRNA in germ cells.

Fig. 9 - alpha-tubuline?

We corrected the figure.

Fig. 11 - how was sperm morphology/motility not rescued on "days 3, 6, 10, 15, or 28 after surgery", but it was in some at 21 and 35? How does this make sense, given the known kinetics of male germ cell development??

We note the reviewer’s concern regarding the timing of motile sperm appearance. Variability among treated mice is expected because transfection efficiency differed between spermatogonia and spermatids. Full spermiogenesis requires ~15 days, and epididymal transit adds ~8 days, consistent with motile sperm appearing around 21 days post-injection in some mice.

And at least one of the sperm in the KO in Fig. B5 looks relatively normal, and the flagellum may be out-of-focus in the image? With only a few sperm for reviewers to see, how can we know these represent the population?

We thank the reviewer for their comment. Upon closer examination of the image, the flagellum of the spermatozoon in question is clearly abnormally short and this is not due to being out of focus. Furthermore, the supplementary figure shows that the KO consistently lacks normal spermatozoa. These defects are consistent with previous findings from our laboratory [22], confirming that the observed phenotype is representative of the KO population rather than an isolated occurrence.

Reviewer #3 (Public review):

Summary:

The authors used a novel technique to treat male infertility. In a proof-of-concept study, the authors were able to rescue the phenotype of a knockout mouse model with immotile sperm using this technique. This could also be a promising treatment option for infertile men.

Strengths:

In their proof-of-concept study, the authors were able to show that the novel technique rescues the infertility phenotype of Armc2 knockout spermatozoa. In the current version of the manuscript, the authors have added data on in vitro fertilisation experiments with Armc2 mRNA-rescued sperm. The authors show that Armc2 mRNA-rescued sperm can successfully fertilise oocytes that develop to the blastocyst stage. This adds another level of reliability to the data.

Weaknesses:

Some minor weaknesses identified in my previous report have already been fixed. The technique is new and may not yet be fully established for all issues. Nevertheless, the data presented in this manuscript opens the way for several approaches to immotile spermatozoa to ensure successful fertilisation of oocytes and subsequent appropriate embryo development.

[Editors' note: The images in Figure 12 do not support the authors' interpretation that 2-cell embryos resulted from in vitro fertilization. Instead, the cells shown appear to be fragmented, unfertilized eggs. Combined with the lack of further development, it seems highly unlikely that fertilization was successful.]

We thank the reviewer for their careful evaluation and constructive feedback. We appreciate the acknowledgment of the strengths of our study, particularly the proof-of-concept demonstration that Armc2-mRNA electroporation can rescue sperm motility in Armc2 knockout mice.

Regarding the concern raised by the editor about Figure 12, we would like to clarify two technical points. First, the IVF experiments were performed using CD1 oocytes and B6D2 sperm. Due to strain-specific incompatibilities, fertilization of CD1 oocytes by B6D2 sperm typically does not progress beyond the two-cell stage (Fernández-González [23] et al., 2008, Biology of Reproduction). Therefore, the observation of two-cell embryos represents the expected limit of development in this cross and serves as a strong indication of successful fertilization, even though further development is not possible. Second, the oocytes used in these experiments were treated with collagenase to remove cumulus cells. This enzymatic treatment can sometimes affect the morphology of early embryos, which may explain why the two-cell embryos in Figure 12 appear less regular or somewhat fragmented. We also included a control showing embryos from B6D2 sperm with the same collagenase treatment on CD1 oocytes, which yielded similar appearances (Fig14 A4).

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.

We have clarified these points in the revised Results and Discussion sections to emphasize that the IVF data indicate partial functional recovery of rescued sperm rather than full fertility restoration. These clarifications address the editor’s concern while accurately representing the technical limitations of the strain combination used in our experiments.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Fig 12 and Supplementary Fig 9 are mislabeled in the text and rebuttal.

We thank the reviewer for pointing this out. We have carefully checked the manuscript and the rebuttal text, and corrected all references to Figure 12 and Supplementary Figure 9 to ensure they are accurately labeled and consistent throughout the text.

Reviewer #3 (Recommendations for the authors):

The contribution of the newly added authors should be clarified. All other aspects of inadequacy raised in my previous report have been adequately addressed.

No further comments.

We thank the reviewer for noting this. The contributions of the newly added authors have been clarified in the Author Contributions section of the revised manuscript. All other points raised in the previous review have been addressed as indicated.

References

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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.

Note: This preprint has been reviewed by subject experts for Review Commons. Content has not been altered except for formatting.

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Referee #2

Evidence, reproducibility and clarity

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.

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.

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.

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.

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.

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.

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.

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.

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.

4) The major finding of the manuscript is of a Mic19 analog in plasmodium should be highlighted. As far as I know, this manuscript could represent the first instance of Mic19 outside of opisthokonts that was not found by sensitive profile HMM searches and certainly the first time such a Mic19 was functionally analyzed.

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).

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.

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?

Minor comments:

Line 33. Anaerobes (eg Giardia) have mitochondria that do produce ATP, unlike aerobic mitochondria

Line 56: Unclear what authors mean by "canonical model of mitochondria"

Lines 75-76: This applies to Mic10 only

Line 80: Cite DOI: 10.1016/j.cub.2020.02.053

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.

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

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.

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.

Line 222: Report male/female crista measurements

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%.

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).

Line 320: incorrect citation. Related to point 1above.

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.

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.

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.

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

1) Does Plasmodium Sam50 co-fractionate with Mic60 and Mic19 in BN PAGE (Fig. 1E)

2) Can Alphafold3 predict a heterotetramer of PfMic60? What about the four Mic19 and Mic60 subunits together. Is this tetramer consistent with the Bock-Bierbaum model. Is this model consistent with the CJ diameter measured in plasmodium, which is perhaps better evidence than that in lines 419-422.

Significance

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.

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.

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.

Reviewer #2 (Public review):

This paper proposes two changes to classic RSA, a popular method to probe neural representation in neuroimaging experiments: computing RSA at row/column level of RDM, and using linear mixed modeling to compute second level statistics, using the individual row/columns to estimate a random effect of stimulus. The benefit of the new method is demonstrated using simulations and a re-analysis of a prior fMRI dataset on object perception and memory encoding.

The author's claim that tRSA is a promising approach to perform more complete modeling of cogneuro data, and to conceptualize representation at the single trial/event level (cf Discussion section on P42), is appealing.

In their revised manuscript, the authors have addressed some previous concerns, now referencing more literature aiming to improve RSA and its associated statistical inferences, and providing more guidance on methodological considerations in the Discussion. However, I wish the authors had more extensively edited the Introduction to better contextualize the work and clarify the specific settings in which they see the method as being beneficial over classic RSA. For example, some of the limitations of cRSA mentioned on page 6, e.g. related to presenting the same stimuli to multiple subjects, seem to be quite specific to settings where the researcher expects differential responses across subjects to fundamentally alter the interpretation, rather than something that will just average out by repeatedly offering the same stimulus, or combining data across subjects. It's not clear to me how the switch from 'matrix-level' to 'row-level' analysis in tRSA necessarily addresses this problem. I would be very helpful if the authors would more explicitly outline what problem the row-level aspect of tRSA is solving; what problem statistical inference via LMM is solving; and walk the reader through a very specific use case (perhaps a toy version of the real-data experiment which is now at the end of the paper). Explaining the utility of tRSA for experimental settings in which assessing representational strength for a single-events is crucial would clarify the contribution of this new method better.

A few weaknesses mentioned in my previous review were not adequately addressed. To demonstrate the utility of the method on real neural recordings, only a single dataset is used with a quite complicated experimental design; it's not clear if there is any benefit of using tRSA on a simpler real dataset. Moreover, the cells of an RDM/RSM reflect pairwise comparisons between response patterns. Because the response patterns are repeatedly compared, the cells of this matrix are not independent of one another. While the authors show examples that failure to meet independence assumptions do not affect results in their specific dataset, it does not get acknowledged as a problem at a more fundamental level. Finally, while the paper now states that 'simulations and example tRSA code' are publicly available, the link points to the lab's general github page containing many lab repositories, in which I could not identify a specific repository related to this paper. This is disappointing given that the main goal of this manuscript is to provide a new method that they encourage others to use; a clear pointer to available code is only a minimal requirement to achieve that goal. A dedicated repository, including documentation, READMEs and tutorials/demo's to run simulations, compare methods, etc. would greatly enhance the paper's contribution.

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”.

When I read this paragraph, it feels like the writer is showing how one problem led to another until things got serious. Instead of just saying “a traffic light was needed,” the paragraph walks me through all the small issues that built up to that decision. It’s basically connecting the dots so I can see why the final outcome actually makes sense.

This section shows that virality isn’t just about how many people see something, it’s also about how others reshape it, sometimes in ways that support the creator’s original purpose. Features like TikTok Duets can amplify a post by letting others add on in a way that stays aligned with the initial intent, but that alignment isn’t guaranteed.

When I first started reading this section, I was prepared to argue that we shouldn't downplay crazy theories just because they're crazy (content like that will always exist). However, I had no idea that these sorts of videos were being peddled to people prone to believing it. On one hand, it's a matter of prioritizing interests and creating a good algorithm. I'm not entirely sure about my ethical stance on this.

It's important to remember that the ideas of America that are valued today weren't what was being fought over then. In a nutshell, it was just the ruling class of the colonies doing what they were already doing, just without outside influence.

Wow, okay so it it's not just me, thank you! Though during the last hundred pages I had gotten used to it and the resistance turned into an urge to not stop reading, while simultaneously being revulsed.

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 feels like the main point of the whole essay. Writing works best when it comes from something you actually need to work through, not just because it’s assigned.

Its me Ethan, this part of the text seems to let students help produce ideas but include methods of doing so. If they also compare the subject to something they are already interested about they will obviously want to find more about it.

reply to u/Yiqu at https://old.reddit.com/r/typewriters/comments/1r08q2i/buying_a_first_typewriter_for_writing/

The first three articles you'll find under https://boffosocko.com/research/typewriter-collection/#Typewriter%20Market will give you a quick crash course about what to consider and look out for in your search.

If you want to get to work, your best bet (and honestly the best value) is to get something from a repair shop that is serviced and ready to go. In the US this means a budget range typically from US$300-$600, or perhaps slightly more if they've recovered the platen which will improve your experience. Prices dramatically in excess of this often include a lot more custom work or less common typefaces which don't necessarily improve your performance (or are people selling typewriters who have less of an idea than you do about typewriters.)

Many hobbyists here may say to get something cheap that "works", but the amount of time and knowledge you have to scaffold to do that is worth a lot of writing time, and often still requires a lot of cleaning, restoration, and potential tinkering which is even more onerous when you just want to get to writing.

In case you haven't found them, some great resources on leveraging typewriters as distraction-free writing devices:

• Flint, Woz Delgado. 2023. The Distraction-Free First Draft. One Idea Press. https://www.oneideapress.com/product-page/the-distraction-free-first-draft.
• Joe Van Cleave: https://www.youtube.com/@Joe_VanCleave
• Damon DiMarco: https://www.youtube.com/channel/UCMJ2zbs0bvcjaTYx5zV52sw

And if you need some serious distraction free advice, since it's hiding as deep knowledge amongst a handful of serious collectors/writers, the bigger your (standard) machine, the more visual space it takes up as you're writing and subtly helps your concentration. Similarly placing it in front of a wall (and not a window) helps a lot too.

It’s wild how much tech can fail when the people building it don't represent the people using it, like that soap dispenser that literally couldn't see dark skin. It really drives home the point that design justice isn't just about the final product, but about making sure disabled and marginalized people are actually the ones in the room making the decisions.

This section highlights how managing disability accessibility is shifting from putting the burden on individuals to "mask" or fix themselves toward designers creating flexible tools that actually adapt to the person. It’s a move from just making someone act "normal" with assistive tech to using ability-based design where programs change their own behavior to match what a user can do.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript uses primarily simulation tools to probe the pathway of cholesterol transport with the smoothened (SMO) protein. The pathway to the protein and within SMO is clearly discovered, and interactions deemed important are tested experimentally to validate the model predictions.

Strengths:

The authors have clearly demonstrated how cholesterol might go from the membrane through SMO for the inner and outer leaflets of a symmetrical membrane model. The free energy profiles, structural conformations, and cholesterol-residue interactions are clearly described.

We thank the reviewer for their kind words.

(1) Membrane Model: The authors decided to use a rather simple symmetric membrane with just cholesterol, POPC, and PSM at the same concentration for the inner and outer leaflets. This is not representative of asymmetry known to exist in plasma membranes (SM only in the outer leaflet and more cholesterol in this leaflet). This may also be important to the free energy pathway into SMO. Moreover, PE and anionic lipids are present in the inner leaflet and are ignored. While I am not requesting new simulations, I would suggest that the authors should clearly state that their model does not consider lipid concentration leaflet asymmetry, which might play an important role.

We thank the reviewer for their comment. Membrane asymmetry is inherent in endogenous systems; we acknowledge that as a limitation of our current model. We have addressed the comment by adding this limitation to our discussion in the manuscript.

Added lines: (End of paragraph 6, Results subsection 2):

“One possibility that might alter the thermodynamic barriers is native membrane asymmetry, particularly the anionic lipid-rich inner leaflet. This presents as a limitation of our current model.”

(2) Statistical comparison of barriers: The barriers for pathways 1 and 2 are compared in the text, suggesting that pathway 2 has a slightly higher barrier than pathway 1. However, are these statistically different? If so, the authors should state the p-value. If not, then the text in the manuscript should not state that one pathway is preferred over the other.

We thank the reviewer for their comment. We have added statistical t-tests for the barriers.

Changes made: (Paragraph 6, Results subsection 2)

“However, we also observe that pathway 1 shows a lower thermodynamic barrier (5.8 ± 0.7 kcal/mol v/s 6.5 ± 0.8 kcal/mol, p = 0.0013)”

(3) Barrier of cholesterol (reasoning): The authors on page 7 argue that there is an enthalpy barrier between the membrane and SMO due to the change in environment. However, cholesterol lies in the membrane with its hydroxyl interacting with the hydrophilic part of the membrane and the other parts in the hydrophobic part. How is the SMO surface any different? It has both characteristics and is likely balanced similarly to uptake cholesterol. Unless this can be better quantified, I would suggest that this logic be removed.

We thank the reviewer for this suggestion. We have removed the line to avoid confusion.

Reviewer #2 (Public review):

Summary:

In this work, the authors applied a range of computational methods to probe the translocation of cholesterol through the Smoothened receptor. They test whether cholesterol is more likely to enter the receptor straight from the outer leaflet of the membrane or via a binding pathway in the inner leaflet first. Their data reveal that both pathways are plausible but that the free energy barriers of pathway 1 are lower, suggesting this route is preferable. They also probe the pathway of cholesterol transport from the transmembrane region to the cysteine-rich domain (CRD).

Strengths:

(1) A wide range of computational techniques is used, including potential of mean force calculations, adaptive sampling, dimensionality reduction using tICA, and MSM modelling. These are all applied rigorously, and the data are very convincing. The computational work is an exemplar of a well-carried out study.

(2) The computational predictions are experimentally supported using mutagenesis, with an excellent agreement between their PMF and mRNA fold change data.

(3) The data are described clearly and coherently, with excellent use of figures. They combine their findings into a mechanism for cholesterol transport, which on the whole seems sound.

(4) The methods are described well, and many of their analysis methods have been made available via GitHub, which is an additional strength.

Weaknesses:

(1) Some of the data could be presented a little more clearly. In particular, Figure 7 needs additional annotation to be interpretable. Can the position of the cholesterol be shown on the graph so that we can see the diameter change more clearly?

We thank the reviewer for this suggestion. We have added the cholesterol positions as requested.

Changes made: (Caption, Figure 7)

“The tunnel profile during cholesterol translocation in SMO. (a) Free energy plot of the zcoordinate v/s the tunnel diameter when cholesterol is present in the core TMD. The tunnel shows a spike in the radius in the TMD domain, indicating the presence of a cholesterol-accommodating cavity. (b) Representative figure for the tunnel when a cholesterol molecule is in the TMD. (c) Same as (a), when cholesterol is at the TMD-CRD interface. (e) same as (b), when cholesterol is at the TMD-CRD interface. (e) same as (a), when cholesterol is at the CRD binding site. (f) same as (b), when cholesterol is at the CRD binding site. Tunnel diameters shown as spheres. Cholesterol positions marked on plots using dotted lines. All snapshots presented are frames taken from MD simulations.”

(2) In Figure 3C, it doesn’t look like the Met is constricting the tunnel at all. What residue is constricting the tunnel here? Can we see the Ala and Met panels from the same angle to compare the landscapes? Or does the mutation significantly change the tunnel? Why not A283 to a bulkier residue? Finally, the legend says that the figure shows that cholesterol can still pass this residue, but it doesn’t really show this. Perhaps if the HOLE graph was plotted, we could see the narrowest point of the tunnel and compare it to the size of cholesterol.

We thank the reviewer for this suggestion. A283 was mutated to methionine as it presents with a longer heavy tail containing sulfur. We have plotted the tunnel radii for both WT and A283M mutants and added them as a supplemental figure. As shown in the figure, the presence of methionine doesn’t completely block the tunnel, but occludes it, thereby increasing the barrier for cholesterol transport slightly.

Changes made: (End of Results subsection 1)

“When we calculated the PMF for cholesterol entry, A^2.60fM mutant showed restricted tunnel but it did not fully block the tunnel (Figure 3—figure Supplement 3).”

(3) The PMF axis in 3b and d confused me for a bit. Looking at the Supplementary data, it’s clear that, e.g., the F455I change increases the energy barrier for chol entering the receptor. But in 3d this is shown as a -ve change, i.e., favourable. This seems the wrong way around for me. Either switch the sign or make this clearer in the legend, please.

We thank the reviewer for this suggestion. We measured ∆PMF as PMF_WT PMF_mutant, hence the negative values. We have added additional text to the legend to clarify this.

Changes made: (Caption, Figure 3)

“(b) ∆Gli1 mRNA fold change (high SHH vs untreated) and ∆ PMF (difference of peak PMF , calculated as PMF_WT - PMF_mutant) plotted for the mutants in Pathway 1. (c) Example mutant A^2_._60fM shows that cholesterol can enter SMO through Pathway 1 even on a bulky mutation. (d) Same as (b) but for Pathway 2 (e) Example mutant L^5.62fA shows that cholesterol can enter SMO through Pathway 2 due to lesser steric hindrance. All snapshots presented are frames taken from MD simulations.”

Changes made: (Caption, Figure 6)

“(b) ∆Gli1 mRNA fold change (high SHH vs untreated) and ∆ PMF (difference of peak PMF, calculated as PMF_WT - PMF_mutant) plotted for mutants along the TMD-CRD pathway. (c, d) Example mutants Y^LDA and F^5.65fA show that cholesterol is unable to translocate through this pathway because of the loss of crucial hydrophobic contacts provided by Y207 and F484 and along the solvent-exposed pathway.”

(4) The impact of G280V is put down to a decrease in flexibility, but it could also be a steric hindrance. This should be discussed.

We thank the reviewer for this suggestion. We have added it as a possible mechanism of the decrease in activity of SMO.

Changes made: (Paragraph 5, Results subsection 1)

“We mutated G280^2.57f  to valine - G^2.57fV to test whether reducing the flexibility of TM2 prevents cholesterol entry into the TMD. Consequently, the activity of mSMO showed a decrease. However, this decrease could also be attributed to steric hindrance added by the presence of a bulky propyl group in valine.”

(5) Are the reported energy barriers of the two pathways (5.8plus minus0.7 and 6.5plus minus0.8 kcal/mol) significantly and/or substantially different enough to favour one over the other? This could be discussed in the manuscript.

We thank the reviewer for this suggestion. We have added statistical t-tests for the barriers.

Changes made: (Paragraph 6, Results subsection 2)

“However, we also observe that pathway 1 shows a lower thermodynamic barrier (5.8 ± 0.7 kcal/mol v/s 6.5 ± 0.8 kcal/mol, p = 0.001)”

(6) Are the energy barriers consistent with a passive diffusion-driven process? It feels like, without a source of free energy input (e.g., ion or ATP), these barriers would be difficult to overcome. This could be discussed.

We thank the reviewer for this suggestion. We have added a discussion to further clarify this point.

Discussion: (Paragraph 6, Results subsection 2)

“These values are comparable to ATP-Binding Cassette (ABC) transporters of membrane lipids, which use ATP hydrolysis (-7.54 ± 0.3 kcal/mol) (Meurer et al., 2017) to drive lipid transport from the membrane to an extracellular acceptor. Some of these transporters share the same mechanism as SMO, where the lipid from the inner leaflet is flipped and transported to the extracellular acceptor protein (Tarling et al., 2013). Additionally, for secondary active transporters that do not use ATP for the transport of substrates, a thermodynamic barrier of 5-6 kcal/mol has been reported in literature. (Chan et al., 2022; Selvam et al., 2019; McComas et al., 2023; Thangapandian et al., 2025).”

(7) Regarding the kinetics from MSM, it is stated that the values seen here are similar to MFS transporters, but this then references another MSM study. A comparison to experimental values would support this section a lot.

We thank the reviewer for this suggestion. We have added a discussion discussing millisecond-scale timescales measured for MFS transporters.

Changes made: (Paragraph 2, Results subsection 5)

“These timescales are comparable to the substrate transport timescales of Major Facilitator Superfamily (MFS) transporters (Chan et al., 2022). Furthermore, several experimental studies have also resolved the millisecond-scale kinetics of MFS transporters (Blodgett and Carruthers, 2005; Körner et al., 2024; Bazzone et al., 2022; Smirnova et al., 2014; Zhu et al., 2019), further corroborating the results from our study.”

Reviewer #2 (Recommendations for the authors):

(1) The heatmaps in Figures 2a and 4a are great. On these, an arrow denotes what looks like a minimum energy path. Is it possible to see this plotted, as this might show the height of the energy barriers more clearly?

We thank the reviewer for this suggestion. We have computed the minimum energy paths for both pathways and presented them in a supplementary figure.

Added lines: (Paragraph 4, Results subsection 1):

For further clarity, we have plotted the minimum energy path taken by cholesterol as it translocates along this pathway (Figure 2—figure Supplement 3)a,b)

Added lines: (Paragraph 4, Results subsection 2):

For further clarity, we have plotted the minimum energy path taken by cholesterol as it translocates along this pathway (Figure 2—figure Supplement 3)c,d)

(2) The tiCA data in S15 is first referred to on line 137, but the technique isn’t introduced until line 222. This makes understanding the data a little confusing. Reordering this might improve readability.

We thank the reviewer for this suggestion. We have reordered the text to make it clearer.

Changes made: (Paragraph 2, Results subsection 1) This provides evidence for multiple stable poses along the pathway as observed in the multiple stable poses of cholesterol in Cryo-EM structures of SMO bound to sterols (Deshpande et al., 2019; Qi et al., 2019b, 2020). A reliable estimate of the barriers comes from using the time-lagged Independent Components (tICs), which project the entire dataset along the slowest kinetic degrees of freedom. Overall, the highest barrier along Pathway 1 is ∼ 5.8 ± 0.7 kcal/mol, and it is associated with the entry of cholesterol into the TMD (Figure 2—Figure Supplement 2).

