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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.

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Referee #3

Evidence, reproducibility and clarity

In this paper, the authors report an interesting phenotype of the LRRK2 G2019S mutation on iron homeostasis in RAW264.7 macrophages. The phenotype is well characterised through proteomic and western blot approaches investigating transferrin and ferritin trafficking. The study is well conducted and data of high quality. The authors also appear to have discovered a cellular context where Rab8 is phosphorylated independently of LRRK2. This is a major finding which can potentially have an important impact in the LRRK2 field. 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. 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.

Significance

Major comments

In Figure 1:

• There is lower LRRK2 expression in LRRK2 G2019S cells, have the authors checked Rab phosphorylation to validate the mutation?
• The authors should specify if their cells are heterozygous or homozygous since they are discussing a dominant interfering mutant.
• The transferrin phenotype validated through proteomics and western blot is solid.
• 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.
• 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.

In Figure 2:

• If the effect is armadillo-dependent, where does LRRK2 G2019S is implicated since there is no kinase domain in these cells?
• The authors do not show any controls (PCR, sequencing) confirming knockout or truncation.
• The data is interesting and the image quality with the insets is very high.

In Figure 3:

• 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.
• 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.
• 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.

In Figure 4:

• 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.
• The vinculin bands in figure 4A are misaligned with the rest of the bands.
• The authors do not have any controls to validate the pRab8 staining in IF. This is an important caveat and needs to be addressed.
• 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. 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 findings https://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

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Referee #2

Evidence, reproducibility and clarity

In this manuscript the authors describe an interesting connection between the Parkinson's kinase LRRK2 and iron trafficking in RAW macrophages. Expression of the LRRK2 G2029S mutation affects the abundance of ferritin heavy and light chains and therefore the uptake and storage of iron. Interestingly, the loss of the kinase domain still had a strong phenotype, suggesting that this is independent of the kinase function.

The paper is well written and excellently cited. The data is convincing and of good quality.

I have only one request and else very minor comments:

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.

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. I would normalize to the average of the control, which will provide an error for the control.

The raw data needs to be submitted to PRIDE or similar. This has not happened yet.

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?

Significance

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.

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Referee #1

Evidence, reproducibility and clarity

Goldman et al describe some novel findings with respect to LRRK and iron handling in a series of RAW macrophage cell lines. This cell background is chosen for its recognized high levels of endogenous LRRK2 protein expression, its somewhat broad use in the field, and the investigators add its relevance due to phagocytosis of red blood cells, thus requiring iron robust metabolic processes. Proteomic analyses of WT and G2019S RAW cells revealed multiple iron-related proteins affected by LRRK2 mutation. A deeper candidate-based analysis revealed complex changes in ferritin heavy and light chain and changes in ferric and ferrous iron. Notably, reliable changes in the levels and/or solubility of NCOA4 result from this pathogenic LRRK2 mutation. Unexpectedly, however, these changes were not sensitive to LRRK2 kinase inhibitor treatment. The investigators suggest a dominant effect rather than loss-of-function as subsequent experiments revealed that these effects could be replicated with a LRRK2 variant lacking the kinase domain (LRRK2-ARM) and were not replicated by LRRK2 KO. The data are internally consistent throughout and could certainly shed new important light onto unique and unexpected effects of this LRRK2 mutation.

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. 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 specie 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.

• Need to make clear in the results whether the G2019S CRISPR mutant is heterozygous or homozygous (presumably homozygous, same for ARM)
• 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.
• 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).
• 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.
• 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.
• 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.
• The legend for 2F is awkward (BSADQRED)
• Why are WT cells not included in Fig 2G?
• 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.
• Have the investigators looked for aberrant Rab trafficking to lysosomes in the LRRK2-arm cells? Is pRab8 mislocalized compared to WT? Other pRabs?
• 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.
• 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.

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.

Significance

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.

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Reply to the reviewers

We would like to thank all the reviewers for their comments and suggestions.

Please find below our point-by-point response to the Reviewers' comments, which details the corrections already made and outlines the planned revisions, experiments, and analyses.

Reviewer 1

Major comments:

• Reviewer 1 commented that the 'manuscript would greatly benefit from having someone spend time on the figures, and associated text, to ensure they are fully comprehensible'. We agree wholeheartedly with the reviewer and apologise. We have now revisited the text, figures, and associated figure legends to ensure that they are more easily accessible and fully comprehensible to readers from across disciplines. This includes adding labels to point out specific anatomical features on images, and ensuring figures and text align. Further specific examples are included in the points below.
• In response to concerns raised by Reviewer 1 relating to: Figure 1 and the lack of figure citations; 'the persistence of mCherry in the H2B Fucci'; how mCherry seems to persist longer in H1 (compare Figs 1D and 1G)':
• We apologise for the lack of figure citations in the text. We have now reworked the figures relating to the constructs (original Figures 1 and S1) and have made these Figures 1, 2 and S1 in our updated version.
• Figure 1 is now an introductory background figure which illustrates the differences between Fucci(SA) and Fucci(CA) reporters, with additional details provided in the associated legend, and call outs to the figure starting in the introduction.
• Regarding 'the persistence of mCherry in the H2B Fucci', what we are trying to articulate is that the mCherry degradation that we observed in the Fucci(2A) expressing DF1 cells extended beyond the end of S phase and into G2/M, compared with what would be expected (Revised Figure 2H, arrows).
• We have now replaced these montages with a more representative example. Additionally, the new images (Figures 2C and 2G) are synchronised (both starting at G2/M), restricted to a single cell cycle, are larger in size, and have the cell cycle stage labelled. We believe these changes will aid interpretation.
• Specifically relating to the lack of labelling in Figure 3A, we agree that this figure was not labelled sufficiently, and neither was there enough detail included in the text or figure legend for readers to follow easily and make their own conclusions. We have now added additional labels to this figure, broken the figure down into more panels (Figures 4A-4D in revised manuscript), and included more detailed descriptions in the associated figure legend and text.
• We thank the reviewer for making the important point that it is 'hard to know where the biosensor is reporting patterns that are already well established (eg neural tube), and where the biosensor is reporting patterns that are novel - and if so, what these patterns are' which was made more challenging by insufficient references to previous studies.
• Firstly, as for the point above, we have now added labels to many of the panels (Figure 4 in revision), including highlighting features such as the non-proliferative dermal condensates and demarcating the proliferative retinal pigmented epithelium (Figures 4F and 4G in revision). Secondly, we have also now included additional references in the text, specifically relating to the neural tube, digits, and forming feathers, where our proliferation profiles are consistent with previous literature.
• With regards to the Reviewer's comment regarding the difficulty in drawing conclusions 'about cell cycle in different tissue layers without sectioning' in original Figure 3B we will include more sections of FuChi embryos which include structures such as mesenchymal condensates.
• To make our data on cell cycle stages as 'cells egress from the primitive streak, to form prechordal plate' clearer we have added additional labels to the figures (Figures 4B and 6E in revised manuscript). We will complement this adding sections of gastrulating FuChi embryos to further demonstrate the cell cycle status of cells that form the pre-chordal plates.

Minor comments

• We have added additional references relating to the data in original Figure 3 (now Figure 4 see above), and any new descriptions of known proliferation profiles that we include will have appropriate citations.
• In this current revision we have addressed figure call out issues, and added labels to enhance readability, clarity and data interpretation. Reviewer 2

Major comments

• Reviewer 2 rightly pointed out that the 'description of the bicistronic tandem-Fucci(CA) system in paragraph 6 is not consistent with what is described in the original bibliographic reference indicated by the authors'. We have now added additional text to properly explain the CDT1 probe dynamics, as per the cited manuscript, and also referenced the schematics to help readers.
• To address whether the FuChi model can be accurately 'used to study embryogenesis' and following up on the suggestion to 'indicate if the size of the embryos is comparable to the wildtype' we have now included size comparisons of FuChi and wild-type/non-transgenic embryos at mid (E9) and late (E18) gestational stages demonstrating that there is no significant difference between genotypes during embryogenesis (Figure 3D in revised manuscript). For all earlier stages, we did not see any developmental or size differences. We believe if there were any differences, these would be reflected in size at the mid and late gestational stages we analysed.
• Reviewer 2 made very valuable observations and suggestions regarding our data and interpretation of somitogenesis, specifically in response to our sentence saying that "the mesenchyme, which is predominantly in G1 as they undergo condensation". Furthermore, they noted that Supplementary Video 4 "shows distinct green fluorescence (S) in the presomitic mesoderm for the first hour or so, only then turning to magenta (G1)". We were asked to review the sentence/video to clarify if this is a significant finding or if this is not representative of their observations.
• We thank the reviewer for this suggestion. From looking again at our timelapse movies, and also analysing additional static images, we agree that presomitic mesoderm (PSM) does appear to be green (S phase), which then may transition to G1 as the somites form. To address this, we plan to quantify cell cycle status in the PSM on embryos to see if this is a significant finding.
• We hope this quantification of the PSM may also enable us to include discussion on how our findings relate to the Cell Cycle model for somitogenesis proposed in the Collier et al, 2000 paper suggested by the Reviewer.
• We agree with the Reviewer that "the fluorescence profiles in original Figure 4C do not seem similar regarding the Myc-tag epitope" and believe this difference is likely just a reflection of the part of the image we used. We will include a more representative image once we have repeated the staining.
• Reviewer 2 has asked for quantitative support for our fluorescence-based interpretations. We thank the reviewer for this suggestion and are now planning to perform quantitative analyses of different tissues (similar to our quantification in germ cells) and in embryos to support our observations. These will include the PSM (see above), neural tube, intestine, and early embryos (also see Reviewer 3 response for blastoderm quantification).
• Since our original submission, we have further refined our in situ hybridisation protocol on FuChi embryos (Figures 5A & B in revision), finding that strong reporter expression is maintained for all the fluorescent proteins of the H1-Fucci(CA)2 reporter. Therefore, the "notably fainter" appearance of the hGMNN-mVenus in Figure 4A from the first version of the paper was likely a result of the experimental protocol not being 100% optimal.
• *

Minor comments

• We have reordered the paragraphs relating to the different Fucci versions in the introduction as per the suggestions by the reviewer for better clarity.
• To address the issues with Fucci system nomenclatures which made reading difficult, we have now added a background figure (new Figure 1 in revised draft) which is cited in the introduction, made sure constructs are introduced appropriately, and ensured we are consistent with our nomenclature.
• Supplementary Figure lettering corrected.
• All figure panels are now mentioned in the main text, and the incorrect call outs noted by the Reviewer have been corrected
• Removed period and included clarifying statement in the figure legend relating to the comment regarding the extraembryonic region in Figure 5 (original) / Figure 6 (revised).
• Other issues raised relating to reference duplication and missing words have been resolved.
• We have corrected the legend of Figure 1 of the original paper, see related Reviewer 1 response provided above.

Reviewer #3

Minor comments

• We have corrected all the figure call outs (see responses to similar comments by Reviewers 1 and 2) to ensure that all data presented is accurately reported.
• We would like to thank the reviewer for suggesting modifications to the cell cycle montages (original figures 1D, 1G and 2F). We agree it would help the reader to enlarge the image, and therefore reduced the montage to include just one cell cycle, and have also included annotations of cell cycle stages in Figures 2C and 2G of the revised manuscript. We have also added some labels to Figure 3E (original figure 2F) and enlarged this.
• In response to Reviewer 3's comment regarding fluorescent intensity. We quantified fluorescence levels in multiple individual DF1 cells expressing either the H1.0-Fucci(CA)2 or H2B-Fucci(SA)2 reporters, and this is shown as the fluorescent index in Figures 2D, 2E, 2H and 2I of the revised manuscript, where reporter levels were measured across time. In terms of overall mean intensity levels of the reporters, we found the reporters to be comparable in brightness and have similar mean intensity levels across the cell populations in the flow cytometry data (Figures 2F and 2J).
• To enhance speedy interpretation, we will also process our supplementary videos to include annotations and arrows to highlight key cells and events (e.g. a cell undergoing mitosis).
• As recommended by Reviewer 3, we have now quantified cell cycle status in blastoderm cells, confirming that a high proportion are in the G2/M phase. We will include these data in the final revision, which will complement our planned quantification of cell cycle status in other tissues (see response to Reviewer 2).
• For our final revision, we will include higher magnification/zoomed in images of selected regions of the somites, neural tube (lumen) and retina (epithelium). Revisiting our images of the neural tube showed that dividing cells lumen did so in the perpendicular plane and we will include these images in our revision to provide further evidence of the fidelity of the FuChi reporter. We thank the reviewer for this excellent idea to show the efficacy of our system.
• To address the levels of proliferation in somites, we plan to generate a cropped video with a fixed ROI to enable proliferation in individual cells of the forming somites to be more readily visualised. This will be further complemented by the quantification of cell cycle status in forming somites (see responses to other reviewers).
• We have added lines to the discussion regarding the use of our reporter in other conventional model systems.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by Sudderick and colleagues describes the development and characterisation of a new generation of cell cycle reporter that can distinguish between cells in G1, S, G2 and M phases. Furthermore, the authors have developed a transgenic chicken line incorporating this reporter and demonstrated faithful discrimination of cell cycle stages in the in vivo context of developing transgenic embryos. Of note is the addition of epitope tags, which facilitate discrimination of cell cycle stages in tissue fixed using various techniques. This is a very important paper for the following reasons:

• The authors have achieved faithful discrimination of all four cell cycle stages, which is a major advance in itself.
• This generation of the FuChi transgenic chick is of enormous importance. This will facilitate accurate in vivo studies in a broad range of fixed and living tissue types and is a major milestone in the further establishment of the chick as a transgenic model system.

Th characterisation of the cell cycle reporter as presented is robust and convincing. The authors further demonstrate the potential utility of the FuChi chickens through their observation of partial cell cycle synchrony during onset of development. I therefore only have minor suggestions that may facilitate easier interpretation of their data.

Results 2

• I can't see any mention of Figures 1C and D. Presumably the authors have carried out fluorescence intensity measurements using the two cell cycle reporters here, but this is not mentioned in the main text.
• Figure 1D&G: I find these difficult to follow given the small size of the cells as presented. The authors may consider enlarging these and clearly annotating for cell cycle stage. They may find it helpful to focus on a single cell cycle, although I appreciate that displaying two cell cycles strengthens the claim of efficacy of the newly developed sensor. The supplementary videos associated with these figure panels are excellent as they display several cells with faithful reporter activity, but again, the authors may wish to annotate a few of these cells to enhance speedy interpretation. I have similar comments for Figure 2F and the associated movie.

Results 4

• The authors state that a large proportion of blastoderm cells were in G2/M. They may wish to formally quantify this, perhaps by performing simple cell counts in designated regions of interest. A similar quantification for gastrulating embryos would also be helpful.
• It would be helpful to see zoomed in images of selected regions of the somites, neural tube and retina displayed in Figure 3B. This would be particularly appropriate in the context of the neural tube and retina (which are not discussed in the main text) as the positioning of the nucleus is defined by the stage of the cell cycle and should therefore serve to highlight the efficacy of the reporter.
• Video 4 beautifully demonstrates the high levels of proliferation in somites, but again, it would be useful to have a zoomed in view. I appreciate the difficulty involved in doing this, given the movement of the embryo, but perhaps the authors could focus on a fixed ROI or present a separate movie of a few cells undergoing a full cell cycle.

Discussion

• The authors could perhaps expand on their discussion about potential utility in other conventional model systems (e.g. mouse, fish, etc).

Significance

General assessment: A timely piece of work that introduces a faithful cell cycle reporter that will be of broad interest.

Advance: The ability to discriminate between all four stages of the cell cycle is a clear advance here.

Audience: Broad interest, including those studying cell cycle and embryonic development in several tissue contexts.

Expertise: Chick embryology, in vivo live imaging, neurogenesis, cellular developmental biology

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Referee #2

Evidence, reproducibility and clarity

Summary:

This work presents a novel transgenic chicken model with fluorescent reporters that allow in vivo monitoring of the four phases of the cell cycle. To achieve this, the authors clearly identify the limitations of previous Fucci systems and developed an optimised reporter construct that overcomes the major technical challenges identified. Addition of epitope tags to cell cycle stage-specific markers further enables antibody detection in fixed tissues. Proof of concept is provided by live imaging of chick embryos in early developmental stages, evidencing dynamic cell cycle states in tissues and migrating cells.

Major comments:

1. Introduction: Description of the bicistronic tandem-Fucci(CA) system in paragraph 6 is not consistent with what is described in the original bibliographic reference indicated by the authors. Namely: "...accumulation of the CTD1 probe..." should be expected in the G1-S transition (not S-G2) and the yellow reporter should be expected in G2 and M phases (not S and G2, as described). Please review this portion of the text.
2. The authors state that "Of note, hatched FuChi chicks are initially smaller than wild type counterparts but grow at comparative rates and are fertile". If the model is to be used to study embryogenesis, it would be useful to indicate if the size of the embryos is comparable to the wildtype, at least for the major developmental stages mentioned in the manuscript.
3. When referring to somitogenesis, the authors state "...the mesenchyme, which is predominantly in G1 as they undergo condensation". Suppl Video 4, however, shows distinct green fluorescence (S) in the presomitic mesoderm for the first hour or so, only then turning to magenta (G1). The authors should review the sentence/video to clarify if this is a significant finding or if this is not representative of their observations.
4. (Optional) It would be interesting to describe if the authors' observations of cell cycle dynamics in the presomitic mesoderm support the proposed Cell Cycle model for somitogenesis (Collier et al., J.Theor.Biol.2000).
5. The fluorescence profiles in Figure 4C do not seem similar regarding the Myc-tag epitope (contrarily to what is stated). The authors should rephrase or revisit this image to clarify their findings.
6. Quantitative support for several fluorescence-based interpretations made throughout the manuscript. In some instances, conclusions are drawn from qualitative differences in signal intensity. For example, the statement in Fig. 4A that hGMNN-mVenus appears "notably fainter" than the other reporters. Incorporating simple quantitative analyses would strengthen these claims and ensure that observed differences reflect biological behaviour rather than technical or optical factors.

Minor comments:

1. Organization of the information in the Introduction: Paragraphs 3-5 introduce sequentially improved versions of the Fucci system. Then, paragraph 6 returns to the system described in the 4th paragraph. Authors should consider including paragraph 5 (description of Fucci4 and its limitations) just prior to the description of chickens as valuable developmental models (current paragraph 8) for clarity of the text.
2. Fucci system nomenclature. Many different Fucci systems are mentioned, but nomenclature consistency throughout the manuscript is lacking, which makes reading difficult. For example, the terms "Fucci(SA)2" and "Fucci(CA)2" should be defined in the introduction, as they are employed to describe the construction of the new biosensor in the following sections.
3. Some figure panels are not mentioned in the main text (for ex. Figures 1B and C, Figure 2C)
4. The legend of Figure 1 (D & G) mentions "denoted by *", but the * seems to be missing in the figure.
5. Supplementary Figure 1 has two D panels (and is missing the E).
6. In the main text, where it reads "...Flow cytometry analysis of three independent PGC lines... (Figures 2G & S2E)", S2E should be replaced by S1E.
7. In the Figure 4A legend, hCDT1-mVenus should be corrected to hCDT1-mcherry. Also, it is not clear why the authors state that "hGMNN-mVenus expression is notably fainter compared with hCDT1-mVenus and H1.0-mCerulean expression".
8. In Figure 5E, the optical sections "i" seem to pertain to the extraembryonic tissue/area opaca and not to anterior mesoderm, as stated in the figure legend. Also, there is a period between "prechordal plate" and "and" in the legend's last sentence.
9. Discussion: The last sentence of the third paragraph lacks "to" between "used" and "interrogate".
10. References 10 and 23 are identical.

Referee cross-commenting

I agree with all comments from reviewers 1 and 3

Significance

This is a beautiful paper, describing a long sought-after model system to study cell cycle dynamics in vivo. The methodological details are thorough, and the results obtained are clearly presented, highlighting the utility of the new model in various embryonic stages and tissues/organs.

This work is of pivotal importance to the developmental/stem cell biology community, as well as to the wider community that employs the chicken embryo as a preclinical model to assess therapeutic or teratogenic potential of biologically- or chemically-derived products.

My expertise is in chicken embryo development, namely gastrulation, somitogenesis and limb bud outgrowth.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript reports the development of a novel Fucci (Fluorescent Ubiquitination-based cell cycle indicator) system for analysing cell cycle analysis, including live imaging of cell cycle. The novel biosensor (H1.0-Fucci(CA)2) has been developed for analyses of chick cells and tissues: chick embryos are a valuable developmental model that have (and in the future, will) particularly informed our understanding of early stages of embryogenesis, and of development of numerous tissues, including the neural tube, somites, limb bud. The authors conclude that the novel system has advantages over previous Fucci systems, including faithful labelling of all four cell cycle phases. Importantly, the authors have generated a stable germline of H1.0-Fucci(CA)2 transgenic chicks, enabling, for the first time, the discrimination and tracking of cells in all 4 phases of the cell cycle - i.e. in vivo studies of cell cycle progression in vivo, in intact tissues and organs. Additional epitope tags mean that the biosensor can be detected in fixed tissues, enabling comparison of cell cycle with expression of mRNA and proteins that mediate other aspects of development/label particular cells and tissues. The authors map proliferation dynamics across numerous tissues in the developing chick, at numerous stages of development, and conclude in particular that transition from S phase may be a key morphogenetic event in gastrulation, as mesendoderm cells leave the primitive streak to form embryonic stuctures such as prechordal plate

Major comments:

The novel biosensor looks to be an incredibly useful tool, and the manuscript suggests patterns of cell cycle progression in different tissues, and at different points in time, that look intriguing. But it is sometimes difficult to draw the strong conclusions suggested by the authors because the text and figures are sometimes difficult to follow. The manuscript would greatly benefit from having someone spend time on the figures, and associated text, to ensure they are fully comprehensible.

Specifically:

Conclusion1: That the new FUCCI biosensor is a superior cell cycle probe, better at discriminating all cell cycle phases than previous versions. I was very convinced by the vidoes (video 1 and 2) but had problems with Figure 1. Potentially, this is because I am not an expert in these types of analyses - but it was not helped by the fact that components of the figure were not cited in the text. I was particularly confused by the statement remarking on 'the persistence of mCherry in the H2B Fucci' as mCherry seems to persist longer in H1 (compare Figs 1D and 1G). Please explain, in the Figure legend, why this appears to be the case.

Conclusion 2: that the FuChi chicks are the first viable stably expressing avian cell cycle biosensor model. I agree, and the authors should be congratulated on the development of this important tool.

Conclusion 3: the authors monitor cell cycle progression in chicks, in vivo, looking at stages from blastoderm, through gastrulation, and into organogenesis, and draw various conclusions

For example: Fig 3A and text: 'as gastrulation progresses, the primitive streak an presomitic mesoderm display...., whereas the .... And neural plate contains...'

Figure 3A covers an enormous range of stages and tissues. The figure is barely labelled. The text and figure need to better align, and key features in each figure panel need to be labelled so that the reader can better follow, and draw conclusions.

Fig 3B: Reports expression in numerous tissues. There are some beautiful examples of cells segregating relative to cell cycle - for instance, in the neural tube. But I found it hard to know where the biosensor is reporting patterns that are already well established (eg neural tube), and where the biosensor is reporting patterns that are novel - and if so, what these patterns are. Again, this is not described adequately in the text (for instance, there is no mention of the neural tube). And in some cases, references are provided (allowing comparison with previous studies) - but in other cases, there are no references to previous studies. The reader must be given the opportunity to compare this study with previous studies.

Overall - I can appreciate that there are some fascinating patterns, but it is very difficult to draw the conclusions suggested by the authors. Primarily this is due to poor labelling of figures, and lack of clarity between figures and text, and poor referencing. Additionally, it is not clear that strong conclusions can be drawn about cell cycle in different tissue layers without sectioning some embryos.

Fig 3C: The authors remark 'The results confirm that the ... FuChi embryos recapitulate known cell cycle profiles of those tissues'. See my comments in 3B.

Conclusion 4: Robust stability of biosensor in fixed tissues. I agree, and the authors should be congratulated for having made a construct that can be paired with in situ hybridisation and immunohistochemistry - this is invaluable.

Conclusion 5: The authors investigate the potential of the new system for live imaging, and focus on a couple of novel dynamic examples.

The data indicating that PGCs at initial migratory stages are not undergoing frequent cell division is clear.

However, the data indicating that cell cycle status changes as cells egress form the primitive streak, to form prechordal plate, is not clear. The figures need to be better labelled, and the text needs to be more clear (eg ' and prechordal plate. and anterior mesoderm'..

Minor comments:

• Specific experimental issues that are easily addressable.

I would recommend that the authors section some embryos, to better support key conclusions (eg in figure 3 and 5) - Are prior studies referenced appropriately?

Not always - see comment above (Fig 3) - Are the text and figures clear and accurate?

No - this needs work. Not all figures cited in text, or cited in wrong order; Figures are poorly labelled - making it hard to follow - Do you have suggestions that would help the authors improve the presentation of their data and conclusions?

Label figures more carefully and ensure figures and text align

Referee cross-commenting

I agree with all comments from reviewers 2 and 3

Significance

• Describe the nature and significance of the advance (e.g. conceptual, technical, clinical) for the field.

Technically this is a fantastic resource. As detailed above, the novel biosensor (H1.0-Fucci(CA)2) has been developed for analyses of chick cells and tissues: chick embryos are a valuable developmental model that have (and in the future, will) particularly informed our understanding of early stages of embryogenesis, and of development of numerous tissues, including the neural tube, somites, limb bud. Increasingly, studies show the importance of cell cycle for development, differentiation and morphogenesis - it is a huge breakthrough to be able to perform in vivo studies of cell cycle progression in intact tissues and organs.<br /> - State what audience might be interested in and influenced by the reported findings.

Broad basic research, including developmental biologists, stem cell biologists, modellers. - Define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

Developmental biologist, with expertise in chick

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Reply to the reviewers

Manuscript number: RC-2025-03280

Corresponding author(s): Stephan Gruber

1. General Statements [optional]

First, we would like to thank the editor at Review Commons for the efficient handling of our manuscript. We also apologize for our delayed response.

We are grateful to all three reviewers for their careful evaluation of our work and for their constructive feedback, which will provide a valuable basis for improving the figures and the text, as described below. We expect to be able to complete the revision following the plan described below quickly.

We note that the reviewer reports (Rev. #1 and Rev. #3) made us realize that the manuscript text was misleading on the following point. Although we used the purified ATP hydrolysis–deficient Smc protein for sybody isolation, this does not restrict the selection to a specific conformation. As described in detail in Vazquez-Nunez et al. (Figure 5), this mutant displays the ATP-engaged conformation only in a smaller fraction of complexes (~25% in the presence of ATP and DNA), consistent with prior in vivo observations reported by Diebold-Durand et al. (Figure 5). Rather than limiting the selection to a particular configuration, our aim was to reduce the prevalence of the predominant rod state in order to broaden the range of conformations represented during sybody selection. Consistent with this interpretation, only a small number of isolated sybodies show strong conformation-specific binding in the presence or absence of ATP/DNA, as observed by ELISA (now included in the manuscript). We will revise the manuscript text accordingly to clarify this point.

2. Description of the planned revisions

Insert here a point-by-point reply that explains what revisions, additional experimentations and analyses are planned to address the points raised by the referees.

• *

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

Gosselin et al., develop a method to target protein activity using synthetic single-domain nanobodies (sybodies). They screen a library of sybodies using ribosome/ phage display generated against bacillus Smc-ScpAB complex. Specifically, they use an ATP hydrolysis deficient mutant of SMC so as to identify sybodies that will potentially disrupt Smc-ScpAB activity. They next screen their library in vivo, using growth defects in rich media as a read-out for Smc activity perturbation. They identify 14 sybodies that mirror smc deletion phenotype including defective growth in fast-growth conditions, as well as chromosome segregation defects. The authors use a clever approach by making chimeras between bacillus and S. pnuemoniae Smc to narrow-down to specific regions within the bacillus Smc coiled-coil that are likely targets of the sybodies. Using ATPase assays, they find that the sybodies either impede DNA-stimulated ATP hydrolysis or hyperactivate ATP hydrolysis (even in the absence of DNA). The authors propose that the sybodies may likely be locking Smc-ScpAB in the "closed" or "open" state via interaction with the specific coiled-coil region on Smc. I have a few comments that the authors should consider:

Major comments: 1. Lack of direct in vitro binding measurements: The authors do not provide measurements of sybody affinities, binding/ unbinding kinetics, stoichiometries with respect to Smc-ScpAB. Additionally, do the sybodies preferentially interact with Smc in ATP/ DNA-bound state? And, do the sybodies affect the interaction of ScpAB with SMC? It is understandable that such measurements for 14 sybodies is challenging, and not essential for this study. Nonetheless, it is informative to have biochemical characterization of sybody interaction with the Smc-ScpAB complex for at least 1-2 candidate sybodies described here.

We agree with the reviewer that adding such data would be reassuring and that obtaining solid data using purified components is not easy even for a smaller selection of sybodies. We have data that show direct binding of Smc to sybodies by various methods including ELISA, pull-downs and by biophysical methods (GCI). Initially, we omitted these data from the manuscript as we are convinced that the mapping data obtained with chimeric SMC proteins is more definitive and relevant. During the revision we will incorporate the ELISA data showing direct binding and also indicating a lack of preference for a specific state of Smc.

Many modes of sybody binding to Smc are plausible The authors provide an elaborate discussion of sybodies locking the Smc-ScpAB complex in open/ closed states. However, in the absence of structural support, the mechanistic inferences may need to be tempered. For example, is it also not possible for the sybodies to bind the inner interface of the coiled-coil, resulting in steric hinderance to coiled-coil interactions. It is also possible that sybody interaction disrupts ScpAB interaction (as data ruling this possibility out has not been provided). Thus, other potential mechanisms would be worth considering/ discussing. In this direction, did AlphaFold reveal any potential insights into putative binding locations?

We have attempted to map the binding by structure prediction, however, so far, even the latest versions of AlphaFold are not able to clearly delineate the binding interface. Indeed, many ways of binding are possible, including disruption of ScpAB interaction. However, since the main binding site is located on the SMC coiled coils, the later scenario would likely be an indirect consequence of altered coiled coil configuration, consistent with our current interpretation.

1. Sybody expression in vivo Have the authors estimated sybody expression in vivo? Are they all expressed to similar levels?

We have tagged selected sybodies with gfp and performed live cell imaging. This showed that they are all roughly equally expressed and that they localize as foci in the cell presumably by binding to Smc complexes loaded onto the chromosome at ParB/parS sites. We will include this data in the revised version of the manuscript.

1. Sybodies should phenocopy ATP hydrolysis mutant of Smc The sybodies were screened against an ATP hydrolysis deficient mutant of Smc, with the rationale that these sybodies would interfere this step of the Smc duty cycle. Does the expression of the sybodies in vivo phenocopy the ATP hydrolysis deficient mutant of Smc? Could the authors consider any phenotypic read-outs that can indicate whether the sybody action results in an smc-null effect or specifically an ATP hydrolysis deficient effect?

As eluded to above, we think that our selection gave rise to sybodies that bind various, possibly multiple Smc conformations. Consistent with this idea, the phenotypes are similar to null mutant rather than the ATP-hydrolysis defective EQ mutant, which display even more severe growth phenotypes. We will add the following notes to the text:

“These conditions favour ATP-engaged particles alongside the typically predominant ATP-disengaged rod-shaped state (add Vazquez Nunez et al., 2021).”

“ELISA data confirm that nearly all clones bind Smc-ScpAB; however, their binding shows little or no dependence on the presence of ATP or DNA.”

Minor comments: 1. It was surprising that no sybodies were found that could target both bacillus and spneu Smc. For example, sybodies targeting the head regions of Smc that might work in a more universal manner. Could the authors comment on the coverage of the sybodies across the protein structure?

It is rather common that sybodies (like antibodies and nanobodies) exhibit strong affinity differences between highly conserved proteins (> 90 % identity). The underlying reasons for such strong discrimination are i) location of less conserved residues primarily at the target protein surface and ii) the large interaction interface between sybody and target which offers multiple vulnerabilities for disturbance, in particular through bulky side chains resulting in steric clashes. Another frequently observed phenomenon is sybody binding to a dominant epitope, which also often applies to nanobodies and antibodies. A great example for this are the dominant epitopes on SARS-CoV-2 RBDs.