Changes made: (Paragraph 3, Results subsection 2)

“On plotting the first two components of tICs, (Figure 2—Figure Supplement 2), we observe that the energetic barrier between η and θ is ∼6.5 ± 0.8 kcal/mol.”

(3) Missing bracket on line 577.

We thank the reviewer for this suggestion. The typo has been fixed.

(4) Line 577: Fig. S2nd?

We thank the reviewer for this suggestion. This typo has been fixed.

Reviewer #3 (Public review):

Summary:

This manuscript presents a study combining molecular dynamics simulations and Hedgehog (Hh) pathway assays to investigate cholesterol translocation pathways to Smoothened (SMO), a G protein-coupled receptor central to Hedgehog signal transduction. The authors identify and characterize two putative cholesterol access routes to the transmembrane domain (TMD) of SMO and propose a model whereby cholesterol traverses through the TMD to the cysteine-rich domain (CRD), which is presented as the primary site of SMO activation. The MD simulations and biochemical experiments are carefully executed and provide useful data.

Weaknesses:

However, the manuscript is significantly weakened by a narrow and selective interpretation of the literature, overstatement of certain conclusions, and a lack of appropriate engagement with alternative models that are well-supported by published data-including data from prior work by several of the coauthors of this manuscript. In its current form, the manuscript gives a biased impression of the field and overemphasizes the role of the CRD in cholesterol-mediated SMO activation. Below, I provide specific points where revisions are needed to ensure a more accurate and comprehensive treatment of the biology.

(1) Overstatement of the CRD as the Orthosteric Site of SMO Activation

The manuscript repeatedly implies or states that the CRD is the orthosteric site of SMO activation, without adequate acknowledgment of alternative models. To give just a few examples (of many in this manuscript):

(a) “PTCH is proposed to modulate the Hh signal by decreasing the ability of membrane cholesterol to access SMO’s extracellular cysteine-rich domain (CRD)” (p. 3).

(b) “In recent years, there has been a vigorous debate on the orthosteric site of SMO” (p. 3).

(c) “cholesterol must travel through the SMO TMD to reach the orthosteric site in the CRD” (p. 4).

(d) “we observe cholesterol moving along TM6 to the TMD-CRD interface (common pathway, Fig. 1d) to access the orthosteric binding site in the CRD” (p. 6).

While the second quote in this list at least acknowledges a debate, the surrounding text suggests that this debate has been entirely resolved in favor of the CRD model. This is misleading and not reflective of the views of other investigators in the field (see, for example, a recent comprehensive review from Zhang and Beachy, Nature Reviews Molecular and Cell Biology 2023, which makes the point that both the CRD and 7TM sites are critical for cholesterol activation of SMO as well as PTCH-mediated regulation of SMO-cholesterol interactions).

In contrast, a large body of literature supports a dual-site model in which both the CRD and the TMD are bona fide cholesterol-binding sites essential for SMO activation. Examples include:

(a) Byrne et al., Nature 2016: point mutation of the CRD cholesterol binding site impairs-but does not abolish-SMO activation by cholesterol (SMO D99A, Y134F, and combination mutants - Fig 3 of the 2016 study).

(b) Myers et al., Dev Cell 2013 and PNAS 2017: CRD deletion mutants retain responsiveness to PTCH regulation and cholesterol mimetics (similar Hh responsiveness of a CRD deletion mutant is also observed in Fig. 4 Byrne et al, Nature 2016).

(c) Deshpande et al., Nature 2019: mutation of residues in the TMD cholesterol binding site blocks SMO activation entirely, strongly implicating the TMD as a required site, in contrast to the partial effects of mutating or deleting the CRD site.

Qi et al., Nature 2019, and Deshpande et al., Nature 2019, both reported cholesterol binding at the TMD site based on high-resolution structural data. Oddly, Deshpande et al., Nature 2019, is not cited in the discussion of TMD binding on p. 3, despite being one of the first papers to describe cholesterol in the TMD site and its necessity for activation (the authors only cite it regarding activation of SMO by synthetic small molecules).

Kinnebrew et al., Sci Adv 2022 report that CRD deletion abolished PTCH regulation, which is seemingly at odds with several studies above (e.g., Byrne et al, Nature 2016; Myers et al, Dev Cell 2013); but this difference may reflect the use of an N-terminal GFP fusion to SMO in the Kinnebrew et al 2022, which could alter SMO activation properties by sterically hindering activation at the TMD site by cholesterol (but not synthetic SMO agonists like SAG); in contrast, the earlier work by Byrne et al is not subject to this caveat because it used an untagged, unmodified form of SMO.

Although overexpression of PTCH1 and SMO (wild-type or mutant) has been noted as a caveat in studies of CRD-independent SMO activation by cholesterol, this reviewer points out that several of the studies listed above include experiments with endogenous PTCH1 and low-level SMO expression, demonstrating that SMO can clearly undergo activation by cholesterol (as well as regulation by PTCH1) in a manner that does not require the CRD.

Recommendation: The authors should revise the manuscript to provide a more balanced overview of the field and explicitly acknowledge that the CRD is not the sole activation site. Instead, a dual-site model is more consistent with available structural, mutational, and functional data. In addition, the authors should reframe their interpretation of their MD studies to reflect this broader and more accurate view of how cholesterol binds and activates SMO.

We thank the reviewer for this comprehensive overview of the existing literature. We agree that cholesterol binding to both the TMD and CRD sites is required for full activation of SMO. As described below in responses to comments, we have made changes to the manuscript to make this point clear. For instance, in the revised manuscript, we refrain from calling the CRD cholesterol binding site the “orthosteric site”. Instead, we highlight that the goal of the manuscript is not to resolve the debate over whether the TMD or CRD site is more important for PTCH1 regulation by SMO but rather to use molecular dynamics to understand the fascinating question of how cholesterol in the membrane can reach the CRD, located at a significant distance above the outer leaflet of the membrane. We believe that this is an important goal since there is an abundance of evidence that supports the view that PTCH1 inhibits SMO by reducing cholesterol access to the CRD. This evidence is now summarized succinctly in the introduction:

Changes made: (Paragraph 4, Introduction)

“While cholesterol binding to both the TMD and CRD sites is required for full SMO activation, our work focuses on how cholesterol gains access to the CRD site, perched above the outer leaflet of the membrane (Luchetti et al., 2016; Kinnebrew et al., 2022). Multiple lines of evidence suggest that PTCH1-regulated cholesterol binding to the CRD plays an instructive role in SMO regulation both in cells and animals. Mutations in residues predicted to make hydrogen bonds with the hydroxyl group of cholesterol bound to the CRD reduced both the potency and efficacy of SHH in cellular signaling assays (Kinnebrew et al., 2022; Byrne et al., 2016) and, more importantly, eliminated HH signaling in mouse embryos (Xiao et al., 2017). Experiments using both covalent and photocrosslinkable sterol probes in live cells directly show that PTCH1 activity reduces sterol access to the CRD (Kinnebrew et al., 2022; Xiao et al., 2017). Notably, our simulations evaluate a path of cholesterol translocation that includes both the TMD and CRD sites: cholesterol first enters the 7-transmembrane domain bundle from the membrane; it then engages the TMD site before continuing along a conduit to the CRD site. Thus, we analyze translocation energetics and residue-level contacts along a path that includes both the TMD and the CRD.”

However, Reviewer 3 makes several comments below that are biased, inaccurate, or selective. We feel it is important to address these so readers can approach the literature from a balanced perspective. Indeed, the eLife review forum provides an ideal venue to present contrasting views on a scientific model. We encourage the editors to publish both Reviewer 3’s comments and our response in full so readers can read the original papers and reach their own conclusions. It is important to note these issues are not relevant to the quality of the computational and experimental data presented in this paper.

We have now removed the term “orthosteric” to describe the CRD site throughout the paper and clearly state in the introduction that “both the CRD and TMD sites are required for SMO activation” but that our focus is on how cholesterol moves from the membrane to the CRD site. There is no doubt that cholesterol binding to the CRD plays a key role in SMO activation– our focus on this path is justified and does not devalue the importance of the TMD site. Our prior models (see Figure 7 of Kinnebrew 2022 explicitly include contributions of both sites).

Now we respond to some of the concerns outlined, individually:

(1) Byrne et al., Nature 2016: point mutation of the CRD cholesterol binding site impairs-but does not abolish-SMO activation by cholesterol (SMO D99A, Y134F, and combination mutants - Fig 3 of the 2016 study)

The fact that a point mutation dramatically diminishes (but does not abolish signaling) does not mean that the CRD cholesterol binding site is not important for SMO regulation. Indeed, the reviewer fails to mention that Song et. al. (Molecular Cell, 2017) found that a SMO protein carrying a subtle mutation at D99 (D95/99N, a residue that makes a hydrogen bond with the cholesterol hydroxyl) completely abolishes SMO signaling in mouse embryos. Thus, the CRD site is critical for SMO activation in an intact animal, justifying our focus on evaluating the path of cholesterol translocation to the CRD site.

(2) Myers et al., Dev Cell 2013 and PNAS 2017: CRD deletion mutants retain responsiveness to PTCH regulation and cholesterol mimetics (similar Hh responsiveness of a CRD deletion mutant is also observed in Fig 4 Byrne et al, Nature 2016).

The Reviewer fails to note that CRD-deleted versions of SMO have markedly (>10-fold) higher basal (i.e. ligand-independent) activity compared to full-length SMO. The response to SHH is minimal (∼2-fold), compared to >50-100-fold with full-length SMO. Thus, CRD-deleted SMO is likely in a non-native conformation. Local changes in cholesterol accessibility caused by PTCH1 inactivation or cholesterol loading can cause small fluctuations in delta-CRD activity, but this cannot be used to infer meaningful insights about how native, full-length SMO (with >10-fold lower basal activity) is regulated. We encourage the reviewer to read our previous paper (Kinnebrew et. al. 2022), which presents a unified view of how the TMD and CRD sites together regulate SMO activation.

A more physiological experiment, reported in Kinnebrew et. al. 2022, tested mutations in residues that make hydrogen bonds with cholesterol at the CRD and TMD sites in the context of full-length SMO. These mutants were stably expressed at moderate levels in Smo^−/− cells. Mutations at the CRD site reduced the fold-increase in signaling output in response to SHH, as would be expected for a PTCH1-regulated site. In contrast, analogous mutations in the TMD site reduced the magnitude of both basal and maximal signaling, without affecting the fold-change in response to SHH. In signaling assays, the key parameter in evaluating the impact of a mutation is whether it impacts the change in output in response to a signal (in this case PTCH1 inactivation by SHH). A mutation in SMO that affects PTCH1 regulation is expected to decrease the fold-change in signaling in response to SHH, a criterion that is fulfilled by mutations in the CRD site. Accordingly, mutations in the CRD site abolish SMO signaling in mouse embryos (Xiao et al., 2017).

(3) Deshpande et al., Nature 2019: mutation of residues in the TMD cholesterol binding site blocks SMO activation entirely, strongly implicating the TMD as a required site, in contrast to the partial effects of mutating or deleting the CRD site.

Introduction of bulky mutations at the TMD site (V333F) that abolish SMO activity were first reported by Byrne et. al. 2016 and were used to markedly increase the stability of SMO for protein expression. These mutations indeed stabilize the inactive state of SMO, increasing protein abundance and completely preventing its localization at primary cilia. SMO variants carrying such bulky mutations cannot be used to infer the importance of the TMD site since they do not distinguish between the following possibilities: (1) SMO is inactive because the sterol cannot bind, or (2) SMO is inactive because it is locked in an inactive conformation, or (3) SMO is inactive because it cannot localize to primary cilia (where it must be localized to activate downstream signaling).

As described in Response 3.3, a better evaluation of the importance of the TMD site is the use of mutations in residues that make hydrogen bonds with the hydroxyl group of TMD cholesterol. These mutations do not markedly increase protein stability or prevent ciliary localization (Kinnebrew 2022, Fig.S2). While a TMD site mutation decreases the magnitude of maximal (and basal) SMO signaling, it does not impact the fold-increase in signal output in response to Hh ligands (the key parameter that should be used to evaluate PTCH1 activity).

(4) Qi et al., Nature 2019, and Deshpande et al., Nature 2019, both reported cholesterol binding at the TMD site based on high-resolution structural data. Oddly, Deshpande et al., Nature 2019 not cited in the discussion of TMD binding on p. 3, despite being one of the first papers to describe cholesterol in the TMD site and its necessity for activation (the authors only cite it regarding activation of SMO by synthetic small molecules)

The reference has now been added at this location in the manuscript.

(5) Kinnebrew et al., Sci Adv 2022 report that CRD deletion abolished PTCH regulation, which is seemingly at odds with several studies above (e.g., Byrne et al, Nature 2016; Myers et al, Dev Cell 2013); but this difference may reflect the use of an N-terminal GFP fusion to SMO in the Kinnebrew et al 2022, which could alter SMO activation properties by sterically hindering activation at the TMD site by cholesterol (but not synthetic SMO agonists like SAG); in contrast, the earlier work by Byrne et al is not subject to this caveat because it used an untagged, unmodified form of SMO.

The reviewer fails to note that CRD deleted versions of SMO have markedly (>10-fold) higher basal activity than full-length SMO. The response to SHH is minimal (∼2fold), compared to >50-fold with full-length SMO. Thus, CRD-deleted SMO is likely in a non-native conformation. Local changes in cholesterol accessibility caused by PTCH1 inactivation or cholesterol loading can cause small fluctuations in delta-CRD activity, but this cannot be used to infer meaningful insights about how native, full-length SMO (with >10-fold lower basal activity) is regulated. Please see Response 3.3 for further details.

Reviewer 3 presents an incomplete picture of the extensive experiments reported in Kinnebrew et. al. to establish the functionality of YFP-tagged delta-CRD SMO. Most importantly, a TMDselective sterol analog (KK174) can fully activate YFP-tagged delta-CRD, showing conclusively that the YFP fusion does not block sterol access to the TMD site. The fact that this protein is nearly unresponsive to SHH highlights the critical role of the CRD-bound cholesterol in SMO regulation by PTCH1. Indeed, the YFP-tagged, CRD-deleted SMO was made purposefully to test the requirement of the CRD in a construct that had normal basal activity. Again, this data justifies the value of investigating the path of cholesterol movement from the membrane via the TMD site to the CRD.

(6) Although overexpression of PTCH1 and SMO (wild-type or mutant) has been noted as a caveat in studies of CRD-independent SMO activation by cholesterol, this reviewer points out that several of the studies listed above include experiments with endogenous PTCH1 and low-level SMO expression, demonstrating that SMO can clearly undergo activation by cholesterol (as well as regulation by PTCH1) in a manner that does not require the CRD.

This comment is inaccurate. The data presented in Deshpande et. al. (and prior work in Myers et. al.) used transient transfection to overexpress SMO in Smo^−/− cells. At the individual cell level transient transfection produces expression levels that are markedly higher (10-1000-fold) than stable expression (in addition to being more variable). Most scientists would agree that stable expression (as used in Kinnebrew 2022) at a moderate expression level is a better system to compare mutant phenotypes, assess basal and activated signaling, and provide an accurate measure of the fold-change in signal output in response to SHH. Notably, introduction of a mutation in the CRD cholesterol binding site at the endogenous mouse Smo locus (an even better experiment than stable expression) leads to complete loss of SMO activity (PMID 28344083). This result again justifies our investigation of the pathway of cholesterol movement from the membrane to the CRD site.

We have changed the initial discussion and reflect a more general outlook.

Changes made: (Paragraph 1, Introduction)

“PTCH modulates the availability of accessible cholesterol at the primary cilium and thereby regulates SMO, with models invoking effects on both the CRD and 7TM pockets.”

Changes made: (Results subsection 3, paragraph 1)

“According to the dual-site model, to reach the binding site in the CRD (ζ), cholesterol translocate along the TMD-CRD interface from the TM binding site (α∗) is required.”

Added lines: (Paragraph 5, Results subsection 3):

“The computational investigation showed here covers the dual-site model, where cholesterol reaches the CRD site via binding to the TM binding site first. In comparison to the CRD site, the TM site is more stable by ∼ 2 kcal/mol (Figure 2—Figure Supplement 3b, d).”

Added lines: (Paragraph 2, Conclusions):

“Here we have explored the role the CRD-site plays in SMO activation. In addition, through simulating the CRD site-dependent SMO activation hypothesis, we have also simulated the TMD site-dependent activation. We show that the overall stability of cholesterol is higher than the CRD site by ∼ 2 kcal/mol.”

(2) Bias in Presentation of Translocation Pathways

The manuscript presents the model of cholesterol translocation through SMO to the CRD as the predominant (if not sole) mechanism of activation. Statements such as: "Cholesterol traverses SMO to ultimately reach the CRD binding site" (p. 6) suggest an exclusivity that is not supported by prior literature in the field. Indeed, the authors’ own MD data presented here demonstrate more stable cholesterol binding at the TMD than at the CRD (p 17), and binding of cholesterol to the TMD site is essential for SMO activation. As such, it is appropriate to acknowledge that cholesterol may activate SMO by translocating through the TM5/6 tunnel, then binding to the TMD site, as this is a likely route of SMO activation in addition to the CRD translocation route they highlight in their discussion.

The authors describe two possible translocation pathways (Pathway 1: TM2/3 entry to TMD; Pathway 2: TM5/6 entry and direct CRD transfer), but do not sufficiently acknowledge that their own empirical data support Pathway 2 as more relevant. Indeed, because their experimental data suggest Pathway 2 is more strongly linked to SMO activation, this pathway should be weighted more heavily in the authors’ discussion. In addition, Pathway 2 is linked to cholesterol binding to both the TMD and CRD sites (the former because the TMD binding site is at the terminus of the hydrophobic tunnel, the latter via the translocation pathway described in the present manuscript), so it is appropriate that Pathway 2 figures more prominently than Pathway 1 in the authors’ discussion.

The authors also claim that "there is no experimental structure with cholesterol in the inner leaflet region of SMO TMD" (p 16). However, a structural study of apo-SMO from the Manglik and Cheng labs (Zhang et al., Nat Comm, 2022) identified a cholesterol molecule docked at the TM5/6 interface and also proposed a "squeezing" mechanism by which cholesterol could enter the TM5/6 pocket from the membrane. The authors do not consider this SMO conformation in their models, nor do they discuss the possibility that conformational dynamics at the TM5/6 interface could facilitate cholesterol flipping and translocation into the hydrophobic conduit, despite both possibilities having precedent in the 2022 empirical cryoEM structural analysis.

Recommendation: The authors should avoid oversimplifying the SMO cholesterol activation process, either by tempering these claims or broadening their discussion to better reflect the complexity and multiplicity of cholesterol access and activation routes for SMO. They should also consider the 2022 apo-SMO cryoEM structure in their analysis of the TM5/6 translocation pathway.

We thank the reviewer for this comprehensive overview of the existing literature and parts we have missed to include in the discussion. We agree with the reviewer, since our data shows that both pathways are probable. Through our manuscript, we have avoided using a competitive approach (that one pathway dominates over the other). Instead, we have evaluated both pathways independently and presented a comparative rather than competitive overview of both pathways from our observations. While we agree that experimental evidence suggests the inner leaflet pathway is possible, we cannot discount the observations made in previous studies that support the outer leaflet pathway, particularly Hedger et al. (2019), Bansal et al. (2023), and Kinnebrew et al. (2021). Therefore, considering the reviewer’s comments have made the following changes:

(1) Added lines: (Paragraph 3, Conclusions):

“We show that the barriers associated with the pathway starting from the outer leaflet are lower by ∼0.7 kcal, (p=0.0013). We also provide evidence that cholesterol can enter SMO via both leaflets, considering that multiple computational and experimental studies have found cholesterol entry sites and activation modulation via the outer leaflet, between TM2TM3. This is countered by evidence from multiple experimental and computational studies corroborating entry via the inner leaflet, between TM5-TM6, including this study. Overall, we posit that cholesterol translocation from either pathway is feasible.”

(2)nChanges made: (Paragraph 6, Results subsection 2)

“Based on our experimental and computational data, we conclude that cholesterol translocation can happen via either pathway. This is supported on the basis of the following observations: mutations along pathway 2 affect SMO activity more significantly, and the presence of a direct conduit that connects the inner leaflet to the TMD binding site. In addition, a resolved structure of SMO in the presence of cholesterol shows a cholesterol situated at the entry point from the membrane into the protein between TM5 and TM6, in the inner leaflet. However, we also observe that pathway 1 shows a lower thermodynamic barrier (5.8 ± 0.7 kcal/mol vs. 6.5 ± 0.8 kcal/mol, p \= 0.0013). Additionally, PTCH1 controls cholesterol accessibility in the outer leaflet. This shows that there is a possibility for transport from both leaflets. One possibility that might alter the thermodynamic barriers is native membrane asymmetry, particularly the anionic lipid-rich inner leaflet. This presents as a limitation of our current model.”

(3)nChanges made: (Paragraph 1, Results subsection 2)

“In a structure resolved in 2022, cholesterol was observed at the interface between the protein and the membrane, in the inner leaflet, between TMs 5 and 6. However, cholesterol in the inner leaflet has a downward orientation, with the polar hydroxyl group pointing intracellularly (η). A striking observation is that this cholesterol binding site pose was never used as a starting point for simulations and was discovered independent of the pose described in Zhang et al. (2022) (Figure 4—Figure Supplement 1).”

(3) Alternative Possibility: Direct Membrane Access to CRD

The possibility that the CRD extracts cholesterol directly from the membrane outer leaflet is not considered. While the crystal structures place the CRD in a stable pose above the membrane, multiple cryo-EM studies suggest that the CRD is dynamic and adopts a variety of conformations, raising the possibility that the stability of the CRD in the crystal structures is a result of crystal packing and that the CRD may be far more dynamic under more physiological conditions.

Recommendation: The authors should explicitly acknowledge and evaluate this potential mechanism and, if feasible, assess its plausibility through MD simulations.

We thank the reviewer for the suggestion. We have addressed this comment by calculating the distance from the lipid headgroups for each lipid in the membrane to the cholesterol binding site. We show that in our study, we do not observe any bending of the CRD over the membrane, precluding any cholesterol from being extracted from the membrane directly.

Added lines: (Paragraph 3, Conclusions):

“An alternative possibility states that the flexibility associated with the CRD would allow it to directly access the membrane, and consequently, cholesterol. In the extensive simulations reported in this study, the binding site of cholesterol in the CRD remains at least 20 Å away from the nearest lipid head group in the membrane, suggesting that such direct extraction and the bending of the CRD do not occur within the timescales sampled (Appendix 2 – Figure 6).

The mechanistic details of this process are still unexplored and form the basis of future work.”