Growth curves (Fig. S3) show a large jump in recovery in growth under sybody induction conditions. Could the authors address this observation here and in the text?

We suppose that this recovery represents suppressor mutants and/or (more likely) improved growth in the absence of functional Smc during nutrient limitation (see Gruber et al., 2013 and Wang et al., 2013). We will add this statement to the text.

L41- Sentence correction: Loop can be removed. Ah, yes, sorry for this confusing error. Thank you. 4. L525 - bsuSmc 'E' :extra E can be removed. To do. Thank you. 5. References need to be properly formatted. To do. Thank you. 6. The authors should add in figure legend for Fig 1i) details on representation of the purple region, and explain the grey strokes for orientation of the loop. To do. 7. How many cells were analysed in the cell biological assays? Legends should include these information. To Be Included.

Reviewer #1 (Significance (Required)):

Overall, this is an impressive study that uses an elegant strategy to find inhibitors of protein activity in vivo. The manuscript is clearly written and the experiments are logical and well-designed. The findings from the study will be significant to the broad field of genome biology, synthetic biology and also SMC biology. Specifically, the coiled coil domain of SMC proteins have been proposed to be of high functional value. The authors have elegantly identified key coiled-coil regions that may be important for function, and parallelly exhibited potential of the use of synthetic sybody/designed binders for inhibition of protein activity.

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

Review: "Single Domain Antibody Inhibitors Target the Coiled Coil Arms of the Bacillus subtilis SMC complex" by Ophélie Gosselin et al, Review Commons RC-2025-03280 Structural Maintenance of Chromosome proteins (SMCs), a family of proteins found in almost all organisms, are organizers of DNA. They accomplish this by a process known as loop extrusion, wherein double-stranded DNA is actively reeled in and extruded into loops. Although SMCs are known to have several DNA binding regions, the exact mechanism by which they facilitate loop extrusion is not understood but is believed to entail large conformational changes. There are currently several models for loop extrusion, including one wherein the coiled coil (CC) arms open, but there is a lack of insightful experimentation and analysis to confirm any of these models. The work presented aims to provide much-needed new tools to investigate these questions: conformation-selective sybodies (synthetic nanobodies) that are likely to alter the CC opening and closing reactions. The authors produced, isolated, and expressed sybodies that specifically bound to Bacillus subtilis Smc-ScpAB. Using chimeric Smc constructs, where the coiled coils were partly replaced with the corresponding sequences from Streptococcus pneumoniae, the authors revealed that the isolated sybodies all targeted the same 4N CC element of the Smc arms. This region is likely disrupted by the sybodies either by stopping the arms from opening (correctly) or forcing them to stay open (enough). Disrupting these functional elements is suggested to cause the Smc-dependent chromosome organization lethal phenotype, implying that arm opening and closing is a key regulatory feature of bacterial Smc-ScpAB. In summary, the authors present a new method for trapping bacterial Smc's in certain conformations using synthetic antibodies. Using these antibodies, they have pinpointed the (previously suggested) 4N region of the coiled coils as an essential site for the opening and closing of the Smc coiled coil arms and that hindering these reactions blocks Smc-driven chromosomal organization. The work has important implications for how we might elucidate the mechanism of DNA loop extrusion by SMC complexes. Some specific comments: Line 75: "likely stabilizing otherwise rare intermediates of the conformational cycle." - sorry, why is that being concluded? Why not stabilizing longer-lived oncformations? We will clarify this statement!

Line 89: Sorry, possibly our lack of understanding: why first ribosome and then phage display?

Ribosome display offers to screen around 10^12 sybodies per selection round (technically unrestricted library size), while for phage display, the library size is restricted to around 10^9 sybodies due to the fact that production of a phage library requires transformation of the phagemid plasmid into E. coli, thereby introducing a diversity bottleneck. This is why the sybody platform starts off with ribosome display. It switches to phage display from round 2 onwards because the output of the initial round of ribosome display is around 10^6 sybodies, which can be easily transferred into the phage display format. Phage display is used to minimize selection biases. For more information, please consult the original sybody paper (PMID: 29792401).

Line 100: Why was only lethality selected? Less severe phenotypes not clear enough?

Yes, colony size is more difficult to score robustly, as the sizes of individual transformant colonies can vary quite widely. The number of isolated sybodies was at the limit of further analysis.

Line 106: Could it be tested somehow if convex and concave library sybodies fold in Bs?

We did not focus on the non-functional sybody candidates and only sybodies of the loop library turned out to cause functional consequences at the cellular level. Notably, we will include gfp-imaging showing that non-lethal sybodies are expressed to similar levels that toxic sybodies. Given the identical scaffold of concave and loop sybodies (they only differ in their CDR3 length), we expect that the concave sybodies fold in the cytoplasm of B. subtilis. For the convex sybodies exhibiting a different scaffold, this will be tested.

Line 125: Could Pxyl be repressed by glucose?

To our knowledge and experience, repression by glucose (catabolite repression) does not work well in this context in B. subtilis.

Line 131: The SMC replacement strain is a cool experiment and removes a lot of doubts!

Thank you! (we agree 😊)

Line 141: The mapping is good and looks reliable, but looks and feels like a tour de force? Of course, some cryo-EM would have been lovely (lines 228-229 understood, it has been tried!).

Yes, we have made several attempts at structural biology. Unfortunately, Smc-ScpAB is not well suited for cryo-EM in our hands and crystallography with Smc fragments and sybodies did not yield well-diffracting crystals.

Line 179: Mmmh. Do we not assume DNA binding on top of the dimerised heads to open the CC (clamp)?

We will clarify the text here.

Line 187: Having sybodies that presumably keep the CC together (closing) and some that do not allow them to come together correctly (opening) is really cool and probably important going forward.

Thank you!

Figure 1 Ai is not very colour-blind friendly.

We are sorry for this oversight. We will try to make the color scheme more inclusive. Thank you for the notification.

Optional: did the authors see any spontaneous mutations emerge that bypass the lethal phenotype of sybody expression?

No, we did not observe spontaneous mutations suppressing the phenotype, possibly due to the limited number of cell generations observed. We tried to avoid suppressors by limiting growth, but this may indeed be a good future approach for further fine map the binding sites and to obtain insights into the mechanism of inhibition.

Optional: we think it would be nice to try some biochemical experiment with BMOE/cysteine-crosslinked B. subtilis Smc in the mid-region (4N or next to it) of the Smc coiled coils to try to further strengthen the story. Some of the authors are experts in this technique and strains might already exist?

We have indeed tried to study the impact of sybody binding on Smc conformation by cysteine cross-linking. However, we were not convinced by the results and thus prefer not to draw any conclusions from them. We will add a corresponding note to the text.

Reviewer #2 (Significance (Required)):

The authors present a new method for trapping bacterial Smc's in certain conformations using synthetic antibodies. Using these antibodies, they have pinpointed the (previously suggested) 4N region of the coiled coils as an essential site for the opening and closing of the Smc coiled coil arms and that hindering these reactions blocks Smc-driven chromosomal organization. The work has important implications for how we might elucidate the mechanism of DNA loop extrusion by SMC complexes. Thank you!

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

Gosselin et al. use the sybody technology to study effects of in vivo inhibition oft he Bacillus subtilis SMC complex. Smc proteins are central DNA binding elements of several complexes that are vital for chromosome dynamics in almost all organisms. Sybodies are selected from three different libraries of the single domain antibodies, using the „transition state" mutant Smc. They identify 14 such mutant sybodies that are lethal when expressed in vivo, because they prevent proper function of Smc. The authors present evidence suggesting that all obtained sybodies bind to a coiled-coil region close to the Smc „neck", and thereby interfere with the Smc activity cycle, as evidenced by defective ATPase activity when Smc is bound to DNA. The study is well done and presented and shows that the strategy is very potent in finding a means to quickly turn off a protein's function in vivo, much quicker than depleting the protein.

The authors also draw conclusions on the molecular mode of action of the SMC complex. The provide a number of suggestive experiments, but in my view mostly indirect evidence for such mechanism.

My main criticism ist hat the authors have used a single - and catalytically trapped form of SMC. They speculate why they only obtain sybodies from one library, and then only idenfity sybodies that bind to a rather small part oft he large Smc protein. While the approach is definitely valuable, it is biassed towards sybodies that bind to Smc in a quite special way, it seems. Using wild type Smc would be interesting, to make more robust statements about the action of sybodies potantially binding to different parts of Smc.

As explained above, we are quite confident the Smc ATPase mutation did not bias the selection in an obvious way. The surprising bias towards coiled coil binding sites has likely other explanations, as they likely form a preferred epitope recognized by sybodies.

Line 105: Alternatively, the other libraries did not produce good binders or these sybodies were 106 not stably expressed in B. subtilis. This could be tested using Western blotting - I am assuming sybody antibodies are commercially avalable. However, this test is not important for the overall study, it would just clarify a minor point.

While there are antibody fragments available to augment the size of sybodies (PMID: 40108246), these recognize 3D-epitopes and are thus not suited for Western blotting. We did not follow up on the negative results much, but would like to point out again that there are several biases that likely emerge for the same reason (bias to library, bias to coiled coil binding site). If correct, then likely few other sybodies are effectively lethal in B. subtilis, with the exception of the ones isolated and characterized. We have added this notion to the manuscript. We have also tested the expression of non-lethal sybodies by gfp-tagging and imaging. These results will be included in the revision.

Fig. 2B: is is odd to count Spo0J foci per cells, as it is clear from the images that several origins must be present within the fluorescent foci. I am fine with the „counting" method, as the images show there is a clear segregation defect when sybodies are expressed, I believe the authors should state, though, that this is not a replication block, but failure to segregate origins.

We agree that this is an important point and will add a corresponding comment to the text.

Testing binding sites of sybodies tot he SMC complex is done in an indirect manner, by using chimeric Smc constructs. I am surprised why the authors have not used in vitro crosslinking: the authors can purify Smc, and mass spectrometry analyses would identify sites where sybodies are crosslinked to Smc. Again, I am fine with the indirect method, but the authors make quite concrete statements on binding based on non-inhibition of chimeric Smc; I can see alternative explanations why a chimera may not be targeted.

We have made several attempts of testing direct binding with mixed outcomes and decided to not include those results in the light of the stronger and more relevant in vivo mapping. However, we will add ELISA results and briefly discuss grating coupled interferometry (GCI) data and pull-downs.

Smc-disrupting sybodies affect the ATPase activity in one of two ways. Again, rather indirect experiments. This leads to the point Revealing Smc arm dynamics through synthetic binders in the discussion. The authors are quite careful in stating that their experiments are suggestive for a certain mode of action of Smc, which is warranted.

In line 245, they state More broadly, the study demonstrates how synthetic binders can trap, stabilize, or block transient conformations of active chromatin-associated machines, providing a powerful means to probe their mechanisms in living cells. This is off course a possible scenario for the use of sybodies, but the study does not really trap Smc in a transient conformation, at least this is not clearly shown.

We agree and will carefully rephrase this statement. Thank you.

Overall, it is an interesting study, with a well-presented novel technology, and a limited gain of knowledge on SMC proteins. We respectfully disagree with the last point, since our unique results highlight the importance of the Smc coiled coils, which are otherwise largely neglected in the SMC literature, likely (at least in part) due the mild effect of single point mutations on coiled coil dynamics.

Reviewer #3 (Significance (Required)):

The work describes the gaining and use of single-binder antibodies (sybodies) to interfere with the function of proteins in bacteria. Using this technology for the SMC complex, the authors demonstrate that they can obtain a significant of binders that target a defined region is SMC and thereby interfere with the ATPase cycle.

The study does not present a strong gain of knowledge of the mode of action of the SMC complex.

As pointed out above, we respectfully disagree with this assertion.

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3. Description of the revisions that have already been incorporated in the transferred manuscript

Please insert a point-by-point reply describing the revisions that were already carried out and included in the transferred manuscript. If no revisions have been carried out yet, please leave this section empty.

• *

4. Description of analyses that authors prefer not to carry out

Please include a point-by-point response explaining why some of the requested data or additional analyses might not be necessary or cannot be provided within the scope of a revision. This can be due to time or resource limitations or in case of disagreement about the necessity of such additional data given the scope of the study. Please leave empty if not applicable.

As pointed out above, there are a few minor points that we prefer not to experimentally address. In particular, we do not consider it as necessary to determine the expression levels of sybodies which were non-inhibitory. We also wish to note that we attempted to obtain structural additional biochemical data and to that end performed cryo-EM, crystallography and cysteine cross-linking experiments. Unfortunately, we did not obtain sybody complex structures and the cross-linking data were unfortunately not conclusive. We also wish to note that the first author has finished her PhD and left the lab, which limits our capacity to add additional experiments. However, as the reviewers also pointed out, the main conclusions are well supported by the data already.

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Referee #3

Evidence, reproducibility and clarity

Gosselin et al. use the sybody technology to study effects of in vivo inhibition oft he Bacillus subtilis SMC complex. Smc proteins are central DNA binding elements of several complexes that are vital for chromosome dynamics in almost all organisms. Sybodies are selected from three different libraries of the single domain antibodies, using the „transition state" mutant Smc. They identify 14 such mutant sybodies that are lethal when expressed in vivo, because they prevent proper function of Smc. The authors present evidence suggesting that all obtained sybodies bind to a coiled-coil region close to the Smc „neck", and thereby interfere with the Smc activity cycle, as evidenced by defective ATPase activity when Smc is bound to DNA. The study is well done and presented and shows that the strategy is very potent in finding a means to quickly turn off a protein's function in vivo, much quicker than depleting the protein.

The authors also draw conclusions on the molecular mode of action of the SMC complex. The provide a number of suggestive experiments, but in my view mostly indirect evidence for such mechanism.

My main criticism ist hat the authors have used a single - and catalytically trapped form of SMC. They speculate why they only obtain sybodies from one library, and then only idenfity sybodies that bind to a rather small part oft he large Smc protein. While the approach is definitely valuable, it is biassed towards sybodies that bind to Smc in a quite special way, it seems. Using wild type Smc would be interesting, to make more robust statements about the action of sybodies potantially binding to different parts of Smc.

Line 105: Alternatively, the other libraries did not produce good binders or these sybodies were 106 not stably expressed in B. subtilis. This could be tested using Western blotting - I am assuming sybody antibodies are commercially avalable. However, this test is not important for the overall study, it would just clarify a minor point.

Fig. 2B: is is odd to count Spo0J foci per cells, as it is clear from the images that several origins must be present within the fluorescent foci. I am fine with the „counting" method, as the images show there is a clear segregation defect when sybodies are expressed, I believe the authors should state, though, that this is not a replication block, but failure to segregate origins.

Testing binding sites of sybodies tot he SMC complex is done in an indirect manner, by using chimeric Smc constructs. I am surprised why the authors have not used in vitro crosslinking: the authors can purify Smc, and mass spectrometry analyses would identify sites where sybodies are crosslinked to Smc. Again, I am fine with the indirect method, but the authors make quite concrete statements on binding based on non-inhibition of chimeric Smc; I can see alternative explanations why a chimera may not be targeted.

Smc-disrupting sybodies affect the ATPase activity in one of two ways. Again, rather indirect experiments. This leads to the point Revealing Smc arm dynamics through synthetic binders in the discussion. The authors are quite careful in stating that their experiments are suggestive for a certain mode of action of Smc, which is warranted.

In line 245, they state More broadly, the study demonstrates how synthetic binders can trap, stabilize, or block transient conformations of active chromatin-associated machines, providing a powerful means to probe their mechanisms in living cells. This is off course a possible scenario for the use of sybodies, but the study does not really trap Smc in a transient conformation, at least this is not clearly shown.

Overall, it is an interesting study, with a well-presented novel technology, and a limited gain of knowledge on SMC proteins.

Significance

The work describes the gaining and use of single-binder antibodies (sybodies) to interfere with the function of proteins in bacteria. Using this technology for the SMC complex, the authors demonstrate that they can obtain a significant of binders that target a defined region is SMC and thereby interfere with the ATPase cycle.

The study does not present a strong gain of knowledge of the mode of action of the SMC complex.

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Referee #2

Evidence, reproducibility and clarity

Review: "Single Domain Antibody Inhibitors Target the Coiled Coil Arms of the Bacillus subtilis SMC complex" by Ophélie Gosselin et al, Review Commons RC-2025-03280

Structural Maintenance of Chromosome proteins (SMCs), a family of proteins found in almost all organisms, are organizers of DNA. They accomplish this by a process known as loop extrusion, wherein double-stranded DNA is actively reeled in and extruded into loops. Although SMCs are known to have several DNA binding regions, the exact mechanism by which they facilitate loop extrusion is not understood but is believed to entail large conformational changes. There are currently several models for loop extrusion, including one wherein the coiled coil (CC) arms open, but there is a lack of insightful experimentation and analysis to confirm any of these models. The work presented aims to provide much-needed new tools to investigate these questions: conformation-selective sybodies (synthetic nanobodies) that are likely to alter the CC opening and closing reactions.

The authors produced, isolated, and expressed sybodies that specifically bound to Bacillus subtilis Smc-ScpAB. Using chimeric Smc constructs, where the coiled coils were partly replaced with the corresponding sequences from Streptococcus pneumoniae, the authors revealed that the isolated sybodies all targeted the same 4N CC element of the Smc arms. This region is likely disrupted by the sybodies either by stopping the arms from opening (correctly) or forcing them to stay open (enough). Disrupting these functional elements is suggested to cause the Smc-dependent chromosome organization lethal phenotype, implying that arm opening and closing is a key regulatory feature of bacterial Smc-ScpAB. In summary, the authors present a new method for trapping bacterial Smc's in certain conformations using synthetic antibodies. Using these antibodies, they have pinpointed the (previously suggested) 4N region of the coiled coils as an essential site for the opening and closing of the Smc coiled coil arms and that hindering these reactions blocks Smc-driven chromosomal organization. The work has important implications for how we might elucidate the mechanism of DNA loop extrusion by SMC complexes.

Some specific comments:

Line 75: "likely stabilizing otherwise rare intermediates of the conformational cycle." - sorry, why is that being concluded? Why not stabilizing longer-lived oncformations?

Line 89: Sorry, possibly our lack of understanding: why first ribosome and then phage display?

Line 100: Why was only lethality selected? Less severe phenotypes not clear enough?

Line 106: Could it be tested somehow if convex and concave library sybodies fold in Bs?

Line 125: Could Pxyl be repressed by glucose?

Line 131: The SMC replacement strain is a cool experiment and removes a lot of doubts!

Line 141: The mapping is good and looks reliable, but looks and feels like a tour de force? Of course, some cryo-EM would have been lovely (lines 228-229 understood, it has been tried!).

Line 179: Mmmh. Do we not assume DNA binding on top of the dimerised heads to open the CC (clamp)?

Line 187: Having sybodies that presumably keep the CC together (closing) and some that do not allow them to come together correctly (opening) is really cool and probably important going forward.

Figure 1 Ai is not very colour-blind friendly. Optional: did the authors see any spontaneous mutations emerge that bypass the lethal phenotype of sybody expression?

Optional: we think it would be nice to try some biochemical experiment with BMOE/cysteine-crosslinked B. subtilis Smc in the mid-region (4N or next to it) of the Smc coiled coils to try to further strengthen the story. Some of the authors are experts in this technique and strains might already exist?

Significance

The authors present a new method for trapping bacterial Smc's in certain conformations using synthetic antibodies. Using these antibodies, they have pinpointed the (previously suggested) 4N region of the coiled coils as an essential site for the opening and closing of the Smc coiled coil arms and that hindering these reactions blocks Smc-driven chromosomal organization. The work has important implications for how we might elucidate the mechanism of DNA loop extrusion by SMC complexes.

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Referee #1

Evidence, reproducibility and clarity

Gosselin et al., develop a method to target protein activity using synthetic single-domain nanobodies (sybodies). They screen a library of sybodies using ribosome/ phage display generated against bacillus Smc-ScpAB complex. Specifically, they use an ATP hydrolysis deficient mutant of SMC so as to identify sybodies that will potentially disrupt Smc-ScpAB activity. They next screen their library in vivo, using growth defects in rich media as a read-out for Smc activity perturbation. They identify 14 sybodies that mirror smc deletion phenotype including defective growth in fast-growth conditions, as well as chromosome segregation defects. The authors use a clever approach by making chimeras between bacillus and S. pnuemoniae Smc to narrow-down to specific regions within the bacillus Smc coiled-coil that are likely targets of the sybodies. Using ATPase assays, they find that the sybodies either impede DNA-stimulated ATP hydrolysis or hyperactivate ATP hydrolysis (even in the absence of DNA). The authors propose that the sybodies may likely be locking Smc-ScpAB in the "closed" or "open" state via interaction with the specific coiled-coil region on Smc. I have a few comments that the authors should consider:

Major comments:

1. Lack of direct in vitro binding measurements: The authors do not provide measurements of sybody affinities, binding/ unbinding kinetics, stoichiometries with respect to Smc-ScpAB. Additionally, do the sybodies preferentially interact with Smc in ATP/ DNA-bound state? And, do the sybodies affect the interaction of ScpAB with SMC? It is understandable that such measurements for 14 sybodies is challenging, and not essential for this study. Nonetheless, it is informative to have biochemical characterization of sybody interaction with the Smc-ScpAB complex for at least 1-2 candidate sybodies described here.
2. Many modes of sybody binding to Smc are plausible The authors provide an elaborate discussion of sybodies locking the Smc-ScpAB complex in open/ closed states. However, in the absence of structural support, the mechanistic inferences may need to be tempered. For example, is it also not possible for the sybodies to bind the inner interface of the coiled-coil, resulting in steric hinderance to coiled-coil interactions. It is also possible that sybody interaction disrupts ScpAB interaction (as data ruling this possibility out has not been provided). Thus, other potential mechanisms would be worth considering/ discussing. In this direction, did AlphaFold reveal any potential insights into putative binding locations?
3. Sybody expression in vivo Have the authors estimated sybody expression in vivo? Are they all expressed to similar levels?
4. Sybodies should phenocopy ATP hydrolysis mutant of Smc The sybodies were screened against an ATP hydrolysis deficient mutant of Smc, with the rationale that these sybodies would interfere this step of the Smc duty cycle. Does the expression of the sybodies in vivo phenocopy the ATP hydrolysis deficient mutant of Smc? Could the authors consider any phenotypic read-outs that can indicate whether the sybody action results in an smc-null effect or specifically an ATP hydrolysis deficient effect?

Minor comments:

1. It was surprising that no sybodies were found that could target both bacillus and spneu Smc. For example, sybodies targeting the head regions of Smc that might work in a more universal manner. Could the authors comment on the coverage of the sybodies across the protein structure?
2. Growth curves (Fig. S3) show a large jump in recovery in growth under sybody induction conditions. Could the authors address this observation here and in the text?
3. L41- Sentence correction: Loop can be removed.
4. L525 - bsuSmc 'E' :extra E can be removed.
5. References need to be properly formatted.
6. The authors should add in figure legend for Fig 1i) details on representation of the purple region, and explain the grey strokes for orientation of the loop.
7. How many cells were analysed in the cell biological assays? Legends should include these information.

Significance

Overall, this is an impressive study that uses an elegant strategy to find inhibitors of protein activity in vivo. The manuscript is clearly written and the experiments are logical and well-designed. The findings from the study will be significant to the broad field of genome biology, synthetic biology and also SMC biology. Specifically, the coiled coil domain of SMC proteins have been proposed to be of high functional value. The authors have elegantly identified key coiled-coil regions that may be important for function, and parallelly exhibited potential of the use of synthetic sybody/designed binders for inhibition of protein activity.

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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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Referee #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.

Major comments

1. The demonstrated ability to recognize stimuli is based on several key assumptions that can hardly be met in reality.

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.

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.

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. 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). 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.

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.
2. Also Mendeley Data DOI:10.17632/bv957x6frk.1 and GitHub https://github.com/Xiaolu-Guo/Combinatorial_ligand_NFkB lead to nowhere.
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.
4. It is difficult to understand how the simulations in response to more than one ligand are performed.

Significance

A lot of work has been done, the methodology is interesting, but the biological conclusions are overstated.

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Referee #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. 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.
2. 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. 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).
3. 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?
4. 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.
5. There is no caption for Figure 3F in the figure legend nor a reference in the main text.

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.

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Referee #1

Evidence, reproducibility and clarity

The authors extend an existing mathematical model of NFkB signalling under stimulation of various single receptors, to model that describes responses to stimulation of multiple receptors simultaneously. They compare this model to experimental data derived from live-cell imaging of mouse macrophages, and modify the model to account for potential antagonism between TLR3 and TLR9 response due to competition for endosomal transport. Using this framework they show that, despite distinguishability decreasing with increasing numbers of heterogenous stimuli, macrophages are still able in principle to distinguish these to a statistically significant degree. I congratulate the authors on an interesting approach that extends and validates an existing mathematical model, and also provides valuable information regarding macrophage response.

There are no major issues affecting the scientific conclusions of the paper, however the lack of detail surrounding the mathematical model and the 'signaling codons' that are used throughout the paper make it difficult to read. This is exacerbated by the fact that I was unable to find Ref 25 which apparently describes the model, however I was able to piece together the essential components from the description in Ref 8 and the supplementary material.

Lots of the minor comments below stem from this, however there are also a few other places that could benefit from some additional clarification and explanation.

Significance:

'...it remains unclear complex...' -> '...it remains unclear whether complex...'

Introduction: 'temporal dynamics of NFkB' - it would be good to be more concrete regarding the temporal dynamics of what aspect of this (expression, binding, conformation, etc), if possible.

'signaling codons' - the behaviour of these is key to the entire paper, so even if they are well described in the reference, it would be good to have a short description as early as possible so that the reader can get an idea in their mind what exactly is being discussed here. Later, it would be good to have concrete description of exactly what these capture.

'This challenge...population of macrophages' - this seems a bit out of place, and is a bit of a run on sentence, so I suggest moving this to the next paragraph and working it into the first sentence there '...regulatory mechanisms, and this challenge could be addressed with a model parameterised to account for heterogeneous...Early models ...', or something similar.

Ref 25: I can't find a paper with this title anywhere, so if it's an accepted preprint then it would be good to have this available as well. That said, I still think it would be difficult to grasp the work done in this paper without some description of the mathematical model here, at least schematically, if not the full set of ODEs. For example, there are numerous references to how this incorporates heterogeneous responses, the 'core module', etc, and the reader has no context of these if they aren't familiar with the structure of the model.

'A key challenge which is...' -> 'A key challenge is...'

'With model simulation ...' -> a bit of a run on sentence, I suggest breaking after 'conditions'.

Results:

This section would benefit from a more in-depth description of the model and experimental setup. In particular for the experiment, the reader never really knows what this workflow for this is, nor what the model ingests as input, and what the predictions are of.

'..mechanistic model was trained...' - trained in this study, or in the previous referenced study?

'determined parameter distributions' - this is where it would be good to have more background on the model. What parameters are these, and what do they correspond to biologically? It would also be nice to see in the methods or supplementary material how this is done (maximum likelihood, etc).

'matching cells with similar core model...' - it's difficult to follow the logic as to why this is done, so I think this needs to be a little clearer. My guess would be that the assumption is that simulated cells with similar 'core' parameters have a similar downstream signalling response, and therefore the receptors can be 'transplanted'. So it would be nice to see exactly what these distributions are and what the effect of a bad match would be.

Some explanation of how this relates to the experimental data the parameters are fit on would also be useful. Is there a correspondence between individual simulated cells and the experimental data for the single ligand stimulation, and then the smallest set of these is taken? Is there also a matching from the simulated multi-receptor modules and the multi-receptor data, and if so, is this done in the same way?

'six signaling codons' - here it would be good to recapitulate what these represent, but also what the 'strength' and 'activity' correspond to (total integrated value, maximum value, etc)

'pre-defined thresholds' - no need to state these numerically in the text (although giving some sense of how/why these were chosen would give some context), but I couldn't find the values of these, nor values corresponding to the signaling codons.

'non-responder cells are likely a result of cellular heterogeneity in receptor modules rather than the core module' - is this the 'ill health' referenced earlier? If so make this clear.

It's also very difficult to follow this chain of logic, given that the reader at this point doesn't have any knowledge of what the 'core' module is, nor the significance of the thresholds on the signaling codons. I would suggest making this much clearer, with reference to each of these.

'...but the model represented these as independent mass action reactions' - the significance of this may not be clear to someone not familiar with biophysical models, so probably better to make it explicit.

'...we trained a random forest classifier...' - is this trained on the 'raw' experimental time series data, or on the signaling codons?

'We also applied a Long Short-Term Memory (LSTM) machine learning model...' - it might be good to reference these three approaches at the beginning of this section, otherwise they seem to come out of the blue a little.

'We then used machine learning classifiers...' - random forests, LSTMs, or a different model?

Discussion:

'...over statistical models...' - suggest maybe 'purely statistical models'

'We found that endosomal transport...' - A paper by Huang, et. al. (https://www.jneurosci.org/content/40/33/6428) observed a synergistic phagocytic response between CpC and pIC stimulation in microglia. This is still consistent with a saturation effect dependent on dose, but may be worth a mention.

'...features termed...' -> 'features, termed'

'...we applied a Long Short-Term Memory (LSTM) machine learning model..' - maybe make clear that this is on the time-series data (also LSTM has already been defined).

Materials and methods:

The descriptions in this section are quite vague, so I would suggest expanding this with more detail from the supplementary material, where things are quite well explained.

'sampling distribution' - not clear what this refers to in this context

'RelA-mVenus mouse strain' - it would be good to mention the relevance of the reporter for NFkB signaling

'...A random forest classifier...' -> a random forest classifier

Significance

This study provides mechanistically interpretable insight on the important question of how immune cells perform target recognition in realistic scenarios, and also provides validation of existing mathematical models by extending these beyond their original domain. The paper uses 'signaling codons' as a proxy for information processing, however in this instance it is cross-validated with an LSTM model that is applied directly to the time series data. Nevertheless, the scope of the paper is such that it does not deal with the question of how these signals are transmitted or used in a downstream immune response. To my knowledge, this is the first time that a well established existing mathematical model of signalling response has been extended and applied to heterogeneous ligand mixtures. These results will be of interest to those studying immune cell responses, and to those interested in basic research on mathematical models of signaling and cellular information processing more generally.

My background is in biophysical models, machine learning, and signaling in cancer. I have a basic understanding of immunology, but no experience in experimental cell biology.

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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.

Learn more at Review Commons

Referee #3

Evidence, reproducibility and clarity

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.

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.

(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).

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.

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.

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.

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".

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.

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.

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.
• 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).
• 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.
• 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.
• 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".
• 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
• 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?
• 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.
• 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).
• Line 404: perhaps undetected or similar would be a better description than "hidden"?

Significance

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 other organism. MICOS subunit knockouts have been characterised 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.

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.

Learn more at Review Commons

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.

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Referee #1

Evidence, reproducibility and clarity

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?

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. 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. 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?)? 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). 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? Figure 3 legend - Please add which statistical test was used and the number of replicates. Figure 4 legend - Please add which statistical test was used and the number of replicates. Figure 5C - the 3D reconstructions are very nice, but what does the red and yellow coloring show? 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?

Significance

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.

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Referee #3

Evidence, reproducibility and clarity

This study builds upon previous work in schizophrenia and other disorders using fibroblasts derived from patients, assessing mitochondrial phenotypes and then using these to identify compounds which reverse these phenotypes. The study is one of the largest of its kind performed to date with 168 patients included. The authors undertake mitochondrial phenotyping and machine learning of the outputted images to be segregate the patients based on clinical features and the associated cellular phenotype. The authors then go on to screening virtually publicly available datasets of cancer cells treated with compounds and also genetic modulations. In doing so, they can identify compounds which modulate the phenotypes and therefore might be of value to test in the patient derived lines. The study has strengths in the large number of samples, the advanced machine learning and the virtual screening. Furthermore, the authors highlight and discuss the limitations of the study well. There are some weaknesses which the authors can address. Firstly in the introduction, although it is comprehensive in some areas, in other areas for example outlining the fibroblast mitochondrial phenotype and indeed the use of patient fibroblasts to identify compounds, there is significant literature missing, particularly in Parkinson's Disease where screening in fibroblasts has resulted in compounds entering Phase 3 clinical trials. In addition to the studies using 100 or more PD patient fibroblast lines for phenotyping and patient stratification have not been included. It would be useful if the authors could comment on the robustness of the phenotypes identified in the fibroblasts over multiple passages. This is important when considering the biological and disease relevance of the phenotypes and it is not something the authors show or comment on. In discussing the genetic manipulations it would be useful to comment on the genes identified in more detail particularly those which are not known to be associated with changes in mitochondrial phenotypes.