(4) Inconsistent Framing of Study Scope and Limitations

The discussion contains some contradictory and misleading language. For example, the authors state that "In this study we only focused on the cholesterol movement from the membrane to the CRD binding site," and then several sentences later state that "We outline the entire translocation mechanism from a kinetic and thermodynamic perspective." These statements are at odds. The former appropriately (albeit briefly) notes the limited scope of the modeling, while the latter overstates the generality of the findings.

In addition, the authors’ narrow focus on the CRD site constitutes a major caveat to the entire work. It should be acknowledged much earlier in the manuscript, preferably in the introduction, rather than mentioned as an aside in the penultimate paragraph of the conclusion.

Recommendation: The authors should clarify the scope of the study and expand the discussion of its limitations. They should explicitly acknowledge that the study models one of several cholesterol access routes and that the findings do not rule out alternative pathways.

We thank the reviewer for the suggestion. We have addressed this comment by explicitly mentioning the scope of the study.

Changes made: (Paragraph 3, Conclusions)

“We outline the entire translocation mechanism from a kinetic and thermodynamic perspective for one of the leading hypotheses for the activation mechanism of SMO.”

(5) Summary:

This study has the potential to make a useful contribution to our understanding of cholesterol translocation and SMO activation. However, in its current form, the manuscript presents an overly narrow and, at times, misleading view of the literature and biological models; as such, it is not nearly as impactful as it could be. I strongly encourage the authors to revise the manuscript to include:

(1) A more balanced discussion of the CRD vs. TMD binding sites.

(2) Acknowledgment of alternative cholesterol access pathways.

(3) More comprehensive citation of prior structural and functional studies.

(4) Clarification of assumptions and scope.

Of note, the above suggestions require little to no additional MD simulations or experimental studies, but would significantly enhance the rigor and impact of the work.

We thank the reviewer for the suggestions. We have taken into account the literature and diverse viewpoints. We have changed the initial discussion and reflected a more general outlook. In the revised version of the manuscript, we have refrained from referring to the CRD site as the orthosteric site. Instead, we refer to it as the CRD sterol-binding site. To better represent the dual-site model, we add further discussion in the Introduction. Through our manuscript, we have avoided using a competitive approach (that one pathway dominates over the other). Instead, we have evaluated both pathways independently and presented a comparative rather than competitive overview of both pathways from our observations. We explicitly mention the scope of the study.

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

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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.

It’s important to keep an open mind and accept constructive criticism positively, because it’s meant to help you grow, not to attack you. On the contrary, it shows that others are on your side and want to see you succeed.

This description makes the tree feel almost wrong or unsettling, especially compared to how trees are usually associated with strength or stability. Calling it “unattractive” and “unhealthy” seems intentional, as if the tree’s physical form mirrors something emotionally off, suggesting that nature here reflects deeper unease rather than comfort.

This stood out to me because it pushes back against the idea of fiction as just storytelling for entertainment. Calling the novel “cannibalistic” suggests it absorbs and reworks history, philosophy, and other forms of knowledge, which makes fiction feel less passive and more like an active way of thinking and understanding the world.

This passage makes me think a lot about art and how one can go about making a painting, or a sculpture, etc. I think it's cool to think of literature this way as well because it is art that is really just expressed more through words.

I agree with this because classrooms look a lot different than they used to, and teaching has had to adjust. Students come in with different backgrounds, learning styles, and needs, so using the same approach for everyone just doesn’t work anymore. I think it’s a good thing that educators are rethinking how lessons are taught, because when learning is more accessible, more students are actually able to participate and succeed instead of feeling left out or behind.

This portion of the presentation will focus on the RSA public key encryption algorithm. As we saw at the end of the previous presentation, the Diffie Hellman algorithm has some impracticalities as we saw. It requires a setup phase, in which Alice has to exchange some public information with with Bob, not only with that Bob with with any Bob (meaning to an imposter without knowing it?) she wishes to exchange a key with. These impracticalities are avoided by another algorithm that we're going to look at RSA algorithm, which is the most widely used cryptographic algorithm. Here's the public key model that it uses. The cryptographic key is broken into two parts, a public and a private part. The public part is used for encrypting, so Bob's public key is used by Alice to encrypt the word hello, running it through the encrypt algorithm and then sending the result. This gibberish here, over to Bob. He uses the private part of his key to decrypt the word the gibberish and retrieve the word hello. The encryption happens using a key that's been divided into two, and as you can see visually, these two parts are related. There really are one key that's been divided in half. Include public model, slide 36

We'll want to see how that happens, how that works. The key is broken into a public and private part. Bob and Allice publish there's public keys, and that's the big difference between RSA and Diffie Hellman. They published them so that all people who want to encrypt messages to Bob can use Bob's public key, Alice and anyone else. Alice encrypts the word hello using Bob's public key and sends the encrypted gibberish to Bob, who decrypts it with his private key? So let's see what makes RSA hard? What protects RSA from Eve? It's also based on a one-way function, and it's our familiar modular arithmetic function, which is easy in one direction and hard, and the other.

The expression:

m^e mod N -> c

m: message (a number) <--RSA requires messages to be represented by numbers. But this is not a problem, right? Everything is binary!

In this case, the m in this expression represents the secret message that's being communicated. The e is a public exponent. It's part of the public key. The N is a public modulus, also part of the public key. And the c is the resulting encrypted message? And again, it's easy to compute m to the E mod n, knowing m, e, and N. But it's very difficult. It's intractable to find m given the encrypted message, plus the public key just e and N.

And again, the idea for the public and private key is that they are two halves of this exponent used in the expression m raised to an exponent mod n and so the trick is to mathematically to get this exponent in such a way that it's very hard to break it in half if you don't know some secrets. So that's a very high level summary of the RSA algorithm. Slide 51

Let's summarize its key features. First, like Diffie Hellman, the RSA algorithm solves the key exchange problem. Unlike Diffie Hellman, however, the RSA public Keys can be widely published and distributed rather than needing to be shared among parties in a encryption transaction and that makes it especially well suited for internet encryption. well suited for internet encryption. And finally, RSA is a secured by the intractability of the prime factorization problem. That's the problem of trying to discover the prime factors of a very, very large number. So here again, we see intractability being used to protect information, just as we did when we used it to help protect passwords from Brute Force attacks (by having too many possible options)

It’s sad that Sindu felt she had to copy a "Western" writing style like Hemingway's just to be taken seriously by her teachers and editors. It shows how much pressure there is for immigrant writers to change their natural voice just to fit into what American readers expect "good" writing to look like.

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

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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.

Response: As with other prion-infected cell lines, HovL cells do not exhibit any specific growth defects, susceptibilities, or phenotypes beyond their ability to propagate prions. This is consistent with established observations in prion research, where immortalized cell lines (and in general in vitro cultures) normally do not show cytotoxicity upon prion infection and, therefore, are used as models for prion propagation rather than for prion toxicity (see https://doi.org/10.1111/jnc.14956 for reference).

We now expanded the relevant section, including technical and conceptual details in the main text of the revised manuscript as follows:

"As reported for other ovinized cell models (66), HovL cells were susceptible to infection by the PG127 strain of ovine prions and capable of sustaining chronic prion propagation, as shown by proteinase K (PK)-digested western blot and by detection of PrPSc using the anti-PrP antibody 6D11, which selectively stains prion-infected cells after fixation and guanidinium treatment (67) (Supp. Fig. 7C-E). Consistent with most prion-propagating cell lines (68), HovL cells did not exhibit specific growth defects, susceptibilities, or overt phenotypes beyond their ability to propagate prions."

19) It is stated that HRNPK depletion from HovL cells increases PrpSC as determined by 6D11 fluorescence, but in the manuscript HRNPK depletion results in cell death. How does this come together?

Response: As explicitly stated in the main text and shown in Fig.6-7, HNRNPK is downregulated (via siRNAs) in the prion experiments rather than fully deleted (via CRISPR) as in the first part of the manuscript. As shown in Supp. Fig. 8B, this downregulation does not affect cell viability within the experimental time window. Therefore, the observed increase in PrPSc levels upon HNRNPK downregulation, as determined by western blot and 6D11 staining, is independent of any potential cell death effects. Moreover, the same siRNA downregulation approach was used by M. Avar et al. (Ref. 26) in comparable experiments, yielding similar outcomes.

20) They show that mTOR inhibition mimics the effect of HNRNPK deletion, why didn't they overexpress mTOR and see if that rescues this? This would indicate a causal relationship.

Response: We appreciate the reviewer's suggestion. We agree that the proposed rescue strategy would be the best approach to indicate a causal relationship. However, we linked the activity of the mTORC1 complex (and not only that of mTOR) to prion propagation. Overexpression of only mTOR would not restore mTORC1 full function, as Rptor would still be downregulated in the context of HNRNPK siRNA silencing (Fig. 7A and Supp. Fig. 8E). Moreover, our RNA-seq data (Supp. Table 5) from HNRNPK ablation indicate the downregulation of other mTORC1 components (namely Pras40 (AKT1S1) and mLST8). Therefore, the rescue of the mTORC1 activity by an overexpression strategy would be a very challenging approach. Given these complexities, to infer causality, we used mTORC1 inhibition (via rapamycin and Torin1) to mimic the effects of HNRNPK downregulation in reducing mTORC1 activity (FIG. 7B).

For clarification, we have now highlighted in Fig. 4C that HNRNPK ablation downregulates also AKT1S1 and mLST8, other than mTOR and Rptor (also attached below), and we have discussed this in the main text as well. We also have clarified in the revised manuscript (where we sometimes inadvertently referred to it as just mTOR inhibition) that the observed effects are due to mTORC1 inhibition, and not simply mTOR inhibition.

21) Flow cytometric data: supplementary Fig of Fig6d. - when they are looking at fixed cells the gating strategy for cells results in the inclusion of a lot of debris. The gate needs to be moved and be more specific to ensure results are interpreted properly. Same with the singlet gating. It's not tight enough, they include doublets as well which will skew their data. The gating strategy needs to be regated.

Response: We have reanalyzed the flow cytometry data in Fig. 6D with a more stringent gating approach to better exclude debris and ensure proper singlet selection. We confirm that there is no change in the final interpretation of the results after applying the updated gating strategy.

Reviewer #2 (Significance (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.

Referee #3

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

Summary: Using a CRISPR-based high throughput abrasion assay, Sellitto et al. identified a list of genes that improve cell viability when deleted in hnRNP K knockout cells. Tfap2c, a transcription factor, was identified as a candidate with potential overlap with a hnRNP K function like modulating glucose metabolism. The deletion of Tfap2c in hnRNP K-deletion background prevented caspase-dependent apoptosis observed in hnRNP K single-deletion cells. Further analysis of bulk RNA-seq in hnRNP K/TFAP2C single- and double-deletion cells revealed the impairment in cellular ATP level. Accordingly, activation of AMPK led to perturbed autophagy in hnRNP K deleted cells. Moreover, the reduction and/or inactivation of the downstream mTOR protein resulted in the reduced phosphorylation of S6. Conversely, the phosphorylation of S6 and E4BP1 can be increased by TFAP2C overexpression. Finally, the pharmacological inhibition of the mTOR pathway increased the PrPSC level. This is an interesting paper potentially providing new mechanical insight of hnRNPK function and its interaction with TFAP2C. However, inconsistencies in TFAP2C expression across cell lines and conflicting mechanistic interpretations complicate conclusions. Co-IP experiments suggested hnRNP K and Tfap2c may interact, though further validation is needed. Several figures require additional clarification, statistical analysis, or experimental validation to strengthen conclusions.

Major comments:

1) Different responses of the TFAP2C expression level to deletion of hnRNPK in the two cell lines (LN-229 C3 and U251-Cas9) should be more adequately addressed. The manuscript focuses on the interaction between hnRNPK and TFAP2C, yet the hnRNPK deletion causes different changes in TFAP2C level in two different lines. Furthermore, in studies where the mechanistic link between hnRNPK and TFAP2C is being investigated, only results from the LN-229 line are presented (Figure 4-7). Thus, it is not clear whether these mechanisms also apply to another line, U251-Cas9, where hnRNPK deletion has the opposite effect on the TFAP1C level. Thus, key experiments should be performed in both lines.

Response: The opposite effects of hnRNPK ablation on TFAP2C expression between LN-229 C3 and U251-Cas9 cells likely reflect intrinsic differences between the two cell lines. However, the viability interaction between hnRNPK and TFAP2C is conserved in both cell models (Fig. 1G-H, 2A-B, Supp. Fig. 3A-B), suggesting that shared molecular functions at the interface of this interaction exist across the lines. In fact, we believe that the opposite effect of hnRNPK ablation on TFAP2C expression in the two lines strengthens (rather than weakens) our model by highlighting how TFAP2C expression modulates cellular sensitivity to HNRNPK ablation, as detailed in our response to Reviewer #2 (Point 10 - Major comments).

Regarding the mechanistic studies presented in FIG. 4-7, our initial goal in using two cell lines was to validate the functional viability interaction between HNRNPK and TFAP2C, as identified in our screening (performed in LN-229 C3 cells). After confirming this interaction, we chose to focus only on LN-229 C3 (beginning with RNA-seq analysis, which then led to subsequent mechanistic studies), as this provided the necessary foundation to investigate prion propagation in HovL cells (derived from LN-229). As a U251 model propagating prions does not exist, we are technically limited in performing prion experiments only in HovL and we do not believe that conducting additional experiments in U251 cells would add substantial value to our work or further our investigation.

We hope this explanation clarifies our rationale and addresses the reviewer's concerns.

2) Although a lot of data are presented, it is not clear how deletion of the TFAP2C reverses the toxicity caused by deletion of hnRNPK. Specifically, the first half of the paper seems to suggest an opposite mechanism than the second half of the paper. In Figure 2-4, the authors suggest a model that TFAP2C deletion has the opposite effect of hnRNPK deletion, thus rescuing toxicity. However, in Figure 5-6, it is suggested TFAP2C overexpression has the opposite effect of hnRNPK deletion. This two opposite effect of TFAP2C make it difficult to understand the models that the authors are proposing. Please also see below comment 2 for Figure 5.

Response: We respectfully disagree with the notion that the first and second halves of the manuscript propose contradictory mechanisms.

In Fig. 2-4, we describe the phenotypic rescue of cell viability upon TFAP2C deletion in hnRNPK-deficient cells. At this stage, we are not proposing a specific molecular mechanism but simply observing a rescue of viability and highlighting underlying transcriptional differences. There is no implication of an opposite molecular mechanism involving the individual activities of hnRNPK and TFAP2C; rather, we focused on the broader effect of TFAP2C deletion on the viability of HNRNPK-lacking cells. In Fig. 5, we isolated a partial mechanism underlying this interaction. We state that: "These data specify a role for TFAP2C in promoting mTORC1-mediated cell anabolism and suggest that its overexpression might hypersensitize cells to HNRNPK ablation by depleting the already limited ATP available, thus making its deletion advantageous". In the discussion, we now further reviewed our explanation: "HNRNPK deletion might cause a metabolic impairment leading to a nutritional crisis and a catabolic shift, whereas TFAP2C activation could promote mTORC1 anabolic functions. Thus, Tfap2c removal may rewire the bioenergetic needs of cells by modulating the mTORC1 signaling and augmenting their resilience to metabolic stress like the one induced by HNRNPK ablation". Therefore, we propose that TFAP2C expression might be particularly detrimental in hnRNPK-deficient cells, as it could push the cell into an anabolic biosynthetic state, further depleting energy stores that the cell is attempting to conserve in response to hnRNPK depletion. Removal of TFAP2C alleviates this metabolic strain. In our view, there is no contradiction between our observations.

We hope this explanation clarifies our rationale and resolves any perceived inconsistency in our model. To further enhance the understanding of our interpretations, we have now also added (in substitution of Fig. 5E of the original manuscript) a graphical scheme (Fig. 5G of the revised manuscript) to visually explain and illustrate our model (attached below for your convenience).

3) Similar to the point above, the first half of the paper focuses on hnRNPK deletion-induced toxicity (Fig. 1-5), while the second half of the paper focuses on hnRNPK deletion-induced PrPSC level (Fig. 6-7). The mechanistic link between these two downstream effects of hnRNPK deletion is not clear and thus, it is difficult to understand the reason that hnRNPK deletion-induced toxicity can be rescued by TFAP2C deletion, while hnRNPK deletion-induced PrPSC level increase can be rescued by TFAP2C overexpression.

Response: Our study is not aimed at comparing viability and prion propagation as interconnected phenotypes but rather at identifying molecular processes regulated by the HNRNPK-TFAP2C interaction. Our study identifies mTORC1 activity as a molecular process at the interface of the HNRNPK-TFAP2C. HNRNPK knockout (or knockdown, which does not affect viability, and therefore is used in the prion section of the manuscript) tones mTORC1 activity down, while TFAP2C overexpression enhances it. This finding suggested an explanation for the viability interaction we observed (see reply to reviewer #3 - Point 2 -Major comments) and it provided a partial mechanism (mTORC1 activity) to explain the effect of HNRNPK knockdown and TFAP2C overexpression on prions.

We hope this clarification addresses the reviewer's concern.

Abstract:

1) Please rephrase and clarify "We linked HNRNPK and TFAP2C interaction to mTOR signaling..." by distinguishing functional, genetic, and direct (molecule-to-molecule) interactions.

Response: 1) We have now clarified it in the text of the revised manuscript as follows:

"We linked HNRNPK and TFAP2C functional and genetic interaction to mTOR signaling, observing that HNRNPK ablation inhibited mTORC1 activity through downregulation of mTOR and Rptor, while TFAP2C overexpression enhanced mTORC1 downstream functions."

2) A sentence reads, "...HNRNPK ablation inhibited mTORC1 activity through downregulation of mTOR and Rptor," although the downregulation of Rptor is observed only at the RNA level. The change in Rptor protein expression level is not reported in the manuscript. Please consider adding an experiment to address this or rephrase the sentence.

Response: 2) We have now added the experiment in Supp. Fig. 9A of the revised manuscript. The blot shows that hnRNP K depletion reduces both mTOR and Rptor protein levels. "hnRNP K depletion inhibited mTORC1 activity through downregulation of mTOR and Rptor".

Figure 2:

1. H and I. Co-IP experiments were done using anti-TFAP2C antibody to the bead. Although the TFAP2C bands show robust signals on the blots, indicating successful enrichment of the protein, hnRNP K bands are very faint. Has the experiment been done by conjugating the hnRNP K antibody to the beads instead? Was the input lysate enriched in the nuclear fraction? Did the lysis buffer include nuclease (if so, please indicate in the figure legend and the methods section)? Addressing these would make the argument, "We also observed specific co-immunoprecipitation of hnRNP K and Tfap2c in LN-229 C3 and U251-Cas9 cells (Fig. 2H-I, Supp. Fig. 3L), suggesting that the two proteins form a complex inside the nucleus" stronger, providing information on potential direct binding.

Response: 1. We refer the reviewer to our response to reviewers #1 and #2 regarding the weak interaction, the nuclease treatment, and the HNRNPK IP (reviewer #1 Point 1 and reviewer #2 Point 11 - Major comments). As for the co-IP input, it was not enriched in the nuclear fraction, but as shown in Supp. Fig. 4A-B hnRNPK and Tfap2c are exclusively nuclear.

Figure 3:

1. C and D. Please add a sentence in the figure legend explaining which means the multiple comparisons were made between (DMSO vs each drug concentration?). Graphing individual data points instead of bars would also be helpful and more informative. Please discuss the lack of dose dependency.

Response: 1. We have now added information about the comparison in the figure legend ("Multiple comparison was made between Z-VAD-FMK and DMSO treatments in ΔHNRNPK cells."), modified the graph to show the individual data points (attached below for your convenience), and expanded the discussion as detailed for reviewer #2 (Point 14 - Major comments). (For completeness, we have also modified Supp. FIG. 5F to show individual data points, and we have combined the graphs (the DMSO control was shared across treatments)).

Supplemental Figure 4 (Now shifted in Supplemental Figure 5):

1. A. Although the trend can be observed, the deletion of hnRNP K does not significantly reduce the GPX4 protein level in LN-229 C3. Therefore, the following statement requires more data points and additional statistical analysis to be accurate: "In LN-229 C3 and U251-Cas9 cells, the deletion of HNRNPK reduced the protein level of GPX4, whereas TFAP2C deletion increased it (Supp. Fig. 4A-B)."

2. A and B. The results are confusing, considering the previous report cited (ref 49) shows an increase in GPX4 with TFAP2C. It may be possible that the deletion of TFAP2C upregulates the expression of proteins with similar functions (e.g., Sp1). If this is the case, the changes in GPX4 expression observed here are a consequence of TFAP2C deletion and may not "suggest a role for HNRNPK and TFAP2C in balancing the protein levels of GPX4."

Response: 1. We agree with the reviewer that in LN-229 C3 cells the reduction of GPX4 protein levels upon HNRNPK deletion did not reach statistical significance in our initial Western blot analysis. To address this concern, we performed six additional independent experiments and repeated the statistical analysis. Although the trend toward reduced GPX4 protein levels remained consistent, statistical significance was still not achieved (p > 0.05). Importantly, this trend is supported by our RNA-seq dataset (Supplementary Table 5), which shows decreased GPX4 expression upon HNRNPK deletion. We have now revised the text to more accurately reflect the experimental observations and to avoid overstating the effect in LN-229 C3 cells as follows:

"In LN-229 C3 and U251-Cas9 cells, deletion of HNRNPK was associated with reduced glutathione peroxidase 4 (GPX4) protein abundance (although not statistically significant in LN-229 C3; p ≈ 0.08), whereas deletion of TFAP2C increased it (Supp. Fig. 5A-B)."

The six new experimental replicas have been added to the uncropped western blot section.

__Response: __2. Concerning the potential role of TFAP2C deletion in upregulating proteins with similar functions, we recognize the reviewer's perspective. However, our primary focus is on the observed trends rather than a definitive mechanistic conclusion. We clarified our wording to acknowledge this possibility while maintaining the relevance of our findings within the broader context of hnRNPK and TFAP2C interactions.

"This last result was interesting as a previous study reported that Tfap2c enhances GPX4 expression (51). Thus, the observed increase upon TFAP2C deletion suggests additional layers of regulation, potentially involving compensatory mechanisms."

Supplemental Figure 5 (Now shifted in Supplemental Figure 6):

1. B. To obtain statistical significance and strengthen the conclusion, more repeated Western blot experiments can be done to quantify the pAMPK/AMPK ratio.

Response: We included three more experiments as detailed in our response to reviewer #1 (Point 2 - Major comments) and reviewer #2 (Point 14 - Major comments).

Figure 5:

1. B. I believe statistical analysis with two replicates or less is not recommended. Although the assay is robust, and the blot is convincing, please consider adding more replicates if the blot is to be quantified and statistically analyzed.

2. "Interestingly, RNA and protein levels of mTOR were downregulated in LN-229 C3ΔHNRNPK cells but were partially rebalanced by the ΔTFAP2C;ΔHNRNPK double deletion (Fig. 4C, Supp. Fig. E)." The statement is based on a slight difference at the protein level between the single deletion and the double deletion, as well as the observation from the bulk RNA-seq data. mTOR (and Rptor) mRNA level can be assessed by RT-qPCR to validate and further support the existing data. It is also curious why deletion of TFAP2C alone, also induced decrease in mTOR, but double deletion rescued mTOR level slightly compared to deletion of HNRNPK alone.

3. C. The main text refers to the changes in the level of phosphorylated E4BP1, stating, "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)." However, the quantification was done on the total E4BP1, which may be because separating pE4BP1 and E4BP1 bands on a blot is challenging. Please consider using phospho-E4BP1 specific antibody or rephrase the sentence mentioned above. The current data suggest the single- and double-deletion of hnRNP K/TFAP2C affect the overall stability of E4BP1, which may be a correlation and not due to the mTOR activity as claimed in "We conclude that HNRNPK and TFAP2C play an essential role in co-regulating cell metabolism homeostasis by influencing mTOR and AMPK activity and expression." How does the cap-dependent translation (or total protein level) change in TFAP2C deleted and overexpressing cells?

Response: 1. We added two additional experiments as detailed in our response to reviewer #1 (Point 3 - Major comment).

__Response: __2. Deletion of TFAP2C does not decrease mTOR levels as shown from the quantification in Fig. 5D. To further support our results, we have now included RT-qPCR in FIG. 5C as suggested by the reviewer. Data are also attached here for your convenience.

__Response: __3. Regarding the assessment of phosphorylated 4EBP1, we think we achieved a clear separation of the differently phosphorylated forms of 4EBP1 in our blots, and we have now added the quantification for High p4EBP1/4EBP1 in Fig. 5E (see also our response to reviewer #2 Point 16 - Major comments). The quantification of total 4EBP1 represents an additional dataset, and we do not claim that 4EBP1 stability is affected by HNRNPK and TFAP2C directly through mTOR, which could be, in fact, correlative. We claim that HNRNPK and TFAP2C modulate mTORC1 and AMPK metabolic signaling as shown by the changed phosphorylation of 4EBP1, S6, AMPK, and ULK1 (Fig. 5C-E, Supp. FIG. 6B, D) and by the regulation of autophagy (Fig. 5B, Supp. Fig. 6C); we did not directly check cap-dependent translation.

We have now rephrased our text to ensure clarity as follows:

"We conclude that HNRNPK and TFAP2C play a role in co-regulating mTORC1 and AMPK expression, signaling, and activity."

Figure 6:

1. A. Did the sihnRNP K increase the TFAP2C level?

2. A and C. Are the total PrP levels lower in TFAP2C overexpressing cells compared to mCherry cells when they are infected?

3. D. Do the TFAP2C protein levels differ between 2-day+72-h and 7-day+96-h?

__Response: __1. Yes, it does. We have now provided the quantification in Fig. 6A, C, and Supp. Fig. 8A (also attached below for your convenience).

__Response: __2. We have now provided the quantification in Fig. 6A and Supp. Fig. 8A. The total PrP does not change in TFAP2C overexpressing cells. Total PrP consists of both PK-resistant PrP (PrPSc) and PK-sensitive PrP (PrPC plus potential other intermediate species), with PrPSc typically present at much lower levels. In our model, PrPC is exogenously expressed at high levels via a vector and remains constant across conditions (Fig. 6C and Supp. Fig. 8C). As a result, any changes in PrPSc may not necessarily reflect on total PrP levels.

__Response: __3. No, there is no statistically significant change. We have now added a representative western blot and the quantification of 3 independent replicates in Supp. Fig. 8D. The other two western blots are only shown in the uncropped western blots section. This dataset is also attached here for your convenience.

Figure 7:

1. I agree with the latter half of the statement: "These findings suggest that HNRNPK influences prion propagation at least in part through mTORC1 signaling, although additional mechanisms may be involved." The first half requires careful rephrasing since (A) Independent of the background siRNA treatment, TFAP2C overexpression by itself can modulate PrPSC level as seen in Fig 6A and B, (B) Although the increase in TFAP2C level is observed with the hnRNP K deletion (Fig 1; LN-229 C3), sihnRNP K treatment may or may not influence the TFAP2C level (Fig 6; quantified data not provided), and (C) In the sihnRNP K-treated cells, E4BP1 level is increased compared to the siNT-treated cells, which was not observed hnRNP K-deleted cells. Discussions and additional experiments (e.g., mTOR knockdown) addressing these points would be helpful.

__Response: __A, B) We respectfully disagree with the possibility that HNRNPK downregulation may increase prion propagation via TFAP2C upregulation. As shown in Fig. 6A-B, D and in Supp. Fig. 8A, TFAP2C overexpression reduces, rather than increases, prion levels. Therefore, it would be inconsistent to suggest that HNNRPK siRNA promotes prion propagation through TFAP2C upregulation (quantification is now provided, see reviewer #3 - Figure 6 - Point 1). C) Concerning 4EBP1 levels, we have quantified the total 4EBP1 (also attached below) and expanded the discussion on potential discrepancies between HNRNPK knockout and knockdown, as the former affects cell viability, while the latter does not. However, as explained also in the previous reply to reviewer #3 - Figure 5 - Point 3, our focus is on the highly phosphorylated band of 4EBP1 (High p4EBP1), which is the direct target of mTORC1 activity. In both the hnRNPK knockout LN-229 C3 (Fig. 5E) and knockdown HovL models (Fig. 7B), phosphorylation of 4EBP1, along with phosphorylation of S6, is clearly reduced (we have now included quantification for Fig. 7B), reinforcing our conclusion that mTORC1 activity is affected by hnRNPK depletion. As the reviewer noted, we do not claim that mTORC1 is the sole mediator of hnRNPK's effect on prion regulation. However, we think that our interpretation of a potential and partial role of mTORC1 inhibition in the effect of HNRNPK downregulation on prion propagation is in line with the data presented in Fig. 6-7 and Supp. Fig. 8-9. For further clarification, we expanded the text according to the new experiments and analysis, and we added mTOR and Raptor siRNA knockdown (Supp. Fig.9C) to further support our conclusions (also attached below for your convenience).

Minor comments:

1. Please clarify "independent cultures." Does this mean technical replicates on the same cell culture plate but different wells or replicated experiments on different days?

__Response: __We have now clarified in each figure legend. "Individually treated wells" means different parental cultures grown and treated separately on the same day. n represents independent experiments on different days.

1. Fig 2G. Please explain how the sigmoidal curves were fitted to the data points under the materials and methods section.

2. Fig 3E and F. Please refer to the comment on Fig 2G above.

__Response: __We have now added the explanation in Materials and Methods as follows:

"Curve Fitting

For sigmoidal curve fitting, we used GraphPad Prism (version X, GraphPad Software). Data in Figure 2G were fitted using nonlinear regression with a least squares regression model. For Figures 3E and 3F, data fitting was performed using an asymmetric sigmoidal model with five parameters (5PL) and log-transformed X-values (log[concentration])."

3.Fig S3 F/H. Quantification of gel bands would be helpful when comparing protein expression changes after different treatments, as band intensities look different across.

__Response: __We have now added the quantifications in Supp. FIG. 3D-H (attached below for your convenience). They confirm that there are no significant differences in the means of the normalized values.

1. Supp Fig 5C and F. These panels can be combined with the corresponding panels in main Figure 5 if space allows so that the readers do not have to flip pages between the main text and Supplemental material.

__Response: __We have now combined the panels. Previous Supp. FIG. 5C and F are now shown in FIG. 6C and E, respectively.

Reviewer #3 (Significance (Required)):

This is an interesting paper potentially providing new mechanical insight of hnRNPK function and its interaction with TFAP2C. It is also important to understand how hnRNPK deletion induces prion propagation and develop methods to mitigate its spread. However, inconsistencies in TFAP2C expression across cell lines and conflicting mechanistic interpretations complicate conclusions. I have expertise in RNA-binding protein, cell biology, and prion disease.

This section makes the privacy vs. security distinction feel very concrete: users may accept some privacy trade-offs, but they still expect platforms to protect the data they collect. The examples about password storage and breaches underline that security failures aren’t just “technical accidents”—they’re governance choices (process, incentives, access controls), and it’s why protections like unique password hashing and 2-factor authentication matter in practice.

I find the concept of securty and privacy on social media incredibly intriguing, as users are almost always promised that just by having a username and password, your data is completely protected, or at least we are given that assumption. However, it's relatively easy to hack into anyone's account if you have the right knowledge and know where to look. Especially if you have the capabality to manage an app or website from the back end, having the ability to go through data within an application can lead to data leaks, and private information you thought no one would have can suddenly be given to the world.

I have heard multiple cases/instances of this happening but never heard of any follow up about this, at least in the cases of social media. Were people's accounts then hacked? What came from this? I'm aware it's bad to generalize based on your own experiences, but I was only ever hacked once on instagram (my account started posting scam advertisements and changed my profile picture), but I just changed my password and the problem went away. Was it a similar case for different users? Did anything serious come from these cases?

It's interesting to see how Leif Erikson named the places based on their practical value. Like the "Land of Flat Rocks" and "Land of Forests", shows that their weren't just exploring for fun, but searching for different materials that would be useful to them.

Mrs. Bird doesn’t let John hide behind “politics.” She basically says: it’s easy to defend this law when it’s just an idea, but what would you actually do if a freezing, hungry runaway showed up at your door? John can talk about the “greater good” in theory, but Mary drags it into real life, where it’s suddenly obvious how cruel it is. Stowe is showing that these arguments only work when you don’t have to look the suffering person in the face.

This is such an awesome effort. Some thoughts while reading:

I have been wary of claims-based review given how hard it is to decouple claims from those made to chase editorial outcomes. I’d be very interested if we might prospectively use this type of result extraction to re-derive a supported claim (regardless of whether that was the claim made) and have that those be the content we operate on. I could even imagine authors using this type of supported content earlier in their workflow to make their narratives more robust rather than only post-hoc in evaluation.

That said, a useful distinction made here is to separate claims based on data/citations from claims that are inference or speculation. The latter of course are important for proposing parsimonious models that one can use as a theoretical framework for subsequent hypothesis generation or orthogonal testing. One awesome application of this in a future machine-readable world would be a forward-looking comparison of inference and speculation type claims with results from the rest of the corpus not just within-paper support.

Not at all a surprise is the increased coverage by LLMs compared to a few human reviewers who indeed likely only have expertise that covers a fraction of any interdisciplinary or collaborative work (the expertise of many authors went into a paper - the expertise of a reviewer is unlikely to span those).

Another thing that strikes me as invaluable here is the implicit and uncited result pairs that really will be essentially to generate knowledge graphs that can more usefully be built upon by new science/other scientists and far less biased than citation graphs.

Finally, as someone who spent many years invested in making the flip to the new eLife model (eliminating accept/reject editorial decisions), I was particularly interested in figure 2a comparing the old and new models. Even if unsupported claims had been dramatically higher or even high in an absolute sense, it would highlight the benefit of public reviews for such content rather than the same content being rejected and published as-is with a stamp of editorial acceptance elsewhere. However it's striking that even with many more claims evaluated by OpenEval, the unsupported claims are low whether authors decide when to stop revising their papers or when acceptance is gated by editors.

This is also the same sort of passive aggressive tone as from before, since he is coupling negotiations from a position of power and basically drawing a hard line that he will not come back unless the Colonel Anderson can guarantee his daughters' safety. But he couples it with a sort of innocent question about schooling as well. It's surprisingly educated in its delivery, since everytime it takes something or delivers a devastating statement, it also balances it with either an outright compliment or a mundane question to dilute the previous blow. It as a whole seems to be establishing a sort of idea that, yes, he's willing to return, but he's actually not, as he's demanding many things that the Colonel can't provide. It's basically a soft rejection of his offer by making it look instead of as a personal decision off of just a refusal to work for him, but by disguising it as a logical decision based on just common working conditions and employment, such as differing wages and benefits. Again, it seems surprisingly well put together and educated, which likely is also intentionally done to undermine the Colonel's position.

how Harold replaced the m in pkm for mastery. This comes very close to my [[Kenniswerk is ambacht 20040924200250]] artisanal view on knowledge work. The focus on practice in community, networks and on your own. Vgl [[% Practice Praktijk OP]]

Some nicely acid comments.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This study presents a system for delivering precisely controlled cutaneous stimuli to freely moving mice by coupling markerless real-time tracking to transdermal optogenetic stimulation, using the tracking signal to direct a laser via galvanometer mirrors. The principal claims are that the system achieves sub-mm targeting accuracy with a latency of <100 ms. The nature of mouse gait enables accurate targeting of forepaws even when mice are moving.

Strengths:

The study is of high quality and the evidence for the claims is convincing. There is increasing focus in neurobiology in studying neural function in freely moving animals, engaged in natural behaviour. However, a substantial challenge is how to deliver controlled stimuli to sense organs under such conditions. The system presented here constitutes notable progress towards such experiments in the somatosensory system and is, in my view, a highly significant development that will be of interest to a broad readership.

Weaknesses:

(1) "laser spot size was set to 2.00 } 0.08 mm2 diameter (coefficient of variation = 3.85)" is unclear. Is the 0.08 SD or SEM? (not stated). Also, is this systematic variation across the arena (or something else)? Readers will want to know how much the spot size varies across the arena - ie SD. CV=4 implies that SD~7 mm. ie non-trivial variation in spot size, implying substantial differences in power delivery (and hence stimulus intensity) when the mouse is in different locations. If I misunderstood, perhaps this helps the authors to clarify. Similarly, it would be informative to have mean & SD (or mean & CV) for power and power density. In future refinements of the system, would it be possible/useful to vary laser power according to arena location?

We thank the reviewer for their comments and for identifying areas needing more clarity. The previous version was ambiguous: 0.08 refers to the standard deviation (SD). We have removed the ambiguity by stating mean ± SD and reporting a unitless coefficient of variation (CV).

The revised text reads “laser spot size was set to 2.00 ± 0.08 mm² (mean ± SD; coefficient of variation = 0.039).” This makes clear that the variability in spot size is minimal: it is 0.08 mm² SD (≈0.03 mm SD in diameter). This should help clarify that spot size variability across the arena is minute and unlikely to contribute meaningfully to differences in stimulus intensity across locations. The power was modulated depending on the experiment, so we provide the unitless CV here in “The absolute optical power and power density were uniform across the glass platform (coefficient of variation 0.035 and 0.029, respectively; Figure 2—figure supplement)”. We are grateful to the reviewer for spotting these omissions.

The reviewer also asks whether, in the future, it is “possible/useful to vary laser power according to arena location”. This is already possible in our system for infrared cutaneous stimulation using analog modulation (Figure 4). We have added the following sentence to make this clearer: “Laser power could be modulated using the analog control.”

(2) "The video resolution (1920 x 1200) required a processing time higher than the frame interval (33.33 ms), resulting in real-time pose estimation on a sub-sample of all frames recorded". Given this, how was it possible to achieve 84 ms latency? An important issue for closed-loop research will relate to such delays. Therefore please explain in more depth and (in Discussion) comment on how the latency of the current system might be improved/generalised. For example, although the current system works well for paws it would seem to be less suited to body parts such as the snout that do not naturally have a stationary period during the gait cycle.

We captured and stored video with a frame-to-frame interval of 33.33 ms (30 fps). DeepLabCut-live! was run in a latency-optimization mode, meaning that new frames are not processed while the network is busy - only the most recent frame is processed when free. The processing latency is measured per processed frame, and intermediate frames are thus skipped while the network is busy. Although a wide field of view and high resolution is required to capture the large environment, increasing the per-frame compute time, the processing latency remained small enough to track and stimulate moving mice. This processing latency of 84 ± 12 ms (mean ± SD) was calculated using the timestamps stored in the output files from DeepLabCut-live!: subtracting the frame acquisition timestamp from the frame processing timestamp across 16,000 processed frames recorded across four mice (4,000 each). In addition, there is a small delay to move the galvanometers and trigger the laser, calculated as 3.3 ± 0.5 ms (mean ± SD; 245 trials). This is described in the manuscript, but can be combined with the processing latency to indicate a total closed-loop delay of ≈87 ms so we have expanded on the ‘Optical system characterization’ subsection in the Methods, adding “We estimated a processing latency of 84 ± 12 ms (mean ± SD) by subtracting…” and that “In the current configuration the end-to-end closed-loop delay is ≈87 ms from the combination of the processing latency and other delays”. To the Discussion, we now comment on how this latency can be reduced and how this can allow for generalization to more rapidly moving body parts.

Reviewer #2 (Public review):

Parkes et al. combined real-time keypoint tracking with transdermal activation of sensory neurons to examine the effects of recruitment of sensory neurons in freely moving mice. This builds on the authors' previous investigations involving transdermal stimulation of sensory neurons in stationary mice. They illustrate multiple scenarios in which their engineering improvements enable more sophisticated behavioral assessments, including (1) stimulation of animals in multiple states in large arenas, (2) multi-animal nociceptive behavior screening through thermal and optogenetic activation, and (3) stimulation of animals running through maze corridors. Overall, the experiments and the methodology, in particular, are written clearly. However, there are multiple concerns and opportunities to fully describe their newfound capabilities that, if addressed, would make it more likely for the community to adopt this methodology:

The characterization of laser spot size and power density is reported as a coefficient of variation, in which a value of ~3 is interpreted as uniform. My interpretation would differ - data spread so that the standard deviation is three times larger than the mean indicates there is substantial variability in the data. The 2D polynomial fit is shown in Figure 2 - Figure Supplement 1A and, if the fit is good, this does support the uniformity claim (range of spot size is 1.97 to 2.08 mm2 and range of power densities is 66.60 to 73.80 mW). The inclusion of the raw data for these measurements and an estimate of the goodness of fit to the polynomials would better help the reader evaluate whether these parameters are uniform across space and how stable the power density is across repeated stimulations of the same location. Even more helpful would be an estimate of whether the variation in the power density is expected to meaningfully affect the responses of ChR2-expressing sensory neurons.

We thank the reviewer for their comments. As also noted in response to Reviewer 1, the coefficient of variation (CV) is now reported in unitless form (rather than a percentage) to ensure clarity. For avoidance of doubt, the CV is 0.039 (3.9%), so the variation in laser spot size is minimal – there is negligible spot size variability across the system. The ranges are indeed consistent with uniformity. We have included the goodness-of-fit estimates in the appropriate figure legend “fit with a two-dimensional polynomial (area R² = 0.91; power R² = 0.75)”. This indicates that the polynomials fit well overall.

The system already allows for control of spot size. To examine whether the variation in the power density affects the responses of ChR2-expressing sensory neurons, we examined this in our previous work that focused more on input-output relationships, demonstrating a steep relationship between spot size (range of 0.02 mm² to 2.30 mm²) and the probability of paw response, demonstrating a meaningful change in response probability (Schorscher-Petcu et al. eLife, 2021). In future studies, we aim to use this approach to “titrate” cutaneous inputs as mice move through their environments.

While the error between the keypoint and laser spot error was reported as ~0.7 to 0.8 mm MAE in Figure 2L, in the methods, the authors report that there is an additional error between predicted keypoints and ground-truth labeling of 1.36 mm MAE during real-time tracking. This suggests that the overall error is not submillimeter, as claimed by the authors, but rather on the order of 1.5 - 2.5 mm, which is considerable given the width of a hind paw is ~5-6 mm and fore paws are even smaller. In my opinion, the claim for submillimeter precision should be softened and the authors should consider that the area of the paw stimulated may differ from trial to trial if, for example, the error is substantial enough that the spot overlaps with the edge of the paw.

We thank the reviewer for identifying a discrepancy in these reported errors. We clarify this below and in the manuscript

The real-time tracking error is the mean absolute Euclidean distance (MAE) between ground truth and DLC on the left hind paw where likelihood was relatively high. More specifically, ground truth was obtained by manual annotation of the left hind paw center. The corresponding DLC keypoint was evaluated in frames with likelihood >0.8 (the stimulation threshold). Across 1,281 frames from five videos of freely exploring mice (30 fps), the MAE was 1.36 mm.

The targeting error is the MAE between ground truth and the laser spot location, so should reflect the real-time tracking error plus errors from targeting the laser. More specifically, this metric was determined by comparing the manually determined ground truth keypoint of the left hind paw and the actual center of the laser spot. Importantly, this metric was calculated using four five-minute high-speed videos recorded at 270 fps of mice freely exploring the open arena (463 frames) and frames were selected with a likelihood threshold >0.8. This allowed us to resolve the brief laser pulses but inadvertently introduced a difference in spatial scaling. After rescaling, the values give a targeting error MAE now in line with the real-time tracking error  (see corrected Figure 2L). This is approximately 1.3 mm across all locomotion speeds categories. These errors are small and are limited by the spatial resolution of the cameras. We thank the reviewer for noting this discrepancy and prompting us to get to its root cause.

We have amended the subtitle on Figure 2L as “Ground truth keypoint to laser spot error” and have avoided the use of submillimeter throughout. We have added the following sentence to clarify this point: “As laser targeting relies on real-time tracking to direct the laser to the specified body part, this metric includes any errors introduced by tracking and targeting”.

As the major advance of this paper is the ability to stimulate animals during ongoing movement, it seems that the Figure 3 experiment misses an opportunity to evaluate state-dependent whole-body reactions to nociceptor activation. How does the behavioral response relate to the animal's activity just prior to stimulation?

The reviewers suggest analysis of state-dependent responses. In the Figure 3 experiment, mice were stimulated up to five times when stationary. Analysis of whole body reactions in stationary mice has been described in (Schorscher-Petcu et al. eLife, 2021) and doing this here would be redundant, so instead we now analyse the responses of moving mice in Figure 5. This new analysis shows robust state-dependent responses during movement as suggested by the reviewer. We find two behavioral clusters: one that is for faster, direct (coherent) movement and the other that is for slower assessment (incoherent) movement. Stimulation during the former results in robust and consistent slowing and shift towards assessment, whereas stimulation during the former results in a reduction in assessment. We describe and interpret these new data in the Results and Discussion sections and add information in the Methods and Figure legend, as given below. We believe that demonstrating movement statedependence is a valuable addition to the paper and thank the reviewer for suggesting this.

Given the characterization of full-body responses to activation of TrpV1 sensory neurons in Figure 4 and in the authors' previous work, stimulation of TrpV1 sensory neurons has surprisingly subtle effects as the mice run through the alternating T maze. The authors indicate that the mice are moving quickly and thus that precise targeting is required, but no evidence is shared about the precision of targeting in this context beyond images of four trials. From the characterization in Figure 2, at max speed (reported at 241 +/- 53 mm/s, which is faster than the high speeds in Figure 2), successful targeting occurs less than 50% of the time. Is the initial characterization consistent with the accuracy in this context? To what extent does inaccuracy in targeting contribute to the subtlety of affecting trajectory coherence and speed? Is there a relationship between animal speed and disruption of the trajectory?