Significance

This study builds on work from multiple labs investigating the utility of fibroblasts to identify phenotypes and find potential novel therapeutics. The size of the cohort and the advanced machine learning methods are a particular strength and this advances the field in this area. The availability of the data and code is a strength to allow others to replicate the findings. The lack of experimental validation of any of the compounds or genes identified by the virtual screening is a weakness which could be addressed.

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Referee #2

Evidence, reproducibility and clarity

In their study, Haghighi et al. seek to build upon prior literature linking alterations in mitochondrial network distribution with various kinds of psychosis. Correlations between subcellular mitochondrial localization and different psychological states is an interesting and potentially fruitful frontier and should be explored; however, despite their ambitious strategy to screen 168 skin fibroblasts from patients experiencing psychosis, and examine various online image databases, there is a concerning number of issues related to the image-analysis approach. The foremost of these is a lack of direct measures of mitochondrial distribution, which might serve to validate their proposed MITO-SLOPE protocol. There is also a worrisome lack of robust controls, which are critical in light of how admittedly subtle some of the distribution phenotypes may be. Overall, the aim to screen differences in mitochondrial distribution is a laudable goal and, in the context of psychological disorders, could be helpful in identifying new therapeutic targets; but the methodology employed in this study does not seem to be sufficiently rigorous to be able to leverage this approach for screening purposes.

I have extensive experience investigating mitochondria with advanced imaging technologies, including super-resolution microscopy as well as high-throughput and 4D imaging modalities. I am also familiar with standard as well as machine-learning approaches for quantifying mitochondrial morphology as well as distribution or trafficking. In my opinion, this study requires substantial revision, both in terms of the indirect and often opaque image-analysis pipeline as well as the inclusion of orthogonal experiments, which could serve to lessen concerns regarding purported differences in mitochondrial distribution, which are so difficult to discern as to be imperceptible. It is worth noting, too, that this study appears to be predicated, in many ways, upon a 2010 study (Cataldo et al.) of mitochondria in patients with bipolar disorder, which appears to reflect its own lack of critical controls for cell size.

Major comments:

The authors state, in the first paragraph of the results section: "By eye, we observed that samples from patients in the control and MDD categories show a more fine-grained, dispersed mitochondrial network extending to the edges of the cell, whereas patients in the categories experiencing psychosis tend to show an agglomerated, thicker network more concentrated around the nucleus. The pattern is subtle and heterogeneous across a cell population." The pattern is indeed subtle. I am concerned that it is so subtle as to be imperceptible. Firstly, it is important to note that the mitochondrial reticulum in BP, SZ, and SZA is more difficult to differentiate, by eye, because the signal appears to be saturated in places, such that the boundaries of individual mitochondria are indistinguishable due to differences in contrast or possibly from the fluorescence intensity itself. Although the authors indicate in the legend that the intensity of the mitochondrial fluorescence was adjusted "for visual clarity," it appears that the contrast needs to be decreased in the BP, SZ, and SZA conditions. It is also important to note that MitoTrackers load into mitochondria in a membrane-potential-dependent fashion. Did the authors detect differences in membrane potential between these groups? While imaging, was the same laser power and gain utilized from condition to condition? With this being said, it is not clear that mitochondria in control and MDD categories have different morphologies from the other conditions. It is also not clear what "fine-grained" means in this context. Is this a comment on aspect ratio? If so, it would be better to use standard terminology. (Why are there large red circular structures in the nucleus? These are likely not mitochondria, so why are they showing up in the channel with MitoTracker?) It is also not evident that one condition has more dispersed mitochondria than another. Given that the authors appear to be making this a central claim of their manuscript, it would seem appropriate to highlight specifically the regions of the different cells that they believe exhibit meaningful differences. If I attempt to look at the merged image, which is important because it is really the only way that one can gauge the relative distance of the mitochondrial network from the edge of the cell, there would seem to be no obvious differences between the conditions. Another key point that I think important to mention, given that it is frequently referenced in this manuscript, Cataldo et al., 2010 indicate that mitochondria in patient fibroblasts with bipolar disorder (BD) are more perinuclear than those in control. However, a cursory inspection of the images from this study (e.g., Figure 2A-B; Figure 4A-D; and Figure 6A-H) unambiguously demonstrate that the BD cells are smaller than the control cells. Of course, if the cells are smaller, the distance from the nucleus will tend to be shorter. In Cataldo et al., 2010, the authors state, "We also measured cell area, cell length, cell width, and cell perimeter of the fibroblasts used in this analysis to verify that the observed mitochondrial distributional differences were not simply a result of BD cells being smaller, shorter, or fatter. No significant differences in any of these measurements were seen based on diagnosis after two sample t tests." Notably, the data is not shown, so it is difficult to appreciate what the variance of the population of cells from control and BD would look like, but it must be said, nevertheless, that the representative images in this paper all point to the BD cells being smaller. In light of this, it would be helpful if Haghighi et al. could add scale bars to all the images (e.g., in Figure 2), so readers can ascertain whether all the cells are portrayed at the same scale and are of similar areas.

As the authors indicate, interpretable measures of mitochondrial morphology include values like size and shape. It is concerning, therefore, that Figure 3 purports to identify a number of significantly different mitochondrial "features" in the patient groups experiencing psychosis, but they do not appear to make an effort to clarify how any of these features might reflect ground truths of mitochondrial architecture, which can be understood directly by values such as aspect ratio, circularity, area, number organelles, number of nodes or branching points in a network, etc. Unless the authors can specifically tie their machine-learning classifications to standard mitochondrial shape descriptors, their classifications will remain opaque and therefore of limited credibility or value. One way to improve the validation of their machine-learning classification methods would be to use empirically sound methods for manipulating a mitochondrial morphology and distribution, which could serve as positive or negative controls. For example, treatment of cells with the uncoupler FCCP would induce mitochondrial fragmentation, treatment with cycloheximide results in stress-induced mitochondrial hyperfusion (SIMH), or treatment with Nocodazole would block mitochondrial trafficking. Treating control cells with these chemicals would help to establish baseline measurements for how far the patient cells are deviating from untreated controls, in one direction or another. Such considerations, I think, are especially important when the mitochondrial phenotypes are so subtle. I agree with the authors' argument that, for the purposes of screening, it is best to focus on a single metric. Based on their apparent discernment of the subtle differences in mitochondrial distribution in patients experiencing psychosis, they opted to examine possible differences in network density. To this end, they developed "MITO-SLOPE." Out of multiple categories of features, they highlight the following as the most powerful for establishing differences in mitochondrial network density:

"(a) A subset of texture measures in the nuclei and cytoplasm area of the mito channel. (b) A subset of features measuring the intensity of the mitochondria area across the cell."

Within the concentric bins around the cell nuclei, they measure:

• FracAtD: Fraction of total stain in an object at a given radius.
• MeanFrac: Mean fractional intensity at a given radius, calculated as the fraction of total intensity normalized by the fraction of pixels at a given radius.
• RadialCV: Coefficient of variation of intensity within a ring, calculated across 8 slices."

While the authors have recommended the use of a single metric for purposes of screening, MITO-SLOPE appears to represent a bundle of metrics, which, in the end, do not amount to a clear readout of what is being measured. From my point of view, if one were interested in measuring mitochondrial distribution, then, in an ideal situation, one would measure the average distance of all the mitochondria from the center of the nucleus. And, since the size of the cell is critical for establishing relative distances to the boundaries or periphery of the cell, one would normalize this metric by cellular area. Thus, the readout would be: [average mitochondrial distance from the nuclear center (µm)]/[cellular area (µm2)]. An even simpler metric could be: [average mitochondrial distance from nuclear center (µm)]/[average cytoplasmic radius (µm)]. When talking about mitochondrial distribution, we typically think in terms of where is the mitochondrial network, on average, in relation to the nucleus (perinuclear) or to the edge of the cell (peripheral). By quantifying the actual mean distance of the mitochondrial network in relation to both the nucleus and the bona fide cell extremities, via the metrics I described above, one can obtain direct measurements of the truly meaningful values related to mitochondrial distribution. It seems deviating from these approaches introduces more and more opportunities for confounding variables.

However, the MITO-SLOPE analysis does not seem to consider this metric. Is this, or a similar variation, not the most direct way to establish differences in the mitochondrial network distribution? I would, of course, at least want to see a discussion of why the authors have not chosen to use the most direct form of quantification for this purely spatial value. Why opt for a multifaceted measurement of a relatively straightforward quantity, when a simpler form of quantification would not only suffice but arguably be more likely to capture the ground truth? With this being said, it is not clear to me why, within MITO-SLOPE there seems to be a reliance on measuring the "intensity" of the mitochondria. (And what intensity is it? Mean intensity per ROI?) Of course, particularly if MitoTrackers were used for staining mitochondria, there will be heterogeneity in fluorescence intensity from organelle to organelle, which introduces potential confounders into the workflow. Furthermore, as indicated above, to know if the subcellular distribution of mitochondria is truly altered, it is essential to know if the cell size has likewise changed. Therefore, any unbiased measure of mitochondrial distribution must take into consideration the size of the cell; however, based on the information provided about MITO-SLOPE, it does not appear that the authors are accounting for possible variations in cell size that might account for alterations in mitochondrial network distribution - i.e., a smaller cell will have a more constrained area in which mitochondria will be able to disperse - thus, not accounting for cell size (area) will yield ambiguous results. For example, how can we know if mitochondrial motility is impaired or if the cell is simply smaller and there is less space in which to move? Another complexity, here, is if the cell boundaries were not accounted for via staining of actin, etc., then establishing a true cell boundary will be very challenging. How many bins are sufficient to capture the whole cell? Just 12? Furthermore, human fibroblasts have a tendency to be quite large (sometimes several hundred microns from end to end); how can the authors account for the whole cell, particularly in cases where part of the cell is beyond the field of view or cells are growing on top of each other, as is often the case?

In Figure 6, there is no control image that could be used as a frame of reference. I have extensive experience imaging A549 cells. The mitochondria in these images appear to be highly fragmented. The staining patterns, particularly of the cells treated with divalproex-sodium, are quite dim, indicating mitochondrial depolarization. Of course, depolarization affects the fluorescence intensity of mitochondria stained with vital dyes, such as MitoTrackers, which will, in turn, presumably affect the values obtained from MITO-SLOPE, which appear to rely on intensity gradients, rather than more concrete spatial coordinates. Also, as indicated above, it is unclear how the authors are establishing the edges of cells without a marker of the plasma membrane or cytoskeleton.

The authors note that "Divalproex-sodium is a benzodiazepine receptor agonist and HDAC inhibitor (Rahman et al. 2025) used to manage a variety of seizure disorders (Willmore 2003) and bipolar disorder(Bond et al. 2010; Cipriani et al. 2013); it shows a positive MITO-SLOPE which is the direction expected to normalize the centralized mitochondrial localization associated with psychosis." Insofar as this recommends the drug for use in "normalizing" perinuclear mitochondria within neurons, it would seem only prudent to mention that this drug also appears to induce mitochondrial depolarization and fragmentation, which are both associated with a range of severe human pathologies. I would caution the authors to not highlight one potential benefit while omitting an obvious side effect involving what appears to be significant perturbation of mitochondrial structure and function. What is the point of normalizing mitochondrial distribution if the mitochondria being redistributed are dysfunctional?

The authors note, in Figure 7, that their MITO-SLOPE analysis was unable to discern a statistically significant difference in cells with specific knockouts of genes associated with mitochondrial trafficking. If the MITO-SLOPE cannot discern a difference in the context of a substantial abrogation of mitochondrial transport capacity, how is it that it could detect meaningful differences where there is only a "subtle" change in distribution? This result would seem to militate strongly against the efficacy of this analysis pipeline and would not recommend its use for unbiased screening and discovery.

Minor comments:

For Figure 6 b and c, "µm" should be "µM."

The introduction and discussion could be more concise.

Significance

This study attempts to fill an important gap in knowledge relating to mitochondrial distribution and psychological disorders. It aims to perform an initial screen to try to validate a novel analysis pipeline called MITO-SLOPE, however, the study appears to lack analytical rigor, both in terms of the underlying cell biology together with the approach for quantification, itself. Conceptually, this study has great promise, but the authors will need to improve their pipeline prior to publication, which will likely require fundamental revisions, including an array of orthogonal measures (largely lacking here) as well as detailed demonstrations of how the segmentation actually works and ultimately yields data reflecting demonstrable mitochondrial trafficking/distribution defects.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The manuscript by Haghighi and McPhie et al. builds upon their previous findings by exploring the mitochondrial localization as a disease-associated phenotype in mental disorders, particularly in psychotic disorders. They recruited a cohort of patients diagnosed with schizophrenia, schizoaffective disorder, bipolar disorder and MDD. By taking advantage of skin biopsies, they screened patient-derived fibroblasts for aberrant mitochondrial localization and morphology using common staining techniques. Then, they use a machine learning approach to classify patients into their respective groups, which was effective for BP, SZA and pooled psychotic patients. Authors then develop a single feature for phenotyping, Mito-SLOPE, a metric of mitochondria density distribution across a cell by radial areas. With this metric, psychotic patients tend to have more nuclear-localized than edge-localized mitochondria; whereas MDD patients show a trend for higher edge-to-nucleus distribution. To find candidate drugs, authors screen publicly available datasets of cells treated with small compounds using mito-SLOPE. Furthermore, authors then apply mitoSLOPE on a CRISPR screen dataset, showcasing the role of mitochondrial dynamics genes and three genes of interest because of their association with psychosis. Finally, they identified the top genes whose KO or overexpression may explain (or reverse) the mitoSLOPE phenotype.

Overall, the manuscript is well-written, the conclusions are supported within their limitations and this work represents an advancement in the field. I recommend it for publication provided these concerns are addressed:

Major comments:

1. The mitoSLOPE measure is very interesting and most likely reflects a subtle changes in mitochondrial transport. How does the microtubule network look like in the patient fibroblasts, are there obvious alterations in e.g. their posttranslational modifications? Is there a difference in mito transport speed or pausing frequency?
2. I concur with the exclusion of compounds that obviously alter cell shape, as the authors mention for the cancer therapeutics. Some cancer therapeutics actually affect microtubule dynamics (see 1st point), which may underlie their effect on both cell shape and mitoSLOPE. To undertand the mechanism of action, the top hits should also be tested for the integrity of the microtubular network and mitochondrial transport parameters.
3. While I agree with the authors' reasoning that the observed phenotype could be a result of the disease or the result of a compensatory mechanism, their hypothesis could be experimentally tested by addition of any of the top hits in order to reverse mitoSLOPE in their patient cell lines. It may not have worked for Lithium in their last manuscript, but the mechanism of action of the novel compounds could be cell intrinsic.
4. Does recreation of the CRISPR cell line in their hands produce the same phenotype?
5. Additionally, the observed phenotypes could also be a product of the medication taken by the patients. Deeper patient data from the cohort may be relevant to put the findings in context. How were patients diagnosed? Which medications were the patients taking? Was substance abuse present? In Mertens et al, Lithium responders and Lithium non-responders showed a differential mitochondrial response, how does this affect their dataset?
6. While MDD itself is not a psychotic disorder, it can still present with psychotic features. Was this evaluated during the recruitment? Also important, were they on antipsychotic medication in addition to antidepressant therapy?
7. The fact that CACNA1C is excluded from the "unbiased" hit discovery (Fig 8) undermines the power of the filtering criteria selected by the authors. Authors should include some discussion around this.

Minor comments:

1. Colored images should be made colorblind-accessible. This applies to microscopy images and graphs.
2. Fig 3: Exact p-values should be reported in the graphs
3. Fig. 5 and Fig 7a-b: It is not immediately clear what the lines in these graphs represent. Is it the individual drug/gene hits in a pre-ranked manner?
4. Fig 6 b-c: should the "m" be capitalized for Molarity?
5. The annotation of divalproex/valproic acid as a "benzodiazepine receptor agonist" is incorrect. While it is known to enhance GABAergic neurotransmission, the mechanism is supported to be through GABA synthesis rather than being a GABA-A receptor agonist (see eg. PMID: 23407051).
6. Supplementary Fig 3 and 4 could be swapped to match the main text order.
7. One reference was inaccessible: Anon, Phenomics-Enabled Discovery and Optimization of Small Molecule RBM39 Degraders as Alternative to CDK12 Targeting in High-Grade Serious Ovarian Cancer (HGSOC).

Significance

Recently, mitochondria have emerged as mediators of anxious behavior and are increasingly studied in the context of neuropsychiatric disorders. However, the molecular mechanisms that connect altered mitochondrial performance to specific neuropathological conditions are unknown. This study extends our knowledge in this realm. While it is in principle an extension of earlier work from the authors (Cataldo, A.M. et al. Am. J. Pathol. 2010), it has added value due to the application of their automated analysis to publicly available datasets, providing a clear technical advance. This identified known as well as novel compounds that could revert the mitochondrial phenotype and makes this study specifically interesting to an audience interested in translational research. The strength of the manuscript certainly lies in the large number of examples studied and their well-rounded discussion of their findings. It is limited by the fact that the phenotype of neuropsychiatric conditions is studied in peripheral cells, and thus may not be a simple cell-autonomous response but a compensatory, systemic response that is not easy to replicate in a fibroblast in isolation. No mechanistic insight is gained on the underlying cell biology in the current format.

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Reply to the reviewers

General statements.

We thank the reviewers for their positive response and useful suggestions on our manuscript. They recognize the ‘proof of concept’ nature of the work and the importance of extending the number of human mutation-specific DMD mouse models from one to five for preclinical research. We feel that the quality of the manuscript has been improved upon implementation of the reviewer’s suggestions.

Reviewer 1.

OPTIONAL - From the point of view of the reviewer, it seems plausible to use CRISP/Cas9 to "clean up" the original hDMDmdx mouse line by selectively removing one of the YACs forming the tail-to-tail tandem in the mouse genome. Once such single copy mouse line is generated (and proven viable?) any subsequent rearrangement of the hDMD transgene would prove much less challenging. Such mouse line would also better represent human model where only one DMD copy is carried on the X chromosome.

The reviewer gives the optional suggestion that the generation of these models could have been combined with the removal of one of the copies of the YAC to extend the use of the new models to CRISPR-based therapies. This is correct, but we note that when the data on the removal of a copy of the YAC were published, our new models were already generated and in different stages of QC, colony building and analysis. The procedure described by Chey et al could be used on our new models, but this would require additional time and funding and is therefore outside the scope of this manuscript.

The labels in figure 2B and 3A would benefit from showing the PCR fragment lengths as well as the sizes of obtained hDMD exon deletions. On could also include an additional figure panel demonstrating the principle of ASO-induced exon skipping

Reviewer #1 also has a minor comment regarding the exact deletions in figure 2B and 3A. For fig. 2B he/she suggests to include the sizes of the PCR fragments next to the gel. Especially for the gel regarding PCR1, which detects the deleted YAC copy, this will not be very informative as this can be (and is) different for different clones depending on the NHEJ-mediated repair in the specific clone. Adding sizes is only interesting for each specific clone, and adding them all will make a very messy figure. The important message from this gel is the presence of any fragment, as the undeleted copy is not amplified under the conditions used. For the gel of PCR2 the opposite is the case, here the PCR fragment shown is simply the undeleted YAC copy, and here we are only interested in the absence of the PCR fragment.

We thank the reviewer for the suggestion of adding the deletion sizes to fig 3A. This made us realize that an additional table with the details of the mutant alleles in all models had been omitted, and we apologize for this error. With the revised version we include details on the size of the deletions and their genomic coordinates (in the human genome as it is in the human YAC) of each of the new models (revised Sup. Table 1). We trust that adding these details will clarify this reviewer’s minor comment.

The reviewer requests to include an additional figure panel demonstrating the principle of ASO-induced exon skipping. We have now added this to the revised version of the manuscript (new fig. 5).

The study is fairly limited in scope and will be of primary interest to those working in the DMD field.

We are aware of 9 clinical trials for exon 51 and 53 studies that are ongoing or were recently stopped. For four of these compounds companies have a license to our hDMDdel52/mdx mouse model, and one of these studies has been published. An additional 7 clinical trials are planned or ongoing for exon 44, 45 and 50 skipping for which the newly developed models are being or can be used for preclinical studies.

Reviewer 2.

To further strengthen the rigor of the study, it would be valuable to include an analysis of potential off-target effects of CRISPR editing, particularly given that double targeting of two YAC copies was required. This is especially important for germline edits, as off-target mutations could introduce confounding phenotypes in the resulting mice. Demonstrating minimal or absent off-target activity would increase confidence in the specificity and safety of the generated models.

There has indeed been one major study suggesting a large number of CRISPR-induced off-target mutations in mouse models. However, this publication was rapidly questioned by multiple groups for having used the wrong control animals and the original publication was retracted (https://doi.org/10.1038/nmeth0518-394a). Another study at that time, using the correct controls, did not find mutations that could be attributed to CRISPR-induced off-target mutations. A more recent study analysed founder animals from transgenic projects using 163 different guide RNAs and concluded ‘In total, only 4.9% (8/163) of guides tested have detectable off-target activity, at a rate of 0.2 Cas9 off-target mutations per founder analysed. In comparison, we observe __~1,100 unique variants in each mouse regardless of genome exposure to Cas9 __indicating off-target variants comprise a small fraction of genetic heterogeneity in Cas9-edited mice.’ In short, the background mutation rate in mice is much higher than the Cas9 off-target mutation rate. In addition to this, we only used guide RNAs that did not have any predicted off-target sites (according to the CRISPOR tool; https://crispor.gi.ucsc.edu/crispor.py) on the same chromosome or in protein coding sequences, so that any undetected off-target mutation will rapidly be lost in the subsequent breeding. We also would like to refer the reviewer to the ‘referee cross-commenting remark’ from reviewer #3 on this topic.

The validation of the dystrophic phenotype is generally convincing. However, the authors should clarify how "human dystrophin" is detected in the deletion models. Since only part of the dystrophin gene in these mice is humanized (the remainder is murine), it is important to specify, also in the results, which antibody was used and which epitope/exon it recognizes. If the antibody targets a deleted exon in a given model, this could lead to misinterpretation of the dystrophin signal. Providing this clarification would ensure the conclusions regarding dystrophin expression are fully supported.

This question is based on the incorrect assumption that only part of the DMD gene in these models is humanized. As described in the original publication on the YAC transgenics the complete human gene is in the YAC. Here, we deleted a particular exon from this complete human DMD gene. In combination with the mdx allele, these mice lack the full-length mouse and human dystrophin isoforms expressed in muscle. As mentioned in the materials section, the human dystrophin protein was detected with the Mandys 106 antibody (recognizing exon 43; amino acids 2063-2078), which only has reactivity with human dystrophin according to the product specification of Sigma Aldrich. We confirmed this for wild type mouse tissue, showing no dystrophin for this antibody. In fig 4 we confirm lack of human dystrophin in the deletion models using this antibody. The mouse and human dystrophin protein was detected with the AB154168 antibody of Abcam (recognizing the last 100 amino acids of the C-terminal part of the protein), which has reactivity with both mouse and human. So neither antibody did target a deleted exon. For the exon skipping validation, solely the Abcam antibody was used, as none of the deleted or skipped exons was recognized by this antibody. Information regarding the targeted protein region has now been added to the materials section.

Additionally, to further strengthen the characterization of the muscular dystrophy phenotype, the authors could quantify muscle fibre size and the percentage of centrally nucleated fibres, both of which are widely accepted quantitative markers of ongoing degeneration/regeneration in DMD models.

and

The validation of exon skipping in the new hDMD deletion models is convincing at the molecular level. However, since the ASOs were injected into both gastrocnemius and triceps muscles, it would be helpful to include at least a brief characterization of the triceps, even in supplementary data, as different muscles can show slightly different pathology and responses. Additionally, while the molecular readouts (RT-PCR and Western blot) demonstrate restoration of dystrophin expression, including simple histological analysis, such as H&E staining, could further support functional improvement and reinforce the physiological relevance of exon skipping in these models.

The proof-of-principle nature of the current manuscript is focused on restoration of dystrophin expression shortly after ASO treatment, and the current sample sizes (n=3 mice per strain) are too limited for actual quantification of histopathological improvements. Furthermore, the timespan between the intramuscular injection and tissue collection (2 weeks) does not allow sufficient time for histopathological improvements to develop. Notably, a large natural history analysis of all these new models is currently ongoing, which includes a large variety of in vivo functional outcome measures and provides a full description of the histopathological aspects of these mice. The proposed characterization of the triceps is now included as supplementary data of the manuscript (Sup. Fig 1).

Reviewer 3.

This reviewer starts with pointing out some typos, or requested rephrasing to sentences for clarification. We appreciate this and have addressed this in the revised version of the manuscript.

Generation of the models: it is not clear why the authors generated line 44 in ES cells, then switched to direct gene editing in zygotes. Was this due to advent of electroporation of zygotes at the time? This may need clarification beyond the sentence "Encouraged by the specificity of our new prescreen workflow and the efficiency of correct targeting of human exon 44 in ES cells, we generated additional models ... directly in mouse zygotes".

The simple answer to this is that we were (pleasantly) surprised ourselves by the efficiency we got in the ES cells (which was based on the previous experience generating the del52 model). For animal welfare reason we prefer to generate models via ES cells if we expect a long and cumbersome quality control process and / or very low efficiency, as ES cells allow us to do this QC before the actual animals are generated, thus reducing the number of animals generated during the model generation phase. Expecting very low efficiency, we originally picked 10 x 96 well plates of clones for this del44 targeting, but after pre-screening the first two plates (192 clones), we realized this was an enormous overkill in clones, and the additional 8 plates were not analysed. With this much higher than expected efficiency, and the power of the two-step pre-screen described in the manuscript, we decided to try the next model (the del45) directly in zygotes. This was found efficient enough to also do the last two models directly in zygotes. We can only speculate on the much higher efficiency than observed for the del52 targeting. Clearly the fact that we knew of the double integration this time allowed us to develop the successful 2-step pre-screen. Another difference is that the del52 model was generated using TALENs as genome editors, whereas now we could use CRISPR/Cas9.

Antisense oligonucleotide treatment: there is no description of the design of the ASOs beyond their sequence in suppl. Table 4. How were they designed? Moreover, they have been injected at two different doses (i.e., 50ul for Exon 51 & 53; 100ul for Exon 44 & 45). What is the rational for this? There is no justification in the manuscript.

The requested additional details on ASO design and dosing have been added to the materials section of the revised manuscript. The reviewer also pointed out that fig 4 includes both a protein sample diluted to 10% of protein of both a C57BL/6J and hDMD/mdx control mouse, and requested a justification for this. We included samples of both wildtype strains to confirm species reactivity of the dystrophin antibodies used, with the AB145168 antibody being specific for both mouse and human protein (showing a dystrophin band in both wildtype samples), and the Mandys106 antibody being specific to only human protein (showing a dystrophin band in the hDMD/mdx control only).

Phenotypic validation of the new models: a description of the mdx line with C57BL/6J mice is mentioned. Is this why Fig.4 includes "10% Bl6" and "10% hDMD/mdx"? If so, this should be clarified in the text (or deleted from the figure). The authors mentioned "As expected, the gastrocnemius of healthy hDMD/mdx mice expressed dystrophin of human origin at wildtype levels". Why would this be expected? If 2 copies of the gene, including the human promoter, are integrated, why would one expect a wildtype level of expression? In fact, in the original paper describing the hDMD/mdx model ('t Hoen et al. 2008), the human transcripts are expressed at 2 to 4-fold higher than their endogenous counterparts (which is in line with the integration of 2 copies).

It is true, as he/she points out, that qRT-PCR data in the original YAC transgenic publication showed double expression of the human transcript, consistent with the double integration. However, fig. 3b in the same paper shows that at the protein level the expression of human DMD is comparable to the mouse protein. We don’t know the reason for the discrepancy between transcript and protein levels in this model, but in the current manuscript we are referring to this protein expression.

A quantification of the expression levels on Figure 4 should be done (normalized to actinin) to resolve this. The size of the Marker should also be added on Figure 4.

We feel that proper quantification can only be done with the utilization of a standard curve. As we expected no, or trace levels of dystrophin in the deletion models, we only included wildtype samples diluted to 10% of wildtype protein. This prevents us from accurate quantification of the trace dystrophin levels observed in the del45 and del51 models. However, as can be appreciated from fig 4, expression is very minimal. We added information on the marker in the materials section, and indicated the size (85 kDa) in the figure legend.

Finally, the authors observed histological hallmarks of the disease in the new models (i.e., muscle degeneration and fibrosis). Although obvious on the images, it may be useful to add indications (e.g., arrows) on the images for readers non familiar with DMD.

We added information on the marker in the materials section, and indicated the size (85 kDa) in the figure legend. Lastly, we also added the requested arrows to the pictures of fig. 4B to allow distinction between different histopathological hallmarks, and refer to these in the figure legend.

Prescreen PCR of hDMD/mdx ES cells (Fig. 2): the authors mentioned that "The PCR conditions were chosen for not being able to amplify the undeleted allele." What does this mean? Was the elongation time reduced? As per the text, the theoretical size of a WT band is around 1.6kb. Yet, on the gel, bands higher than 1kb are visible for some clones.

This is indeed based on the extension time of the PCR reaction shown in PCR 1 from fig 2B, amplified with primers upstream and downstream of the deleted region (see fig 1 and 2A). However, the approx. 1.6 kb fragment the reviewer refers to is the undeleted-specific amplification shown in Fig 2B PCR 2, which is the result of a primer outside and a primer inside the deleted region (fig 1and 2A). Amplification of the undeleted copy with the primers used in PCR 1 would give a fragment of 3902 nt. The deletion of exon 44 in the final model is 3584 nt, which details will be shown in the excel file that was erroneously omitted (see our response to reviewer #1), with the PCR 1 product of the deleted copy in the clone used for the mouse model being 318 nt. It is straight-forward to select an extension time that would be insufficient for a 3.9 kb fragment, but which can amplify fragments that are shorter due to the deletion. Even in a clone with a single copy of exon 44 deleted, one would not expect to see the 3902 nt fragment due to preferential amplification of the much shorter mutant band. This has now been clarified in the legend of figure 2 of the revised version of the manuscript.

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Referee #3

Evidence, reproducibility and clarity

The manuscript by van Putten et al. describes the generation and initial characterization of four new mouse models of DMD, based on the previously generated hDMD/mdx murine model, which expressed human dystrophin from a yeast artificial chromosome (YAC) in a DMD null (mdx) background. The four new models are based on the deletion of four Exons (44, 45, 51 & 53), which accounts for most human deletions (hotspot) in DMD.

The description of the generation of these models using CRISPR/Cas9 gene editing is thorough, and the quality control is adequate. Moreover, preliminary testing of exon skipping therapy using ASO showed it is possible to restore the production of dystrophin protein (albeit truncated) in these models, which increase their translational value. Although the study is valuable and methodologically sound, there are minor points that need to be addressed:

• Few typos need to be corrected:
  • "Therapeutic approaches aiming to restore dystrophin for DMD are based on the discrepancy between DMD and BMD mutations." This needs to be rephrased to clarify the meaning for readers not familiar with DMD.
  • "Western blot and immune fluorescence analysis on gastrocnemius muscles..." replace" immune fluorescence" with immunofluorescence.
  • "Two weeks after the last injection muscles were isolated, and RNA and protein was isolated from muscle..." protein WERE isolated.
  • "However, gene editing-based therapies could run into the same unpredictable outcome reduced efficiency of a therapy ..." This sentence is confusing, consider rephrasing.
• Generation of the models: it is not clear why the authors generated line 44 in ES cells, then switched to direct gene editing in zygotes. Was this due to advent of electroporation of zygotes at the time? This may need clarification beyond the sentence "Encouraged by the specificity of our new prescreen workflow and the efficiency of correct targeting of human exon 44 in ES cells, we generated additional models ... directly in mouse zygotes".
• Antisense oligonucleotide treatment: there is no description of the design of the ASOs beyond their sequence in suppl. Table 4. How were they designed? Moreover, they have been injected at two different doses (i.e., 50ul for Exon 51 & 53; 100ul for Exon 44 & 45). What is the rational for this? There is no justification in the manuscript.
• Phenotypic validation of the new models: a description of the mdx line with C57BL/6J mice is mentioned. Is this why Fig.4 includes "10% Bl6" and "10% hDMD/mdx"? If so, this should be clarified in the text (or deleted from the figure). The authors mentioned "As expected, the gastrocnemius of healthy hDMD/mdx mice expressed dystrophin of human origin at wildtype levels". Why would this be expected? If 2 copies of the gene, including the human promoter, are integrated, why would one expect a wildtype level of expression? In fact, in the original paper describing the hDMD/mdx model ('t Hoen et al. 2008), the human transcripts are expressed at 2 to 4-fold higher than their endogenous counterparts (which is in line with the integration of 2 copies). A quantification of the expression levels on Figure 4 should be done (normalized to actinin) to resolve this. The size of the Marker should also be added on Figure 4. Finally, the authors observed histological hallmarks of the disease in the new models (i.e., muscle degeneration and fibrosis). Although obvious on the images, it may be useful to add indications (e.g., arrows) on the images for readers non familiar with DMD.
• Prescreen PCR of hDMD/mdx ES cells (Fig. 2): the authors mentioned that "The PCR conditions were chosen for not being able to amplify the undeleted allele." What does this mean? Was the elongation time reduced? As per the text, the theoretical size of a WT band is around 1.6kb. Yet, on the gel, bands higher than 1kb are visible for some clones.

Referee cross-commenting

The comments from the other reviewers seem fair, reasonable, and should be easily addressed by the authors. The off-target analysis might however be a bit of a stretch, given that (as per published data) the off-target rate is low (i.e., no higher than genetic drift) in mouse zygotes when using CRISPR RNPs, and any potential off-target mutation could easily be segregated out by means of backcrossing.

Significance

The four new mouse models generated in this study will advance the field both at the preclinical and the clinical levels, because they more closely recapitulate the human mutations linked to DMD than previous models, while presenting with a translational potential (the authors showed a proof of concept of exon-skipping therapy in these mice).

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Referee #2

Evidence, reproducibility and clarity

Summary:

The authors generated four novel humanized DMD mouse models carrying deletions of exons 44, 45, 51, or 53 in the human DMD gene on an mdx C57BL/6J background. They developed an optimized CRISPR-Cas9 pre-screening workflow for embryonic stem cells and zygotes, allowing efficient and precise targeting of the human DMD YAC, which carries a complex double tail-to-tail integration. The models display absent or trace dystrophin and classical DMD muscle pathology, including fibrosis. ASO-mediated exon skipping of flanking exons successfully restores dystrophin expression, validating their use for preclinical testing of mutation-specific therapies. These models address a key limitation of the standard mdx mouse, which carries a mutation only in exon 23, and provide a more clinically relevant platform for evaluating human sequence-specific therapeutic strategies for the most frequently mutated DMD exons.

Minor comments:

1. The pre-screen workflow and model generation are impressive and well-optimized. To further strengthen the rigor of the study, it would be valuable to include an analysis of potential off-target effects of CRISPR editing, particularly given that double targeting of two YAC copies was required. This is especially important for germline edits, as off-target mutations could introduce confounding phenotypes in the resulting mice. Demonstrating minimal or absent off-target activity would increase confidence in the specificity and safety of the generated models.
2. The validation of the dystrophic phenotype is generally convincing. However, the authors should clarify how "human dystrophin" is detected in the deletion models. Since only part of the dystrophin gene in these mice is humanized (the remainder is murine), it is important to specify, also in the results, which antibody was used and which epitope/exon it recognizes. If the antibody targets a deleted exon in a given model, this could lead to misinterpretation of the dystrophin signal. Providing this clarification would ensure the conclusions regarding dystrophin expression are fully supported. Additionally, to further strengthen the characterization of the muscular dystrophy phenotype, the authors could quantify muscle fibre size and the percentage of centrally nucleated fibres, both of which are widely accepted quantitative markers of ongoing degeneration/regeneration in DMD models.
3. The validation of exon skipping in the new hDMD deletion models is convincing at the molecular level. However, since the ASOs were injected into both gastrocnemius and triceps muscles, it would be helpful to include at least a brief characterization of the triceps, even in supplementary data, as different muscles can show slightly different pathology and responses. Additionally, while the molecular readouts (RT-PCR and Western blot) demonstrate restoration of dystrophin expression, including simple histological analysis, such as H&E staining, could further support functional improvement and reinforce the physiological relevance of exon skipping in these models.

Significance

This study presents a clear and technically robust advance in the field of Duchenne muscular dystrophy (DMD) preclinical research. The strongest aspects are the generation of four novel humanized DMD mouse models carrying clinically relevant exon deletions (44, 45, 51, 53) and the development of an optimized CRISPR-Cas9 pre-screening workflow that efficiently and precisely targets the human DMD YAC, despite its complex double tail-to-tail integration. These models display relevant dystrophic phenotypes and are validated for ASO-mediated exon skipping, demonstrating their applicability for preclinical testing of mutation-specific therapies.

Compared to existing models, such as the standard mdx mouse or previously generated hDMDdel52/mdx line, these new models address the critical limitation that most human DMD mutations cluster outside exon 23, providing a more clinically relevant system. The study extends knowledge both technically, by demonstrating an efficient pre-screening workflow for complex humanized YAC edits, and functionally, by creating models that allow preclinical evaluation of human sequence-specific therapeutic strategies for the most frequent DMD mutations. The audience for this work includes basic and translational researchers in the muscular dystrophy, gene therapy, and genome editing fields, as well as clinicians interested in the development and preclinical testing of exon skipping and gene-editing therapies. These models will likely be widely used to optimize therapy design, dosage, and delivery, enhancing translatability to clinical applications.

Field of expertise: Duchenne muscular dystrophy, preclinical models, genome editing, exon skipping therapies, regenerative medicine.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The study describes the creation and preliminary validation of four humanized mouse DMD models. The authors utilized the pre-existing hDMDmdx mouse line as a platform to generate clinically relevant models that carry the deletion of exons 44, 45, 51 and 52 of the hDMD transgene using CRISPR/Cas9 technology. This proved somewhat challenging as the hDMD YAC transgene present in the original hDMDmdx line is inserted as a tail-to-tail tandem in the mouse genome. The initial mouse line carrying deletion of exon 44 was performed using a combination of CRISPR/Cas9 and ES cell technologies whereas the remaining mouse lines were generated by applying CRISPR technology directly of hDMCmdx zygotes. In order to identify and select ES cell lines and animals carrying the desired deletion patterns, the authors devised a two steps PCR-based selection strategy followed by a copy number PCR for individual hDMD exons. Once the desired mouse lines were obtained, the authors performed Western blots and histological staining to prove the loss of the hDMD protein expression and the appearance of associated DMD muscle phenotypes. Finally, in vivo experiment was carried out where intramuscular injection of exon-specific ASOs lead to exon skipping and partial restoration of the expression of the truncated but potentially functional hDMD protein variants. The experiment was carried out solely as a proof-of-concept and was terminated before any therapeutic effect of the ASOs could be potentially observed. Nevertheless, the authors argue (correctly) that such models can prove useful in future development of treatment strategies for DMD.

Major comments:

The study has clear aims and is well described. The performed experiments support the final conclusions presented in the paper. OPTIONAL - From the point of view of the reviewer, it seems plausible to use CRISP/Cas9 to "clean up" the original hDMDmdx mouse line by selectively removing one of the YACs forming the tail-to-tail tandem in the mouse genome. Once such single copy mouse line is generated (and proven viable?) any subsequent rearrangement of the hDMD transgene would prove much less challenging. Such mouse line would also better represent human model where only one DMD copy is carried on the X chromosome.

Minor comments:

The labels in figure 2B and 3A would benefit from showing the PCR fragment lengths as well as the sizes of obtained hDMD exon deletions. On could also include an additional figure panel demonstrating the principle of ASO-induced exon skipping

Significance

General Assessment:

The study is fairly limited in scope and will be of primary interest to those working in the DMD field. The new patient-derived hDMD exon deletions will allow testing and validation of human therapeutic moieties in mouse models but as such the study does not advance our knowledge about DMD or transgenic mouse model generation.

Advance:

Perhaps the only novelty is a very diligent genotyping approach aimed at identifying lines where both exons in the tail-to-tail hDMD tandem have been deleted. Given the extensive work put into this approach, the author may have missed an opportunity to reengineer the original hDMDmdx mouse line (see OPTIONAL) to generate a mouse line where any future modifications of the hDMD allele would be much more accessible to both CRISPR-mediate NHEJ and HDR approaches.

Audience:

The study is fairly limited in scope and will be of primary interest to those working in the DMD field.

Reviewer's expertise focuses on CRISPR/Cas9 technologies and transgenic mouse model generation.

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Reply to the reviewers

COMBINED REVIEW REPORTS

__1.1. The biochemical and biophysical experiments performed in this study were well designed, data were clear and the conclusions were well supported by the results. One potential improvement is to check whether NLS could affect the normal activation targets of ΔNp63α, such as KRT14 and other epithelial genes. This could complement the experiments testing the inhibition effect of ΔNp63α on p53-mediated gene activation. This will be interesting, as ΔNp63α is a master regulator in epithelial cells via regulation of diverse epithelial genes. __

We thank the Review for such useful comment. In order to further investigate the relationship between p63 nuclear import and function, and the importance of the oligomerization driven tolerance to point mutations in the latter, we have now performed a number of novel experiments. First of all, we have included both DNp63a NLSn and NLSc mutants in DNA binding/p53 -inhibition assays shown in original Figure 7. The new data is shown in Figure 4E and Supplementary Figure__ S5__. As expected, such mutants had a much smaller effect on DNA binding/p53-inhibition as compared to the NLSbip mutant, further establishing a functional link between p63 nuclear levels and transcriptional activity, and proving the functional relevance of the compensatory mechanism evolved by p63 to tolerate the effect of mutations inactivating either NLSn or NLSc.

In addition, and as specifically suggested by the Reviewer, we have measured the effect of NLS impairing mutations on the ability of DNap63 to transactivate the K14 and the Bax promoters, which. Our results, shown in revised Figure 4F and 4G, as well as in Supplementary Figure S6 clearly show that both DNp63a NLSn and NLSc mutants transactivate the promoters at undistinguishable levels compared to the wild-type, consistent with their minimal effect on DNA binding and nuclear transport, while the NLSbip mutation, which prevents nuclear localization and DNA binding, also prevents transcriptional transactivation.

__1.2. A minor suggestion: authors could consider use p63 rather than ΔNp63α in the manuscript. The heterogenous sequences of NLS regions are relevant for the delta isoform of p63. In addition, all experiments performed in the study are not necessarily specific for the biology of the ΔNp63α isoform, but they are probably informative for all p63 isoforms. __

We thank the Reviewer for this suggestion. We have modified the text in the discussion to introduce this concept. Indeed, we expect the bipartite NLS to mediate nuclear transport of most p63 isoforms, whereas the p63 delta isoform, which lacks NLSn, would be transported into the nucleus by NLSc. We have modified the text in the Discussion section to make this point clearer and more explicit "the bipartite NLS identified here is responsible for nuclear localization of most p63 isoforms, while p63 delta is transported into the nucleus by NLSc: SIKKRRSPD)." To further corroborate this statement, we have also included new data obtained with the TAp63a and gNp63a isoforms. Our data clearly show that nuclear import of both isoforms depends on the NLSbip identified here and is mediated by the IMPa/b1 heterodimer, so that the findings obtained for the ΔNp63α isoform can be generalized to others. The new data is shown in Figure 3 and in Supplementary Figure S3.

__1.3. Another minor suggestion: As p63 forms a tetramer when binding to DNA sequence for gene regulation, it would be good for authors to speculate the role of NLS and its variations in tetramerization. __

We thank the Reviewer for such comment. Since the NLS is located outside of the tetramerization domain, it is not expected to play a direct role in tetramerization. We have addressed this issue by generating computational models of ΔNp63α and DNp63α;mNLS dimers and tetramers to allow a direct comparison. The new data is shown in Figure 5A-D and Supplementary Figure S11A-D. The data suggests that mutation of the NLS residues, which lies outside of the oligomerizaiton domain, does not affect ΔNp63α oligomerization abilities supporting the experimental evidences from Figure 5E (BRET experiments).

__

2.1. In immunofluorescence images it is sometime difficult to see nuclear accumulation. Single channels of the GFP signal may help to make the point. __

We thank the Reviewer for pointing out this issue. We have provided single channels for every microscopic image in Supplemental Figures.

__ 2.2. The binding assays in Fig. 3 would profit from using the most efficient imp a variant together with imp beta to show potential cooperative binding.__

We thank the Reviewer for such comment, which helped enhancing the physiological relevance of our binding data. We have now introduced the requested data in Supplementary Figure S2A. In the revised Figure panel, we compared binding of FITC-labelled p63-NLS peptide to either full length IMPa1 alone, IMPa1DIBB and pre-heterodimerized IMPa1/IMPb1 complex. The data are consistent with a classical binding mode whereby interaction with IMPb1 releases full length IMPa1 binding minor and major binding sites by engaging with the autoinhibitory IBB domain. To corroborate our results even further and demonstrate the bipartite nature of p63 NLS identified here, we have also performed FP experiments between p63-NLS and LTA SV40 NLS (a well characterized monopartite NLS) in the presence of either wt IMPa1DIBB or its minor and major site mutants. As expected from a bipartite NLS, either mutation impaired binding significantly, whereas the mutation of the minor site had a much smaller effect on binding of SV40 LTA NLS. The new data, shown in Supplementary Figure S2BC and Supplementary Table S3 confirm our hypothesis by highlighting a very strong binding affinity reduction of p63 NLS peptide for IMPa1 major site mutant (

__2.3. please mention that NTR can also recognize 3D structures of structural RNAs, e.g. tRNAs or miRNAs __

We thank the Reviewer for this very useful suggestion. We have now introduced this concept in the Introduction and added two references to support our statement. The paragraph is as follows: "Additionally, Exportin 5 and Exportin-T evolved to recognize specific RNA structures within pre-miRNAs and t-RNAs, respectively (5, 6)."

2.4. longer TA isoforms

We have added corrected the typo and we thank the Reviewer for noticing it.

__ 2.5. homologues or orthologues? __

We thank the reviewer for pointing out this issue. We have corrected the text, so now IMPas and members of the p53 family are referred to as paralogs and not as orthologs

__3.1. The major function of DNp63a seems to be that of a bookmarking factor that ensures the establishment of an epithelial transcriptional program. It is found to bind more to enhancer than to promoter regions. While it might also act for a few genes as a classical transcription factor (K14). this bookmarking and interaction with other transcriptional regulators seems to be its major task. This should be included in the introduction. __

We thank the Reviewer for this suggestion. The Introduction has been modified as requested to incorporate this important concept "Additionally, p63 has been shown to act as a pioneer factor, shaping the chromatin and enhancer landscape, thus regulating accessibility to activating and repressing transcription factors (18-20)."

__ 3.2. "DNp63a can be imported into the nucleus as a dimer" What is the evidence that DNp63a is imported as a dimer and not as a tetramer? Although functional not really relevant, because all conclusions drawn for a dimer are true for a tetramer (such as the mutation compensation), this statement (and others in the text) should either be substantiated or modified. __

The Reviewer is correct in pointing out that, while p63 isoforms bind DNA as tetramers (7), the precise oligomeric state at which nuclear import occurs is not firmly established. Indeed, little is known about the regulation of the p63 oligomerization process during nucleocytoplasmic trafficking. While TA isoforms are generally maintained in an inactive, closed, and dimeric conformation-requiring external stimuli such as phosphorylation to undergo activation and tetramerization-ΔNp63α has been reported to form tetramers even in the absence of such stimuli (4, 8). In light of this, we have modified the text to explicitly acknowledge the possibility that ΔNp63α may be transported into the nucleus either as a dimer or as a tetramer, rather than implying a single obligatory oligomeric state.

Importantly, to directly address the Reviewer's concern, we have broadened the scope of the manuscript to include additional p63 isoforms, particularly TAp63α, which is predominantly present as a dimer under basal conditions. Our new data (Figure 3) demonstrate that TAp63α is efficiently translocated into the nucleus via the IMPα/β1 heterodimer in an NLSbip-dependent manner. Notably, despite its inability to form tetramers, TAp63α displays a similar tolerance to mutations that inactivate individual basic clusters within the bipartite NLS, analogous to what is observed for ΔNp63α (Supplementary Figure S11).

Together, these results formally demonstrate that dimerization is sufficient to support efficient nuclear import in the presence of NLS-inactivating mutations, and that higher-order oligomerization (i.e., tetramerization) is not required for this property. We have therefore revised the manuscript accordingly to avoid over-interpretation and to more accurately reflect the experimental evidence.

__ 3.3. The explanation for the difference in the sensitivity of mutations in the bipartite NLS in the isolated peptide experiments and experiments with the full length DNp63a is intriguing. Unfortunately, it is not based on direct experimental evidence. To proof their model (which is the central claim of this manuscript) they should fuse the bipartite NLS to any dimerization module (e.g. a leucine zipper sequence) and show that by dimerization of the bipartite NLS the same results towards mutations are obtained as for full length DNp63a. This would strongly support their model. __

We agree that the model for nuclear transport is a central claim of our work, and deserves additional experimental validation. In order to support our hypothesis, in the revised manuscript we have generated a number of additional DNp63a mutants uncapable of self-interaction, based on deletion of residues 301-347(p63-DOD).

We have now:

(i) Validated the inability of the DOD mutant to self-interact by means of BRET assays in living cells, whereby a strong decrease in BRET ratio is observed compared to wild-type DNp63a (New Figure 6E and New Supplementary Figure S8).

(ii) Shown that, in such context, substitution of either the N-terminal or C-terminal basic stretch of amino acids in the NLS is sufficient to impact p63 nuclear import, whereas in the context of the full-length protein, they are not (New Figure 6F-H, and New Supplementary Figure S9).

(iii) Shown that while FLAG-p63 wt could relocalize to the nucleus YFP-p63mNLSbip but not YFP-p63;DOD;mNLSbip (New Supplementary Figure S10).

We believe that these new data further demonstrate the impact of p63 self-association on subcellular localization and strongly support our hypothesis. We greatly thank the Reviewer for their inspiring comment, which led to a significant improvement of our manuscript.

References

Lotz R, Osterburg C, Chaikuad A, Weber S, Akutsu M, Machel AC, et al. Alternative splicing in the DBD linker region of p63 modulates binding to DNA and iASPP in vitro. Cell Death Dis. 2025;16(1):4. Ciribilli Y, Monti P, Bisio A, Nguyen HT, Ethayathulla AS, Ramos A, et al. Transactivation specificity is conserved among p53 family proteins and depends on a response element sequence code. Nucleic Acids Res. 2013;41(18):8637-53. Monti P, Ciribilli Y, Bisio A, Foggetti G, Raimondi I, Campomenosi P, et al. ∆N-P63alpha and TA-P63alpha exhibit intrinsic differences in transactivation specificities that depend on distinct features of DNA target sites. Oncotarget. 2014;5(8):2116-30. Pitzius S, Osterburg C, Gebel J, Tascher G, Schafer B, Zhou H, et al. TA*p63 and GTAp63 achieve tighter transcriptional regulation in quality control by converting an inhibitory element into an additional transactivation domain. Cell Death Dis. 2019;10(10):686. Okada C, Yamashita E, Lee SJ, Shibata S, Katahira J, Nakagawa A, et al. A high-resolution structure of the pre-microRNA nuclear export machinery. Science. 2009;326(5957):1275-9. Kutay U, Lipowsky G, Izaurralde E, Bischoff FR, Schwarzmaier P, Hartmann E, et al. Identification of a tRNA-specific nuclear export receptor. Mol Cell. 1998;1(3):359-69. Enthart A, Klein C, Dehner A, Coles M, Gemmecker G, Kessler H, et al. Solution structure and binding specificity of the p63 DNA binding domain. Scientific reports. 2016;6:26707. Deutsch GB, Zielonka EM, Coutandin D, Weber TA, Schafer B, Hannewald J, et al. DNA damage in oocytes induces a switch of the quality control factor TAp63alpha from dimer to tetramer. Cell. 2011;144(4):566-76.

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Referee #3

Evidence, reproducibility and clarity

Demarinis et al describe a detailed analysis of different stretches of basic amino acids located between the DBD and the OD of DNp63a to act as nuclear localization signals. They convincingly show that two stretches exist that form a bipartite NLS. They combine both functional import data with structure determination of the NLS sequence with IMP⍺ showing that both parts interact with the major and the minor site. The data are presented well provide a very good model of how nuclear important is regulated for DNp63a.

This is a nice study of the bipartite NLS of DNp63a. Most interestingly, the authors show that nuclear import experiments using either the isolated peptide fused to GFP or DNp63a have a different outcome when the individual sequences are mutated. While in the case of the isolated peptide experiments a mutation in either of the two sequences has a measurable effect, this is not the case in the full length DNp63a context. The authors explain this with the oligomeriic state of DNp63a, which provides additional sequences from the other monomers within the tetramer, even when one of the NLS sequences is mutated. They provide alphaFold models to support this explanation. This in trans substitution effect explains why the NLS is not a mutation hotspot for inactivating DNp63a. These results are new and interesting in the context of how DNp63a regulates the development of epithelial tissues.

Criticism:

1. The major function of DNp63a seems to be that of a bookmarking factor that ensures the establishment of an epithelial transcriptional program. It is found to bind more to enhancer than to promoter regions. While it might also act for a few genes as a classical transcription factor (K14). this bookmarking and interaction with other transcriptional regulators seems to be its major task. This should be included in the introduction.
2. "DNp63a can be imported into the nucleus as a dimer" What is the evidence that DNp63a is imported as a dimer and not as a tetramer? Although functional not really relevant, because all conclusions drawn for a dimer are true for a tetramer (such as the mutation compensation), this statement (and others in the text) should either be substantiated or modified.
3. The explanation for the difference in the sensitivity of mutations in the bipartite NLS in the isolated peptide experiments and experiments with the full length DNp63a is intriguing. Unfortunately it is not based on direct exerimental evidence. To proof their model (which is the central claim of this manuscript) they should fuse the bipartite NLS to any dimerization module (e.g. a leucine zipper sequence) and show that by dimerization of the bipartite NLS the same results towards mutations are obtained as for full length DNp63a. This would strongly support their model.

Significance

Demarinis et al describe a detailed analysis of different stretches of basic amino acids located between the DBD and the OD of DNp63a to act as nuclear localization signals. They convincingly show that two stretches exist that form a bipartite NLS. They combine both functional import data with structure determination of the NLS sequence with IMP⍺ showing that both parts interact with the major and the minor site. The data are presented well provide a very good model of how nuclear important is regulated for DNp63a.

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Referee #2

Evidence, reproducibility and clarity

Summary

General assessment:

The authors show a number of generally very solid experiments that consistently support what is stated in the headline and further developed. They use wt and recombinant deltaN63alpha (N63) to sort out a previously published NLS whose inactivation did not lead to preventing nuclear localization of N63. The authors convincingly show that import is governed by a bipartite NLS. The interesting observation is that - when the bipartite stretch is transferred to GFP to drive the import, each motif is required - but the full-length protein tolerates alterations in either motif. The puzzle is solved by further structural analysis of binding of the NLS to importin alpha that shows the bipartite signal to work as expected. However, additional binding studies using BRET demonstrate dimerization that brings two copies of N63 and thus two bipartite signals together that compensate for mutations in one or the other part. Transcriptional activity of p53 can be modulated consistently with nuclear import, i.e. functional NLS motifs.

The manuscript is overall in a very mature state, and I foresee publication essentially in its present form. A few suggestions may be considered prior to publication:

1. In immunofluorescence images it is sometime difficult to see nuclear accumulation. Single channels of the GFP signal may help to make the point.
2. The binding assays in Fig. 3 would profit from using the most efficient imp a variant together with imp beta to show potential cooperative binding.
3. wording:

please mention that NTR can also recognize 3D structures of structural RNAs, e.g. tRNAs or miRNAs

longer TA isoforms

homologues or orthologues?

Significance

General assessment:

see above: this is a very consistent and mature study that can be pubslihed essentially in its present form.

Advance:

Even though the described mechanisms are not novel, they clarify how N63 is imported into human cell nuclei. We understand that in molecular mechanism and can deduce that the amounts of nuclear N63 are directly linked to its transcriptional response on p53.

Audience:

I see that this is interesting to experts in the nucleo-cytoplasmic transport field since it adds a novel aspect how robustness of import via dimerization can be reached. Beyond, the work brings news in translational research for physiology and pathology of epithelial tissue differentiation and homeostasis.

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Referee #1

Evidence, reproducibility and clarity

In this manuscript, authors performed a solid biochemical and biophysical study to identify the nuclear localization signal (NLS) of the transcription factor p63 and its regulatory mechanism. By deletion and mutagenesis experiments, the two partially overlapping NLS were identified. They were shown to have relatively minor consequences for nuclear localization when disrupted individually but the nuclear localization was abolished when both were affected. The nuclear localization was important for transactivation activity but not for dimerization. In addition, authors also performed bioinformatics analysis and showed that sequences of part of these NLS were diverse in p63 in different species. This led to the conclusion that NLS of p63 is quite robust for nuclear localization which not easily affected by sequence divergence. This is important information for the p63 field.

Major comments

The biochemical and biophysical experiments performed in this study were well designed, data were clear and the conclusions were well supported by the results. One potential improvement is to check whether NLS could affect the normal activation targets of ΔNp63α, such as KRT14 and other epithelial genes. This could complement the experiments testing the inhibition effect of ΔNp63α on p53-mediated gene activation. This will be interesting, as ΔNp63α is a master regulator in epithelial cells via regulation of diverse epithelial genes.

Major comments

The biochemical and biophysical experiments performed in this study were well designed, data were clear and the conclusions were well supported by the results. One potential improvement is to check whether NLS could affect the normal activation targets of ΔNp63α, such as KRT14 and other epithelial genes. This could complement the experiments testing the inhibition effect of ΔNp63α on p53-mediated gene activation. This will be interesting, as ΔNp63α is a master regulator in epithelial cells via regulation of diverse epithelial genes.

Minor comments

A minor suggestion: authors could consider use p63 rather than ΔNp63α in the manuscript. The heterogenous sequences of NLS regions are relevant for the delta isoform of p63. In addition, all experiments performed in the study are not necessarily specific for the biology of the ΔNp63α isoform, but they are probably informative for all p63 isoforms. Another minor suggestion: As p63 forms a tetramer when binding to DNA sequence for gene regulation, it would be good for authors to speculate the role of NLS and its variations in tetramerization.

Significance

In this manuscript, authors performed a biochemical and biophysical study on nuclear localization signal (NLS) of the transcription factor ΔNp63α, a topic that is not yet fully understood. Previous study did not yet provide sufficiently convincing evidence for NLS that is essential for ΔNp63α nuclear localization. Authors also investigated the robustness of the NLS and its function, which provides important information for the field of p63, a key factor in epithelial development and in cancer.

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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.

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Referee #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.

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.
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.
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.

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.

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Referee #1

Evidence, reproducibility and clarity

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.

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.

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?

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.

"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.

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.

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.

Page 13: why were young and old defined this way? Authors should provide their reasoning and/or citations for this grouping.

Figure 4e: It may help with interpretation to have these Sankey-like graph edges be proportional to the number of metabolites.

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.

Figure 5: "Tukey's p.adj < 0.05" . Was this a Tukey's post-hoc test? This should be explicitly stated.

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?

Please clarify if/how enrichment analyses account for varying set sizes and redundant metabolite memberships across pathways, which can bias over-representation analysis results.

Significance

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.

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.

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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.

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Referee #3

Evidence, reproducibility and clarity

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.
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.
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.

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.
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.

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.

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.

Supplemental Figure 4.

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."

Supplemental Figure 5.

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

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?

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?

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.

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?
2. Fig 2G. Please explain how the sigmoidal curves were fitted to the data points under the materials and methods section.
3. Fig 3E and F. Please refer to the comment on Fig 2G above.
4. 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.
5. 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.

Significance

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.

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Referee #2

Evidence, reproducibility and clarity

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-2 (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:

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?
2. Is there a minimal amount of Cas9 required for editing?
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?
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?
5. To rank the 763 enriched genes, they multiply the -log10FDR with their effect size - is this a standard step that is normally undertaken?
6. The 32 genes selected- they were ablated individually using constructs with one guide RNA or four guide RNAs?
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?
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?
9. As both HNRNPK and TFAP2C modulate glucose metabolism, the authors have chosen to explore the epistatic interaction. This is most reasonable.
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?
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?
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?
13. The RNA-seq comparisons- the authors use log2 FC <0.5 upregulated or genes downregulated by a similar amount- this is a very low cut off and would include essentially minimal changes in expression - not convinced of the significance of such low-level 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. 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.
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).
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. 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. 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. 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? 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. 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.

Significance

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-2 (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.

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Referee #1

Evidence, reproducibility and clarity

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

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 proximity on DNA that is linking the 2 proteins, including a DNAase treatment would clarify.

Supplemental Fig 5B - The western blot images for pAMPK don't really look like a 2 fold increase in phosphorylation in HNRNPK deletion.

Fig. 5A - I don't think it is proper to do statistics on an of 2. 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? 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. 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.

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.

Minor Comments

Page 12 - no mention of chloroquine in the text or related data.

Page 12 - Supp. Fig. E - should be 5E

Significance

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.

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Reply to the reviewers

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

Summary:

The study provides a comprehensive overview of genome size variation in two related species of the genus Epidendrum, which appear to be homoploid, although their DNA content more closely corresponds to that of heteroploid species. While I have a few serious concerns regarding the data analysis, the study itself demonstrates a well-designed approach and offers a valuable comparison of different methods for genome size estimation. In particular, I would highlight the analysis of repetitive elements, which effectively explains the observed differences between the species. However, I encourage the authors to adopt a more critical perspective on the k-mer analysis and the potential pitfalls in data interpretation.

Major comments:

R1. p. 9: Genome size estimation via flow cytometry is an incorrect approach. The deviation is approximately 19% for E. anisatum and about 25% for E. marmoratum across three repeated measurements of the same tissue over three days? These values are far beyond the accepted standards of best practice for flow cytometry, which recommend a maximum deviation of 2-5% between repeated measurements of the same individual. Such variability indicates a systemic methodological issue or improper instrument calibration. Results with this level of inconsistency cannot be considered reliable estimates of genome size obtained by flow cytometry. If you provide the raw data, I can help identify the likely source of error, but as it stands, these results are not acceptable.

__A: __Thanks a lot for pointing out this issue. We have identified the source of the wide interval after consulting with the staff of LabNalCit. We originally used human peripheral blood mononuclear cells (PBMCs) as a reference to estimate the genome size (GS) of P. sativum and used the resulting range to estimate the GS of Epidendrum. We calculated P. sativum's GS using a wide human GS range of 6-7 Gb, which resulted in a wide range of P. sativum GS and, consequently, in a wide range of GS for our samples. Therefore, the wide range reported is not an issue with the instruments, but about the specifics of the analysis.

__We have done the following changes: __

1. Reducing the range we calculated of P. sativum's GS using a narrower human genome size range (6.41-6.51; Piovesan et al. 2019; DOI: 10.1186/s13104-019-4137-z), and using these intervals to calculate our sample's GS.
2. We have explained our procedure in the methods, changed our results as required, and included a supplementary table with cytometry data (Supplementary Data Table 1).
3. Human peripheral blood mononuclear cells (PBMCs) from healthy individuals were used as a standard laboratory reference to calculate the P. sativum genome size. Pisum sativum and the Epidendrum samples were analyzed in a CytoFLEX S flow cytometer (Beckman-Coulter), individually and in combination with the internal references (PBMCs and P. sativum, respectively). Cytometry data analysis was performed using FlowJo® v. 10 (https://www.flowjo.com/). A genome size value for the Epidendrum samples was calculated as the average of the minimum and maximum 1C/2C values obtained from three replicates of the DNA content histograms of each tissue sample. Minimum and maximum values come from the interval of P. sativum estimations based on the human genome size range (human genome size range: 6.41-6.51; Piovesan et al. 2019).
4. The 1C value in gigabases (Gb; calculated from mass in pg) of E. anisatum ranged from 2.55 to 2.62 Gb (mean 1C value = 2.59 Gb) and that of E. marmoratum from 1.11 to 1.18 Gb (mean 1C value = 1.13 Gb; Supplementary Data Table S1).
5. We also eliminated from Figure 3 the range we had estimated previously.
6. Finally, we changed the focus of the comparison and discussion of the evaluation of the bioinformatic estimations, highlighting this deviation rather than whether the GS bioinformatic estimations fall within the cytometric interval. We calculated the Mean Absolute Deviation (MAD) as the absolute difference between the genome size estimates using k-mers and flow cytometry. This meant changing the results in P. 11 and 12 and adding to Fig. 3 two boxplots depicting the MAD. We have also added Supplementary Data Fig. S3 depicting the absolute deviations for E. anisatum and E. marmoratum per tool using the estimates generated from a k-mer counting with a maximum k-mer coverage value of 10,000 using 16 different values of k; a Supplementary Data Figure S5 depicting the mean absolute deviations resulting from the different subsampled simulated depths of coverage of 5×, 10×, 20×, 30×, and 40×; and finally a Supplementary Data Fig. S6 depicting the MAD changes as a function of depth of coverage for E. anisatum and E. marmoratum.