We thank the reviewer for pointing out the discrepancy in the reported maximum speed. We have corrected the error in the main text: the average maximum speed is 142 ± 26 mm/s (four mice).

The self-paced T-maze alternation task in Figure 5 demonstrates that mice running in a maze can be stimulated using this method. We did not optimize the particular experimental design to assess the hit accuracy, as this was determined in Figure 2. Instead, we optimized for the pulse frequencies, meaning the galvanometers tracked with processed frames but the laser was triggered whether or not the paw was actually targeted. However, even in this case with the system pulsing in the free-run mode, the laser hit rate was 54 ± 6% (mean ± sem, n = 7 mice). We have weakened references to submillimeter as it was only inferred from other experiments and was not directly measured here. We find in this experiment that stimulation in freely moving mice can cause them to briefly halt and evaluate. In the future, we will use experimental designs to more optimally examine learning.

The reviewer also asks if there is a relationship between speed and disruption of the trajectory. We find that this is the case as described above with our additional analysis.

Reviewer #3 (Public review):

Summary:

To explore the diverse nature of somatosensation, Parkes et al. established and characterized a system for precise cutaneous stimulation of mice as they walk and run in naturalistic settings. This paper provides a framework for real-time body part tracking and targeted optical stimuli with high precision, ensuring reliable and consistent cutaneous stimulation. It can be adapted in somatosensation labs as a general technique to explore somatosensory stimulation and its impact on behavior, enabling rigorous investigation of behaviors that were previously difficult or impossible to study.

Strengths:

The authors characterized the closed-loop system to ensure that it is optically precise and can precisely target moving mice. The integration of accurate and consistent optogenetic stimulation of the cutaneous afferents allows systematic investigation of somatosensory subtypes during a variety of naturalistic behaviors. Although this study focused on nociceptors innervating the skin (Trpv1::ChR2 animals), this setup can be extended to other cutaneous sensory neuron subtypes, such as low-threshold mechanoreceptors and pruriceptors. This system can also be adapted for studying more complex behaviors, such as the maze assay and goal-directed movements.

Weaknesses:

Although the paper has strengths, its weakness is that some behavioral outputs could be analyzed in more detail to reveal different types of responses to painful cutaneous stimuli. For example, paw withdrawals were detected after optogenetically stimulating the paw (Figures 3E and 3F). Animals exhibit different types of responses to painful stimuli on the hind paw in standard pain assays, such as paw lifting, biting, and flicking, each indicating a different level of pain. Improving the behavioral readouts from body part tracking would greatly strengthen this system by providing deeper insights into the role of somatosensation in naturalistic behaviors. Additionally, if the laser spot size could be reduced to a diameter of 2 mm², it would allow the activation of a smaller number of cutaneous afferents, or even a single one, across different skin types in the paw, such as glabrous or hairy skin.

We thank the reviewer for highlighting how our system can be combined with improved readouts of coping behavior to provide deeper insights. Optogenetic and infrared cutaneous stimulation are well established generators of coping behaviors (lifting, flicking, licking, biting, guarding). Detection of these behaviors is an active and evolving field with progress being made regularly (e.g. Jones et al., eLife 2020 [PAWS];  Wotton et al., Mol Pain 2020; Zhang et al., Pain 2022; Oswell et al., bioRxiv 2024 [LUPE]; Barkai et al., Cell Reports Methods 2025 [BAREfoot], along with more general tools like Hsu et al., Nature Communications 2021 [B-SOiD]; Luxem et al., Communications Biology 2022 [VAME]; Weinreb et al,. Nature Methods 2024 [Keypoints-MoSeq]). One output of our system is bodypart keypoints, which are the typical input to many of these tools. We will leave the readers and users of the system to decide which tools are appropriate for their experimental designs - the focus of this current manuscript is describing the novel stimulation approach in moving animals.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) It is hard to see how the rig is arranged from the render of Figure 2AB due to the components being black on black. A particularly useful part of Fig2AB is the aerial view in panel B that shows the light paths. I suggest adding the labelling of Figure 2A also to that. The side/rear views could perhaps be deleted, allowing the aerial view to be larger.

We appreciate this suggestion and have revised Figure 2B to improve the visibility of the optomechanical components. We have enlarged the side and aerial views, removed the rear view, and added further labels to the aerial view.

(2) MAE - to interpret the 0.54 result, it would be useful to state the arena size in this paragraph.

Thank you. We have added the arena size in this paragraph and also added scales in the relevant figure (Figure 2).

(3) "pairwise correlations of R = 0.999 along both x- and y-axes". Is this correlation between hindpaw keypoint and galvo coordinates?

Yes, we have added the following to clarify: “...between galvanometer coordinates and hind paw keypoints”

(4) Latency was 84 ms. Is this mainly/entirely the delay between DLC receiving the camera image and outputting key point coordinates?

Yes, we hope that the additional detail in the Methods and Discussion described above will now clarify the current closed-loop latencies.

(5) "Mice move at variable speeds": in this sentence, spell out when "speed" refers to mouse and when it refers to hindpaw. Similarly, Fig 2i. The sentence is potentially confusing to general readers (paws stationary although the mouse is moving). Presumably, it's due to gait. I suggest explaining this here.

The speed values that relate to the mouse body and paws are now clearer in the main text and in the legend for Figure 2I.

(6) Figure 2k and associated main text. It is not clear what "success/hit rate" means here.

We have added the following sentence in the main text: “Hit accuracy refers to the percentage of trials in which the laser successfully targeted (‘hit’) the intended hind paw.” and use hit accuracy throughout instead of success rate.

(7) Figure 2L. All these points are greater than the "average" 0.54 reported in the text. How is this possible?

The MAE of 0.54 mm refers to the “predicted and actual laser spot locations” (that is, the difference between where the calibration map should place the laser spot and where it actually fell), while Figure 2L MAE values refers to the error between the ground truth keypoint to laser spot (that is, the error between the human-observed paw target and where the laser spot fell). The latter error will include the former error so is expected to be larger. We have clarified this point throughout the text, for example, stating “As laser targeting relies on real-time tracking to direct the laser to the specified body part, this metric inherently accounts for any errors introduced by the tracking and targeting.”. This is also discussed above in response to Reviewer 2.

(8) "large circular arena". State the size here

We have added this to the Figure 2 legend.

(9) Figure 3c-left. Can the contrast between the mouse and floor be increased here?

We have improved the contrast in this image.

(10) Figure 5c. It is unclear what C1, C2, etc refers to. Mice?

Yes, these refer to mice. We have removed reference to these now as they are not needed.

(11) Discussion. A comment. There is scope for elaborating on the potential for new research by combining it with new methods for measurements of neural activity in freely moving animals in the somatosensory system.

Thank you. We agree and have added more detail on this in the discussion stating “The system may be combined with existing tools to record neural activity in freely-moving mice, such as fiber photometry, miniscopes, or large-scale electrophysiology, and manipulations of this neural activity, such as optogenetics and chemogenetics. This can allow mechanistic dissection of cell and circuit biology in the context of naturalistic behaviors.”

Reviewer #3 (Recommendations for the authors):

(1) Include the number of animals for behavior assays for the panels (e.g., Figures 4G).

Where missing, we now state the number of animals in panels.

(2) If representative responses are shown, such as in Figures 3E and 4F, include the average response with standard deviation so readers can appreciate the variation in the responses.

We appreciate the suggestion to show variability in the responses. We have made several changes to Figures 3 and 4. Specifically, to illustrate the variability across multiple trials more clearly, Figure 3E now shows representative keypoint traces for each body part from two mice during their 5 trials. For Figure 4, we have re-analyzed the thermal stimulation trials and shown a raster plot of keypoint-based local motion energy (Figure 4E) sorted by response latency for hundreds of trials. Figure 4G now presents the cumulative distribution for all trials and animals for thermal (18 wild-type mice, 315 trials) and optogenetic stimulation trials (9 Trpv1::ChR2 mice, 181 trials). We also now provide means ± SD for the key metrics for optogenetic and thermal stimulation trials in Figure 4 in the Results section. This keeps the manuscript focused on the methodological advances while showing the trial variability.

(3) "optical targeting of freely-moving mice in a large environments" should be "optical targeting of freely-moving mice in a large environment".

Corrected

(4) Define fps when you first mention this in the manuscript.

Added

(5) Data needs to be shown for the claim "Mice concurrently turned their heads toward the stimulus location while repositioning their bodies away from it".

We state this observation to qualify that the stimulation of stationary mice resulted in behavioral responses “consistent with previous studies”. It would be redundant to repeat our full analysis and might distract from the novelty of the current manuscript. We have restricted this sentence to make it clearer: “Consistent with previous studies, we observed the whole-body behaviors like head orienting concurrent with local withdrawal (Browne et al., Cell Reports 2017; Blivis et al., eLife, 2017.)”

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

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Reply to the reviewers

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

Summary:

Damaris et al. perform what is effectively an eQTL analysis on microbial pangenomes of E. coli and P. aeruginosa. Specifically, they leverage a large dataset of paired DNA/RNA-seq information for hundreds of strains of these microbes to establish correlations between genetic variants and changes in gene expression. Ultimately, their claim is that this approach identifies non-coding variants that affect expression of genes in a predictable manner and explain differences in phenotypes. They attempt to reinforce these claims through use of a widely regarded promoter calculator to quantify promoter effects, as well as some validation studies in living cells. Lastly, they show that these non-coding variations can explain some cases of antibiotic resistance in these microbes.

Major comments

Are the claims and the conclusions supported by the data or do they require additional experiments or analyses to support them?

The authors convincingly demonstrate that they can identify non-coding variation in pangenomes of bacteria and associate these with phenotypes of interest. What is unclear is the extent by which they account for covariation of genetic variation? Are the SNPs they implicate truly responsible for the changes in expression they observe? Or are they merely genetically linked to the true causal variants. This has been solved by other GWAS studies but isn't discussed as far as I can tell here.

We thank the reviewer for their effective summary of our study. Regarding our ability to identify variants that are causal for gene expression changes versus those that only “tag” the causal ones, here we have to again offer our apologies for not spelling out the limitation of GWAS approaches, namely the difficulty in separating associated with causal variants. This inherent difficulty is the main reason why we added the in-silico and in-vitro validation experiments; while they each have their own limitations, we argue that they all point towards providing a causal link between some of our associations and measured gene expression changes. We have amended the discussion (e.g. at L548) section to spell our intention out better and provide better context for readers that are not familiar with the pitfalls of (bacterial) GWAS.

They need to justify why they consider the 30bp downstream of the start codon as non-coding. While this region certainly has regulatory impact, it is also definitely coding. To what extent could this confound results and how many significant associations to expression are in this region vs upstream?

We agree with the reviewer that defining this region as “non-coding” is formally not correct, as it includes the first 10 codons of the focal gene. We have amended the text to change the definition to “cis regulatory region” and avoided using the term “non-coding” throughout the manuscript. Regarding the relevance of this including the early coding region, we have looked at the distribution of associated hits in the cis regulatory regions we have defined; the results are shown in Supplementary Figure 3.

We quantified the distribution of cis associated variants and compared them to a 2,000 permutations restricted to the -200bp and +30bp window in both E. coli * (panel A) and P. aeruginosa* (panel B). As it can be seen, the associated variants that we have identified are mostly present in the 200bp region and the +30bp region shows a mild depletion relative to the random expectation, which we derived through a variant position shuffling approach (2,000 replicates). Therefore, we believe that the inclusion of the early coding region results in an appreciable number of associations, and in our opinion justify its inclusion as a putative “cis regulatory region”.

The claim that promoter variation correlates with changes in measured gene expression is not convincingly demonstrated (although, yes, very intuitive). Figure 3 is a convoluted way of demonstrating that predicted transcription rates correlate with measured gene expression. For each variant, can you do the basic analysis of just comparing differences in promoter calculator predictions and actual gene expression? I.e. correlation between (promoter activity variant X)-(promoter activity variant Y) vs (measured gene expression variant X)-(measured gene expression variant Y). You'll probably have to

We realize that we may not have failed to properly explain how we carried out this analysis, which we did exactly in the way the reviewer suggests here. We had in fact provided four example scatterplots of the kind the reviewer was requesting as part of Figure 4. We have added a mention of their presence in the caption of Figure 3.

Figure 7 it is unclear what this experiment was. How were they tested? Did you generate the data themselves? Did you do RNA-seq (which is what is described in the methods) or just test and compare known genomic data?

We apologize for the lack of clarity here; we have amended the figure’s caption and the corresponding section of the results (i.e. L411 and L418) to better highlight how the underlying drug susceptibility data and genomes came from previously published studies.

Are the data and the methods presented in such a way that they can be reproduced?

No, this is the biggest flaw of the work. The RNA-Seq experiment to start this project is not described at all as well as other key experiments. Descriptions of methods in the text are far too vague to understand the approach or rationale at many points in the text. The scripts are available on github but there is no description of what they correspond to outside of the file names and none of the data files are found to replicate the plots.

We have taken this critique to heart, and have given more details about the experimental setup for the generation of the RNA-seq data in the methods as well as the results sections. We have also thoroughly reviewed any description of the methods we have employed to make sure they are more clearly presented to the readers. We have also updated our code repository in order to provide more information about the meaning of each script provided, although we would like to point out that we have not made the code to be general purpose, but rather as an open documentation on how the data was analyzed.

Figure 8B is intended to show that the WaaQ operon is connected to known Abx resistance genes but uses the STRING method. This requires a list of genes but how did they build this list? Why look at these known ABx genes in particular? STRING does not really show evidence, these need to be substantiated or at least need to justify why this analysis was performed.

We have amended the Methods section (“Gene interaction analysis”, L799) to better clarify how the network shown in this panel was obtained. In short, we have filtered the STRING database to identify genes connected to members of the waa operon with an interaction score of at least 0.4 (“moderate confidence”), excluding the “text mining” field. Antimicrobial resistance genes were identified according to the CARD database. We believe these changes will help the readers to better understand how we derived this interaction.

Are the experiments adequately replicated and statistical analysis adequate?

An important claim on MIC of variants for supplementary table 8 has no raw data and no clear replicates available. Only figure 6, the in vitro testing of variant expression, mentions any replicates.

We have expanded the relevant section in the Methods (“Antibiotic exposure and RNA extraction”, L778) to provide more information on the way these assays were carried out. In short, we carried out three biological replicates, the average MIC of two replicates in closest agreement was the representative MIC for the strain. We believe that we have followed standard practice in the field of microbiology, but we agree that more details were needed to be provided in order for readers to appreciate this.

Minor comments

Specific experimental issues that are easily addressable..

Are prior studies referenced appropriately?

There should be a discussion of eQTLs in this. Although these have mostly been in eukaryotes a. https://doi.org/10.1038/s41588-024-01769-9 ; https://doi.org/10.1038/nrg3891.

We have added these two references, which provide a broader context to our study and methodology, in the introduction.

Line 67. Missing important citation for Ireland et al. 2020 https://doi.org/10.7554/eLife.55308

Line 69. Should mention Johns et al. 2018 (https://doi.org/10.1038/nmeth.4633) where they study promoter sequences outside of E. coli

Line 90 - replace 'hypothesis-free' with unbiased

We have implemented these changes.

Line 102 - state % of DEGs relative to the entire pan-genome

Given that the study is focused on identifying variants that were associated with changes in expression for reference genes (i.e. those present in the reference genome), we think that providing this percentage would give the false impression that our analysis include accessory genes that are not encoded by the reference isolate, which is not what we have done.

Figure 1A is not discussed in the text

We have added an explicit mention of the panels in the relevant section of the results.

Line 111: it is unclear what enrichment was being compared between, FIgures 1C/D have 'Gene counts' but is of the total DEGs? How is the p-value derived? Comparing and what statistical test was performed? Comparing DEG enrichment vs the pangenome? K12 genome?

We have amended the results and methods section, as well as Figure 1’s caption to provide more details on how this analysis was carried out.

Line 122-123: State what letters correspond to these COG categories here

We have implemented the clarifications and edits suggested above

Line 155: Need to clarify how you use k-mers in this and how they are different than SNPs. are you looking at k-mer content of these regions? K-mers up to hexamers or what? How are these compared. You can't just say we used k-mers.

We have amended that line in the results section to more explicitly refer to the actual encoding of the k-mer variants, which were presence/absence patterns for k-mers extracted from each target gene’s promoter region separately, using our own developed method, called panfeed. We note that more details were already given in the methods section, but we do recognize that it’s better to clarify things in the results section, so that more distracted readers get the proper information about this class of genetic variants.

Line 172: It would be VERY helpful to have a supplementary figure describing these types of variants, perhaps a multiple-sequence alignment containing each example

We thank the reviewer for this suggestion. We have now added Supplementary Figure 3, which shows the sequence alignments of the cis-regulatory regions underlying each class of the genetic marker for both E. coli and P. aeruginosa.

Figure 4: THis figure is too small. Why are WaaQ and UlaE being used as examples here when you are supposed to be explicitly showing variants with strong positive correlations?

We rearranged the figure’s layout to improve its readability. We agree that the correlation for waaQ and ulaE is weaker than for yfgJ and kgtP, but our intention was to not simply cherry-pick strong examples, but also those for which the link between predicted promoter strength and recorded gene expression was less obvious.

Figure 4: Why is there variation between variants present and variant absent? Is this due to other changes in the variant? Should mention this in the text somewhere

Variability in the predicted transcription rate for isolates encoding for the same variant is due to the presence of other (different) variants in the region surrounding the target variant. PromoterCalculator uses nucleotide regions of variable length (78 to 83bp) to make its predictions, while the variants we are focusing on are typically shorter (as shown in Figure 4). This results in other variants being included in the calculation and therefore slightly different predicted transcription rates for each strain. We have amended the caption of Figure 4 to provide a succinct explanation of these differences.

Line 359: Need to talk about each supplementary figure 4 to 9 and how they demonstrate your point.

We have expanded this section to more explicitly mention the contents of these supplementary figures and why they are relevant for the findings of this section (L425).

Are the text and figures clear and accurate?

Figure 4 too small

We have fixed the figure, as described above

Acronyms are defined multiple times in the manuscript, sometimes not the first time they are used (e.g. SNP, InDel)

Figure 8A - Remove red box, increase label size

Figure 8B - Low resolution, grey text is unreadable and should be darker and higher resolution

Line 35 - be more specific about types of carbon metabolism and catabolite repression

Line 67 - include citation for ireland et al. 2020 https://doi.org/10.7554/eLife.55308

Line 74 - You talk about looking in cis but don't specify how mar away cis is

Line 75 - we encoded genetic variants..... It is unclear what you mean here

Line 104 - 'were apart of operons' should clarify you mean polycistronic or multi-gene operons. Single genes may be considered operonic units as well.

We have addressed all the issues indicated above.

Figure 2: THere is no axis for the percents and the percents don't make sense relative to the bars they represent??

We realize that this visualization might not have been the most clear for readers, and have made the following improvement: we have added the number of genes with at least one association before the percentage. We note that the x-axis is in log scale, which may make it seem like the light-colored bars are off. With the addition of the actual number of associated genes we think that this confusion has been removed.

Figure 2: Figure 2B legend should clarify that these are individual examples of Differential expression between variants

Line 198-199: This sentence doesn't make sense, 'encoded using kmers' is not descriptive enough

Line 205: Should be upfront about that you're using the Promoter Calculator that models biophysical properties of promoter sequences to predict activity.

Line 251: 'Scanned the non-coding sequences of the DEGs'. This is far too vague of a description of an approach. Need to clarify how you did this and I didn't see in the method. Is this an HMM? Perfect sequence match to consensus sequence? Some type of alignment?

Line 257-259: This sentence lacks clarity

We have implemented all the suggested changes and clarified the points that the reviewer has highlighted above.

Line346: How were the E. coli isolates tested? Was this an experiment you did? This is a massive undertaking (1600 isolates * 12 conditions) if so so should be clearly defined

While we have indicated in the previous paragraph that the genomes and antimicrobial susceptibility data were obtained from previously published studies, we have now modified this paragraph (e.g. L411 and L418) slightly to make this point even clearer.

Figure 6A: The tile plot on the right side is not clearly labeled and it is unclear what it is showing and how that relates to the bar plots.

In the revised figure, we have clarified the labeling of the heatmap to now read “Log2(Fold Change) (measured expression)” to indicate that it represents each gene’s fold changes obtained from our initial transcriptomic analysis. We have also included this information in the caption of the figure, making the relationship between the measured gene expression (heatmap) and the reporter assay data (bar plots) clear to the reader.

FIgure 6B: typo in legend 'Downreglation'

We thank the review for pointing this out. The typo has been corrected to “Down regulation” in the revised figure.

Line 398: Need to state rationale for why Waaq operon is being investigated here. WHy did you look into individual example?

We thank the reviewer for asking for a clarification here. Our decision to investigate the waaQ gene was one of both biological relevance and empirical evidence. In our analysis associating non-coding variants with antimicrobial resistance using the Moradigaravand et al. dataset, we identified a T>C variant at position 3808241 that was associated with resistance to Tobramycin. We also observed this variant in our strain collection, where it was associated with expression changes of the gene, suggesting a possible functional impact. The waa operon is involved in LPS synthesis, a central determinant of the bacteria’s outer membrane integrity and a well established virulence factor. This provided a plausible biological mechanism through which variation could influence antimicrobial susceptibility. As its role in resistance has not been extensively characterized, this represents a good candidate for our experimental validation. We have now included this rationale in our revised manuscript (i.e. L476).

Figure 8: Can get rid of red box

We have now removed the red box from Figure 8 in the revised version.

Line 463 - 'account for all kinds' is too informal

Mix of font styles throughout document

We have implemented all the suggestions and formatting changes indicated above.

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

In their manuscript "Cis non-coding genetic variation drives gene expression changes in the E. coli and P. aeruginosa pangenomes", Damaris and co-authors present an extensive meta-analysis, plus some useful follow up experiments, attempting to apply GWAS principles to identify the extent to which differences in gene expression between different strains within a given species can be directly assigned to cis-regulatory mutations. The overall principle, and the question raised by the study, is one of substantial interest, and the manuscript here represents a careful and fascinating effort at unravelling these important questions. I want to preface my review below (which may otherwise sound more harsh than I intend) with the acknowledgment that this is an EXTREMELY difficult and challenging problem that the authors are approaching, and they have clearly put in a substantial amount of high quality work in their efforts to address it. I applaud the work done here, I think it presents some very interesting findings, and I acknowledge fully that there is no one perfect approach to addressing these challenges, and while I will object to some of the decisions made by the authors below, I readily admit that others might challenge my own suggestions and approaches here. With that said, however, there is one fundamental decision that the authors made which I simply cannot agree with, and which in my view undermines much of the analysis and utility of the study: that decision is to treat both gene expression and the identification of cis-regulatory regions at the level of individual genes, rather than transcriptional units. Below I will expand on why I find this problematic, how it might be addressed, and what other areas for improvement I see in the manuscript:

We thank the reviewer for their praise of our work. A careful set of replies to the major and minor critiques are reported below each point.