R1. p. 14 and some parts of Introduction: It may seem unusual, to say the least, to question genome size estimation in orchids using flow cytometry, given that this group is well known for extensive endoreplication. However, what effect does this phenomenon have on genome size analyses based on k-mers, or on the correct interpretation of peaks in k-mer histograms? How can such analyses be reliably interpreted when most nuclei used for DNA extraction and sequencing likely originate from endoreplicated cells? I would have expected a more detailed discussion of this issue in light of your results, particularly regarding the substantial variation in genome size estimates across different k-mer analysis settings. Could endoreplication be a contributing factor?

A:

We reworded the introduction p.3, 2nd paragraph to make our point on the effect of endoreplication on flow cytometry clearer. We eliminated the following sentence from discussion p. 15 : "Difficulties for cytometric estimation of genome size can thus be taxon-specific. Therefore, cross-validating flow cytometry and bioinformatics results can be the most effective method for estimating plant genome size, especially when only tissues suspected to show significant endoreplication, such as leaves, are available" We added the following, p. 18: Genome size estimation for non-model species is considered a highly standardized approach. However, tissue availability and intrinsic genome characteristics (large genomes, polyploidy, endoreplication, and the proportion of repetitive DNA) can still preclude genome size estimation (e.g. Kim et al. 2025) using cytometry and bioinformatic tools. Cross-validating flow cytometry and bioinformatics results might be particularly useful in those cases. For example, when only tissues suspected of showing significant conventional endoreplication, such as leaves, are available, bioinformatic tools can help to confirm that the first peak in cytometry histograms corresponds to 2C. Conversely, bioinformatic methods can be hindered by partial endoreplication, which only flow cytometry can detect.

     4. We included a paragraph discussing the effect of CE and PE on bioinformatic GS estimation P. 17:

Besides ploidy level, heterozygosity, and the proportion of repetitive DNA, k-mer distribution can be modified by endoreplication. Since endoreplication of the whole genome (CE) produces genome copies (as in preparation for cell division, but nuclear and cell division do not occur ), we do not expect an effect on genome size estimates based on k-mer analyses. In contrast, PE alters coverage of a significant proportion of the genome, affecting k-mer distributions and genome size estimates (Piet et al., 2022). Species with PE might be challenging for k-mer-based methods of genome size estimation.

R1. You repeatedly refer to the experiment on genome size estimation using analyses with maximum k-mer coverage of 10,000 and 2 million, under different k values. However, I would like to see a comparison - such as a correlation analysis - that supports this experiment. The results and discussion sections refer to it extensively, yet no corresponding figure or analysis is presented.

A:

We had previously included the results of the analyses using different k-mer coverage in the Supplementary Data Figure S2. We have added, to formally compare the results using analyses with maximum k-mer coverage of 10,000 and 2 million, a Wilcoxon paired signed-rank test, which showed a significant difference, p. 12: The estimated genome sizes using a maximum count value of 10,000 were generally lower for all tools in both species compared to using a maximum count value of 2 million (median of 2M experiment genome size - median of 10K experiment genome size= 0.24 Gb). The estimated genome size of the 2 million experiment also tended to be closer to the flow cytometry genome size estimation with significantly lower MAD than the 10K experiment (Wilcoxon paired signed-rank test p = 0.0009). In the 10K experiment (Supplementary Data Figure S2; S3), the tool with the lowest MAD for E. anisatum was findGSE-het (0.546 Gb) and for E. marmoratum it was findGSE-hom (0.116 Gb).

 2. We have added a boxplot in the Supplementary Data Figure S3 depicting the mean absolute deviations using maximum k-mer coverage of 10,000 and 2 million compared to flow cytometry.

Minor comments:

R1. p. 3: You stated: "Flow cytometry is the gold standard for genome size estimation, but whole-genome endoreplication (also known as conventional endoreplication; CE) and strict partial endoreplication (SPE) can confound this method." How did you mean this? Endopolyploidy is quite common in plants and flow cytometry is an excellent tool how to detect it and how to select the proper nuclei fraction for genome size estimation (if you are aware of possible misinterpretation caused by using inappropriate tissue for analysis). The same can be applied for partial endoreplication in orchids (see e.g. Travnicek et al 2015). Moreover, the term "strict partial endoreplication" is outdated and is only used by Brown et al. In more recent studies, the term partial endoreplication is used (e.g. Chumova et al. 2021- 10.1111/tpj.15306 or Piet et al. 2022 - 10.1016/j.xplc.2022.100330).

A:

We have reworded the paragraph where we stated "Flow cytometry is the gold standard for genome size estimation", as in the answer to Major comment 2. Additionally, we highlighted in the discussion how, while FC is the gold standard for GS estimation, studying multiple alternatives to it may be important for cases in which live tissue is not available or is available only to a limited extent (i.e. only certain tissues), p. 18 We have changed the term "strict partial endoreplication" to partial endoreplication (PE).

R1. p. 5: "...both because of its outstanding taxic diversity..." There is no such thing as "taxic" diversity - perhaps you mean taxonomic diversity or species richness.

__A: __We have changed "taxic diversity" to "species diversity".

R1. p. 6: In description of flow cytometry you stated: "Young leaves of Pisum sativum (4.45

pg/1C; Doležel et al. 1998) and peripheral blood mononuclear cells (PBMCs) from healthy

individuals...". What does that mean? Did you really use blood cells? For what purpose?

A: Please find the explanation and the modifications we've made in the answer to major comment 1.

R1. p. 7: What do you mean by this statement "...reference of low-copy nuclear genes for each species..."? As far as I know, the Granados-Mendoza study used the Angiosperm v.1 probe set, so did you use that set of probes as reference?

__A: __We rewrote: "To estimate the allele frequencies, the filtered sequences were mapped to a

reference of low-copy nuclear genes for each species" to:

To estimate the allele frequencies, the filtered sequences were mapped to the Angiosperm v.1 low-copy nuclear gene set of each species.

R1. p. 7: Chromosome counts - there is a paragraph of methodology used for chromosome counting, but no results of this important part of the study.

A: We are including a supplementary figure (Supplementary Data Figure 7) with micrographs of the chromosomes of E. anisatum and E. marmoratum.

R1. p. 12: Depth of coverage used in repeatome analysis - why did you use different coverage for both species? Any explanation is needed.

A: To make explicit the fact that the depth of coverage is determined automatically by the analysis with no consideration for the amount of input reads, but only of the graph density and the amount of RAM available (Box 3 in Novak et al. 2020), we rewrote:

"To estimate the proportion of repetitive DNA, the individual protocol analyzed reads corresponding to depths of coverage of 0.06× for Epidendrum anisatum and 0.43× for E. marmoratum." to

To estimate the proportion of repetitive DNA, the RepeatExplorer2 individual protocol determined a max number of analyzed reads (Nmax) corresponding to depths of coverage of 0.06x for Epidendrum anisatum and 0.43x for E. marmoratum.

R1. p. 16: The variation in genome size of orchids is even higher, as the highest known DNA amount has been estimated in Liparis purpureoviridis - 56.11 pg (Travnicek et al 2019 - doi: 10.1111/nph.15996)

A: We have updated it.

R1. Fig. 1 - Where is the standard peak on Fig. 1? You mention it explicitly on page 9 where you are talking about FCM histograms.

A: We reworded the results, eliminating the references to the standard internal reference.

Reviewer #1 (Significance (Required)):

Significance

This study provides a valuable contribution to understanding genome size variation in two Epidendrum species by combining flow cytometry, k-mer analysis, and repetitive element characterization. Its strength lies in the integrative approach and in demonstrating how repetitive elements can explain interspecific differences in DNA content. The work is among the first to directly compare flow cytometric and k-mer-based genome size estimates in orchids, extending current knowledge of genome evolution in this complex plant group. However, the study would benefit from a more critical discussion of the limitations and interpretative pitfalls of k-mer analysis and from addressing methodological inconsistencies in the cytometric data. The research will interest a specialized audience in plant genomics, cytogenetics, and genome evolution, particularly those studying non-model or highly endoreplicated species.

Field of expertise: plant cytogenetics, genome size evolution, orchid genomics.

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

Summary:

With this work, the authors provide genome profiling information on the Epidendrum genus. They performed low-coverage short read sequencing and analysis, as well as flow cytometry approaches to estimate genome size, and perform comparative analysis for these methods. They also used the WGS dataset to test different approaches and models for genome profiling, as well as repeat abundance estimation, empathising the importance of genome profiling to provide basic and comparative genomic information in our non-model study species. Results show that the two "closely-related" Epidendrum species analysed (E. marmoratum and E. anisatum) have different genome profiles, exhibiting a 2.3-fold genome size difference, mostly triggered by the expansion of repetitive elements in E. marmoratum, specially of Ty3-Gypsy LTR-retrotransposon and a 172 tandem repeat (satellite DNA).

Major comments:

Overall, the manuscript is well-written, the aim, results and methods are explained properly, and although I missed some information in the introduction, the paper structure is overall good, and it doesn't lack any important information. The quality of the analysis is also adequate and no further big experiments or analysis would be needed.

However, from my point of view, two main issues would need to be addressed:

__R2. __The methods section is properly detailed and well explained. However, the project data and scripts are not available at the figshare link provided, and the BioProject code provided is not found at SRA. This needs to be solved as soon as possible, as if they're not available for review reproducibility of the manuscript cannot be fully assessed.

__A: __We have made public the .histo files for all depths of coverage and cluster table files necessary to reproduce the results. We will also make public a fraction of the sequencing sufficient to reproduce our genome size and repetitive DNA results as soon as the manuscript is formally published. Whole dataset availability will be pending on the publication of the whole genome draft.

R2. The authors specify in the methods that 0.06x and 0.43x sequencing depths were used as inputs for the RE analysis of E. anisatum and E. marmoratum. I understand these are differences based on the data availability and genome size differences. However, they don't correspond to either of the recommendations from Novak et al (2020):

In the context of individual analysis: "The number of analyzed reads should correspond to 0.1-0.5× genome coverage. In the case of repeat-poor species, coverage can be increased up to 1.0-1.5×." Therefore, using 0.06x for E. anisatum should be justified, or at least addressed in the discussion.

Moreover, using such difference in coverage might affect any comparisons made using these results. Given that the amount of reads is not limiting in this case, why such specific coverages have been used should be discussed in detail.

In the context of comparative analysis: "Because different genomes are being analyzed simultaneously, the user must decide how they will be represented in the analyzed reads, choosing one of the following options. First, the number of reads analyzed from each genome will be adjusted to represent the same genome coverage. This option provides the same sensitivity of repeat detection for all analyzed samples and is therefore generally recommended; however, it requires that genome sizes of all analyzed species are known and that they do not substantially differ. In the case of large differences in genome sizes, too few reads may be analyzed from smaller genomes, especially if many species are analyzed simultaneously. A second option is to analyze the same number of reads from all samples, which will provide different depth of analysis in species differing in their genome sizes, and this fact should be considered when interpreting analysis results. Because each of these analysis setups has its advantages and drawbacks, it is a good idea to run both and cross-check their results."

Therefore, it should be confirmed how much it was used for this approach (as in the methods it is only specified how much it was used for the individual analysis), and why.

__A: __In Box 3, Novak et al (2020) explain that the number of analyzed reads (Nmax) is determined automatically by RepeatExplorer2, based on the graph density and available RAM. Therefore, the reported depths of coverage are results, not the input of the analysis. We tried different amounts of reads as input and got consistently similar results, so we kept the analysis using the whole dataset.

For the comparative analysis, we have added the resulting depth of coverage and explained that we used the same number of reads for both species.

Added to methods:

"For the comparative protocol, we used the same amount of reads for both species".

Added to results:

"To estimate the proportion of repetitive DNA, the RepeatExplorer2 individual protocol determined a maximum number of analyzed reads (Nmax) corresponding to depths of coverage of 0.06x for E. anisatum and 0.43x for E. marmoratum. "

"The RepeatExplorer2 comparative protocol determined a maximum number of analyzed reads (Nmax) corresponding to depths of coverage of approximately 0.14x for E. marmoratum and 0.06x for E. anisatum"

This is consistent with other works which utilize RepeatExplorer2, for example, Chumová et al (2021; https://doi.org/10.1111/tpj.15306), who wrote: "The final repeatome analysis for each species was done using a maximum number of reads representing between 0.049x and 1.389x of genome coverage."

Minor comments:

General comments:

• The concept of genome endoreplication and the problem it represents for C-value estimations needs to be better contextualised. It would be nice to have some background information in the introduction on how this is an issue (specially in Orchid species). Results shown are valuable and interesting but require a little more context on how frequent this is in plants, especially in Orchids, and across different tissues.

__A: __We have included information about the variation of conventional and partial endoreplication in plants.

Differences in CE may also occur between individuals or even respond to environmental factors (Barow 2006). In contrast, PE results in cells that replicate only a fraction (P) of the genome (Brown et al. 2017) and it has only been reported in Orchidaceae (Brown et al. 2017). CE and PE can occur in one or several endoreplication rounds, and different plant tissues may have different proportions of 2C, 4C, 8C ... nC or 2C, 4E, 8E, ... nE nuclear populations, respectively. The 2C nuclear population sometimes constitutes only a small fraction in differentiated somatic tissues and can be overlooked by cytometry (Trávníček et al. 2015). Using plant tissues with a high proportion of the 2C population (such as orchid ovaries and pollinaria) can help overcome this difficulty (Trávníček et al. 2015; Brown et al. 2017).

Comments and suggestions on the figures:

__R2. __In fig 1, the flow cytometry histograms need to be more self-explanatory. What are the Y axis "counts" of? Also, please either place the label for both rows or for each, but don't make it redundant. The axis fonts need to be made a bit larger too. If possible, explain briefly in the figure legend (and not only in the text) what each peak means.

__A: __We have modified the figure adding legends for Y and X axes, eliminated redundant labels, and changed the font size.

__R2. __Fig 5. Horizontal axis labels are illegible. Please make these larger (maybe make the plot wider by moving the plot legend to the top/bottom of the figure? - just a suggestion).

__A: __We consider the horizontal axis label to be superfluous and we removed it.

Small text editing suggestions:

R2. Methods, "Ploidy level estimation and chromosome counts" section. It would be easier for the reader if this paragraph were either divided into two methods sections, or into two paragraphs at least, since these are two very different approaches and provide slightly different data or information.

A: We slightly modified: "Chromosome number was counted from developing root tips" to

"Additionally, to confirm ploidy level, chromosome number was counted from developing root tips" and changed the subtitle to only "Ploidy level estimation".

R2. Methods, "Genome size estimation by k-mer analysis" section. Please specify whether the coverage simulations (of 5x to 40x) were made based on 1c or 2c of the genome size? I assumed haploid genome size but best to clarify.

A: We have added it to P7: "To assess the suitability of the whole dataset and estimate the minimum coverage required for genome size estimation, the depth of coverage of both datasets was calculated based on the flow cytometry 1C genome size values."

R2. Results, "Genome size estimation by k-mer analysis and ploidy estimation" section. In the first two paragraphs, the results presented appear to conform to anticipated patterns based on known properties of these types of datasets. Although this information confirms expected patterns, it does not provide new or biologically significant insights into the genomes analysed. It may be beneficial to further summarize these paragraphs so that the focus of this section can shift toward the comparison of methods and the biological interpretation of the genome profiles of Epidendrum.

__A: __We agree that those paragraphs deviate a little from the focus of our results. However, we believe they provide useful information both for pattern confirmation in a relatively understudied field and for readers which may not be very familiar with the methods utilized.

__R2. __Discussion, "Genome size estimation using flow cytometry" section. In the second paragraph, it is discussed how potential endoduplication events can "trick" the flow cytometry measurements. This has probably previously been discussed on other C-value calculation studies and would benefit from context from literature. How does this endoduplication really affect C-value measurements across plant taxa? I understand it is a well-known issue, so maybe add some references?

A: We have included in the Introduction information about CE and PE and their associated references. P. 3 and 4.

__R2. __Discussion, "Repetitive DNA composition in Epidendrum anisatum and E. marmoratum" section. In the second paragraph, when mentioning the relative abundance of Ty3-gypsy and Ty1-copia elements, it is also worth mentioning their differences in genomic distribution and the potential structural role of Ty3-gypsy elements.

A: We added this paragraph in P.20:

"Ty3-gypsy elements are frequently found in centromeric and pericentromeric regions, and may have an important structural role in heterochromatin (Jin et al. 2004; Neumann et al. 2011; Ma et al. 2023), particularly those with chromodomains in their structure (chromovirus, i.e. Tekay, CRM transposons; Neumann et al. 2011). Conversely, Ty1-copia elements tend to be more frequent in gene-rich regions (Wang et al. 2025A). However, Ty3-gypsy chromovirus elements can be found outside the heterochromatin regions (Neumann et al. 2011), and in Pennisetum purpureum (Poaceae) Ty1-copia elements are more common in pericentromeric regions (Yu et al. 2022)."

R2. Discussion, "Repetitive DNA composition in Epidendrum anisatum and E. marmoratum" section. In the third paragraph, it is mentioned that both species have 2n=40. I believe these are results from this work since there is a methods section for chromosome counting. This data should therefore go into results.

__A: __We have added the chromosome count micrographs as Supplementary Data Fig. S7

R2. Discussion, "Repetitive DNA composition in Epidendrum anisatum and E. marmoratum" section. I'd recommend expanding a bit more on repetitive DNA differences based on the RepeatExplorer results. Providing references on whether this has been found in other taxa would be helpful too. For example, Ogre bursts have been previously described in other species (e.g. legumes, Wang et al., 2025). Moreover, I consider worth highlighting and discussing other interesting differences found, such as the differences in unknown repeats (could be due to one species having "older" elements- too degraded to give any database hits- compared to the other), or Class II TE differences between species (and how these account less for genome size difference because of their size), etc.

A: We have rearranged and added discussion expanding on the role of repetitive DNA in E. anisatum and E. marmoratum and how it relates to the repetitive DNA in other species. This includes Ogre transposons, an expanded Ty1-copia vs. Ty3-gypsy discussion, and a section on unclassified repeats and can be found on P.19 to P.21.

Reviewer #2 (Significance (Required)):

Overall, this study provides a valuable contribution to our understanding of genome size diversity and repetitive DNA dynamics within Epidendrum, particularly through its combined use of low-coverage sequencing, flow cytometry, and comparative genome profiling. Its strongest aspects lie in the clear methodological framework and the integration of multiple complementary approaches, which together highlight substantial genome size divergence driven by repeat proliferation-an insight of clear relevance for orchid genomics and plant genome evolution more broadly.

While the work would benefit from improved data availability, additional contextualization of the problem of endoreduplication in flow cytometry, and clarification of some figure elements and methodological details, the study nonetheless advances the field by presenting new comparative genomic information for two understudied species and by evaluating different strategies for genome profiling in non-model taxa.

The primary audience will include researchers in non-model plant genomics, cytogenetics, and evolutionary biology, although the methodological comparisons may also be useful to a broader community working on genome characterization in diverse lineages. My expertise is in plant genomics, genome size evolution, and repetitive DNA biology; I am not a specialist in flow cytometry instrumentation or cytological methods, so my evaluation of those aspects is based on general familiarity rather than technical depth.

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

A review on "Nuclear genome profiling of two Mexican orchids of the genus Epidendrum" by Alcalá-Gaxiola et al. submitted to ReviewCommons

The present manuscript presented genomic data for two endemic Maxican orchids: Epidendrum anisatum and E. marmoratum. Authors aim to determine the genome size and ploidy using traditional (flow cytometry and chromosome counts) and genomic techniques (k-mer analysis, heterozygosity), along with the repetitive DNA composition characterization.

Considering the genomic composition, the main difference observed in repeat composition between the two species was attributed to the presence of a 172 bp satDNA (AniS1) in E. anisatum, which represents about 11% of its genome but is virtually absent in E. marmoratum. The differences in the genomic proportion of AniS1 and Ty3-gypsy/Ogre lineage TEs between E. anisatum and E. marmoratum are suggested as potential drivers of the GS difference identified between the two species.

Our main concern are about the GS estimation and chromosome number determination. Along with many issues related to GS estimations by flow cytometry, results related to chromosome number determination are missing on the manuscript. Improvements in both techiniques and results are crucial since authors aim to compare different methods to GS and ploidy determination.

__R3. __Genome size: Following the abstract, it is no possible to understand that authors confirm the GS by flow cytometry - as clarified after on the manuscript. Please, since the approach used to obtain the results are crucial on this manuscript, make it clear on the abstract.

A: We have highlighted the congruence of flow cytometry and bioinformatic approaches in the abstract:

"Multiple depths of coverage, k values, and k-mer-based tools for genome size estimation were explored and contrasted with cytometry genome size estimations. Cytometry and k-mer analyses yielded a consistently higher genome size for E. anisatum (mean 1C genome size = 2.59 Gb) than * E. marmoratum* (mean 1C genome size = 1.13 Gb), which represents a 2.3-fold genome size difference."

__R3.__Flow cytometry methodology: For a standard protocol, it is mandatory to use, at least, three individuals, each one analyzed on triplicate. Is is also important to check the variation among measurements obtained from the same individual and the values obtained from different individuals. Such variation should be bellow 3%. The result should be the avarege C-value following the standard deviation, what inform us the variation among individuals and measurements.

__A: __We have done three technical replicates of each tissue of the individuals of E. anisatum and E. marmoratum. To show the variation from different replicates and tissues, we have included the Supplementary Data Table S1. Intraspecific variation on genome size is beyond the scope of this work.

__R3. __Checking Fig. 1, we could not see the Pisum peack. If authors performed an analysis with external standart, it should be clarified on Methods. I suggest always use internal standard.

Besides, comparing Fig. 1 for leave and pollinium, it seems to be necessary to set up the Flow Cytoemtry equipament. Note that the 2C peack change its position when comparing different graphs. The data could be placed more central on x-axis by setting the flow cytometry.

Action Required: Considering that authors want to compare indirect genomic approaches to determine the GS, I suggest authors improve the GS determination by Flow Cytometry.

Please, on Methodology section, keep both techniques focused on GS close one another. Follow the same order on Methodology, Results and Discussion sections.

__A: __We have made several changes on the estimation and reporting of the flow cytometry genome size estimation. Among these:

We have clarified the use of the P. sativum internal standard and PBMC's in methods (P.6). We have added the associated mean coefficient of variation for both the sample and the internal reference in Supplementary Data Table S1, in order to show that the variation is not the result of an instrument error. We have changed the order of the paragraphs in the methods section to follow the order in other sections.

__R3. __Chromosome count: In Introduction section (page 5), the authors explicitly aim to provide "bioinformatics ploidy level estimation and chromosome counting." Furthermore, the Methods section (page 7, subsection "Ploidy level estimation and chromosome counts") details a specific protocol for chromosome counting involving root tip pretreatment, fixation, and staining. However, no results regarding chromosome counting are presented in the manuscript. There are no micrographs of metaphase plates, no tables with counts, and no mention of the actual counts in the Results section or Supplementary Material. Despite this absence of evidence, the Discussion (Page 18) states: "ploidy and chromosome counts of both E. anisatum and E. marmoratum are the same (2n=40)." The value of 2n=40 is presented as a finding of this study, however, there is no reference to this results.

Action Required: The authors must resolve this discrepancy by either providing the missing empirical data (micrographs and counts). This detail needs to be reviewed with greater care and scientific integrity.

__A: __We have added the chromosome count micrographs as Supplementary Data Fig. S7.

Minor reviews (Suggestions):

__R3. __Refining the Title (Optional): Although the current title is descriptive, we believe it undersells the value of the manuscript. Since this study provides the first genome profiling and repeatome characterization for the genus Epidendrum and offers important insights into the calibration of bioinformatics tools and flow cytometry for repetitive genomes, I suggest modifying the title to reflect these aspects. The comparative access of GS is also an importante feature. This would make the article more attractive to a broader audience interested in genomics of non-model organisms.

__A: __We have changed the title to "Nuclear genome profiling of two species of Epidendrum (Orchidaceae): genome size, repeatome and ploidy"

__R3. __Botanical Nomenclature (Optional): Although citing taxonomic authorities is not strictly required in all fields of plant sciences, most botanical journals expect the full author citation at the first mention of each species. Including this information would improve the nomenclatural rigor of the manuscript and align it with common practices in botanical publishing.

A: We have added the citation of the taxonomic authorities:

"This study aims to use two closely related endemic Mexican species, Epidendrum anisatum Lex and Epidendrum marmoratum A. Rich. & Galeotti, to provide the first genomic profiling for this genus..."

__R3. __Abbreviation of Genus Names: I noticed inconsistencies in the abbreviation of scientific names throughout the manuscript. Standard scientific style dictates that the full genus name (Epidendrum) should be written out only at its first mention in the Abstract and again at the first mention in the main text. Thereafter, it should be abbreviated (e.g., E. anisatum, E. marmoratum), unless the name appears at the beginning of a sentence or if abbreviation would cause ambiguity with another genus. Please revise the text to apply this abbreviation consistently.

A: We have made the changes requested as necessary.

__R3. __Genome Size Notation: In the Abstract and throughout the text, genome size estimates are presented using the statistical symbol for the mean (x). While mathematically accurate, this notation is generic and does not immediately inform the reader about the biological nature of the DNA content (i.e., whether it refers to the gametic 1C or somatic 2C value). In plant cytometry literature, it is standard practice to explicitly label these values using C-value terminology to prevent ambiguity and eliminate the effect of the number of chromosome sets (Bennett & Leitch 2005; Greilhuber et al. 2005; Doležel et al. 2018). I strongly suggest replacing references to "x" with "1C" (e.g., changing "x = 2.58 Gb" to "mean 1C value = 2.58 Gb") to ensure immediate clarity and alignment with established conventions in the field.

__A: __We have revised the text in every instance, for example, in the results section:

"The 1C value in gigabases (Gb; calculated from mass in pg) of E. anisatum ranged from 2.55 to 2.62 Gb (mean 1C value = 2.59 Gb) and that of E. marmoratum from 1.11 to 1.18 Gb (mean 1C value = 1.13 Gb; Supplementary Data Table S1)."

__R3. __Justification of the Sequencing Method: Although the sequencing strategy is clearly described, the manuscript would benefit from a bit more contextualization regarding the choice of low-pass genome skimming. In the Introduction, a short justification of why this approach is suitable for estimating genome size, heterozygosity, and repeat composition, particularly in plants with large, repeat-rich genomes, would help readers better understand the methodological rationale. Likewise, in the Methods section, briefly outlining why the selected sequencing depth is appropriate, and how it aligns with previous studies using similar coverage levels, would strengthen the clarity of the methodological framework. These additions would make the rationale behind the sequencing approach more transparent and accessible to readers who may be less familiar with low-coverage genomic strategies.

__A: __We have added the following short sentence in P.7:

"This sequencing method produces suitable data sets without systematic biases, allowing the estimation of genome size and the proportion of repetitive DNA. "

__R3. __Wording Improvement Regarding RepeatExplorer2 Results: In the Results section, several sentences attribute biological outcomes to the RepeatExplorer2 "protocols" (e.g., "According to this protocol, both species have highly repetitive genomes..."; "The comparative protocol showed a 67% total repeat proportion, which falls between the estimated repeat proportions of the two species according to the results of the individual protocol"). Since the RepeatExplorer2 protocol itself only provides the analytical workflow and not species-specific results, this phrasing may be misleading.

A: We have rephrased these sections to emphasize that these are "the results of" the protocols and not the protocols themselves.

Reviewer #3 (Significance (Required)):

Significance

General assessment

Strengths

1.First Detailed Genomic Profile for the Genus Epidendrum: The study provides the first integrated dataset on genome size, ploidy, heterozygosity, and repeatome for species of the genus Epidendrum, a novel contribution for an extremely diverse and under-explored group in terms of cytogenomics.

Cross-validation of in vitro and in silico analyses: Flow cytometry is considered the gold standard for genome size (GS) estimation because it physically measures DNA quantity (Doležel et al. 2007; Śliwińska 2018). However, it typically requires fresh tissue, which is not always available. Conversely, k-mer analysis is a rapid bioinformatics technique utilizing sequencing data that does not rely on a reference genome. Nevertheless, it is frequently viewed with skepticism or distrust due to discrepancies with laboratory GS estimates (Pflug et al. 2020; Hesse 2023). In this study, by comparing computational results with flow cytometry data, the authors were able to validate the reliability of computational estimates for the investigated species. Since the 'true' GS was already established via flow cytometry, the authors used this value as a benchmark to test various software tools (GenomeScope, findGSE, CovEst) and parameters. This approach allowed for the identification of which tools perform best for complex genomes. For instance, they found that tools failing to account for heterozygosity (such as findGSE-hom) drastically overestimated the genome size of E. anisatum, whereas GenomeScope and findGSE-het (which account for heterozygosity) yielded results closer to the flow cytometry values. Thus, they demonstrated that this cross-validation is an effective method for estimating plant genome sizes with greater precision. This integrative approach is essential not only for defining GS but also for demonstrating how bioinformatics methods must be calibrated (particularly regarding depth of coverage and maximum k-mer coverage) to provide accurate data for non-model organisms when flow cytometry is not feasible.

Limitations

1. Limited Taxonomic Sampling: The study analyzes only two species of Epidendrum, which restricts the ability to make broad inferences regarding genome evolution across the genus. Given the outstanding diversity of Epidendrum (>1,800 species), the current sampling is insufficient to propose generalized evolutionary patterns. As the authors state by the end of the Discussion (page 18) "Future work should investigate to what extent LTR transposons and satellite DNA have been responsible for shaping genome size variation in different lineages of Epidendrum, analyzing a greater portion of its taxic diversity in an evolutionary context.". 2.Lack of Cytogenetic Results and Mapping: One of the major finding of this study is the identification of the AniS1 satellite as a potential key driver of the genome size difference between the species, occupying ~11% of the E. anisatum genome and virtually absent in E. marmoratum. While the authors use bioinformatic metrics (C and P indices) to infer a dispersed organization in the Discussion (Page 18), the study lacks physical validation via Fluorescence in situ Hybridization (FISH) - and a basic validation of the chromosome number. Without cytogenetic mapping, it is impossible to confirm the actual chromosomal distribution of this massive repetitive array, for instance, whether it has accumulated in specific heterochromatic blocks (e.g., centromeric or subtelomeric regions) or if it is genuinely interspersed along the chromosome arms. I suggest acknowledging this as a limitation in the Discussion, as the physical organization of such abundant repeats has significant implications for understanding the structural evolution of the species' chromosomes.

Advance

To the best of our knowledge, this study represents the first comprehensive genome profiling and repeatome characterization for any species of the genus Epidendrum. By integrating flow cytometry, k-mer-based approaches, and low-pass sequencing, the authors provide the first insights into the genomic architecture of Epidendrum, including quantitative assessments of transposable elements, lineage-specific satellite DNA, and repeat-driven genome expansion. This constitutes both a technical and a conceptual advance: technically, the study demonstrates the feasibility and limitations of combining in vitro and in silico methods for genome characterization in large, repeat-rich plant genomes; conceptually, it offers new evolutionary perspectives on how repetitive elements shape genome size divergence within a highly diverse orchid lineage. These results broaden the genomic knowledge base for Neotropical orchids and establish a foundational reference for future comparative, cytogenomic, and phylogenomic studies within Epidendrum and related groups.

Audience

This study will primarily interest a broad audience, including researchers in plant genomics, evolutionary biology, cytogenomics, and bioinformatics, especially those working with non-model plants or groups with large, repetitive genomes. It also holds relevance for scientists engaged in genome size evolution, repetitive DNA biology, and comparative genomics. Other researchers are likely to use this work as a methodological reference for genome profiling in non-model taxa, especially regarding the integration of flow cytometry and k-mer-based estimations and the challenges posed by highly repetitive genomes. The detailed repeatome characterization, including identification of lineage-specific satellites and retrotransposon dynamics, will support comparative genomic analyses, repeat evolution studies, and future cytogenetic validation (e.g., FISH experiments). Additionally, this dataset establishes a genomic baseline that can inform phylogenomic studies, species delimitation, and evolutionary inference within Epidendrum and related orchid groups.

Reviewer's Backgrounds

The review was prepared by two reviewers. Our expertise lies in evolution and biological diversity, with a focus on cytogenomic and genome size evolution. Among the projects in development, the cytogenomics evolution of Neotropical orchids is one of the main studies (also focused on Epidendrum). These areas shape my perspective in evaluating the evolutionary, cytogenomic, and biological implications of the study. However, we have limited expertise in methodologies related to k-mer-based genome profiling and heterozygosity modeling. Therefore, our evaluation does not deeply assess the technical validity of these analytical pipelines.

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Referee #3

Evidence, reproducibility and clarity

A review on "Nuclear genome profiling of two Mexican orchids of the genus Epidendrum" by Alcalá-Gaxiola et al. submitted to ReviewCommons

The present manuscript presented genomic data for two endemic Maxican orchids: Epidendrum anisatum and E. marmoratum. Authors aim to determine the genome size and ploidy using traditional (flow cytometry and chromosome counts) and genomic techniques (k-mer analysis, heterozygosity), along with the repetitive DNA composition characterization.

Considering the genomic composition, the main difference observed in repeat composition between the two species was attributed to the presence of a 172 bp satDNA (AniS1) in E. anisatum, which represents about 11% of its genome but is virtually absent in E. marmoratum. The differences in the genomic proportion of AniS1 and Ty3-gypsy/Ogre lineage TEs between E. anisatum and E. marmoratum are suggested as potential drivers of the GS difference identified between the two species.

Our main concern are about the GS estimation and chromosome number determination. Along with many issues related to GS estimations by flow cytometry, results related to chromosome number determination are missing on the manuscript. Improvements in both techiniques and results are crucial since authors aim to compare different methods to GS and ploidy determination.

Genome size: Following the abstract, it is no possible to understand that authors confirm the GS by flow cytometry - as clarified after on the manuscript. Please, since the approach used to obtain the results are crucial on this manuscript, make it clear on the abstract. Flow cytometry methodology: For a standart protocol, it is mandatory to use, at least, three individuals, each one analyzed on triplicate. Is is also important to check the variation among measurements obtained from the same individual and the values obtained from different individuals. Such variation should be bellow 3%. The result should be the avarege C-value following the standard deviation, what inform us the variation among individuals and measurements. Checking Fig. 1, we could not see the Pisum peack. If authors performed an analysis with external standart, it should be clarified on Methods. I suggest always use internal standard. Besides, comparing Fig. 1 for leave and pollinium, it seems to be necessary to set up the Flow Cytoemtry equipament. Note that the 2C peack change its position when comparing different graphs. The data could be placed more central on x-axis by setting the flow cytometry. Action Required: Considering that authors want to compare indirect genomic approaches to determine the GS, I suggest authors improve the GS determination by Flow Cytometry. Please, on Methodology section, keep both techniques focused on GS close one another. Follow the same order on Methodology, Results and Discussion sections.

Chromosome count: In Introduction section (page 5), the authors explicitly aim to provide "bioinformatics ploidy level estimation and chromosome counting." Furthermore, the Methods section (page 7, subsection "Ploidy level estimation and chromosome counts") details a specific protocol for chromosome counting involving root tip pretreatment, fixation, and staining. However, no results regarding chromosome counting are presented in the manuscript. There are no micrographs of metaphase plates, no tables with counts, and no mention of the actual counts in the Results section or Supplementary Material. Despite this absence of evidence, the Discussion (Page 18) states: "ploidy and chromosome counts of both E. anisatum and E. marmoratum are the same (2n=40)." The value of 2n=40 is presented as a finding of this study, however, there is no reference to this results. Action Required: The authors must resolve this discrepancy by either providing the missing empirical data (micrographs and counts). This detail needs to be reviewed with greater care and scientific integrity. Minor reviews (Sugestions): Refining the Title (Optional): Although the current title is descriptive, we believe it undersells the value of the manuscript. Since this study provides the first genome profiling and repeatome characterization for the genus Epidendrum and offers important insights into the calibration of bioinformatics tools and flow cytometry for repetitive genomes, I suggest modifying the title to reflect these aspects. The comparative access of GS is also an importante feature. This would make the article more attractive to a broader audience interested in genomics of non-model organisms. 

Botanical Nomenclature (Optional): Although citing taxonomic authorities is not strictly required in all fields of plant sciences, most botanical journals expect the full author citation at the first mention of each species. Including this information would improve the nomenclatural rigor of the manuscript and align it with common practices in botanical publishing.

Abbreviation of Genus Names: I noticed inconsistencies in the abbreviation of scientific names throughout the manuscript. Standard scientific style dictates that the full genus name (Epidendrum) should be written out only at its first mention in the Abstract and again at the first mention in the main text. Thereafter, it should be abbreviated (e.g., E. anisatum, E. marmoratum), unless the name appears at the beginning of a sentence or if abbreviation would cause ambiguity with another genus. Please revise the text to apply this abbreviation consistently.

Genome Size Notation: In the Abstract and throughout the text, genome size estimates are presented using the statistical symbol for the mean (x). While mathematically accurate, this notation is generic and does not immediately inform the reader about the biological nature of the DNA content (i.e., whether it refers to the gametic 1C or somatic 2C value). In plant cytometry literature, it is standard practice to explicitly label these values using C-value terminology to prevent ambiguity and eliminate the effect of the number of chromosome sets (Bennett & Leitch 2005; Greilhuber et al. 2005; Doležel et al. 2018). I strongly suggest replacing references to "x" with "1C" (e.g., changing "x = 2.58 Gb" to "mean 1C value = 2.58 Gb") to ensure immediate clarity and alignment with established conventions in the field.

Justification of the Sequencing Method: Although the sequencing strategy is clearly described, the manuscript would benefit from a bit more contextualization regarding the choice of low-pass genome skimming. In the Introduction, a short justification of why this approach is suitable for estimating genome size, heterozygosity, and repeat composition, particularly in plants with large, repeat-rich genomes, would help readers better understand the methodological rationale. Likewise, in the Methods section, briefly outlining why the selected sequencing depth is appropriate, and how it aligns with previous studies using similar coverage levels, would strengthen the clarity of the methodological framework. These additions would make the rationale behind the sequencing approach more transparent and accessible to readers who may be less familiar with low-coverage genomic strategies.

Wording Improvement Regarding RepeatExplorer2 Results: In the Results section, several sentences attribute biological outcomes to the RepeatExplorer2 "protocols" (e.g., "According to this protocol, both species have highly repetitive genomes..."; "The comparative protocol showed a 67% total repeat proportion, which falls between the estimated repeat proportions of the two species according to the results of the individual protocol"). Since the RepeatExplorer2 protocol itself only provides the analytical workflow and not species-specific results, this phrasing may be misleading.

Significance

General assessment

Strengths

1. First Detailed Genomic Profile for the Genus Epidendrum: The study provides the first integrated dataset on genome size, ploidy, heterozygosity, and repeatome for species of the genus Epidendrum, a novel contribution for an extremely diverse and under-explored group in terms of cytogenomics.
2. Cross-validation of in vitro and in silico analyses: Flow cytometry is considered the gold standard for genome size (GS) estimation because it physically measures DNA quantity (Doležel et al. 2007; Śliwińska 2018). However, it typically requires fresh tissue, which is not always available. Conversely, k-mer analysis is a rapid bioinformatics technique utilizing sequencing data that does not rely on a reference genome. Nevertheless, it is frequently viewed with skepticism or distrust due to discrepancies with laboratory GS estimates (Pflug et al. 2020; Hesse 2023). In this study, by comparing computational results with flow cytometry data, the authors were able to validate the reliability of computational estimates for the investigated species. Since the 'true' GS was already established via flow cytometry, the authors used this value as a benchmark to test various software tools (GenomeScope, findGSE, CovEst) and parameters. This approach allowed for the identification of which tools perform best for complex genomes. For instance, they found that tools failing to account for heterozygosity (such as findGSE-hom) drastically overestimated the genome size of E. anisatum, whereas GenomeScope and findGSE-het (which account for heterozygosity) yielded results closer to the flow cytometry values. Thus, they demonstrated that this cross-validation is an effective method for estimating plant genome sizes with greater precision. This integrative approach is essential not only for defining GS but also for demonstrating how bioinformatics methods must be calibrated (particularly regarding depth of coverage and maximum k-mer coverage) to provide accurate data for non-model organisms when flow cytometry is not feasible.

Limitations

1. Limited Taxonomic Sampling: The study analyzes only two species of Epidendrum, which restricts the ability to make broad inferences regarding genome evolution across the genus. Given the outstanding diversity of Epidendrum (>1,800 species), the current sampling is insufficient to propose generalized evolutionary patterns. As the authors state by the end of the Discussion (page 18) "Future work should investigate to what extent LTR transposons and satellite DNA have been responsible for shaping genome size variation in different lineages of Epidendrum, analyzing a greater portion of its taxic diversity in an evolutionary context.".
2. Lack of Cytogenetic Results and Mapping: One of the major finding of this study is the identification of the AniS1 satellite as a potential key driver of the genome size difference between the species, occupying ~11% of the E. anisatum genome and virtually absent in E. marmoratum. While the authors use bioinformatic metrics (C and P indices) to infer a dispersed organization in the Discussion (Page 18), the study lacks physical validation via Fluorescence in situ Hybridization (FISH) - and a basic validation of the chromosome number. Without cytogenetic mapping, it is impossible to confirm the actual chromosomal distribution of this massive repetitive array, for instance, whether it has accumulated in specific heterochromatic blocks (e.g., centromeric or subtelomeric regions) or if it is genuinely interspersed along the chromosome arms. I suggest acknowledging this as a limitation in the Discussion, as the physical organization of such abundant repeats has significant implications for understanding the structural evolution of the species' chromosomes.

Advance

To the best of our knowledge, this study represents the first comprehensive genome profiling and repeatome characterization for any species of the genus Epidendrum. By integrating flow cytometry, k-mer-based approaches, and low-pass sequencing, the authors provide the first insights into the genomic architecture of Epidendrum, including quantitative assessments of transposable elements, lineage-specific satellite DNA, and repeat-driven genome expansion. This constitutes both a technical and a conceptual advance: technically, the study demonstrates the feasibility and limitations of combining in vitro and in silico methods for genome characterization in large, repeat-rich plant genomes; conceptually, it offers new evolutionary perspectives on how repetitive elements shape genome size divergence within a highly diverse orchid lineage. These results broaden the genomic knowledge base for Neotropical orchids and establish a foundational reference for future comparative, cytogenomic, and phylogenomic studies within Epidendrum and related groups.

Audience

This study will primarily interest a broad audience, including researchers in plant genomics, evolutionary biology, cytogenomics, and bioinformatics, especially those working with non-model plants or groups with large, repetitive genomes. It also holds relevance for scientists engaged in genome size evolution, repetitive DNA biology, and comparative genomics. Other researchers are likely to use this work as a methodological reference for genome profiling in non-model taxa, especially regarding the integration of flow cytometry and k-mer-based estimations and the challenges posed by highly repetitive genomes. The detailed repeatome characterization, including identification of lineage-specific satellites and retrotransposon dynamics, will support comparative genomic analyses, repeat evolution studies, and future cytogenetic validation (e.g., FISH experiments). Additionally, this dataset establishes a genomic baseline that can inform phylogenomic studies, species delimitation, and evolutionary inference within Epidendrum and related orchid groups.

Reviewer's Backgrounds

The review was prepared by two reviewers. Our expertise lies in evolution and biological diversity, with a focus on cytogenomic and genome size evolution. Among the projects in development, the cytogenomics evolution of Neotropical orchids is one of the main studies (also focused on Epidendrum). These areas shape my perspective in evaluating the evolutionary, cytogenomic, and biological implications of the study. However, we have limited expertise in methodologies related to k-mer-based genome profiling and heterozygosity modeling. Therefore, our evaluation does not deeply assess the technical validity of these analytical pipelines.

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

Summary:

With this work, the authors provide genome profiling information on the Epidendrum genus. They performed low-coverage short read sequencing and analysis, as well as flow cytometry approaches to estimate genome size, and perform comparative analysis for these methods. They also used the WGS dataset to test different approaches and models for genome profiling, as well as repeat abundance estimation, empathising the importance of genome profiling to provide basic and comparative genomic information in our non-model study species. Results show that the two "closely-related" Epidendrum species analysed (E. marmoratum and E. anisatum) have different genome profiles, exhibiting a 2.3-fold genome size difference, mostly triggered by the expansion of repetitive elements in E. marmoratum, specially of Ty3-Gypsy LTR-retrotransposon and a 172 tandem repeat (satellite DNA).

Major comments:

Overall, the manuscript is well-written, the aim, results and methods are explained properly, and although I missed some information in the introduction, the paper structure is overall good, and it doesn't lack any important information. The quality of the analysis is also adequate and no further big experiments or analysis would be needed. However, from my point of view, two main issues would need to be addressed:

• The methods section is properly detailed and well explained. However, the project data and scripts are not available at the figshare link provided, and the BioProject code provided is not found at SRA. This needs to be solved as soon as possible, as if they're not available for review reproducibility of the manuscript cannot be fully assessed.
• The authors specify in the methods that 0.06x and 0.43x sequencing depths were used as inputs for the RE analysis of E. anisatum and E. marmoratum. I understand these are differences based on the data availability and genome size differences. However, they don't correspond to either of the recommendations from Novak et al (2020):

In the context of individual analysis: "The number of analyzed reads should correspond to 0.1-0.5× genome coverage. In the case of repeat-poor species, coverage can be increased up to 1.0-1.5×." Therefore, using 0.06x for E. anisatum should be justified, or at least addressed in the discussion. Moreover, using such difference in coverage might affect any comparisons made using these results. Given that the amount of reads is not limiting in this case, why such specific coverages have been used should be discussed in detail.

In the context of comparative analysis: "Because different genomes are being analyzed simultaneously, the user must decide how they will be represented in the analyzed reads, choosing one of the following options. First, the number of reads analyzed from each genome will be adjusted to represent the same genome coverage. This option provides the same sensitivity of repeat detection for all analyzed samples and is therefore generally recommended; however, it requires that genome sizes of all analyzed species are known and that they do not substantially differ. In the case of large differences in genome sizes, too few reads may be analyzed from smaller genomes, especially if many species are analyzed simultaneously. A second option is to analyze the same number of reads from all samples, which will provide different depth of analysis in species differing in their genome sizes, and this fact should be considered when interpreting analysis results. Because each of these analysis setups has its advantages and drawbacks, it is a good idea to run both and cross-check their results." Therefore, it should be confirmed how much it was used for this approach (as in the methods it is only specified how much it was used for the individual analysis), and why.

Minor comments:

General comments:

• The concept of genome endoreplication and the problem it represents for C-value estimations needs to be better contextualised. It would be nice to have some background information in the introduction on how this is an issue (specially in Orchid species). Results shown are valuable and interesting but require a little more context on how frequent this is in plants, especially in Orchids, and across different tissues.

Comments and suggestions on the figures:

• In fig 1, the flow cytometry histograms need to be more self-explanatory. What are the Y axis "counts" of? Also, please either place the label for both rows or for each, but don't make it redundant. The axis fonts need to be made a bit larger too. If possible, explain briefly in the figure legend (and not only in the text) what each peak means.
• Fig 5. Horizontal axis labels are illegible. Please make these larger (maybe make the plot wider by moving the plot legend to the top/bottom of the figure? - just a suggestion).

Small text editing suggestions:

• Methods, "Ploidy level estimation and chromosome counts" section. It would be easier for the reader if this paragraph was either divided into two methods sections, or into two paragraphs at least, since these are two very different approaches and provide slightly different data or information.
• Methods, "Genome size estimation by k-mer analysis" section. Please specify whether the coverage simulations (of 5x to 40x) were made based on 1c or 2c of the genome size? I assumed haploid genome size but best to clarify.
• Results, "Genome size estimation by k-mer analysis and ploidy estimation" section. In the first two paragraphs, the results presented appear to conform to anticipated patterns based on known properties of these types of datasets. Although this information confirms expected patterns, it does not provide new or biologically significant insights into the genomes analysed. It may be beneficial to further summarize these paragraphs so that the focus of this section can shift toward the comparison of methods and the biological interpretation of the genome profiles of Epidendrum.
• Discussion, "Genome size estimation using flow cytometry" section. In the second paragraph, it is discussed how potential endoduplication events can "trick" the flow cytometry measurements. This has probably previously been discussed on other C-value calculation studies and would benefit from context from literature. How does this endoduplication really affect C-value measurements across plant taxa? I understand it is a well-known issue, so maybe add some references?
• Discussion, "Repetitive DNA composition in Epidendrum anisatum and E. marmoratum" section. In the second paragraph, when mentioning the relative abundance of Ty3-gypsy and Ty1-copia elements, it is also worth mentioning their differences in genomic distribution and the potential structural role of Ty3-gypsy elements.
• Discussion, "Repetitive DNA composition in Epidendrum anisatum and E. marmoratum" section. In the third paragraph, it is mentioned that both species have 2n=40. I believe these are results from this work since there is a methods section for chromosome counting. This data should therefore go into results.
• Discussion, "Repetitive DNA composition in Epidendrum anisatum and E. marmoratum" section. I'd recommend expanding a bit more on repetitive DNA differences based on the RepeatExplorer results. Providing references on whether this has been found in other taxa would be helpful too. For example, Ogre bursts have been previously described in other species (e.g. legumes, Wang et al., 2025). Moreover, I consider worth highlighting and discussing other interesting differences found, such as the differences in unknown repeats (could be due to one species having "older" elements- too degraded to give any database hits- compared to the other), or Class II TE differences between species (and how these account less for genome size difference because of their size), etc.

Significance

Overall, this study provides a valuable contribution to our understanding of genome size diversity and repetitive DNA dynamics within Epidendrum, particularly through its combined use of low-coverage sequencing, flow cytometry, and comparative genome profiling. Its strongest aspects lie in the clear methodological framework and the integration of multiple complementary approaches, which together highlight substantial genome size divergence driven by repeat proliferation-an insight of clear relevance for orchid genomics and plant genome evolution more broadly.

While the work would benefit from improved data availability, additional contextualization of the problem of endoreduplication in flow cytometry, and clarification of some figure elements and methodological details, the study nonetheless advances the field by presenting new comparative genomic information for two understudied species and by evaluating different strategies for genome profiling in non-model taxa.

The primary audience will include researchers in non-model plant genomics, cytogenetics, and evolutionary biology, although the methodological comparisons may also be useful to a broader community working on genome characterization in diverse lineages. My expertise is in plant genomics, genome size evolution, and repetitive DNA biology; I am not a specialist in flow cytometry instrumentation or cytological methods, so my evaluation of those aspects is based on general familiarity rather than technical depth.

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Referee #1

Evidence, reproducibility and clarity

Summary:

The study provides a comprehensive overview of genome size variation in two related species of the genus Epidendrum, which appear to be homoploid, although their DNA content more closely corresponds to that of heteroploid species. While I have a few serious concerns regarding the data analysis, the study itself demonstrates a well-designed approach and offers a valuable comparison of different methods for genome size estimation. In particular, I would highlight the analysis of repetitive elements, which effectively explains the observed differences between the species. However, I encourage the authors to adopt a more critical perspective on the k-mer analysis and the potential pitfalls in data interpretation.

Major comments:

p. 9: Genome size estimation via flow cytometry is an incorrect approach. The deviation is approximately 19% for E. anisatum and about 25% for E. marmoratum across three repeated measurements of the same tissue over three days? These values are far beyond the accepted standards of best practice for flow cytometry, which recommend a maximum deviation of 2-5% between repeated measurements of the same individual. Such variability indicates a systemic methodological issue or improper instrument calibration. Results with this level of inconsistency cannot be considered reliable estimates of genome size obtained by flow cytometry. If you provide the raw data, I can help identify the likely source of error, but as it stands, these results are not acceptable.

p. 14 and some parts of Introduction: It may seem unusual, to say the least, to question genome size estimation in orchids using flow cytometry, given that this group is well known for extensive endoreplication. However, what effect does this phenomenon have on genome size analyses based on k-mers, or on the correct interpretation of peaks in k-mer histograms? How can such analyses be reliably interpreted when most nuclei used for DNA extraction and sequencing likely originate from endoreplicated cells? I would have expected a more detailed discussion of this issue in light of your results, particularly regarding the substantial variation in genome size estimates across different k-mer analysis settings. Could endoreplication be a contributing factor?

You repeatedly refer to the experiment on genome size estimation using analyses with maximum k-mer coverage of 10,000 and 2 million, under different k values. However, I would like to see a comparison - such as a correlation analysis - that supports this experiment. The results and discussion sections refer to it extensively, yet no corresponding figure or analysis is presented.

Minor comments:

p. 3: You stated: "Flow cytometry is the gold standard for genome size estimation, but whole-genome endoreplication (also known as conventional endoreplication; CE) and strict partial endoreplication (SPE) can confound this method." How did you mean this? Endopolyploidy is quite common in plants and flow cytometry is an excellent tool how to detect it and how to select the proper nuclei fraction for genome size estimation (if you are aware of possible misinterpretation caused by using inappropriate tissue for analysis). The same can be applied for partial endoreplication in orchids (see e.g. Travnicek et al 2015). Moreover, the term "strict partial endoreplication" is outdated and is only used by Brwon et al. In more recent studies, the term partial endoreplication is used (e.g. Chumova et al. 2021- 10.1111/tpj.15306 or Piet et al. 2022 - 10.1016/j.xplc.2022.100330).

p. 5: "...both because of its outstanding taxic diversity..." There is no such thing as "taxic" diversity - perhaps you mean taxonomic diversity or species richness.

p. 6: In description of flow cytometry you stated: "Young leaves of Pisum sativum (4.45 pg/1C; Doležel et al. 1998) and peripheral blood mononuclear cells (PBMCs) from healthy individuals...". What does that mean? Did you really use blood cells? For what purpose?

p. 7: What do you mean by this statement "...reference of low-copy nuclear genes for each species..."? As far as I know, the Granados-Mendoza study used the Angiosperm v.1 probe set, so did you use that set of probes as reference?

p. 7: Chromosome counts - there is a paragraph of methodology used for chromosome counting, but no results of this important part of the study.

p. 12: Depth of coverage used in repeatome analysis - why did you use different coverage for both species? Any explanation is needed.

p. 16: The variation in genome size of orchids is even higher, as the highest known DNA amount has been estimated in Liparis purpureoviridis - 56.11 pg (Travnicek et al 2019 - doi: 10.1111/nph.15996)

Fig. 1 - Where is the standard peak on Fig. 1? You mention it explicitly on page 9 where you are talking about FCM histograms.

Significance

This study provides a valuable contribution to understanding genome size variation in two Epidendrum species by combining flow cytometry, k-mer analysis, and repetitive element characterization. Its strength lies in the integrative approach and in demonstrating how repetitive elements can explain interspecific differences in DNA content. The work is among the first to directly compare flow cytometric and k-mer-based genome size estimates in orchids, extending current knowledge of genome evolution in this complex plant group. However, the study would benefit from a more critical discussion of the limitations and interpretative pitfalls of k-mer analysis and from addressing methodological inconsistencies in the cytometric data. The research will interest a specialized audience in plant genomics, cytogenetics, and genome evolution, particularly those studying non-model or highly endoreplicated species.

Field of expertise: plant cytogenetics, genome size evolution, orchid genomics.

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Reply to the reviewers

Manuscript number: RC-2025-03131

Corresponding author(s): Ginto George and Adriana Ordoñez

1. General Statements

We thank the reviewers for their careful evaluation of our work and for their constructive and insightful comments. We are pleased that both reviewers found the study to be well executed, clearly presented, and of interest to the ER stress and UPR community. We have carefully considered all comments and revised the manuscript accordingly. We believe these revisions have substantially strengthened the clarity, robustness, and conceptual impact of the study.

2. Point-by-point description of the revisions

Below we provide a detailed, point-by-point response to the reviewers' comments and describe the revisions and new data included in the revised manuscript.

Reviewer 1 & 2 (common points)

1. __ Description of the BiP::GFP reporter as a readout of ATF6α activity.__
2. Comment: Both reviewers are concerned about whether BiP::GFP is a reliable and specific reporter for ATF6α
3. Response: In response, we have clarified in the revised manuscript the details of the BiP promoter fragment used in this reporter, explicitly detailing the presence of an ERSE-I element motif (CCAAT-N9-CCACG), the most specifically and robustly activated by ATF6α (new Supplemental Fig. S1). This reporter was first characterised in our recently published study (Tung et al., 2024 eLife), where we demonstrated that BiP::GFP expression is ATF6α dependent, as CRISPR/Cas9-mediated disruption of endogenous ATF6α resulted in a marked reduction in BiP::GFP fluorescence compared with parental cells. Furthermore, treatment with ER stress in the presence of Ceapin-A7 (a small molecule that blocks ATF6⍺ activation by tethering it to the lysosome) effectively blocked activation of the ATF6⍺ fluorescent reporter, whereas the S1P inhibitor partially attenuated the BiP::sfGFP signal in stressed cells (Tung et al., 2024 eLife; Supplemental S1D). We have now reproduced these findings in the present study, further confirming that the BiP::GFP reporter is highly dependent on ATF6α activation, and we present these data in a new Supplemental Fig. S1B.

__ Correlation between BiP::GFP reporter activity and BiP expression levels.__

• Comment: Both reviewers requested correlation of the BiP::GFP reporter activity and endogenous BiP levels.
• __Response: __To address this point, we have measured BiP mRNA levels in parental and Slc33a1-depleted cells under both basal conditions and ER stress conditions. These measurements correlated well with the BiP::GFP reporter activity assessed by flow cytometry and are shown in Supplemental Fig. S3E.

__ Does ATF6α respond to other ER stressors in Slc33a1-deleted cells?__

• Comment: Both reviewers accepted our claim that ATF6α activation is partially attenuated in Slc33a1-deleted cells exposed to ER stressors tunicamycin (Tm) and 2-Deoxy-D-glucose (2DG) but raised the possibility that ATF6α signalling might respond differently to other ER stressors.
• Response: To address this point, we have performed new experiments assessing ATF6α activation (BiP::GFP activity) in both Slc33a1-deleted and parental cells in response to additional ER stressors, including dithiothreitol (DTT) and thapsigargin (Tg). These new data, presented in a new Supplemental Fig. S3B and S3C, show that Slc33a1-deletion also attenuates ATF6α signalling in cells treated with dithiothreitol (DTT) and thapsigargin (Tg).

__ Deletion of all NAT8 family members.__

• Comment: Both reviewers suggested that deletion of all NAT8 family members was required to conclusively distinguish their role from that of SLC33A1.
• __Response: __We agree with this assessment and have now generated cells in which both Nat8 and Nat8b are simultaneously deleted. These new data, included in a new Supplemental Fig. S9, strengthen the comparison with SLC33A1 deficiency and rule out potential redundancy among NAT8 family members. Notably, simultaneous inactivation of Nat8 and Nat8b resulted in the same phenotype observed upon single Nat8 deletion, namely activation of both the IRE1 and ATF6α branches of the UPR. These findings (discussed in detail) are consistent with previous studies implicating protein acetylation in ER proteostasis but suggest that a defect in protein acetylation is unlikely to contribute to the consequences of SLC33A1 deficiency in terms of ATF6α

__ Generalisability beyond CHO-K1 cells.__

• Comment: Reviewer 1 raised concerns regarding validation of our findings beyond CHO-K1 cells.
• Response: While we acknowledge that validation in additional cell types would further strengthen the study, we now explicitly discuss the technical challenges encountered when attempting to generate clonal Slc33a1 knockouts in aneuploid human cell lines, such as HeLa. This limitation is now clearly acknowledged in the revised version, and our conclusions are framed accordingly.

__ Relationship between basal ATF6 and IRE1 signalling.__

• Comment: Both reviewers argued that BiP::GFP does not appear to be active under basal conditions in parental cells, and therefore a failure to activate ATF6 would not be expected to affect the conditions of the cells basally. Thereby questioning how attenuated basal ATF6 activity in the SLC33a1 deleted cells could account for the derepression observed in the IRE1 pathway.

• Response: The logic of the reviewer's critique is impeccable, and we thank them for the opportunity to clarify this important issue. Whilst the basal fluorescent signal arising from BiP::GFP (the ATF6α reporter) is indeed weak, it is not null. This is evident by comparing the BiP::GFP signal in wildtype and ATF6α -deleted cells (new Supplemental Fig. S1B) These experiments revealed a significant reduction in basal BiP::GFP fluorescence in ATF6αΔ cells compared with parental dual-reporter cells, indicating that the BiP::GFP reporter has basal activity that is dependent on ATF6α. These new data are consistent with previous published observations demonstrated that treatment with Ceapin, an ATF6α-specific inhibitor, lowered BiP::GFP fluorescence in tunicamycin-treated cells to levels below those observed in untreated controls (Tung et al., eLife 2024). Together these observations indicate that ATF6α is active basally in CHO-K1 cells. Given the established cross-pathway repression of IRE1 by ATF6α signalling, it renders plausible our suggestion that the basal activation of the XBP1::mCherry (IRE1-reporter) observed basally in the SLC33a1 deleted cells arises from the partial interruption of ATF6α Reviewer 1 (additional points)

• __ Effect of deleting sialic acid-modifying acetyltransferases.__

• Comment: Reviewer 1 suggested that comparing the consequences of deleting SLC33a1 and the sialic acid- modifying acetyltransferases that operate downstream of the putative acetyl-CoA transporter could be informative.
• Response: In response to this valuable suggestion, we have now examined the impact of deleting Casd1, the gene encoding the Golgi acetyltransferase responsible for modifying sialic acids on ATF6α activity, comparing the consequences to Slc33a1. New Supplemental Fig. S8 reveals partial phenotypic overlap between the two deletions, suggesting that the loss of SLC33A1 exerts some of its effects on CHO cells by compromising sialic acid modification.

__ Potential effects on ATF6-like proteins (SREBP1/2, CREB3L).__

• Comment: Reviewer 1 suggested that we evaluate the effect of SLC33A1 loss on other ATF6-like transcription factors.

• Response: We took this advice to heart, but our attempts to compare SREBP2 processing in wildtype and SLC33A1 knockout cells were frustrated by the low quality of the antibodies available to us. Reviewer 2 (additional points)

• __ Physiological state and clonal adaptation of Slc33a1-deleted cells.__

• __Comment: __Reviewer 2 raised concerns regarding the physiological state of the Slc33a1-deleted cells and the potential impact of clonal adaptation or selection pressure on the consequences of genetic manipulation.
• Response: This is a valid concern. Deconvoluting direct from indirect effects are a challenge in any genetics-based experiment. To try and address this point, we compared the proliferation capacity of three pairs of parental CHO-K1 clones with their derivative Slc33a1-deletion variants using the IncuCyte assay. As shown in new Supplemental Fig. S2D, the Slc33a1 deletion variants had no consistent fitness disadvantage revealed by this assay. Whilst cell mass accretion is only one measure of comparability between cell lines, we deem these observations to indicate that a comparison between SLC33A1 wildtype and mutant CHO-K1 cells is unlikely to be compromised by gross underlying differences in cell fitness.

__ Responsiveness of PERK signalling to ER stress.__

• Comment: Reviewer 2 asked whether PERK signalling, which appears basally activated due to higher basal IRE1 signalling in the Slc33a1-deleted cells, remains responsive to ER stress.
• Response: To address this point, we treated cells with ER stressors and assessed PERK pathway activation. As shown in new Supplemental Fig. S4C, PERK signalling remains functional and responsive to ER stress in Slc33a1-depleted cells.