In the entire discussion from lines roughly 100-130, the authors frequently dissect out apparently differentially expressed genes from non differentially expressed genes within the same operons... I honestly wonder whether this is a useful distinction. I understand that by the criteria set forth by the authors it is technically correct, and yet, I wonder if this is more due to thresholding artifacts (i.e., some genes passing the authors' reasonable-yet-arbitrary thresholds whereas others in the same operon do not), and in the process causing a distraction from an operon that is in fact largely moving in the same direction. The authors might wish to either aggregate data in some way across known transcriptional units for the purposes of their analysis, and/or consider a more lenient 'rescue' set of significance thresholds for genes that are in the same operons as differentially expressed genes. I would favor the former approach, performing virtually all of their analysis at the level of transcriptional units rather than individual genes, as much of their analysis in any case relies upon proper assignment of genes to promoters, and this way they could focus on the most important signals rather than get lots sometimes in the weeds of looking at every single gene when really what they seem to be looking at in this paper is a property OF THE PROMOTERS, not the genes. (of course there are phenomena, such as rho dependent termination specifically titrating expression of late genes in operons, but I think on the balance the operon-level analysis might provide more insights and a cleaner analysis and discussion).

We agree with the reviewer that the peculiar nature of transcription in bacteria has to be taken into account in order to properly quantify the influence of cis variants in gene expression changes. We therefore added the exact analysis the reviewer suggested; that is, we ran associations between the variants in cis to the first gene of each operon and a phenotype that considered the fold-change of all genes in the operon, via a weighted average (see Methods for more details). As reported in the results section (L223), we found a similar trend as with the original analysis: we found the highest proportion of associations when encoding cis variants using k-mers (42% for E. coli and 45% for P. aeruginosa). More importantly, we found a high degree of overlap between this new “operon-level” association analysis and the original one (only including the first gene in each operon). We found a range of 90%-94% of associations overlapping for E. coli and between 75% and 91% for P. aeruginosa, depending on the variant type. We note that operon definitions are less precise for P. aeruginosa, which might explain the higher variability in the level of overlap. We have added the results of this analysis in the results section.

This also leads to a more general point, however, which I think is potentially more deeply problematic. At the end of the day, all of the analysis being done here centers on the cis regulatory logic upstream of each individual open reading frame, even though in many cases (i.e., genes after the first one in multi-gene operons), this is not where the relevant promoter is. This problem, in turn, raises potentially misattributions of causality running in both directions, where the causal impact on a bona fide promoter mutation on many genes in an operon may only be associated with the first gene, or on the other side, where a mutation that co-occurs with, but is causally independent from, an actual promoter mutation may be flagged as the one driving an expression change. This becomes an especially serious issue in cases like ulaE, for genes that are not the first gene in an operon (at least according to standard annotations, the UlaE transcript should be part of a polycistronic mRNA beginning from the ulaA promoter, and the role played by cis-regulatory logic immediately upstream of ulaE is uncertain and certainly merits deeper consideration. I suspect that many other similar cases likewise lurk in the dataset used here (perhaps even moreso for the Pseudomonas data, where the operon definitions are likely less robust). Of course there are many possible explanations, such as a separate ulaE promoter only in some strains, but this should perhaps be carefully stated and explored, and seems likely to be the exception rather than the rule.

While we again agree with the reviewer that some of our associations might not result in a direct causal link because the focal variant may not belong to an actual promoter element, we also want to point out how the ability to identify the composition of transcriptional units in bacteria is far from a solved problem (see references at the bottom of this comment, two in general terms, and one characterizing a specific example), even for a well-studied species such as E. coli. Therefore, even if carrying out associations at the operon level (e.g. by focusing exclusively on variants in cis for the first gene in the operon) might be theoretically correct, a number of the associations we find further down the putative operons might be the result of a true biological signal.

1. Conway, T., Creecy, J. P., Maddox, S. M., Grissom, J. E., Conkle, T. L., Shadid, T. M., Teramoto, J., San Miguel, P., Shimada, T., Ishihama, A., Mori, H., & Wanner, B. L. (2014). Unprecedented High-Resolution View of Bacterial Operon Architecture Revealed by RNA Sequencing. mBio, 5(4), 10.1128/mbio.01442-14. https://doi.org/10.1128/mbio.01442-14

2. Sáenz-Lahoya, S., Bitarte, N., García, B., Burgui, S., Vergara-Irigaray, M., Valle, J., Solano, C., Toledo-Arana, A., & Lasa, I. (2019). Noncontiguous operon is a genetic organization for coordinating bacterial gene expression. Proceedings of the National Academy of Sciences, 116(5), 1733–1738. https://doi.org/10.1073/pnas.1812746116

3. Zehentner, B., Scherer, S., & Neuhaus, K. (2023). Non-canonical transcriptional start sites in E. coli O157:H7 EDL933 are regulated and appear in surprisingly high numbers. BMC Microbiology, 23(1), 243. https://doi.org/10.1186/s12866-023-02988-6

Another issue with the current definition of regulatory regions, which should perhaps also be accounted for, is that it is likely that for many operons, the 'regulatory regions' of one gene might overlap the ORF of the previous gene, and in some cases actual coding mutations in an upstream gene may contaminate the set of potential regulatory mutations identified in this dataset.

We agree that defining regulatory regions might be challenging, and that those regions might overlap with coding regions, either for the focal gene or the one immediately upstream. For these reasons we have defined a wide region to identify putative regulatory variants (-200 to +30 bp around the start codon of the focal gene). We believe this relatively wide region allows us to capture the most cis genetic variation.

Taken together, I feel that all of the above concerns need to be addressed in some way. At the absolute barest minimum, the authors need to acknowledge the weaknesses that I have pointed out in the definition of cis-regulatory logic at a gene level. I think it would be far BETTER if they performed a re-analysis at the level of transcriptional units, which I think might substantially strengthen the work as a whole, but I recognize that this would also constitute a substantial amount of additional effort.

As indicated above, we have added a section in the results section to report on the analysis carried out at the level of operons as individual units, with more details provided in the methods section. We believe these results, which largely overlap with the original analysis, are a good way to recognize the limitation of our approach and to acknowledge the importance of gaining a better knowledge on the number and composition of transcriptional units in bacteria, for which, as the reference above indicates, we still have an incomplete understanding.

Having reached the end of the paper, and considering the evidence and arguments of the authors in their totality, I find myself wondering how much local x background interactions - that is, the effects of cis regulatory mutations (like those being considered here, with or without the modified definitions that I proposed above) IN THE CONTEXT OF A PARTICULAR STRAIN BACKGROUND, might matter more than the effects of the cis regulatory mutations per se. This is a particularly tricky problem to address because it would require a moderate number of targeted experiments with a moderate number of promoters in a moderate number of strains (which of course makes it maximally annoying since one can't simply scale up hugely on either axis individually and really expect to tease things out). I think that trying to address this question experimentally is FAR beyond the scope of the current paper, but I think perhaps the authors could at least begin to address it by acknowledging it as a challenge in their discussion section, and possibly even identify candidate promoters that might show the largest divergence of activities across strains when there IS no detectable cis regulatory mutation (which might be indicative of local x background interactions), or those with the largest divergences of effect for a given mutation across strains. A differential expression model incorporating shrinkage is essential in such analysis to avoid putting too much weight on low expression genes with a lot of Poisson noise.

We again thank the reviewer for their thoughtful comments on the limitations of correlative studies in general, and microbial GWAS in particular. In regards to microbial GWAS we feel we may have failed to properly explain how the implementation we have used allows to, at least partially, correct for population structure effects. That is, the linear mixed model we have used relies on population structure to remove the part of the association signal that is due to the genetic background and thus focus the analysis on the specific loci. Obviously examples in which strong epistatic interactions are present would not be accounted for, but those would be extremely challenging to measure or predict at scale, as the reviewer rightfully suggests. We have added a brief recap of the ability of microbial GWAS to account for population structure in the results section (“A large fraction of gene expression changes can be attributed to genetic variations in cis regulatory regions”, e.g. L195).

I also have some more minor concerns and suggestions, which I outline below:

It seems that the differential expression analysis treats the lab reference strains as the 'centerpoint' against which everything else is compared, and yet I wonder if this is the best approach... it might be interesting to see how the results differ if the authors instead take a more 'average' strain (either chosen based on genetics or transcriptomics) as a reference and compared everything else to that.

While we don’t necessarily disagree with the reviewer that a “wild” strain would be better to compare against, we think that our choice to go for the reference isolates is still justified on two grounds. First, while it is true that comparing against a reference introduces biases in the analysis, this concern would not be removed had we chosen another strain as reference; which strain would then be best as a reference to compare against? We think that the second point provides an answer to this question; the “traditional” reference isolates have a rich ecosystem of annotations, experimental data, and computational predictions. These can in turn be used for validation and hypothesis generation, which we have done extensively in the manuscript. Had we chosen a different reference isolate we would have had to still map associations to the traditional reference, resulting in a probable reduction in precision. An example that will likely resonate with this reviewer is that we have used experimentally-validated and high quality computational operon predictions to look into likely associations between cis-variants and “operon DEGs”. This analysis would have likely been of worse quality had we used another strain as reference, for which operon definitions would have had to come from lower-quality predictions or be “lifted” from the traditional reference.

Line 104 - the statement about the differentially expressed genes being "part of operons with diverse biological functions" seems unclear - it is not apparent whether the authors are referring to diversity of function within each operon, or between the different operons, and in any case one should consider whether the observation reflects any useful information or is just an apparently random collection of operons.

We agree that this formulation could create confusion and we have elected to remove the expression “with diverse biological functions”, given that we discuss those functions immediately after that sentence.

Line 292 - I find the argument here somewhat unconvincing, for two reasons. First, the fact that only half of the observed changes went in the same direction as the GWAS results would indicate, which is trivially a result that would be expected by random chance, does not lend much confidence to the overall premise of the study that there are meaningful cis regulatory changes being detected (in fact, it seems to argue that the background in which a variant occurs may matter a great deal, at least as much as the cis regulatory logic itself). Second, in order to even assess whether the GWAS is useful to "find the genetic determinants of gene expression changes" as the authors indicate, it would be necessary to compare to a reasonable, non-straw-man, null approach simply identifying common sequence variants that are predicted to cause major changes in sigma 70 binding at known promoters; such a test would be especially important given the lack of directional accuracy observed here. Along these same lines, it is perhaps worth noting, in the discussion beginning on line 329, that the comparison is perhaps biased in favor of the GWAS study, since the validation targets here were prioritized based on (presumably strong) GWAS data.

We thank the reviewer for prompting us into reasoning about the results of the in-vitro validation experiments. We agree that the agreement between the measured gene expression changes agree only partly with those measured with the reporter system, and that this discrepancy could likely be attributed to regulatory elements that are not in cis, and thus that were not present in the in-vitro reporter system. We have noted this possibility in the discussion. Additionally, we have amended the results section to note that even though the prediction in the direction of gene expression change was not as accurate as it could be expected, the prediction of whether a change would be present (thus ignoring directionality) was much higher.

I don't find the Venn diagrams in Fig 7C-D useful or clear given the large number of zero-overlap regions, and would strongly advocate that the authors find another way to show these data.

While we are aware that alternative ways to show overlap between sets, such as upset plots, we don’t actually find them that much easier to parse. We actually think that the simple and direct Venn diagrams we have drawn convey the clear message that overlaps only exist between certain drug classes in E. coli, and virtually none for P. aeruginosa. We have added a comment on the lack of overlap between all drug classes and the differences between the two species in the results section (i.e. L436 and L465).

In the analysis of waa operon gene expression beginning on line 400, it is perhaps important to note that most of the waa operon doesn't do anything in laboratory K12 strains due to the lack of complete O-antigen... the same is not true, however, for many wild/clinical isolates. It would be interesting to see how those results compare, and also how the absolute TPMs (rather than just LFCs) of genes in this operon vary across the strains being investigated during TOB treatment.

We thank the reviewer for this helpful suggestion. We examined the absolute expression (TPMs) of waa operon genes under the baseline (A) and following exposure to Tobramycin (B). The representative TPMs per strain were obtained by averaging across biological replicates. We observed a constitutive expression of the genes in the reference strain (MG1655) and the other isolates containing the variant of interest (MC4100, BW25113). In contrast, strains lacking the variants of interest (IAI76 and IAI78), showed lower expression of these operon genes under both conditions. Strain IAI77, on the other hand, displayed increased expression of a subset of waa genes post Tobramycin exposure, indicating strain-specific variation in transcriptional response. While the reference isolate might not have the O-antigen, it certainly expresses the waa operon, both constitutively and under TOB exposure.

I don't think that the second conclusion on lines 479-480 is fully justified by the data, given both the disparity in available annotation information between the two species, AND the fact that only two species were considered.

While we feel that the “Discussion” section of a research paper allows for speculative statements, we have to concede that we have perhaps overreached here. We have amended this sentence to be more cautious and not mislead readers.

Line 118: "Double of DEGs"

Line 288 - presumably these are LOG fold changes

Fig 6b - legend contains typos

Line 661 - please report the read count (more relevant for RNA-seq analysis) rather than Gb

We thank the reviewer for pointing out the need to make these edits. We have implemented them all.

Source code - I appreciate that the authors provide their source code on github, but it is very poorly documented - both a license and some top-level documentation about which code goes with each major operation/conclusion/figure should be provided. Also, ipython notebooks are in general a poor way in my view to distribute code, due to their encouragement of nonlinear development practices; while they are fine for software development, actual complete python programs along with accompanying source data would be preferrable.

We agree with the reviewer that a software license and some documentation about what each notebook is about is warranted, and we have added them both. While we agree that for “consumer-grade” software jupyter notebooks are not the most ergonomic format, we believe that as a documentation of how one-time analyses were carried out they are actually one of the best formats we could think of. They in fact allow for code and outputs to be presented alongside each other, which greatly helped us to iterate on our research and to ensure that what was presented in the manuscript matched the analyses we reported in the code. This is of course up for debate and ultimately specific to someone’s taste, and so we will keep the reviewer’s critique in mind for our next manuscript. And, if we ever decide to package the analyses presented in the manuscript as a “consumer-grade” application for others to use, we would follow higher standards of documentation and design.

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

In this manuscript, Damaris et al. collected genome sequences and transcriptomes from isolates from two bacterial species. Data for E. coli were produced for this paper, while data for P. aeruginosa had been measured earlier. The authors integrated these data to detect genes with differential expression (DE) among isolates as well as cis-expression quantitative trait loci (cis-eQTLs). The authors used sample sizes that were adequate for an initial exploration of gene regulatory variation (n=117 for E. coli and n=413 for P. aeruginosa) and were able to discover cis eQTLs at about 39% of genes. In a creative addition, the authors compared their results to transcription rates predicted from a biophysical promoter model as well as to annotated transcription factor binding sites. They also attempted to validate some of their associations experimentally using GFP-reporter assays. Finally, the paper presents a mapping of antibiotic resistance traits. Many of the detected associations for this important trait group were in non-coding genome regions, suggesting a role of regulatory variation in antibiotic resistance.

A major strength of the paper is that it covers an impressive range of distinct analyses, some of which in two different species. Weaknesses include the fact that this breadth comes at the expense of depth and detail. Some sections are underdeveloped, not fully explained and/or thought-through enough. Important methodological details are missing, as detailed below.

We thank the reviewer for highlighting the strengths of our study. We hope that our replies to their comments and the other two reviewers will address some of the limitations.

Major comments:

1. An interesting aspect of the paper is that genetic variation is represented in different ways (SNPs & indels, IRG presence/absence, and k-mers). However, it is not entirely clear how these three different encodings relate to each other. Specifically, more information should be given on these two points:

2. it is not clear how "presence/absence of intergenic regions" are different from larger indels.

In order to better guide readers through the different kinds of genetic variants we considered, we have added a brief explanation about what “promoter switches” are in the introduction (“meaning that the entire promoter region may differ between isolates due to recombination events”, L56). We believe this clarifies how they are very different in character from a large deletion. We have kept the reference to the original study (10.1073/pnas.1413272111) describing how widespread these switches are in E. coli as a way for readers to discover more about them.

• I recommend providing more narration on how the k-mers compare to the more traditional genetic variants (SNPs and indels). It seems like the k-mers include the SNPs and indels somehow? More explanation would be good here, as k-mer based mapping is not usually done in other species and is not standard practice in the field. Likewise, how is multiple testing handled for association mapping with k-mers, since presumably each gene region harbors a large number of k-mers, potentially hugely increasing the multiple testing burden?

We indeed agree with the reviewer in thinking that representing genetic variants as k-mers would encompass short variants (SNP/InDels) as well as larger variants and promoters presence/absence patterns. We believe that this assumption is validated by the fact that we identify the highest proportion of DEGs with a significant association when using this representation of variants (Figure 2A, 39% for both species). We have added a reference to a recent review on the advantages of k-mer methods for population genetics (10.1093/molbev/msaf047) in the introduction. Regarding the issue of multiple testing correction, we have employed a commonly recognized approach that, unlike a crude Bonferroni correction using the number of tested variants, allows for a realistic correction of association p-values. We used the number of unique presence/absence patterns, which can be shared between multiple genetic variants, and applied a Bonferroni correction using this number rather than the number of variants tested. We have expanded the corresponding section in the methods (e.g. L697) to better explain this point for readers not familiar with this approach.

1. What was the distribution of association effect sizes for the three types of variants? Did IRGs have larger effects than SNPs as may be expected if they are indeed larger events that involve more DNA differences? What were their relative allele frequencies?

We appreciate the suggestion made by the reviewer to look into the distribution of effect sizes divided by variant type. We have now evaluated the distribution of the effect sizes and allele frequencies for the genetic markers (SNPs/InDels, IGRs, and k-mers) for both species (Supplementary Figure 2). In E. coli, IGR variants showed somewhat larger median effect sizes (|β| = 4.5) than SNPs (|β| = 3.8), whereas k-mers displayed the widest distribution (median |β| = 5.2). In P. aeruginosa, the trend differed with IGRs exhibiting smaller effects (median |β| = 3.2), compared to SNPs/InDels (median |β| =5.1) and k-mers (median |β| = 6.2). With respect to allele frequencies, SNPs/InDels generally occured at lower frequencies (median AF = 0.34 for E.coli, median AF = 0.33 for P. aeruginosa), whereas IGRs (median AF = 0.65 for E. coli and 0.75 for P. aeruginosa) and k-mers (median AF = 0.71 for E. coli and 0.65 for P. aeruginosa) were more often at the intermediate to higher frequencies respectively. We have added a visualization for the distribution of effect sizes (Supplementary Figure 2).

1. The GFP-based experiments attempting to validate the promoter effects for 18 genes are laudable, and the fact that 16 of them showed differences is nice. However, the fact that half of the validation attempts yielded effects in the opposite direction of what was expected is quite alarming. I am not sure this really "further validates" the GWAS in the way the authors state in line 292 - in fact, quite the opposite in that the validations appear random with regards to what was predicted from the computational analyses. How do the authors interpret this result? Given the higher concordance between GWAS, promoter prediction, and DE, are the GFP assays just not relevant for what is going on in the genome? If not, what are these assays missing? Overall, more interpretation of this result would be helpful.

We thanks the reviewer for their comment, which is similar in nature to that raised by reviewer #2 above. As noted in our reply above we have amended the results and discussion to indicate that although the direction of gene expression change was not highly accurate, focusing on the magnitude (or rather whether there would be a change in gene expression, regardless of the direction), resulted in a higher accuracy. We postulate that the cases in which the direction of the change was not correctly identified could be due to the influence of other genetic elements in trans with the gene of interest.

1. On the same note, it would be really interesting to expand the GFP experiments to promoters that did not show association in the GWAS. Based on Figure 6, effects of promoter differences on GFP reporters seem to be very common (all but three were significant). Is this a higher rate than for the average promoter with sequence variation but without detected association? A handful of extra reporter experiments might address this. My larger question here is: what is the null expectation for how much functional promoter variation there is?

We thank the reviewer for this comment. We agree that estimating the null expectation for the functional promoter would require testing promoter alleles with sequence variation that are not associated in the GWAS. Such experiments, which would directly address if the observed effects in our study exceeds background, would have required us to prepare multiple constructs, which was unfortunately not possible for us due to staff constraints. We therefore elected to clarify the scope of our GFP reporter assays instead. These experiments were designed as a paired comparison of the wild-type and the GWAS-associated variant alleles of the same promoter in an identical reporter background, with the aim of testing allele-specific functional effects for GWAS hits (Supplementary Figure 6). We also included a comparison in GFP fluorescence between the promoterless vector (pOT2) and promoter-containing constructs; we observed higher GFP signals in all but four (yfgJ, fimI, agaI, and yfdQ) variant-containing promoter constructs, which indicates that for most of the construct we cloned active promoter elements. We have revised the manuscript text accordingly to reflect this clarification and included the control in the supplementary information as Supplementary Figure 6.

1. Were the fold-changes in the GFP experiments statistically significant? Based on Figure 6 it certainly looks like they are, but this should be spelled out, along with the test used.

We thank the reviewer for pointing this out. We have reviewed Figure 6 to indicate significant differences between the test and control reporter constructs. We used the paired student’s t-test to match the matched plate/time point measurements. We also corrected for multiple testing using the Benhamini-Hochberg correction. As seen in the updated Figure 6A, 16 out of the 18 reporter constructs displayed significant differences (adjusted p-value

1. What was the overall correlation between GWAS-based fold changes and those from the GFP-based validation? What does Figure 6A look like as a scatter plot comparing these two sets of values?

We thank the reviewer for this helpful suggestion, which allows us to more closely look into the results of our in-vitro validation. We performed a direct comparison of RNAseq fold changes from the GWAS (x-axis) with the GFP reporter measurements (y-axis) as depicted in the figure above. The overall correlation between the two was weak (Pearson r = 0.17), reflecting the lack of thorough agreement between the associations and the reporter construct. We however note that the two metrics are not directly comparable in our opinion, since on the x-axis we are measuring changes in gene expression and on the y-axis changes in fluorescence expression, which is downstream from it. As mentioned above and in reply to a comment from reviewer 2, the agreement between measured gene expression and all other in-silico and in-vitro techniques increases when ignoring the direction of the change. Overall, we believe that these results partly validate our associations and predictions, while indicating that other factors in trans with the regulatory region contribute to changes in gene expression, which is to be expected. The scatter plot has been included as a new supplementary figure (Supplementary Figure 7).

1. Was the SNP analyzed in the last Results section significant in the gene expression GWAS? Did the DE results reported in this final section correspond to that GWAS in some way?

The T>C SNP upstream of waaQ did not show significant association with gene expression in our cis GWAS analysis. Instead, this variant was associated with resistance to tobramycin when referencing data from Danesh et al, and we observed the variant in our strain collection. We subsequently investigated whether this variant also influenced expression of the waa operon under sub-inhibitory tobramycin exposure. The differential expression results shown in the final section therefore represent a functional follow-up experiment, and not a direct replication of the GWAS presented in the first part of the manuscript.

1. Line 470: "Consistent with the differences in the genetic structure of the two species" It is not clear what differences in genetic structure this refers to. Population structure? Genome architecture? Differences in the biology of regulatory regions?

The awkwardness of that sentence is perhaps the consequence of our assumption that readers would be aware of the differences in population genetics differences between the two species. We however have realized that not much literature is available (if at all!) about these differences, which we have observed during the course of this and other studies we have carried out. As a result, we agree that we cannot assume that the reader is similarly familiar with these differences, and have changed that sentence (i.e. L548) to more directly address the differences between the two species, which will presumably result in a diverse population structure. We thank the reviewer for letting us be aware of a gap in the literature concerning the comparison of pangenome structures across relevant species.

1. Line 480: the reference to "adaption" is not warranted, as the paper contains no analyses of evolutionary patterns or processes. Genetic variation is not the same as adaptation.

We have amended this sentence to be more adherent to what we can conclude from our analyses.

1. There is insufficient information on how the E. coli RNA-seq data was generated. How was RNA extracted? Which QC was done on the RNA; what was its quality? Which library kits were used? Which sequencing technology? How many reads? What QC was done on the RNA-seq data? For this section, the Methods are seriously deficient in their current form and need to be greatly expanded.

We thank the reviewer for highlighting the need for clearer methodological detail. We have expanded this section (i.e. L608) to fully describe the generation and quality control of the E. coli RNA-seq data including RNA extraction and sequencing platform.

1. How were the DEG p-values adjusted for multiple testing?

As indicated in the methods section (“Differential gene expression and functional enrichment analysis”), we have used DEseq2 for E. coli, and LPEseq for P. aeruginosa. Both methods use the statistical framework of the False Discovery Rate (FDR) to compute an adjusted p-value for each gene. We have added a brief mention of us following the standard practice indicated by both software packages in the methods.

1. Were there replicates for the E. coli strains? The methods do not say, but there is a hint there might have been replicates given their absence was noted for the other species.

In the context of providing more information about the transcriptomics experiments for E. coli, we have also more clearly indicated that we have two biological replicates for the E. coli dataset.

1. There needs to be more information on the "pattern-based method" that was used to correct the GWAS for multiple tests. How does this method work? What genome-wide threshold did it end up producing? Was there adjustment for the number of genes tested in addition to the number of variants? Was the correction done per variant class or across all variant classes?

In line with an earlier comment from this reviewer, we have expanded the section in the Methods (e.g. L689) that explains how this correction worked to include as many details as possible, in order to provide the readers with the full context under which our analyses were carried out.

1. For a paper that, at its core, performs a cis-eQTL mapping, it is an oversight that there seems not to be a single reference to the rich literature in this space, comprising hundreds of papers, in other species ranging from humans, many other animals, to yeast and plants.

We thank both reviewer #1 and #3 for pointing out this lack of references to the extensive literature on the subject. We have added a number of references about the applications of eQTL studies, and specifically its application in microbial pangenomes, which we believe is more relevant to our study, in the introduction.

Minor comments:

1. I wasn't able to understand the top panels in Figure 4. For ulaE, most strains have the solid colors, and the corresponding bottom panel shows mostly red points. But for waaQ, most strains have solid color in the top panel, but only a few strains in the bottom panel are red. So solid color in the top does not indicate a variant allele? And why are there so many solid alleles; are these all indels? Even if so, for kgtP, the same colors (i.e., nucleotides) seem to seamlessly continue into the bottom, pale part of the top panel. How are these strains different genotypically? Are these blocks of solid color counted as one indel or several SNPs, or somehow as k-mer differences? As the authors can see, these figures are really hard to understand and should be reworked. The same comment applies to Figure 5, where it seems that all (!) strains have the "variant"?

We thank the reviewer for pointing out some limitations with our visualizations, most importantly with the way we explained how to read those two figures. We have amended the captions to more explicitly explain what is shown. The solid colors in the “sequence pseudo-alignment” panels indicate the focal cis variant, which is indicated in red in the corresponding “predicted transcription rate” panels below. In the case of Figure 5, the solid color indicates instead the position of the TFBS in the reference.

1. Figure 1A & B: It would be helpful to add the total number of analyzed genes somewhere so that the numbers denoted in the colored outer rings can be interpreted in comparison to the total.

We have added the total number of genes being considered for either species in the legend.

1. Figure 1C & D: It would be better to spell out the COG names in the figure, as it is cumbersome for the reader to have to look up what the letters stand for in a supplementary table in a separate file.

While we do not disagree with the awkwardness of having to move to a supplementary table to identify the full name of a COG category, we also would like to point out that the very long names of each category would clutter the figure to a degree that would make it difficult to read. We had indeed attempted something similar to what the reviewer suggests in early drafts of this manuscript, leading to small and hard to read labels. We have therefore left the full names of each COG category in Supplementary Table 3.

1. Line 107: "Similarly," does not fit here as the following example (with one differentially expressed gene in an operon) is conceptually different from the one before, where all genes in the operon were differentially expressed.

We agree and have amended the sentence accordingly.

1. Figure 5 bottom panel: it is odd that on the left the swarm plots (i.e., the dots) are on the inside of the boxplots while on the right they are on the outside.

We have fixed the position of the dots so that they are centered with respect to the underlying boxplots.

1. It is not clear to me how only one or a few genes in an operon can show differential mRNA abundance. Aren't all genes in an operon encoded by the same mRNA? If so, shouldn't this mRNA be up- or downregulated in the same manner for all genes it encodes? As I am not closely familiar with bacterial systems, it is well possible that I am missing some critical fact about bacterial gene expression here. If this is not an analysis artifact, the authors could briefly explain how this observation is possible.

We thanks the reviewer for their comment, which again echoes one of the main concerns from reviewer #2. As noted in our reply above, it has been established in multiple studies (see the three we have indicated above in our reply to reviewer #2) how bacteria encode for multiple “non-canonical” transcriptional units (i.e. operons), due to the presence of accessory terminators and promoters. This, together with other biological effects such as the presence of mRNA molecules of different lengths due to active transcription and degradation and technical noise induced by RNA isolation and sequencing can result in variability in the estimation of abundance for each gene.

So is this simple substitution Cipher uncrackable? Well, let's wait a minute here. It's not, for example, one of the pieces of information we can use in analyzing simple substitution is the letter frequencies of the English language or any language If you looked at a histogram of English letter frequencies, you'd see that e is the most frequent letter just above 12 percent, T is the second most frequent at somewhere around nine percent, a is very frequent at more than eight percent and so forth, so you would see this familiar pattern in any text that you encrypted. For example, if you encrypted it using the simple substitution Cipher, you might get this pattern, but you'd still see a peak where the letter that was substituted for e occurs. And maybe this is the peak for T, and maybe this is the peak for a. By analyzing those peaks and valleys, you can determine how the message was encrypted, can figure out the key. But, wait a minute… frequency analysis works!<br /> Slide 21, 22 chart

E.G. If you sorted by frequencies. Now, you can see this very clearly if you sort the two histograms, they're practically identical, and that's what lets the analyst with some effort, of course, figure out the key and break the message so you can break simple substitution cipher using frequency analysis. That makes Eve happy, Alice and Bob are not very happy about that. Eve wins … you don’t need brute force. Frequency analysis will break simple substitution. slide 23, 24 chart

The lasting success of these missionaries is still shown in present day Philippines. With nearly 90% of the country apart of the Christian faith, it's the largest Christian nation on the Asian continent. The vast majority of these Christians are Roman Catholic, just like the Spaniards who settled in Philippines in the 1500's https://blogs.loc.gov/international-collections/2018/07/catholicism-in-the-philippines-during-the-spanish-colonial-period-1521-1898/

Reference:

Preprints. (2024). Traditional ecological knowledge and environmental stewardship. https://doi.org/10.20944/preprints202406.1838.v1

“Traditional Ecological Knowledge (TEK) represents a knowledge system grounded in lived experience and intergenerational learning.”(Preprints,2024)

This article connects strongly to our course because in class we will study sustainability and social-ecological systems, In class we already discussed about social ecological system where we learned that Environmental management is not just technical but it's also related to social and historical things. In class. we discussed about how ecosystems and humans influence each other, which is exactly what Traditional ecological knowledge is based on. TEK is defined as generations of observation, trial and error instead of short term scientific studies and policies. This article also connects to discussion about whose knowledge is considered valid in environmental decision making. The course gives the idea that ignoring indigenous people's knowledge leads to ineffective policies and wrong results. This article support the course argument that for effective environmental management multiple ways of knowing the TEK is necessary. This article also reinforces that sustainability is not just about protecting nature but also about respecting culture, people and historical experience.

This sentence in itself is very important and impactful. People can judge others hobbies or interests and see their perspective on it has boring or uninteresting. For that person is it something more than just what meets the eyes. It’s something that they enjoy, find meaningful, interesting etc. This just introduces the difference between people. We all have different ideas, interests, etc.

That’s such a good reminder that “private” messaging usually just means “not public,” not “only between two people.” It makes me want to be more careful about what I assume is truly confidential when I DM. I also think it’s wild how much of this is automated—like filtering, scanning, or flagging messages without us noticing. It raises a real question of how much privacy we’re actually trading for convenience.

I found the donkey protest example helpful for understanding how responsibility can be separated from action. Just like the donkey does not understand the protest it carries, bots can perform actions without intention or awareness. This makes it harder to assign responsibility, since the people who design, deploy, or benefit from a bot may all have different roles and intentions.

It's not as simple as just using CDC - there are a ton of downstream issues like these schema issues that makes it harder

Reviewer #1 (Public review):

Summary:

This paper investigates the control signals that drive event model updating during continuous experience. The authors apply predictions from previously published computational models to fMRI data acquired while participants watched naturalistic video stimuli. They first examine the time course of BOLD pattern changes around human-annotated event boundaries, revealing pattern changes preceding the boundary in anterior temporal and then parietal regions, followed by pattern stabilization across many regions. The authors then analyze time courses around boundaries generated by a model that updates event models based on prediction error and another that uses prediction uncertainty. These analyses reveal overlapping but partially distinct dynamics for each boundary type, suggesting that both signals may contribute to event segmentation processes in the brain.

Strengths:

The question addressed by this paper is of high interest to researchers working on event cognition, perception, and memory. There has been considerable debate about what kinds of signals drive event boundaries, and this paper directly engages with that debate by comparing prediction error and prediction uncertainty as candidate control signals.

The authors use computational models that explain significant variance in human boundary judgments, and they report the variance explained clearly in the paper.

The authors' method of using computational models to generate predictions about when event model updating should occur is a valuable mechanistic alternative to methods like HMM or GSBS, which are data-driven.

The paper utilizes an analysis framework that characterizes how multivariate BOLD pattern dissimilarity evolves before and after boundaries. This approach offers an advance over previous work focused on just the boundary or post-boundary points.

Weaknesses:

Boundaries derived from prediction error and uncertainty are correlated for the naturalistic stimuli. This raises some concerns about how well their distinct contributions to brain activity can be separated. While the authors attempt to look at the unique variance, there is a limit to how effectively this can be done without experimentally dissociating prediction error and uncertainty.

The authors reports an average event length of ~20 seconds, and they also look +20 and -20 seconds around each event boundary. Thus, it's unclear how often pre- and post-boundary timepoints are part of adjacent events. This complicates the interpretations of the reported timecourses.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper investigates the control signals that drive event model updating during continuous experience. The authors apply predictions from previously published computational models to fMRI data acquired while participants watched naturalistic video stimuli. They first examine the time course of BOLD pattern changes around human-annotated event boundaries, revealing pattern changes preceding the boundary in anterior temporal and then parietal regions, followed by pattern stabilization across many regions. The authors then analyze time courses around boundaries generated by a model that updates event models based on prediction error and another that uses prediction uncertainty. These analyses reveal overlapping but partially distinct dynamics for each boundary type, suggesting that both signals may contribute to event segmentation processes in the brain.

Strengths:

(1) The question addressed by this paper is of high interest to researchers working on event cognition, perception, and memory. There has been considerable debate about what kinds of signals drive event boundaries, and this paper directly engages with that debate by comparing prediction error and prediction uncertainty as candidate control signals.

(2) The authors use computational models that explain significant variance in human boundary judgments, and they report the variance explained clearly in the paper.

(3) The authors' method of using computational models to generate predictions about when event model updating should occur is a valuable mechanistic alternative to methods like HMM or GSBS, which are data-driven.

(4) The paper utilizes an analysis framework that characterizes how multivariate BOLD pattern dissimilarity evolves before and after boundaries. This approach offers an advance over previous work focused on just the boundary or post-boundary points.

We appreciate this reviewer’s recognition of the significance of this research problem, and of the value of the approach taken by this paper.

Weaknesses:

(1) While the paper raises the possibility that both prediction error and uncertainty could serve as control signals, it does not offer a strong theoretical rationale for why the brain would benefit from multiple (empirically correlated) signals. What distinct advantages do these signals provide? This may be discussed in the authors' prior modeling work, but is left too implicit in this paper.

We added a brief discussion in the introduction highlighting the complementary advantages of prediction error and prediction uncertainty, and cited prior theoretical work that elaborates on this point. Specifically, we now note that prediction error can act as a reactive trigger, signaling when the current event model is no longer sufficient (Zacks et al., 2007). In contrast, prediction uncertainty is framed as proactive, allowing the system to prepare for upcoming changes even before they occur (Baldwin & Kosie, 2021; Kuperberg, 2021). Together, this makes clearer why these two signals could each provide complementary benefits for effective event model updating.

"One potential signal to control event model updating is prediction error—the difference between the system’s prediction and what actually occurs. A transient increase in prediction error is a valid indicator that the current model no longer adequately captures the current activity. Event Segmentation Theory (EST; Zacks et al., 2007) proposes that event models are updated when prediction error increases beyond a threshold, indicating that the current model no longer adequately captures ongoing activity. A related but computationally distinct proposal is that prediction uncertainty (also termed "unpredictability") can serve as a control signal (Baldwin & Kosie, 2021). The advantage of relying on prediction uncertainty to detect event boundaries is that it is inherently proactive: the cognitive system can start looking for cues about what might come next before the next event starts (Baldwin & Kosie, 2021; Kuperberg, 2021). "

(2) Boundaries derived from prediction error and uncertainty are correlated for the naturalistic stimuli. This raises some concerns about how well their distinct contributions to brain activity can be separated. The authors should consider whether they can leverage timepoints where the models make different predictions to make a stronger case for brain regions that are responsive to one vs the other.

We addressed this concern by adding an analysis that explicitly tests the unique contributions of prediction error– and prediction uncertainty–driven boundaries to neural pattern shifts. In the revised manuscript, we describe how we fit a combined FIR model that included both boundary types as predictors and then compared this model against versions with only one predictor. This allowed us to identify the variance explained by each boundary type over and above the other. The results revealed two partially dissociable sets of brain regions sensitive to error- versus uncertainty-driven boundaries (see Figure S1), strengthening our argument that these signals make distinct contributions.

"To account for the correlation between uncertainty-driven boundaries and error-driven boundaries, we also fitted a FIR model that predicted pattern dissimilarity from both types of boundaries (combined FIR) for each parcel. Then, we performed two likelihood ratio tests: combined FIR to error FIR, which measures the unique contribution of uncertainty boundaries to pattern dissimilarity, and combined FIR to uncertainty FIR, which measures the unique contribution of error boundaries to pattern dissimilarity. The analysis also revealed two dissociable sets of brain regions associated with each boundary type (see Figure S1)."

(3) The authors refer to a baseline measure of pattern dissimilarity, which their dissimilarity measure of interest is relative to, but it's not clear how this baseline is computed. Since the interpretation of increases or decreases in dissimilarity depends on this reference point, more clarity is needed.

We clarified how the FIR baseline is estimated in the methods section. Specifically, we now explain that the FIR coefficients should be interpreted relative to a reference level, which reflects the expected dissimilarity when timepoints are far from an event boundary. This makes it clear what serves as the comparison point for observed increases or decreases in dissimilarity.

"The coefficients from the FIR model indicate changes relative to baseline, which can be conceptualized as the expected value when far from event boundaries."

(4) The authors report an average event length of ~20 seconds, and they also look at +20 and -20 seconds around each event boundary. Thus, it's unclear how often pre- and post-boundary timepoints are part of adjacent events. This complicates the interpretations of the reported time courses.

This is related to reviewer's 2 comment, and it will be addressed below.

(5) The authors describe a sequence of neural pattern shifts during each type of boundary, but offer little setup of what pattern shifts we might expect or why. They also offer little discussion of what cognitive processes these shifts might reflect. The paper would benefit from a more thorough setup for the neural results and a discussion that comments on how the results inform our understanding of what these brain regions contribute to event models.

We thank the reviewer for this advice on how better to set the context for the different potential outcomes of the study. We expanded both the introduction and discussion to better set up expectations for neural pattern shifts and to interpret what these shifts may reflect. In the introduction, we now describe prior findings showing that sensory regions tend to update more quickly than higher-order multimodal regions (Baldassano et al., 2017; Geerligs et al., 2021, 2022), and we highlight that it remains unclear whether higher-order updates precede or follow those in lower-order regions. We also note that our analytic approach is well-suited to address this open question. In the discussion, we then interpret our results in light of this framework. Specifically, we describe how we observed early shifts in higher-order areas such as anterior temporal and prefrontal cortex, followed by shifts in parietal and dorsal attention regions closer to event boundaries. This pattern runs counter to the traditional bottom-up temporal hierarchy view and instead supports a model of top-down updating, where high-level representations are updated first and subsequently influence lower-level processing (Friston, 2005; Kuperberg, 2021). To make this interpretation concrete, we added an example: in a narrative where a goal is reached midway—for instance, a mystery solved before the story formally ends—higher-order regions may update the event representation at that point, and this updated model then cascades down to shape processing in lower-level regions. Finally, we note that the widespread stabilization of neural patterns after boundaries may signal the establishment of a new event model.

Excerpt from Introduction:

“More recently, multivariate approaches have provided insights into neural representations during event segmentation. One prominent approach uses hidden Markov models (HMMs) to detect moments when the brain switches from one stable activity pattern to another (Baldassano et al., 2017) during movie viewing; these periods of relative stability were referred to as "neural states" to distinguish them from subjectively perceived events. Sensory regions like visual and auditory cortex showed faster transitions between neural states. Multi-modal regions like the posterior medial cortex, angular gyrus, and intraparietal sulcus showed slower neural state shifts, and these shifts aligned with subjectively reported event boundaries. Geerligs et al. (2021, 2022) employed a different analytical approach called Greedy State Boundary Search (GSBS) to identify neural state boundaries. Their findings echoed the HMM results: short-lived neural states were observed in early sensory areas (visual, auditory, and somatosensory cortex), while longer-lasting states appeared in multi-modal regions, including the angular gyrus, posterior middle/inferior temporal cortex, precuneus, anterior temporal pole, and anterior insula. Particularly prolonged states were found in higher-order regions such as lateral and medial prefrontal cortex.

The previous evidence about evoked responses at event boundaries indicates that these are dynamic phenomena evolving over many seconds, with different brain areas showing different dynamics (Ben-Yakov & Henson, 2018; Burunat et al., 2024; Kurby & Zacks, 2018; Speer et al., 2007; Zacks, 2010). Less is known about the dynamics of pattern shifts at event boundaries (e.g. whether shifts observed in higher-order regions precedes or follow shifts observed in lower-level regions), because the HMM and GSBS analysis methods do not directly provide moment-by-moment measures of pattern shifts. Both the spatial and temporal aspects of evoked responses and pattern shifts at event boundaries have the potential to provide evidence about two potential control processes (error-driven and uncertainty-driven) for event model updating.”

Excerpt from Discussion:

“We first characterized the neural signatures of human event segmentation by examining both univariate activity changes and multivariate pattern changes around subjectively identified event boundaries. Using multivariate pattern dissimilarity, we observed a structured progression of neural reconfiguration surrounding human-identified event boundaries. The largest pattern shifts were observed near event boundaries (~4.5s before) in dorsal attention and parietal regions; these correspond with regions identified by Geerligs et. al as shifting their patterns on a fast to intermediate timescale (2022). We also observed smaller pattern shifts roughly 12 seconds prior to event boundaries in higher-order regions within anterior temporal cortex and prefrontal cortex, and these are slow-changing regions identified by Geerligs et. al (2022). This is puzzling. One prevalent proposal, based on the idea of a cortical hierarchy of increasing temporal receptive windows (TRWs), suggests that higher-order regions should update representations after lower-order regions do (Chang et al., 2021). In this view, areas with shorter TRWs (e.g., word-level processors) pass information upward, where it is integrated into progressively larger narrative units (phrases, sentences, events). This proposal predicts neural shifts in higher-order regions to follow those in lower-order regions. By contrast, our findings indicate the opposite sequence. Our findings suggest that the brain might engage in top-down event representation updating, with changes in coarser-grain representations propagating downward to influence finer-grain representations. (Friston, 2005; Kuperberg, 2021). For example, in a narrative where the main goal is achieved midway—such as a detective solving a mystery before the story formally ends—higher-order regions might update the overarching event representation at that point, and this updated model could then cascade down to reconfigure how lower-level regions process the remaining sensory and contextual details. In the period after a boundary (around +12 seconds), we found widespread stabilization of neural patterns across the brain, suggesting the establishment of a new event model. Future work could focus on understanding the mechanisms behind the temporal progression of neural pattern changes around event boundaries.”

Reviewer #2 (Public review):

Summary:

Tan et al. examined how multivoxel patterns shift in time windows surrounding event boundaries caused by both prediction errors and prediction uncertainty. They observed that some regions of the brain show earlier pattern shifts than others, followed by periods of increased stability. The authors combine their recent computational model to estimate event boundaries that are based on prediction error vs. uncertainty and use this to examine the moment-to-moment dynamics of pattern changes. I believe this is a meaningful contribution that will be of interest to memory, attention, and complex cognition research.

Strengths:

The authors have shown exceptional transparency in terms of sharing their data, code, and stimuli, which is beneficial to the field for future examinations and to the reproduction of findings. The manuscript is well written with clear figures. The study starts from a strong theoretical background to understand how the brain represents events and has used a well-curated set of stimuli. Overall, the authors extend the event segmentation theory beyond prediction error to include prediction uncertainty, which is an important theoretical shift that has implications in episodic memory encoding, the use of semantic and schematic knowledge, and attentional processing.

We thank the reader for their support for our use of open science practices, and for their appreciation of the importance of incorporating prediction uncertainty into models of event comprehension.

Weaknesses:

The data presented is limited to the cortex, and subcortical contributions would be interesting to explore. Further, the temporal window around event boundaries of 20 seconds is approximately the length of the average event (21.4 seconds), and many of the observed pattern effects occur relatively distal from event boundaries themselves, which makes the link to the theoretical background challenging. Finally, while multivariate pattern shifts were examined at event boundaries related to either prediction error or prediction uncertainty, there was no exploration of univariate activity differences between these two different types of boundaries, which would be valuable.