In addition to the points above, we have addressed several presentation and clarity issues raised by the reviewers, including figure labelling, image presentation, and schematic models. The Discussion has also been revised to more explicitly acknowledge the current limitations of the study while emphasising its central conceptual advance: namely, that loss of SLC33A1 results in a discordant UPR state in which IRE1 and PERK are activated, whereas ATF6α trafficking and transcriptional output are selectively compromised.

The following table summarises the major changes made to the figures in the revised manuscript to facilitate tracking the modifications introduced

Figure

Figure Panels

Amendment (if any)

Fig 4

4B (modified)

Scale bar added.

Fig 5

5B (modified)

Labelling correction according to the reviewer.

Fig S1 (new)

S1A-S1B

New data detailing the BiP promoter fragment and the reliability of the BiP::GFP reporter as a readout for ATF6α activity in cells.

Fig S2 (modified)

S2D (new)

New IncuCyte data added.

Fig S3 (modified)

S3B, S3C and S3E (new)

Panels B and C: New data from DTT and thapsigargin treatments, respectively. __Panel E: __New data from BiP mRNA levels under 2DG treatment in parental and Slc33a1-deleted cells.

Fig S4 (new)

S4C (new)

__Panels A and B: __Previously shown as panels in Fig. S2C and S2D.

__Panel C: __New data on the PERK response to ER stress in Slc33a1-deleted cells.

Fig S7 (new)

S7A-S7C (new)

New sanger sequencing chromatograms displaying the targeted exonic regions of the Casd1, Nat8 and Nat8b. * *

Fig S8 (new)

S8A-S8B (new)

Casd1-deleted data added.

Fig S9 (new)

Unique panel

New data comparing Nat8/Nat8b-deleted cells with single Nat8-deleted cells.

We thank the reviewers again for their insightful comments, which have significantly strengthened the manuscript. We believe the revised study clarifies key mechanistic points and provides a stronger conceptual advance regarding the role of SLC33A1 in UPR regulation.

Sincerely,

Adriana Ordóñez

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Referee #2

Evidence, reproducibility and clarity

Summary

The authors employed a genome-wide CRISPR-Cas9 screen to search for the genes selectively involved in the activation of ER stress sensor ATF6. Deletion of Slc33a1, which encodes a transporter of acetyl-CoA into the ER lumen, compromised the ATF6 pathway (as assessed by BiP::GFP reporter), while IRE1 and PERK were activated in basal conditions, in the absence of ER stress (as assessed by XBP1s::mCherry reporter and endogenous XBP1s and CHOP::GFP reporter). Moreover, IRE1, but not ATF6, replied to ER stress. Consistently, in Slc33a1Δ cells upon ER stress the levels of the processed N-ATF6α were significantly lowered compared to the parental cells, and microscopy study showed that in Slc33a1-deficient cells ATF6 is translocated to Golgi even in the absence of ER stress, but fails to reach the nucleus even after ER stress is imposed. Golgi-type sugar modification of ATF6α is decreased in Slc33a1Δ cells. These data show the importance of SLC33A1 for ATF6 processing and functioning through the mechanism which remains to be revealed.

Major comments.

Taken together, the reported data do support the conclusion about the role of SLC33A1 functioning in post-ER maturation of ATF6. Data and methods are presented in a reproducible way. Still, there are several issues worth attention.

1. While BiP::GFP reporter is very useful, it would be more convincing to show the level of BiP in Slc33a1Δ cells by WB.
2. Another concern is the state of Slc33a1Δ cells. While adaptation is a general problem of clonal cells, the cells used in this study (with XBP1 highly spliced, CHOP upregulated, and ATF6 pro-survival pathway inhibited) are probably very sick, and the selection pressure/adaptation is very strong in this cell line. I would suggest the authors to clarify this issue.
3. Authors showed that, based on CHOP::GFP reporter data, PERK was activated in the absence of ER stress and the activation was due to IRE1 signalling. But did PERK reply to the ER stress?
4. An important question is a subcellular location of SLC33A1. Huppke et al. (cited in the manuscript) showed that FLAG- and GFP-tagged SLC33A1 was colocalized with Golgi markers. While that may be due to overexpression of the protein, it deserves consideration, given that ATF6 is stuck in Golgi upon depletion of SLC33A1.
5. OPTIONAL. Regarding the role of acetylation in compromising ATF6 function: since both SLC33A1 deficiency and depletion of Nat8 have broad effects, glycosylation of ATF6 upon depletion of Nat8 should be assessed (similarly to Fig 5), to demonstrate the difference in glycosylation pattern upon the absence of SLC33A1 and Nat8 and strengthen the conclusions.

Minor comments.

1. Apart from the table of the cell lines, it would be useful to add to the supplementary a simple-minded scheme of the reporters used in this study (BiP::GFP, CHOP::GFP, XBP1s::mCherry) specifying the mechanism of the readout and the harbored protein and other important details (e.g., whether mRNA of XBP1s::mCherry reporter could be processed by IRE1).
2. Fig 2B and Fig 3A - the percentage of spliced XBP1 in parental cells is about 30% according to the graphs, but it looks more like 5%.
3. Fig 3B - It would probably be better to demonstrate the processing of endogenous ATF6. It could help to avoid the problems with alternative translation (even though anti-ATF6 antibodies are known to be tricky).
4. In Fig 4B - could be better to show Golgi marker separately. In Fig 4B and E the bars are missing (and cells in Fig 4B look bigger than in Fig 4E). Magnification of the insets should be further increased.
5. As the authors mention, 2-deoxy-D-glucose (2DG) is known to be the ER stress inducer, acting via prevention of N-glycosylation of proteins. Also, N-glycosylation state of ATF6 has been suggested to influence its trafficking. Thus, even if the control cells were treated in the same way, 2DG may not be the best ER-stress inducer to study ATF6 trafficking. Indeed, altered sugar modification of ATF6α in Slc33a1Δ cells (Fig 5) was tracked using Thapsigargin.
6. Minor comment on Fig 7 - recent data (Belyy et al., 2022) suggest IRE1 is a dimer even in the absence of ER stress.

Referee cross-commenting

I agree with Reviewer 1 that the authors need to clarify that authors need to clarify better how exactly BiP::GFP reporter works and whether it reflects ATF6 activation (rev 1 pointed to unclear responsiveness of the reporter to ATF6 and I asked to show the level of BiP by WB and the scheme of the mechanisms of readouts of the reporters)

I also agree with the comment on 2-DG which for some experiments may not be the best choice to activate UPR (or as Reviewer 1 pointed out shouldn't be the only one used to induce UPR). I still think that there's no contradiction in partial cleavage of ATF6 and suppression of BiP::GFP in Slc33a1Δ cells if then (as authors show) it doesn't reach nucleus.

Significance

General assessment. The article shows the necessity of SLC33A1, a transporter of acetyl-CoA in ER lumen, for ATF6 processing and functioning. It is well-written. However, the molecular mechanism which underlies the link is yet to be discovered (and this is clearly mentioned by the authors).

The study is of interest for the basic research and of potential interest for clinical research.

My main field of expertise is UPR. While I have broad knowledge and interest in protein science in general, my experience with protein glycosylation is rather limited.

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Referee #1

Evidence, reproducibility and clarity

Summary:

In this manuscript, the authors follow up on the results from a previous CRISPR screen in CHO-K1 cells demonstrating that knockout of the ER acetyl-CoA transporter Slc33a1 suppresses ATF6 activation. The authors show in these cells that, in response to 2-DG, the Slc33a1 deletion results in constitutive activation of the UPR except for the ATF6 pathway, which appears to traffic constitutively to the Golgi but to not be cleaved there. They show using an uncleavable ATF6 that loss of Slc33a1 delays formation of an O-glycosylated form of at least this version of the protein, and they also find that single deletion of the ER acetyltransferases NAT8 and NAT8B also constitutively activates the UPR, but that activation in this case includes activation of ATF6. The mechanism by which Acetyl-CoA might impact ATF6 activation is not elucidated.

Major Comments:

The following conclusions are well-supported:

• That loss of Slc33a1 results in IRE1 and PERK activation but not ATF6 activation
• That ATF6 traffics at least to some degree constitutively to the Golgi when Slc33a1 is deleted, which is a counterintuitive finding given the apparent lack of ATF6 activation
• That loss of Slc33a1 can alter the level O-glycosylation and the preponderance of sialylated N-glycans on at least ATF6
• Generally speaking, I find the wording to be careful and precise

The following claims are less convincing:

• That loss of Slc33a1 results in universal suppression of ATF6 activation. The effect in response to 2-DG is unquestionably strong at least at the level of Bip-GFP reporter (although it's not clear from this paper nor the previous one from this group how much of the Bip promoter this reporter encodes-which is important because only a minimal Bip promoter is exclusively responsive to ATF6). However, the impairment of ATF6 activation in response to tunicamycin (Fig. 1C) is very modest, and no other stressors were tested (DTT and TG were used for other purposes, not to test ATF6 activation). One might actually expect this pathway, if it affects glycosylation pathways, to be particularly sensitive to a stressor like 2-DG that would have knock-on effects on glycosylation. Admittedly, it does seem to be true in the basal condition (i.e., absent an exogenous ER stress) that IRE1 and PERK are activated where ATF6 is not. At some level, it's hard to reconcile the almost complete suppression of Bip-GFP induction in Slc33a1 cells in response to 2DG with the fact that in Fig. 3, cleavage clearly seems to be occurring, albeit to a lesser extent
• That regulation of ATF6 is a broadly applicable consequence of Slc33a1 action. Unless I've missed it, all experiments are performed in CHO-K1 cells, so how broadly applicable this pathway is not clear.
• That loss of Slc33a1 "deregulated activation of the IRE1 branch of the UPR." It is clear that IRE1 is activated when Slc33a1 is deleted (that the authors show this repeatedly in different parental cell lines provides a high degree of rigor). However, at least through the CHOP-GFP reporter, PERK is activated as well. Although 4u8C suppresses this activation, the suppression is not complete, there are no orthogonal ways of showing this (e.g., loss of KD of IRE1), and the converse experiment (examining IRE1 activation when PERK is lost or inhibited) was not done. Thus, while I agree that the data shown are consistent with PERK activation being downstream of IRE1, they are not definitive enough to, in my opinion, rule out the more parsimonious explanation for their own data and what is already published in the field that loss of Slc33a1 causes ER stress (thus in principle activating all 3 pathways of the UPR-including ATF6 transit to the Golgi) but that it also, separately, inhibits activation of ATF6 (and possibly other things? See below)-a possibility acknowledged towards the end of the Discussion.
• That "Nat8 and Slc33a1 influence ER homeostasis and ATF6 signaling through distinct mechanisms". This conclusion would require simultaneous deletion of both Nat8 and NAT8B because of possible redundancy/compensatory effects.
• If I'm understanding the authors' argument correctly, they seem to be invoking that the ATF6 activation defect underlies/is upstream of the activation of IRE1 in Slc33a1 KO cells. But if that understanding is correct, it seems fairly unlikely, as the authors' data show no evidence that ATF6 is activated in parental cells under basal conditions (Fig. 3B) and thus no reason to expect that failure to activate ATF6 by itself would result in appreciable phenotype in cells-an idea also consistent with the general lack of phenotype in ATF6-null MEF and other cells.

Minor Comments:

• The alteration in O-glycosylation levels of ATF6 is interesting, but it might or might not be relevant to ATF6 activation, and if it isn't, then the paper provides no mechanism for why loss of Slc33a1 has the effects on ATF6 that it does. What about other similar molecules, like ATF6B (surprising that this was not examined), SREBP1/2, a non-glycoyslatable ATF6, and/or one of the other CREB3L proteins?
• Does Slc33a1 deletion cause other ER resident proteins to constitutively mislocalize to the Golgi?
• As mentioned above, does loss/knockdown of Slc33a1 activate IRE1 and PERK but not ATF6 in other cell types?
• Also as mentioned above, how do the UPR (all 3 branches) in cells lacking Slc33a1 respond to TG or DTT? This and the preceding comments are important toward making the claim that Slc33a1 is actually a regulator of ATF6. The time required to do these experiments will depend on whether creation of more stable lines is required, and whether they are worth doing depends on how broad the authors wish the scope of the paper to be.
• It's surprising that the authors didn't do comparable experiments to what is shown in Fig. 6 but deleting the acetyltransferases that modify sialic acids, which I believe are known.
• The authors mis-describe the data from Fig. 5B. EndoH and PNGaseF should collapse ATF6 to a 0N form, not a 1N form (what is labeled as 2N should be 1N, and it looks like the true 2N band is partially obscured by the strong 3N band.

Referee cross-commenting

While reviewer #2 and I have somewhat different opinions on the strength of the evidence, we seem fairly well-aligned on the overall significance of the work.

Significance

The conceptual advance in this paper is that, while loss of Slc33a1 seems widely disruptive to ER function-an idea that has been advanced in the literature before-it seems to have unique and discordant effects on ATF6 relative to the other UPR pathways. The paper does not offer a conclusive mechanism by which these effects are realized, and the sole focus on ATF6 makes it difficult to fully contextualize the findings, but the data are of high quality and, while the scope is somewhat narrow, the phenotype is likely to be of interest to those concerned with ER stress and UPR signaling, which also describes my own expertise.

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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.

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Referee #3

Evidence, reproducibility and clarity

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.

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.

3. 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?

4. 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?
5. 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.
6. 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?
7. 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.
8. 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?
9. 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?
10. 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?
11. 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.
12. 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.
13. How were the DEG p-values adjusted for multiple testing?
14. 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.
15. 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?
16. 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.

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"?
2. 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.
3. 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.
4. 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.
5. 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.
6. 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.

Significance

To my knowledge, this work represents the first cis-eQTL mapping in bacteria. As such, it is a useful and interesting exploration of this space that complements the large body of literature on this question in eukaryotic systems. This expansion to bacterial systems is especially interesting given the unique features of bacterial compared to eukaryotic genomes, including a small (10-15%) noncoding fraction of the genome and gene organization in operons. The work will be of interest to readers in the fields of complex trait genetics, gene expression, and regulatory variation. For context of this assessment, I am an expert in genomics and the study of genetic variation in gene expression in eukaryotic systems. I have limited knowledge about bacterial genetics and biology, as well as of antibiotic resistance.

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Referee #2

Evidence, reproducibility and clarity

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:

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).

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. 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. 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. 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.

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.

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. 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.

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.

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.

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.

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

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.

Significance

Overall the key strength of the study is the heroic merging of large genetic and transcriptomic datasets to address the question of how much variation in gene expression can be assigned to cis regulatory mutations in E. coli and in P. aeruginosa. The authors find that only a minority of genes can have such an assignment explaining expression variation, which highlights both the many factors (local and global) impacting gene expression, and the difficulty in trying to predict and understand expression patterns in different strains. I believe that with suitable modification, the manuscript will be of great interest to a broad audience interested in bacterial genomics, gene regulation, and systems/synthetic biology.

Reviewer Expertise: I consider myself a bacterial systems biologist and routinely use high throughput experiments to understand bacterial gene regulation.

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Referee #1

Evidence, reproducibility and clarity

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.

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?

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

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?

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.

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.

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.

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

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 Line 102 - state % of DEGs relative to the entire pan-genome Figure 1A is not discussed in the text 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? Line 122-123: State what letters correspond to these COG categories here 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. 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 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? 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 Line 359: Need to talk about each supplementary figure 4 to 9 and how they demonstrate your point.

Are the text and figures clear and accurate? Figure 4 too small 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. Figure 2: THere is no axis for the percents and the percents don't make sense relative to the bars they represent?? 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 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 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. FIgure 6B: typo in legend 'Downreglation' Line 398: Need to state rationale for why Waaq operon is being investigated here. WHy did you look into individual example? Figure 8: Can get rid of red box Line 463 - 'account for all kinds' is too informal Mix of font styles throughout document

Significance

Provide contextual information to readers (editors and researchers) about the novelty of the study, its value for the field and the communities that might be interested. The following aspects are important:General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

This study applies eQTL concepts to bacterial pangenomes to understand how genetic variation in non-coding regions contributes to microbial phenotypes, which is clever and has not been done in bacterial communities (although has been done in yeast isolates, see citation above). They characterize these same variants using in silico promoter predictions, in vitro experiments, layer biological mechanism via transcription factor binding site mapping, and study associated antibiotic resistance phenotypes. These are all good ideas, but none of these points are very developed. The antibiotic work in particular was a missed opportunity as this is the most impactful demonstration of their approach. For instance, to what extent do these eQTLs explain resistance across isolates vs coding changes? Are non-coding variants more responsible for antibiotic resistance than coding variants? Given how easy it is to adapt gene expression vs establishing other mechanisms, this is plausible. How could knowing this change how we treat infections? While a general overview of their strategy is fine, the approaches are under-described and unclear so difficult to truly assess.

Advance: compare the study to the closest related results in the literature or highlight results reported for the first time to your knowledge; does the study extend the knowledge in the field and in which way? Describe the nature of the advance and the resulting insights (for example: conceptual, technical, clinical, mechanistic, functional,...).

To my knowledge and from a cursory search, this is the first pan-genome mapping of non-coding variants to transcriptional changes in bacteria. This is a good idea that could be applied to any microbe for which large transcriptomic datasets of strains are available or could be generated and is helpful for understanding genetic variation and the architecture of bacterial regulatory systems.

Audience: describe the type of audience ("specialized", "broad", "basic research", "translational/clinical", etc...) that will be interested or influenced by this research; how will this research be used by others; will it be of interest beyond the specific field?

This would be of interest to individuals interested in population genetics, gene regulation, and microbial evolution. It could inspire similar studies of other microbes to understand the contribution of non-coding changes to phenotypes across whole genomes.

Please define your field of expertise with a few keywords to help the authors contextualize your point of view. Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

I am an expert on bacterial gene regulation, especially concerning how promoter activity is encoded within sequences. I have less experience on using GWAS.

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Reply to the reviewers

In our manuscript, we describe a role for the nuclear mRNA export factor UAP56 (a helicase) during metamorphic dendrite and presynapse pruning in flies. We characterize a UAP56 ATPase mutant and find that it rescues the pruning defects of a uap56 mutant. We identify the actin severing enzyme Mical as a potentially crucial UAP56 mRNA target during dendrite pruning and show alterations at both the mRNA and protein level. Finally, loss of UAP56 also causes presynapse pruning defects with actin abnormalities. Indeed, the actin disassembly factor cofilin is required for pruning specifically at the presynapse.

We thank the reviewers for their constructive comments, which we tried to address experimentally as much as possible. To summarize briefly, while all reviewers saw the results as interesting (e. g., Reviewer 3's significance assessment: "Understanding how post-transcriptional events are linked to key functions in neurons is important and would be of interest to a broad audience") and generally methodologically strong, they thought that our conclusions regarding the potential specificity of UAP56 for Mical mRNA was not fully covered by the data. To address this criticism, we added more RNAi analyses of other mRNA export factors and rephrased our conclusions towards a more careful interpretation, i. e., we now state that the pruning process is particularly sensitive to loss of UAP56. In addition, reviewer 1 had technical comments regarding some of our protein and mRNA analyses. We added more explanations and an additional control for the MS2/MCP system. Reviewers 2 and 3 wanted to see a deeper characterization of the ATPase mutant provided. We generated an additional UAP56 mutant transgene, improved our analyses of UAP56 localization, and added a biochemical control experiment. We hope that our revisions make our manuscript suitable for publication.

1. Point-by-point description of the revisions

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Comments by reviewer 1.

Major comments

1.

For Figure 4, the MS2/MCP system is not quantitative. Using this technique, it is impossible to determine how many RNAs are located in each "dot". Each of these dots looks quite large and likely corresponds to some phase-separated RNP complex where multiple RNAs are stored and/or transported. Thus, these data do not support the conclusion that Mical mRNA levels are reduced upon UAP56 knockdown. A good quantitative microscopic assay would be something like smFISH. Additinally, the localization of Mical mRNA dots to dendrites is not convincing as it looks like regions where there are dendritic swellings, the background is generally brighter.

Our response

We indeed found evidence in the literature that mRNPs labeled with the MS2/MCP or similar systems form condensates (Smith et al., JCB 2015). Unfortunately, smFISH is not established for this developmental stage and would likely be difficult due to the presence of the pupal case. To address whether the Mical mRNPs in control and UAP56 KD neurons are comparable, we characterized the MCP dots in the respective neurons in more detail and found that their sizes did not differ significantly between control and UAP56 KD neurons. To facilitate interpretability, we also increased the individual panel sizes and include larger panels that only show the red (MCP::RFP) channel. We think these changes improved the figure. Thanks for the insight.

Changes introduced: Figure 5 (former Fig. 4): Increased panel size for MCP::RFP images, left out GFP marker for better visibility. Added new analysis of MCP::RFP dot size (new Fig. 5 I).

1.

Alternatively, levels of Mical mRNA could be verified by qPCR in the laval brain following pan-neuronal UAP56 knockdown or in FACS-sorted fluorescently labeled da sensory neurons. Protein levels could be analyzed using a similar approach.

Our response

We thank the reviewer for this comment. Unfortunately, these experiments are not doable as neuron-wide UAP56 KD is lethal (see Flybase entry for UAP56). From our own experience, FACS-sorting of c4da neurons would be extremely difficult as the GFP marker fluorescence intensity of UAP56 KD neurons is weak - this would likely result in preferential sorting of subsets of neurons with weaker RNAi effects. In addition, FACS-sorting whole neurons would not discriminate between nuclear and cytoplasmic mRNA.

The established way of measuring protein content in the Drosophila PNS system is immunofluorescence with strong internal controls. In our case, we also measured Mical fluorescence intensity of neighboring c1da neurons that do not express the RNAi and show expression levels as relative intensities compared to these internal controls. This procedure rules out the influence of staining variation between samples and is used by other labs as well.

1.

In Figure 5, the authors state that Mical expression could not be detected at 0 h APF. The data presented in Fig. 5C, D suggest the opposite as there clearly is some expression. Moreover, the data shown in Fig. 5D looks significantly brighter than the Orco dsRNA control and appears to localize to some type of cytoplasmic granule. So the expression of Mical does not look normal.

Our response

We thank the reviewer for this comment. In the original image in Fig. 5 C, the c4da neuron overlaps with the dendrite from a neighboring PNS neuron (likely c2da or c3da). The latter neuron shows strong Mical staining. We agree that this image is confusing and exchanged this image for another one from the same genotype.

Changes introduced: Figure 5 L (former Fig. 5 C): Exchanged panel for image without overlap from other neuron.

1.

Sufficient data are not presented to conclude any specificity in mRNA export pathways. Data is presented for one export protein (UAP56) and one putative target (Mical). To adequately assess this, the authors would need to do RNA-seq in UAP56 mutants.

Our response

We thank the reviewer for this comment. To address this, we tested whether knockdown of three other mRNA export factors (NXF1, THO2, THOC5) causes dendrite pruning defects, which was not the case (new Fig. S1). While these data are consistent with specific mRNA export pathways, we agree that they are not proof. We therefore toned down our interpretation and removed the conclusion about specificity. Instead, we now use the more neutral term "increased sensibility (to loss of UAP56)".

Changes introduced: Added new Figure S1: RNAi analyses of NXF1, THO2 and THOC5 in dendrite pruning. Introduced concluding sentence at the end of first Results paragraph: We conclude that c4da neuron dendrite pruning is particularly sensitive to loss of UAP56. (p. 6)

1.

In summary, better quantitative assays should be used in Figures 4 and 5 in order to conclude the expression levels of either mRNA or protein. In its current form, this study demonstrates the novel finding that UAP56 regulates dendrite and presynaptic pruning, potentially via regulation of the actin cytoskeleton. However, these data do not convincingly demonstrate that UAP56 controls these processes by regulating of Mical expression and defintately not by controlling export from the nucleus.

Our response

We hope that the changes we introduced above help clarify this.

1.

While there are clearly dendrites shown in Fig. 1C', the cell body is not readily identifiable. This makes it difficult to assess attachment and suggests that the neuron may be dying. This should be replaced with an image that shows the soma.

Our response

We thank the reviewer for this comment. Changes introduced: we replaced the picture in the panel with one where the cell body is more clearly visible.

1.

The level of knockdown in the UAS56 RNAi and P element insertion lines should be determined. It would be useful to mention the nature of the RNAi lines (long/short hairpin). Some must be long since Dcr has been co-expressed. Another issue raised by this is the potential for off-target effects. shRNAi lines would be preferable because these effects are minimized.

Our response

We thank the reviewer for this comment. Assessment of knockdown efficiency is a control to make sure the manipulations work the way they are intended to. As mRNA isolation from Drosophila PNS neurons is extremely difficult, RNAi or mutant phenotypes in this system are controlled by performing several independent manipulations of the same gene. In our case, we used two independent RNAi lines (both long hairpins from VDRC/Bloomington and an additional insertion of the VDRC line, see Table S1) as well as a mutant P element in a MARCM experiment, i. e., a total of three independent manipulations that all cause pruning defects, and the VDRC RNAi lines do not have any predicted OFF targets (not known for the Bloomington line). If any of these manipulations would not have matched, we would have generated sgRNA lines for CRISPR to confirm.

Minor comments:

1.

The authors should explain what EB1:GFP is marking when introduced in the text.

Our response

We thank the reviewer for this comment. Changes introduced: we explain the EB1::GFP assay in the panel with one where the cell body is more clearly visible.

1.

The da neuron images throughout the figures could be a bit larger.

Our response

We thank the reviewer for this comment. Changes introduced: we changed the figure organization to be able to use larger panels:

• the pruning analysis of the ATPase mutations (formerly Fig. 2) is now its own figure (Figure 3).

• we increased the panel sizes of the MCP::RFP images (Figure 5 A - I, formerly Fig. 4).

Reviewer #1 (Significance (Required)):

Strengths:

The methodology used to assess dendrite and presynaptic prunings are strong and the phenotypic analysis is conclusive.

Our response

We thank the reviewer for this comment.

Weakness:

The evidence demonstrating that UAP56 regulates the expression of Mical is unconvincing. Similarly, no data is presented to show that there is any specificity in mRNA export pathways. Thus, these major conclusions are not adequately supported by the data.

Our response

We hope the introduced changes address this comment.

__Reviewer #2 (Evidence, reproducibility and clarity (Required)): __

In this paper, the authors describe dendrite pruning defects in c4da neurons in the DEXD box ATPase UAP56 mutant or in neuronal RNAi knockdown. Overexpression UAP56::GFP or UAP56::GFPE194Q without ATPase activity can rescue dendrite pruning defects in UAP56 mutant. They further characterized the mis-localization of UAP56::GFPE194Q and its binding to nuclear export complexes. Both microtubules and the Ubiquitin-proteasome system are intact in UAP56RNAi neurons. However, they suggest a specific effect on MICAL mRNA nuclear export shown by using the MS2-MCP system., resulting in delay of MICAL protein expression in pruned neurons. Furthermore, the authors show that UAP56 is also involved in presynaptic pruning of c4da neuros in VNC and Mica and actin are also required for actin disassembly in presynapses. They propose that UAP56 is required for dendrite and synapse pruning through actin regulation in Drosophila. Following are my comments.

Major comments

1.

The result that UAP56::GFPE194Q rescues the mutant phenotype while the protein is largely mis-localized suggests a novel mechanism or as the authors suggested rescue from combination of residual activities. The latter possibility requires further support, which is important to support the role mRNA export in dendrite and pre-synapse pruning. One approach would be to examine whether other export components like REF1, and NXF1 show similar mutant phenotypes. Alternatively, depleting residual activity like using null mutant alleles or combining more copies of RNAi transgenes could help.

Our response

We thank the reviewer for this comment. We agree that the mislocalization phenotype is interesting and could inform further studies on the mechanism of UAP56. To further investigate this and to exclude that this could represent a gain-of-function due to the introduced mutation, we made and characterized a new additional transgene, UAP56::GFP E194A. This mutant shows largely the same phenotypes as E194Q, with enhanced interactions with Ref1 and partial mislocalization to the cytoplasm. In addition, we tested whether knockdown of THO2, THOC5 or NXF1 causes pruning defects (no).

Changes introduced:

• added new Figure S1: RNAi analyses of NXF1, THO2 and THOC5 in dendrite pruning.

• made and characterized a new transgene UAP56 E194A (new Fig. 2 B, E, E', 3 C, C', E, F).

1.

The localization of UAP56::GFP (and E194Q) should be analyzed in more details. It is not clear whether the images in Fig. 2A and 2B are from confocal single sections or merged multiple sections. The localization to the nuclear periphery of UAP56::GFP is not clear, and the existence of the E194Q derivative in both nucleus and cytosol (or whether there is still some peripheral enrichment) is not clear if the images are stacked.

Our response

We thank the reviewer for this comment. It is correct that the profiles in the old Figure 2 were from single confocal sections from the displayed images. As it was difficult to create good average profiles with data from multiple neurons, we now introduce an alternative quantification based on categories (nuclear versus dispersed) which includes data from several neurons for each genotype, including the new E194A transgene (new Fig 3 G). Upon further inspection, the increase at the nuclear periphery was not always visible and may have been a misinterpretation. We therefore removed this statement.

Changes introduced:

• added new quantitative analysis of UAP56 wt and E/A, E/Q mutant localization (new Fig 3 G).

1.

The Ub-VV-GFP is a new reagent, and its use to detect active proteasomal degradation is by the lack of GFP signals, which could be also due to the lack of expression. The use of Ub-QQ-GFP cannot confirm the expression of Ub-VV-GFP. The proteasomal subunit RPN7 has been shown to be a prominent component in the dendrite pruning pathway (Development 149, dev200536). Immunostaining using RPN7 antibodies to measure the RPN expression level could be a direct way to address the issue whether the proteasomal pathway is affected or not.

Our response

We thank the reviewer for this comment. We agree that it is wise to not only introduce a positive control for the Ub-VV-GFP sensor (the VCP dominant-negative VCP QQ), but also an independent control. As mutants with defects in proteasomal degradation accumulate ubiquitinated proteins (see, e. g., Rumpf et al., Development 2011), we stained controls and UAP56 KD neurons with antibodies against ubiquitin and found that they had similar levels (new Fig. S3).

Changes introduced:

• added new ubiquitin immunofluorescence analysis (new Fig. S3).

1.

Using the MS2/MCP system to detect the export of MICAL mRNA is a nice approach to confirm the UAP56 activity; lack of UAP56 by RNAi knockdown delays the nuclear export of MS2-MICAL mRNA. The rescue experiment by UAS transgenes could not be performed due to the UAS gene dosage, as suggested by the authors. However, this MS2-MICAL system is also a good assay for the requirement of UAP56 ATPase activity (absence in the E194Q mutant) in this process. Could authors use the MARCM (thus reduce the use of UAS-RNAi transgene) for the rescue experiment? Also, the c4da neuronal marker UAS-CD8-GFP used in Fig4 could be replaced by marker gene directly fused to ppk promoter, which can save a copy of UAS transgene. The results from the rescue experiment would test the dependence of ATPase activity in nuclear export of MICAL mRNA.

Our response

We thank the reviewer for this comment. This is a great idea but unfortunately, this experiment was not feasible due to the (rare) constraints of Drosophila genetics. The MARCM system with rescue already occupies all available chromosomes (X: FLPase, 2nd: FRT, GAL80 + mutant, 3rd: GAL4 + rescue construct), and we would have needed to introduce three additional ones (MCP::RFP and two copies of unmarked genomic MICAL-MS2, all on the third chromosome) that would have needed to be introduced by recombination. Any Drosophilist will see that this is an extreme, likely undoable project :-(

1.

The UAP56 is also involved in presynaptic pruning through regulating actin assembly, and the authors suggest that Mical and cofilin are involved in the process. However, direct observation of lifeact::GFP in Mical or cofilin RNAi knockdown is important to support this conclusion.

Our response

We thank the reviewer for this comment. In response, we analyzed the lifeact::GFP patterns of control and cofilin knockdown neurons and found that loss of cofilin also leads to actin accumulation (new Fig. 7 I, J).

Changes introduced:

• new lifeact analysis (new Fig. 7 I, J).

Minor comments:

1.

RNA localization is important for dendrite development in larval stages (Brechbiel JL, Gavis ER. Curr Biol. 20;18(10):745-750). Yet, the role of UAP56 is relatively specific and shown only in later-stage pruning. It would need thorough discussion.