The fact that we observed neural pattern shifts well before boundaries was indeed unexpected, and we now offer a more extensive interpretation in the discussion section. Specifically, we added text noting that shifts emerged in higher-order anterior temporal and prefrontal regions roughly 12 seconds before boundaries, whereas shifts occurred in lower-level dorsal attention and parietal regions closer to boundaries. This sequence contrasts with the traditional bottom-up temporal hierarchy view and instead suggests a possible top-down updating mechanism, in which higher-order representations reorganize first and propagate changes to lower-level areas (Friston, 2005; Kuperberg, 2021). (See excerpt for Reviewer 1’s comment #5.)

With respect to univariate activity, we did not find strong differences between error-driven and uncertainty-driven boundaries. This makes the multivariate analyses particularly informative for detecting differences in neural pattern dynamics. To support further exploration, we have also shared the temporal progression of univariate BOLD responses on OpenNeuro (BOLD_coefficients_brain_animation_pe_SEM_bold.html and BOLD_coefficients_brain_animation_uncertainty_SEM_bold.html in the derivatives/figures/brain_maps_and_timecourses/ directory; https://doi.org/10.18112/openneuro.ds005551.v1.0.4) for interested researchers.

Reviewer #3 (Public review):

Summary:

The aim of this study was to investigate the temporal progression of the neural response to event boundaries in relation to uncertainty and error. Specifically, the authors asked (1) how neural activity changes before and after event boundaries, (2) if uncertainty and error both contribute to explaining the occurrence of event boundaries, and (3) if uncertainty and error have unique contributions to explaining the temporal progression of neural activity.

Strengths:

One strength of this paper is that it builds on an already validated computational model. It relies on straightforward and interpretable analysis techniques to answer the main question, with a smart combination of pattern similarity metrics and FIR. This combination of methods may also be an inspiration to other researchers in the field working on similar questions. The paper is well written and easy to follow. The paper convincingly shows that (1) there is a temporal progression of neural activity change before and after an event boundary, and (2) event boundaries are predicted best by the combination of uncertainty and error signals.

We thank the reviewer for their thoughtful and supportive comments, particularly regarding the use of the computational model and the analysis approaches.

Weaknesses:

(1) The current analysis of the neural data does not convincingly show that uncertainty and prediction error both contribute to the neural responses. As both terms are modelled in separate FIR models, it may be that the responses we see for both are mostly driven by shared variance. Given that the correlation between the two is very high (r=0.49), this seems likely. The strong overlap in the neural responses elicited by both, as shown in Figure 6, also suggests that what we see may mainly be shared variance. To improve the interpretability of these effects, I think it is essential to know whether uncertainty and error explain similar or unique parts of the variance. The observation that they have distinct temporal profiles is suggestive of some dissociation,but not as convincing as adding them both to a single model.

We appreciate this point. It is closely related to Reviewer 1's comment 2; please refer to our response above.

(2) The results for uncertainty and error show that uncertainty has strong effects before or at boundary onset, while error is related to more stabilization after boundary onset. This makes me wonder about the temporal contribution of each of these. Could it be the case that increases in uncertainty are early indicators of a boundary, and errors tend to occur later?

We also share the intuition that increases in uncertainty are early indicators of a boundary, and errors tend to occur later. If that is the case, we would expect some lags between prediction uncertainty and prediction error. We examined lagged correlation between prediction uncertainty and prediction error, and the optimal lag is 0 for both uncertainty-driven and error-driven models. This indicates that when prediction uncertainty rises, prediction error also simultaneously rises.

Author response image 1.

(3) Given that there is a 24-second period during which the neural responses are shaped by event boundaries, it would be important to know more about the average distance between boundaries and the variability of this distance. This will help establish whether the FIR model can properly capture a return to baseline.

We have added details about the distribution of event lengths. Specifically, we now report that the mean length of subjectively identified events was 21.4 seconds (median 22.2 s, SD 16.1 s). For model-derived boundaries, the average event lengths were 28.96 seconds for the uncertainty-driven model and 24.7 seconds for the error-driven model.

" For each activity, a separate group of 30 participants had previously segmented each movie to identify fine-grained event boundaries (Bezdek et al., 2022). The mean event length was 21.4 s (median 22.2 s, SD 16.1 s). Mean event lengths for uncertainty-driven model and error-driven model were 28.96s, and 24.7s, respectively (Nguyen et al., 2024)."

(4) Given that there is an early onset and long-lasting response of the brain to these event boundaries, I wonder what causes this. Is it the case that uncertainty or errors already increase at 12 seconds before the boundaries occur? Or if there are other makers in the movie that the brain can use to foreshadow an event boundary? And if uncertainty or errors do increase already 12 seconds before an event boundary, do you see a similar neural response at moments with similar levels of error or uncertainty, which are not followed by a boundary? This would reveal whether the neural activity patterns are specific to event boundaries or whether these are general markers of error and uncertainty.

We appreciate this point; it is similar to reviewer 2’s comment 2. Please see our response to that comment above.

(5) It is known that different brain regions have different delays of their BOLD response. Could these delays contribute to the propagation of the neural activity across different brain areas in this study?

Our analyses use ±20 s FIR windows, and the key effects we report include shifts ~12s before boundaries in higher-order cortex and ~4.5s pre-boundary in dorsal attention/parietal areas. Given the literature above, region-dependent BOLD delays are much smaller (~1–2s) than the temporal structure we observe (Taylor et al., 2018), making it unlikely that HRF lag alone explains our multi-second, region-specific progression.

(6) In the FIR plots, timepoints -12, 0, and 12 are shown. These long intervals preclude an understanding of the full temporal progression of these effects.

For page length purposes, we did not include all timepoints. We uploaded a brain animation of all timepoints and coefficients for each parcel in Openneuro (PATTERN_coefficients_brain_animation_human_fine_pattern.html and PATTERN_coefficients_lines_human_fine.html in the derivatives/figures/brain_maps_and_timecourses/ directory; https://doi.org/10.18112/openneuro.ds005551.v1.0.4) for interested researchers.

References

Taylor, A. J., Kim, J. H., & Ress, D. (2018). Characterization of the hemodynamic response function across the majority of human cerebral cortex. NeuroImage, 173, 322–331. https://doi.org/10.1016/j.neuroimage.2018.02.061

This section helped me better understand what the Reddit API actually is and how PRAW works behind the scenes. I didn’t really think about the fact that it’s just sending requests to Reddit and getting specific data back based on rules. The warning about the documentation being hard to read feels very accurate, because most official docs are kind of confusing for beginners. It was also interesting to realize that Reddit collects way more data than what the API lets us see.

I found it interesting that APIs create a filtered version of reality for researchers and developers. When we analyze Reddit data through the API, it’s easy to forget that we are only seeing what the platform allows us to see, not the full picture of user behavior. This makes me wonder how data mining conclusions might change if hidden data—like deleted interactions or internal metrics—were included.

Kahle’s main argument is that universal access to knowledge is not just an ideal, it’s something we already have the tools, money, and systems to achieve if we choose to act on it.

Kahle’s main argument is that universal access to knowledge is not just an ideal, it’s something we already have the tools, money, and systems to achieve if we choose to act on it.

The author emphasizes that digital libraries aren’t just about easy access, they change how research can be done. It’s a shift from visiting a library to interacting with the material in new computational ways.

The consistency is also impressive given the fact that when the causal arrow is reversed and one considers research that investigates the influence of repressive behavior on dissent (exploring one of the core aspects of collective action theory regarding the importance of costs), the results are highly inconsistent.

This is the part that confuses researchers. We know that dissent causes repression, but we don't know if repression actually stops dissent. Sometimes people get scared and go home (negative impact), but other times it just makes them angrier and leads to more protests (positive impact). It’s a puzzle because the government keeps using repression even though they aren't totally sure it works.

(I remember we only need to do one post, I'm doing an additional one because I had thoughts I wanted to express) It seems to me that the early focuses on truth, impartiality, purity, etc. especially as they relate to the history of a nation are indicative of a sort of imperialist, or just broadly nationalist approach to record keeping. The concept of a pure truth that is muddied by human inadequacies seems tied to other scientific movements of the time like eugenics. It feels like a weird comparison to make, but you see the common thread of logic drawn from evolutionary theory and various industrial philosophies: Humans are flawed, thus we must erase the fallible parts of humanity so that there is only the most rational and advantageous parts left. It's interesting to see how much archival theory was dominated by a similar approach until the material impracticality forced a change in perspective.

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

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Reply to the reviewers

We sincerely appreciate the feedback, attention to detail and timeliness of the referees for our manuscript. Below, we provide a point-by-point response to all comments from the referees, detailing the changes we have already made, and those that are in progress. Referee's comments will appear in bolded text, while our responses will be unbolded. Any text quoted directly from the manuscript will be italicised and contained within "quotation marks". Additionally, we have grouped all comments into four categories (structural changes, minor text changes, experimental changes, figure changes), comments are numbered 1-n in each of these categories. Please note: this response to reviewer's comments included some images that cannot be embedded in this text-only section.

1. General Statements

We appreciate the overall highly positive and enthusiastic comments from all reviewers, who clearly appreciated the technical difficulty of this study, and noted amongst other things that this study represents" a major contribution to the future advancement of oocyst-sporozoite biology" and the development of the segmentation score for oocysts as a "major advance[ment]". We apologise for the omission of line numbers on the document sent to reviewers, we removed these for the bioRxiv submission without considering that this PDF would be transferred across to Review Commons.

We have responded to all reviewers comments through a variety of text changes, experimental inclusions, or direct query response. Significant changes to the manuscript since initial submission are as follows:

1. Refinement of rhoptry biogenesis model: Reviewers requested more detail around the content of the AORs, which we had previously suggested were a vehicle for rhoptry biogenesis as we saw they carried the rhoptry neck protein RON4. To address this, we first attempted to address this using antibodies against rhoptry bulb proteins but were unsuccessful. We then developed a * berghei* line where there rhoptry bulb protein RhopH3 was GFP-tagged. Using this parasite line, we observed that the earliest rhoptry-like structure, which we had previously interpreted as an AOR contained RhopH3. By contrast, RhopH3 was absent from AORs. Reflecting these observations we have renamed this initial structure the 'pre-rhoptry' and suggested a model for rhoptry biogenesis where rhoptry neck cargo are trafficked via the AOR but rhoptry bulb cargo are trafficked by small vesicles that move along the rootlet fibre (previously observed by EM).
2. Measurement of rhoptry neck vs bulb: While not directly suggested by the reviewers, we have also included an analysis that estimates the proportion of the sporozoite rhoptry that represents the rhoptry neck. By contrast to merozoites, which we show are overwhelmingly represented by the rhoptry bulb, the vast majority of the sporozoite rhoptry represents the rhoptry neck.
3. Measurement of subpellicular microtubules: One reviewer asked if we could measure the length of subpellicular microtubules where we had previously observed that they were longer on one side of the sporozoite than the other. We have now provided absolute and relative (% sporozoite length) length measurements for these subpellicular microtubules and also calculated the proportion of the microtubule that is polyglutamylated.
4. More detailed analysis of RON11cKD rhoptries: Multiple comments suggested a more detailed analysis of the rhoptries that were formed/not formed in RON11cKD We have included an updated analysis that shows the relative position of these rhoptries in sporozoites.

2. Point-by-point description of the revisions

Reviewer #1

Minor text changes (Reviewer #1)

1. __Text on page 12 could be condensed to highlight the new data of ron4 staining of the AOR. __

We agree with the reviewer that it is a reasonable suggestion. After obtaining additional data on the contents of the AOR (as described in General Statements #1), this section has been significantly rewritten to highlight these findings. 2.

__Add reference on page 3 after 'disrupted parasites' __

This sentence has been rewritten slightly with some references included and now reads: "Most data on these processes comes from electron microscopy studies 6-8, with relatively few functional reports on gene deleted or disrupted parasites9-11. 3.

__Change 'the basal complex at the leading edge' - this seems counterintuitive __

This change has been made. 4.

__Change 'mechanisms underlying SG are poorly' - what mechanisms? of invasion or infection? __

This was supposed to read "SG invasion" and has now been fixed. 5.

__On page 4: 'handful of proteins' __

This error has been corrected. 6.

__What are the 'three microtubule spindle structures'? __

The three microtubule spindle structures: hemispindle, mitotic spindle, and interpolar spindle are now listed explicitly in the text. 7.

__On page 5: 'little is known' - please describe what is known, also in other stages. At the end of the paper I would like to know what is the key difference to rhoptry function in other stages? __

The following sentence already detailed that we had recently used U-ExM to visualise rhoptry biogenesis in blood-stage parasites, but the following two sentences have been added to provide extra detail on these findings: "In that study, we defined the timing of rhoptry biogenesis showing that it begun prior to cytokinesis and completed approximate coincident with the final round of mitosis. Additionally, we observed that rhoptry duplication and inheritance was coupled with centriolar plaque duplication and nuclear fission." 8.

__change 'rhoptries golgi-derived, made de novo' __

This has been fixed. 9.

__change 'new understand to' __

This change has been made 10.

__'rhoptry malformations' seem to be similar in sporozoites and merozoites. Is that surprising/new? __

We assume this is in reference to mention of "rhoptry malformations" in the abstract. In the RON11 merozoite study (PMID:39292724) the authors noted no gross rhoptry malformations, only that one was not formed/missing. The abstract sentence has been changed to the following to better reflect this nuance: "*We show that stage-specific disruption of RON11 leads to a formation of sporozoites that only contain half the number of rhoptries of controls like in merozoites, however unlike in merozoites the majority of rhoptries appear grossly malformed."

* 11.

__What is known about crossing the basal lamina. Where rhoptries thought to be involved in this process? Or is it proteins on the surface or in other secretory organelles? __

We are unaware of any studies that specifically look at sporozoites crossing the SG basal lamina. A review, although now ~15 years old stated that "No information is available as to how the sporozoites traverse the basal lamina" (PMID:19608457) and we don't know any more information since then. To try and better define our understanding of rhoptry secretion during SG invasion, we have added the following sentence:

"It is currently unclear precisely when during these steps of SG invasion rhoptry proteins are required, but rhoptry secretion is thought to begin before in the haemolymph before SG invasion16." 12.

__On page change/specify: 'wide range of parasite structures' __

The structures observed have been listed: centriolar plaque, rhoptry, apical polar rings, rootlet fibre, basal complex, apicoplast. 13.

__On page 7: is Airyscan2 a particular method or a specific microscope? __

Airyscan2 is a detector setup on Zeiss LSM microscopes, this was already detailed in the materials and methods sections, but figure legends have been clarified to read: "...imaged by an LSM900 microscopy with an Airyscan2 detector". 14.

__how large is RON11? __

RON11 is 112 kDa in * berghei*, as noted in the text. 15.

__There is no causal link between ookinete invasion and oocyst developmental asynchrony __

We have deleted the sentence that implied that ookinete invasion was responsible for oocyst asynchrony. This section now simply states that "Development of each oocyst within a midgut is asynchronous..." 16.

__First sentence of page 24 appears to contradict what is written in results____ I don't understand the first two sentences in the paragraph titled Comparison between Plasmodium spp __

This sentence was worded confusingly, making it appear contradictory when that was not the intention. The sentence has been changed to more clearly support what is written in the discussion and now reads: "Our extensive analysis only found one additional ultrastructural difference between Plasmodium spp."

__On page 25 or before the vast number of electron microscopy studies should be discussed and compared with the authors new data. __

It is not entirely clear which new data should be specifically discussed based on this comment. However, we have added a new paragraph that broadly compares MoTissU-ExM and our findings with other imaging methods previously used on mosquito-stage malaria parasites:

"*Comparison of MoTissU-ExM and other imaging modalities

Prior to the development of MoTissU-ExM, imaging of mosquito-stage malaria parasites in situ had been performed using electron microscopy7,8,11,28, conventional immunofluorescence assays (IFA)10, and live-cell microscopy25. MoTissU-ExM offers significant advantages over electron microscopy techniques, especially volume electron microscopy, in terms of accessibility, throughput, and detection of multiple targets. While we have benchmarked many of our observations against previous electron microscopy studies, the intracellular detail that can be observed by MoTissU-ExM is not as clear as electron microscopy. For example, previous electron microscopy studies have observed Golgi-derived vesicles trafficking along the rootlet fibre8 and distinguished the apical polar rings44; both of which we could not observe using MoTissU-ExM. Compared to conventional IFA, MoTissU-ExM dramatically improves the number and detail of parasite structures/organelles that can be visualised while maintaining the flexibility of target detection. By contrast, it can be difficult or impossible to reliably quantify fluorescence intensity in samples prepared by expansion microscopy, something that is routine for conventional IFA. For studying temporally complex processes, live-cell microscopy is the 'gold-standard' and there are some processes that fundamentally cannot be studied or observed in fixed cells. We attempt to increase the utility of MoTissU-ExM in discerning temporal relationships through the development of the segmentation score but note that this cannot be applied to the majority of oocyst development. Collectively, MoTissU-ExM offers some benefits over these previously applied techniques but does not replace them and instead serves as a novel and complementary tool in studying the cell biology of mosquito-stage malaria parasites.**"

*

__First sentence on page 27: there are many studies on parasite proteins involved in salivary gland invasion that could be mentioned/discussed. __

The sentence in question is "To the best of our knowledge, the ability of sporozoites to cross the basal lamina and accumulate in the SG intercellular space has never previously been reported."

This sentence has now been changed to read as follows: "While numerous studies have characterized proteins whose disruption inhibited SG invasion9,10,15,59-63, to the best of our knowledge the ability of sporozoites to cross the basal lamina and accumulate in the SG intercellular space has never previously been reported ."

__On page 10 I suggest to qualify the statement 'oocyst development has typcially been inferred by'. There seem a few studies that show that size doesn't reflect maturation. __

In our opinion, this statement is already qualified in the following sentence which reads: "Recent studies have shown that while oocysts increase in size initially, their size eventually plateaus (11 days pot infection (dpi) in P. falciparum4)."

__On page 16 the authors state that different rhoptries might have different function. This is an interesting hypothesis/result that could be mentioned in the abstract. __

The abstract already contains the following statement: "...and provide the first evidence that rhoptry pairs are specialised for different invasion events." We see this as an equivalent statement.

Experimental changes (Reviewer #1)

1. On page 19: do the parasites with the RON11 knockout only have the cytoplasmic or only the apical rhoptries?

The answer to this is not completely clear. We have added the following data to Figures 6 and 8 where we quantify the proportion of rhoptries that are either apical or cytoplasmic: In both wildtype parasites and RON11ctrl parasites, oocyst spz rhoptries are roughly 50:50 apical:cytoplasmic (with a small but consistent majority apical), while almost all rhoptries are found at the apical end (>90%) in SG spz. Presumably, after the initial apical rhoptries are 'used up' during SG invasion, the rhoptries that were previously cytoplasmic take their place. In RON11cKD the ratio of apical:cytoplasmic rhoptries is fairly similar to control oocyst spz. In RON11cKD SG spz, the proportion of cytoplasmic rhoptries decreases but not to the same extent as in wildtype or RON11Ctrl. From this, we infer that the two rhoptries that are lost/not made in RON11cKD sporozoites are likely a combination of both the apical and cytoplasmic rhoptries we find in control sporozoites.

__in panel G: Are the dense granules not micronemes? What are the dark lines? Rhoptries?? __

We have labelled all of Figure 1 more clearly to point out that the 'dark lines' are indeed rhoptries. Additionally, we have renamed the 'protein-dense granules' to 'protein-rich granules', as it seems we are suggesting that these structures are dense granules the secretory organelle. At this stage we simply do not know what all of these granules are. The observation that some but not all of these granules contain CSP (Supplementary Figure 2) suggests that they may represent heterogenous structures. It is indeed possible that some are micronemes, however, we think it is unlikely that they are all micronemes for a number of reasons: (1) micronemes are not nearly this protein dense in other Plasmodium lifecycle stages, (2) some of them carry CSP which has not been demonstrated to be micronemal, (3) very few of these granules are present in SG sporozoites, which would be unexpected because microneme secretion is required for hepatocyte invasion.

__Figure 2 seems to add little extra compared to the following figures and could in my view go to the supplement. __

We agree that Figure 2b adds little and so have moved that to Supplementary Figure 2, but think that the relative ease at which it can be distinguished if sporozoites are in the secretory cavity or SG epithelial cell is a key observation because of the difficulty in doing this by conventional IFA.

__On page 8 the authors mention a second layer of CSP but do not further investigate it. It is likely hard to investigate this further but to just let it stand as it is seems unsatisfactory, considering that CSP is the malaria vaccine. What happens if you add anti-CSP antibodies? I would suggest to shorten the opening paragraphs of this paper and to focus on the rhoptries. This could be done be toning down the text on all aspects that are not rhoptries and point to the open question some of the observations such as the CSP layers raise for future studies. __

When writing the manuscript, we were unsure whether to include this data at all as it is a purely incidental finding. We had no intention of investigating CSP specifically, but anti-CSP antibodies were included in most of the salivary gland imaging experiments so we could more easily find sporozoites. Given the tremendous importance of CSP to the field, we figured that these observations were potentially important enough that they should be reported in the literature even though they are not something we have the intention or resources to investigate subsequently. Additionally, after consultation with other microscopists we think there is a reasonable chance that this double-layer effect could be a product of chemical fixation. To account for this, we have qualified the paragraph on CSP with this sentence:

"We cannot determine if there is any functional significance of this second CSP layer and considering that it has not been observed previously it may well represent an artefact of chemical (paraformaldehyde) fixation."

__Maybe include more detail of the differences between species on rhoptry structure into Figure 4. I would encourage to move the Data on rhoptries in Figure S6 to the main text ie to Figure 4. __

We have moved the images of developing rhoptries in * falciparum *(previously Figure S6a and b) into figure 4, which now looks as follows:

Figure S8 (previously S6c) now consists only of the MG spz rhoptry quantification

Manuscript structural changes (Reviewer #1)

1. Abstract: don't focus on technique but on the questions you tried to answer (ie rewrite or delete the 3rd and 4th sentence)

2. 'range of cell biology processes' - I understand the paper that the key discovery concerns rhoptry biogenesis and function, so focus on that, all other aspects appear rather peripheral.

3. 'Much of this study focuses on the secretory organelles': I would suggest to rewrite the intro to focus solely on those, which yield interesting findings.

4. Page 11: I am tempted to suggest the authors start their study with Figure 3 and add panel A from Figure 2 to it. This leads directly to their nice work on rhoptries. Other features reported in Figures 1 and 2 are comparatively less exciting and could be moved to the supplement or reported in a separate study.____ Page 23: I suggest to delete the first sentence and focus on the functional aspects and the discoveries.

5. __Maybe add a conclusion section rather than a future application section, which reads as if you want to promoted the use of ultrastructure expansion microscopy. To my taste the technological advance is a bit overplayed considering the many applications of this techniques over the last years, especially in parasitology, where it seems widely used. In any case, please delete 'extraordinarily' __