Our response

We thank reviewer 2 for this comment. We added the following paragraph to the discussion: "UAP56 has also been shown to affect cytoplasmic mRNA localization in Drosophila oocytes (Meignin and Davis, 2008), opening up the possibility that nuclear mRNA export and cytoplasmic transport are linked. It remains to be seen whether this also applies to dendritic mRNA transport (Brechbiel and Gavis, 2008)." (p.13)

1.

Could authors elaborate on the possible upstream regulators that might be involved, as described in "alternatively, several cofilin upstream regulators have been described (Rust, 2015) which might also be involved in presynapse pruning and subject to UAP56 regulation" in Discussion?

Our response

We thank reviewer 2 for this comment. In the corresponding paragraph, we cite as example now that cofilin is regulated by Slingshot phosphatases and LIM kinase (p.14).

1.

In Discussion, the role of cofilin in pre- and post-synaptic processes was described. The role of Tsr/Cofilin regulating actin behaviors in dendrite branching has been described in c3da and c4da neurons (Nithianandam and Chien, 2018 and other references) should be included in Discussion.

Our response

We thank reviewer 2 for this comment. In response we tested whether cofilin is required for dendrite pruning and found that this, in contrast to Mical, is not the case (new Fig. S6). We cite the above paper in the corresponding results section (p.12).

Changes introduced:

• new cofilin dendrite pruning analysis (new Fig. S6).

• added cofilin reference in Results.

1.

The authors speculate distinct actin structures have to be disassembled in dendrite and presynapse pruning in Discussion. What are the possible actin structures in both sites could be elaborated.

Our response

We thank reviewer 2 for this comment. In response, we specify in the Discussion: "As Mical is more effective in disassembling bundled F-actin than cofilin (Rajan et al., 2023), it is interesting to speculate that such bundles are more prevalent in dendrites than at presynapses." (p14)

Reviewer #2 (Significance (Required)):

The study initiated a genetic screen for factors involved in a dendrite pruning system and reveals the involvement of nuclear mRNA export is an important event in this process. They further identified the mRNA of the actin disassembly factor MICAL is a candidate substrate in the exporting process. This is consistent with previous finding that MICAL has to be transcribed and translated when pruning is initiated. As the presynapses of the model c4da neuron in this study is also pruned, the dependence on nuclear export and local actin remodeling were also shown. Thus, this study has added another layer of regulation (the nuclear mRNA export) in c4da neuronal pruning, which would be important for the audience interested in neuronal pruning. The study is limited for the confusing result whether ATPase activity of the exporting factor is required.

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

Summary: In the manuscript by Frommeyer, Gigengack et al. entitled "The UAP56 mRNA Export Factor is Required for Dendrite and Synapse Pruning via Actin Regulation in Drosophila" the authors surveyed a number of RNA export/processing factors to identify any required for efficient dendrite and/or synapse pruning. They describe a requirement for a general poly(A) RNA export factor, UAP56, which functions as an RNA helicase. They also study links to aspects of actin regulation.

Overall, while the results are interesting and the impact of loss of UAP56 on the pruning is intriguing, some of the data are overinterpreted as presented. The argument that UAP56 may be specific for the MICAL RNA is not sufficiently supported by the data presented. The two stories about poly(A) RNA export/processing and the actin regulation seem to not quite be connected by the data presented. The events are rather distal within the cell, making connecting the nuclear events with RNA to events at the dendrites/synapse challenging.

Our response

We thank reviewer 3 for this comment. To address this, we tested whether knockdown of three other mRNA export factors (NXF1, THO2, THOC5) causes dendrite pruning defects, which was not the case (new Fig. S1). While these data are consistent with specific mRNA export pathways, we agree that they are not proof. We therefore toned down our interpretation and removed the conclusion about specificity. Instead, we now use the more neutral term "increased sensibility (to loss of UAP56)".

We agree that it is a little hard to tie cofilin to UAP56, as we currently have no evidence that cofilin levels are affected by loss of UAP56, even though both seem to affect lifeact::GFP in a similar way (new Fig. 7 I, J). However, a dysregulation of cofilin can also occur through dysregulation of upstream cofilin regulators such as Slingshot and LIM kinase, making such a relationship possible.

Changes introduced:

• added new Figure S1: RNAi analyses of NXF1, THO2 and THOC5 in dendrite pruning.

• introduced concluding sentence at the end of first Results paragraph: "We conclude that c4da neuron dendrite pruning is particularly sensitive to loss of UAP56." (p. 6)

• add new lifeact::GFP analysis of cofilin KD (new Fig. I, J).

• identify potential other targets from the literature in the Discussion (Slingshot phosphatases and LIM kinase, p.14).

There are a number of specific statements that are not supported by references. See, for example, these sentences within the Introduction- "Dysregulation of pruning pathways has been linked to various neurological disorders such as autism spectrum disorders and schizophrenia. The cell biological mechanisms underlying pruning can be studied in Drosophila." The Drosophila sentence is followed by some specific examples that do include references. The authors also provide no reference to support the variant that they create in UAP56 (E194Q) and whether this is a previously characterized fly variant or based on an orthologous protein in a different system. If so, has the surprising mis-localization been reported in another system?

Our response

We thank reviewer 3 for this comment. We added the following references on pruning and disease:

1) Howes, O.D., Onwordi, E.C., 2023. The synaptic hypothesis of schizophrenia version III: a master mechanism. Mol. Psychiatry 28, 1843-1856.

2) Tang, G., et al., 2014. Loss of mTOR-dependent macroautophagy causes autistic-like synaptic pruning deficits. Neuron 83, 1131-43.

To better introduce the E194 mutations, we explain the position of the DECD motif in the Walker B domain, give the corresponding residues in the human and yeast homologues and cite papers demonstrating the importance of this residue for ATPase activity:

3) Saguez, C., et al., 2013. Mutational analysis of the yeast RNA helicase Sub2p reveals conserved domains required for growth, mRNA export, and genomic stability. RNA 19:1363-71.

4) Shen, J., et al., 2007. Biochemical Characterization of the ATPase and Helicase Activity of UAP56, an Essential Pre-mRNA Splicing and mRNA Export Factor. J. Biol. Chem. 282, P22544-22550.

We are not aware of other studies looking at the relationship between the UAP56 ATPase and its localization. Thank you for pointing this out!

Specific Comments:

Specific Comment 1: Figure 1 shows the impact of loss of UAP56 on neuron dendrite pruning. The experiment employs both two distinct dsRNAs and a MARCM clone, providing confidence that there is a defect in pruning upon loss of UAP56. As the authors mention screening against 92 genes that caused splicing defects in S2 cells, inclusion of some examples of these genes that do not show such a defect would enhance the argument for specificity with regard to the role of UAP56. This control would be in addition to the more technical control that is shown, the mCherry dsRNA.

Our response

We thank reviewer 3 for this comment. To address this, we included the full list of screened genes with their phenotypic categorization regarding pruning (103 RNAi lines targeting 64 genes) as Table S1. In addition, we also tested four RNAi lines targeting the nuclear mRNA export factors Nxf1, THO2 and THOC5 which do not cause dendrite pruning defects (Fig. S1).

Changes introduced:

• added RNAi screen results as a list in Table S1.

• added new Figure S1: RNAi analyses of NXF1, THO2 and THOC5 in dendrite pruning.

Specific Comment 2: Later the authors demonstrate a delay in the accumulation of the Mical protein, so if they assayed these pruning events at later times, would the loss of UAP56 cause a delay in these events as well? Such a correlation would enhance the causality argument the authors make for Mical levels and these pruning events.

Our response

We thank reviewer 3 for this comment. Unfortunately, this is somewhat difficult to assess, as shortly after the 18 h APF timepoint, the epidermal cells that form the attachment substrate for c4da neuron dendrites undergo apoptosis. Where assessed (e. g., Wang et al., 2017, Development) 144: 1851–1862), this process, together with the reduced GAL4 activity of our ppk-GAL4 during the pupal stage (our own observations), eventually leads to pruning, but the causality cannot be easily attributed anymore. We therefore use the 18 h APF timepoint essentially as an endpoint assay.

Specific Comment 3: Figure 2 provides data designed to test the requirement for the ATPase/helicase activity of UAP56 for these trimming events. The first observation, which is surprising, is the mislocalization of the variant (E194Q) that the authors generate. The data shown does not seem to indicate how many cells the results shown represent as a single image and trace is shown the UAP56::GFP wildtype control and the E194Q variant.

Our response

We thank reviewer 3 for this comment. It is correct that the traces shown are from single confocal sections. To better display the phenotypic penetrance, we now added a categorical analysis that shows that the UAP56 E194Q mutant is completely mislocalized in the majority of cells assessed (and the newly added E194A mutant in a subset of cells).

Changes introduced:

• added categorical quantification of UAP56 variant localization (new Fig. 2 G).

__Specific Comment 4: __Given the rather surprising finding that the ATPase activity is not required for the function of UAP56 characterized here, the authors do not provide sufficient references or rationale to support the ATPase mutant that they generate. The E194Q likely lies in the Walker B motif and is equivalent to human E218Q, which can prevent proper ATP hydrolysis in the yeast Sub2 protein. There is no reference to support the nature of the variant created here.

Our response

We thank reviewer 3 for this comment. To better introduce the E194 mutations, we explain the position of the DECD motif in the Walker B domain, give the corresponding residues in the human and yeast homologues (Sub2) and cite papers demonstrating the importance of this residue for ATPase activity:

1) Saguez, C., et al., 2013. Mutational analysis of the yeast RNA helicase Sub2p reveals conserved domains required for growth, mRNA export, and genomic stability. RNA 19:1363-71.

2) Shen, J., et al., 2007. Biochemical Characterization of the ATPase and Helicase Activity of UAP56, an Essential Pre-mRNA Splicing and mRNA Export Factor. J. Biol. Chem. 282, P22544-22550.

__Specific Comment 5: __Given the surprising results, the authors could have included additional variants to ensure the change has the biochemical effect that the authors claim. Previous studies have defined missense mutations in the ATP-binding site- K129A (Lysine to Alanine): This mutation, in both yeast Sub2 and human UAP56, targets a conserved lysine residue that is critical for ATP binding. This prevents proper ATP binding and consequently impairs helicase function. There are also missense mutations in the DEAD-box motif, (Asp-Glu-Ala-Asp) involved in ATP binding and hydrolysis. Mutations in this motif, such as D287A in yeast Sub2 (corresponding to D290A in human UAP56), can severely disrupt ATP hydrolysis, impairing helicase activity. In addition, mutations in the Walker A (GXXXXGKT) and Walker B motifs are can impair ATP binding and hydrolysis in DEAD-box helicases. Missense mutations in these motifs, like G137A (in the Walker A motif), can block ATP binding, while E218Q (in the Walker B motif)- which seems to be the basis for the variant employed here- can prevent proper ATP hydrolysis.

Our response

We thank reviewer 3 for this comment. Our cursory survey of the literature suggested that mutations in the Walker B motif are the most specific as they still preserve ATP binding and their effects have not well been characterized overall. In addition, these mutations can create strong dominant-negatives in related helicases (e. g., Rode et al., 2018 Cell Reports, our lab). To better characterize the role of the Walker B motif in UAP56, we generated and characterized an alternative mutant, UAP56 E194A. While the E194A variant does not show the same penetrance of localization phenotypes as E194Q, it also is partially mislocalized, shows stronger binding to Ref1 and also rescues the uap56 mutant phenotypes without an obvious dominant-negative effect, thus confirming our conclusions regarding E194Q.

Changes introduced:

• added biochemical, localization and phenotypic analysis of newly generated UAP56 E194A variant (new Figs. 2 B, 2 E, E', 3 C, C'). categorical quantification of UAP56 variant localization (new Fig. 2 G).

__Specific Comment 6: __The co-IP results shown in Figure 2C would also seem to have multiple potential interpretations beyond what the authors suggest, an inability to disassemble a complex. The change in protein localization with the E194Q variant could impact the interacting proteins. There is no negative control to show that the UAP56-E194Q variant is not just associated with many, many proteins. Another myc-tagged protein that does not interact would be an ideal control.

Our response

We thank reviewer 3 for this comment. To address this comment, we tried to co-IP UAP56 wt or UAP56 E194Q with a THO complex subunit THOC7 (new Fig. S2). The results show that neither UAP56 variant can co-IP THOC7 under our conditions (likely because the UAP56/THO complex intermediate during mRNA export is disassembled in an ATPase-independent manner (Hohmann et al., Nature 2025)).

Changes introduced:

• added co-IP experiment between UAP56 variants and THOC7 (new Fig. S2).

__Specific Comment 7: __With regard to Figure 3, the authors never define EB1::GFP in the text of the Results, so a reader unfamiliar with this system has no idea what they are seeing. Reading the Materials and Methods does not mitigate this concern as there is only a brief reference to a fly line and how the EB1::GFP is visualized by microscopy. This makes interpretation of the data presented in Figure 3A-C very challenging.

Our response

We thank reviewer 3 for pointing this out. We added a description of the EB1::GFP analysis in the corresponding Results section (p.8).

__Specific Comment 8: __The data shown for MICAL MS2 reporter localization in Figure 4 is nice, but is also fully expected on many former studies analyzing loss of UAP56 or UAP56 hypomorphs in different systems. While creating the reporter is admirable, to make the argument that MICAL localization is in some way preferentially impacted by loss of UAP56, the authors would need to examine several other transcripts. As presented, the authors can merely state that UAP56 seems to be required for the efficient export of an mRNA transcript, which is predicted based on dozens of previous studies dating back to the early 2000s.

Our response

Firstly, thank you for commenting on the validity of the experimental approach! The primary purpose of this experiment was to test whether the mechanism of UAP56 during dendrite pruning conforms with what is known about UAP56's cellular role - which it apparently does. We also noted that our statements regarding the specificity of UAP56 for Mical over other transcripts are difficult. While our experiments would be consistent with such a model, they do not prove it. We therefore toned down the corresponding statements (e. g., the concluding sentence at the end of first Results paragraphis now: "We conclude that c4da neuron dendrite pruning is particularly sensitive to loss of UAP56." (p. 6)).

Minor (and really minor) points:

In the second sentence of the Discussion, the word 'developing' seems to be mis-typed "While a general inhibition of mRNA export might be expected to cause broad defects in cellular processes, our data in develoing c4da neurons indicate that loss of UAP56 mainly affects pruning mechanisms related to actin remodeling."

Sentence in the Results (lack of page numbers makes indicating where exactly a bit tricky)- "We therefore reasoned that Mical expression could be more challenging to c4da neurons." This is a complete sentence as presented, yet, if something is 'more something'- the thing must be 'more than' something else. Presumably, the authors mean that the length of the MICAL transcript could make the processing and export of this transcript more challenging than typical fly transcripts (raising the question of the average length of a mature transcript in flies?).

Our response

Thanks for pointing these out. The typo is fixed, page numbers are added. We changed the sentence to: "Because of the large size of its mRNA, we reasoned that MICAL gene expression could be particularly sensitive to loss of export factors such as UAP56." (p.9) We hope this is more precise language-wise.

Reviewer #3 (Significance (Required)):

Understanding how post-transcriptional events are linked to key functions in neurons is important and would be of interest to a broad audience.

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Referee #3

Evidence, reproducibility and clarity

Summary:

In the manuscript by Frommeyer, Gigengack et al. entitled "The UAP56 mRNA Export Factor is Required for Dendrite and Synapse Pruning via Actin Regulation in Drosophila" the authors surveyed a number of RNA export/processing factors to identify any required for efficient dendrite and/or synapse pruning. They describe a requirement for a general poly(A) RNA export factor, UAP56, which functions as an RNA helicase. They also study links to aspects of actin regulation.

Overall, while the results are interesting and the impact of loss of UAP56 on the pruning is intriguing, some of the data are overinterpreted as presented. The argument that UAP56 may be specific for the MICAL RNA is not sufficiently supported by the data presented. The two stories about poly(A) RNA export/processing and the actin regulation seem to not quite be connected by the data presented. The events are rather distal within the cell, making connecting the nuclear events with RNA to events at the dendrites/synapse challenging.

There are a number of specific statements that are not supported by references. See, for example, these sentences within the Introduction- "Dysregulation of pruning pathways has been linked to various neurological disorders such as autism spectrum disorders and schizophrenia. The cell biological mechanisms underlying pruning can be studied in Drosophila." The Drosophila sentence is followed by some specific examples that do include references. The authors also provide no reference to support the variant that they create in UAP56 (E194Q) and whether this is a previously characterized fly variant or based on an orthologous protein in a different system. If so, has the surprising mis-localization been reported in another system?

Specific Comments:

Figure 1 shows the impact of loss of UAP56 on neuron dendrite pruning. The experiment employs both two distinct dsRNAs and a MARCM clone, providing confidence that there is a defect in pruning upon loss of UAP56. As the authors mention screening against 92 genes that caused splicing defects in S2 cells, inclusion of some examples of these genes that do not show such a defect would enhance the argument for specificity with regard to the role of UAP56. This control would be in addition to the more technical control that is shown, the mCherry dsRNA. Later the authors demonstrate a delay in the accumulation of the Mical protein, so if they assayed these pruning events at later times, would the loss of UAP56 cause a delay in these events as well? Such a correlation would enhance the causality argument the authors make for Mical levels and these pruning events.

Figure 2 provides data designed to test the requirement for the ATPase/helicase activity of UAP56 for these trimming events. The first observation, which is surprising, is the mislocalization of the variant (E194Q) that the authors generate. The data shown does not seem to indicate how many cells the results shown represent as a single image and trace is shown the UAP56::GFP wildtype control and the E194Q variant.

Given the rather surprising finding that the ATPase activity is not required for the function of UAP56 characterized here, the authors do not provide sufficient references or rationale to support the ATPase mutant that they generate. The E194Q likely lies in the Walker B motif and is equivalent to human E218Q, which can prevent proper ATP hydrolysis in the yeast Sub2 protein. There is no reference to support the nature of the variant created here.

Given the surprising results, the authors could have included additional variants to ensure the change has the biochemical effect that the authors claim. Previous studies have defined missense mutations in the ATP-binding site- K129A (Lysine to Alanine): This mutation, in both yeast Sub2 and human UAP56, targets a conserved lysine residue that is critical for ATP binding. This prevents proper ATP binding and consequently impairs helicase function. There are also missense mutations in the DEAD-box motif, (Asp-Glu-Ala-Asp) involved in ATP binding and hydrolysis. Mutations in this motif, such as D287A in yeast Sub2 (corresponding to D290A in human UAP56), can severely disrupt ATP hydrolysis, impairing helicase activity. In addition, mutations in the Walker A (GXXXXGKT) and Walker B motifs are can impair ATP binding and hydrolysis in DEAD-box helicases. Missense mutations in these motifs, like G137A (in the Walker A motif), can block ATP binding, while E218Q (in the Walker B motif)- which seems to be the basis for the variant employed here- can prevent proper ATP hydrolysis.

The co-IP results shown in Figure 2C would also seem to have multiple potential interpretations beyond what the authors suggest, an inability to disassemble a complex. The change in protein localization with the E194Q variant could impact the interacting proteins. There is no negative control to show that the UAP56-E194Q variant is not just associated with many, many proteins. Another myc-tagged protein that does not interact would be an ideal control.

With regard to Figure 3, the authors never define EB1::GFP in the text of the Results, so a reader unfamiliar with this system has no idea what they are seeing. Reading the Materials and Methods does not mitigate this concern as there is only a brief reference to a fly line and how the EB1::GFP is visualized by microscopy. This makes interpretation of the data presented in Figure 3A-C very challenging. The data shown for MICAL MS2 reporter localization in Figure 4 is nice, but is also fully expected on many former studies analyzing loss of UAP56 or UAP56 hypomorphs in different systems. While creating the reporter is admirable, to make the argument that MICAL localization is in some way preferentially impacted by loss of UAP56, the authors would need to examine several other transcripts. As presented, the authors can merely state that UAP56 seems to be required for the efficient export of an mRNA transcript, which is predicted based on dozens of previous studies dating back to the early 2000s.

Minor (and really minor) points:

In the second sentence of the Discussion, the word 'developing' seems to be mis-typed "While a general inhibition of mRNA export might be expected to cause broad defects in cellular processes, our data in develoing c4da neurons indicate that loss of UAP56 mainly affects pruning mechanisms related to actin remodeling."

Sentence in the Results (lack of page numbers makes indicating where exactly a bit tricky)- "We therefore reasoned that Mical expression could be more challenging to c4da neurons." This is a complete sentence as presented, yet, if something is 'more something'- the thing must be 'more than' something else. Presumably, the authors mean that the length of the MICAL transcript could make the processing and export of this transcript more challenging than typical fly transcripts (raising the question of the average length of a mature transcript in flies?).

Significance

Understanding how post-transcriptional events are linked to key functions in neurons is important and would be of interest to a broad audience.

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Referee #2

Evidence, reproducibility and clarity

In this paper, the authors describe dendrite pruning defects in c4da neurons in the DEXD box ATPase UAP56 mutant or in neuronal RNAi knockdown. Overexpression UAP56::GFP or UAP56::GFPE194Q without ATPase activity can rescue dendrite pruning defects in UAP56 mutant. They further characterized the mis-localization of UAP56::GFPE194Q and its binding to nuclear export complexes. Both microtubules and the Ubiquitin-proteasome system are intact in UAP56RNAi neurons. However, they suggest a specific effect on MICAL mRNA nuclear export shown by using the MS2-MCP system., resulting in delay of MICAL protein expression in pruned neurons. Furthermore, the authors show that UAP56 is also involved in presynaptic pruning of c4da neuros in VNC and Mica and actin are also required for actin disassembly in presynapses. They propose that UAP56 is required for dendrite and synapse pruning through actin regulation in Drosophila. Following are my comments.

Major comments

1. The result that UAP56::GFPE194Q rescues the mutant phenotype while the protein is largely mis-localized suggests a novel mechanism or as the authors suggested rescue from combination of residual activities. The latter possibility requires further support, which is important to support the role mRNA export in dendrite and pre-synapse pruning. One approach would be to examine whether other export components like REF1, and NXF1 show similar mutant phenotypes. Alternatively, depleting residual activity like using null mutant alleles or combining more copies of RNAi transgenes could help.

2. The localization of UAP56::GFP (and E194Q) should be analyzed in more details. It is not clear whether the images in Fig. 2A and 2B are from confocal single sections or merged multiple sections. The localization to the nuclear periphery of UAP56::GFP is not clear, and the existence of the E194Q derivative in both nucleus and cytosol (or whether there is still some peripheral enrichment) is not clear if the images are stacked.

3. The Ub-VV-GFP is a new reagent, and its use to detect active proteasomal degradation is by the lack of GFP signals, which could be also due to the lack of expression. The use of Ub-QQ-GFP cannot confirm the expression of Ub-VV-GFP. The proteasomal subunit RPN7 has been shown to be a prominent component in the dendrite pruning pathway (Development 149, dev200536). Immunostaining using RPN7 antibodies to measure the RPN expression level could be a direct way to address the issue whether the proteasomal pathway is affected or not.

4. Using the MS2/MCP system to detect the export of MICAL mRNA is a nice approach to confirm the UAP56 activity; lack of UAP56 by RNAi knockdown delays the nuclear export of MS2-MICAL mRNA. The rescue experiment by UAS transgenes could not be performed due to the UAS gene dosage, as suggested by the authors. However, this MS2-MICAL system is also a good assay for the requirement of UAP56 ATPase activity (absence in the E194Q mutant) in this process. Could authors use the MARCM (thus reduce the use of UAS-RNAi transgene) for the rescue experiment? Also, the c4da neuronal marker UAS-CD8-GFP used in Fig4 could be replaced by marker gene directly fused to ppk promoter, which can save a copy of UAS transgene. The results from the rescue experiment would test the dependence of ATPase activity in nuclear export of MICAL mRNA.

5. The UAP56 is also involved in presynaptic pruning through regulating actin assembly, and the authors suggest that Mical and cofilin are involved in the process. However, direct observation of lifeact::GFP in Mical or cofilin RNAi knockdown is important to support this conclusion.

Minor comments

1. RNA localization is important for dendrite development in larval stages (Brechbiel JL, Gavis ER. Curr Biol. 20;18(10):745-750). Yet, the role of UAP56 is relatively specific and shown only in later-stage pruning. It would need thorough discussion.

2. Could authors elaborate on the possible upstream regulators that might be involved, as described in "alternatively, several cofilin upstream regulators have been described (Rust, 2015) which might also be involved in presynapse pruning and subject to UAP56 regulation" in Discussion?

3. In Discussion, the role of cofilin in pre- and post-synaptic processes was described. The role of Tsr/Cofilin regulating actin behaviors in dendrite branching has been described in c3da and c4da neurons (Nithianandam and Chien, 2018 and other references) should be included in Discussion.

4. The authors speculate distinct actin structures have to be disassembled in dendrite and presynapse pruning in Discussion. What are the possible actin structures in both sites could be elaborated.

Significance

The study initiated a genetic screen for factors involved in a dendrite pruning system and reveals the involvement of nuclear mRNA export is an important event in this process. They further identified the mRNA of the actin disassembly factor MICAL is a candidate substrate in the exporting process. This is consistent with previous finding that MICAL has to be transcribed and translated when pruning is initiated. As the presynapses of the model c4da neuron in this study is also pruned, the dependence on nuclear export and local actin remodeling were also shown. Thus, this study has added another layer of regulation (the nuclear mRNA export) in c4da neuronal pruning, which would be important for the audience interested in neuronal pruning. The study is limited for the confusing result whether ATPase activity of the exporting factor is required.

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Referee #1

Evidence, reproducibility and clarity

Summary:

This manuscript by Frommeyer et al. explores the role of the helicase and regulator of nuclear export, UAP56, in the control of dendrite and presynaptic pruning in Drosophila larval da sensory neurons. The authors present evidence showing that UAP56 regulates these processes via the actin cytoskeleton and suggest that this is occurs by controlling the expression of the actin severing enzyme, Mical.

Major comments:

The most signficant issue with the manuscript is that some of the major conclusions are not supported by the data. Additional experiment would need to be completed in order support these claims. These (and other) major comments are as follows:

1. For Figure 4, the ms2/MCP system is not quantitative. Using this technique, it is impossible to determine how many RNAs are located in each "dot". Each of these dots looks quite large and likely corresponds to some phase-separated RNP complex where multiple RNAs are stored and/or transported. Thus, these data do not support the conclusion that Mical mRNA levels are reduced upon UAP56 knockdown. A good quantitative microscopic assay would be something like smFISH. Additinally, the localization of Mical mRNA dots to dendrites is not convincing as it looks like regions where there are dendritic swellings, the background is generally brighter.

2. Alternatively, levels of Mical mRNA could be verified by qPCR in the laval brain following pan-neuronal UAP56 knockdown or in FACS-sorted fluorescently labeled da sensory neurons. Protein levels could be analyzed using a similar approach.

3. In Figure 5, the authors state that Mical expression could not be detected at 0 h APF. The data presented in Fig. 5C, D suggest the opposite as there clearly is some expression. Moreover, the data shown in Fig. 5D looks significantly brighter than the Orco dsRNA control and appears to localize to some type of cytoplasmic granule. So the expression of Mical does not look normal.

4. Sufficient data are not presented to conclude any specificity in mRNA export pathways. Data is presented for one export protein (UAP56) and one putative target (Mical). To adequately assess this, the authors would need to do RNA-seq in UAP56 mutants.

5. In summary, better quantitative assays should be used in Figures 4 and 5 in order to conclude the expression levels of either mRNA or protein. In its current form, this study demonstrates the novel finding that UAP56 regulates dendrite and presynaptic pruning, potentially via regulation of the actin cytoskeleton. However, these data do not convincingly demonstrate that UAP56 controls these processes by regulating of Mical expression and defintately not by controlling export from the nucleus.

6. While there are clearly dendrites shown in Fig. 1C', the cell body is not readily identifiable. This makes it difficult to assess attachment and suggests that the neuron may be dying. This should be replaced with an image that shows the soma.

7. The level of knockdown in the UAS56 RNAi and P element insertion lines should be determined. It would be useful to mention the nature of the RNAi lines (long/short hairpin). Some must be long since Dcr has been co-expressed. Another issue raised by this is the potential for off-target effects. shRNAi lines would be preferable because these effects are minimized.

Minor comments:

1. The authors should explain what EB1:GFP is marking when introduced in the text.

2. The da neuron images througout the figures could be a bit larger.

Significance

Strengths:

The methodology used to assess dendrite and presynaptic prunings are strong and the phenotypic analysis is conclusive.

Weakness:

The evidence demonstrating that UAP56 regulates the expression of Mical is unconvincing. Similarly, no data is presented to show that there is any specificity in mRNA export pathways. Thus, these major conclusions are not adequately supported by the data.

Advance:

The findings that UAP56 regulate dendrite and synaptic pruning are novel. As is its specific regulation of the actin cytoskeleton. These findings are restricted to a phenotypic analysis and do not show that it is not simply due to the disruption of general mRNA export.

Audience:

In its current form the manuscript whould be of interest to an audience who specializes in the study of RNA binding proteins in the control of neurodevelopment. This would include scientists who work in invertebrate and vertebrate model systems.

My expertise:

My lab uses Drosophila to study the role of RNA binding proteins in neurodevelopment and neurodegeneration. Currently, we use flies as a model to better understand the molecular pathogenesis of neurodevelopmenal disorders such as FXS and ASD.

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Reply to the reviewers

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

*Using genetics and microscopy approaches, Cabral et al. investigate how fission yeast regulates its length and width in response to osmotic, oxidative, or low glucose stress. Miller et al. have recently found that the cell cycle regulators Cdc25, Cdc13 and Cdr2 integrate information about cell volume, time and cell surface area into the cellular decision when to divide. Cabral now build on this work and test how disruption of these regulators affects cell size adaptation. They find that each stress condition shows a distinct dependence on the individual regulators, suggesting that the complex size control network enables optimized size adaptation for each condition. Overall, the manuscript is clear and the detailed methods ensure that the experiments can be replicated.

Major comments:

1.) It would be much easier to follow the authors' conclusions, if in addition to surface area to volume ratio, length and width, they would also plot cell volume at division in Figs. 1-4.*

AUTHOR RESPONSE: Due to space constraints in the main (and supplemental) figures, we focused on SA:Vol ratio together with cell length and width, which directly define cell geometry in rod-shaped fission yeast. Surface area and volume are derived from these measurements and can be misleading when considered alone, as similar surface area or volume values can arise from distinct combinations of length and width. The SA:Vol ratio therefore serves as a robust integrative metric for capturing coordinated changes in length and width that reshape cell geometry. We would be happy to include individual surface area and volume plots if requested.

2.) To me, it seems that maybe even more than upon osmotic stress, the cdc13-2x strain differs qualitatively from WT in low glucose conditions, where the increased SA-V ratio is almost completely abolished.

AUTHOR RESPONSE: We agree with the reviewer and have revised the manuscript text to point out this difference. The newly added text states: “Under low glucose, cdc13-2x cells also showed a WT-like response, decreasing length and increasing in SA:Vol ratio (Figures 3B-D). However, this SA:Vol increase was reduced compared to WT (1% vs 8.5%; Figures 1D and 3B), suggesting impaired geometric remodeling under glucose limitation.”

3.) It is not entirely clear to me why two copies of Cdc13 would qualitatively affect the responses. Shouldn't the extra copy behave similarly to the endogenous one and therefore only lead to quantitative changes? Maybe the authors can discuss this more clearly or even test a strain in which Cdc13 function is qualitatively disrupted.

AUTHOR RESPONSE: Increased Cdc13 protein concentration in cdc13-2x cells disrupts the typical time-scaling of Cdc13 protein. Consistent with this, cdc13-2x cells enter mitosis at a smaller cell size. We have modified the text to clarify this point. The new text states: “To access the role of the Cdc13 time-sensing pathway, we disrupted Cdc13 protein abundance by creating a cdc13-2x strain carrying an additional copy of cdc13 integrated at an exogenous locus. cdc13-2x cells divided at a smaller size than WT, reflecting accelerated mitotic entry upon disruption of typical time-scaling of Cdc13 protein (Figure S1A).”

4.) I don't see why the authors come to the conclusion that under osmotic stress cells would maximize cell volume. It leads to a decreased cell length, doesn't it?

AUTHOR RESPONSE: WT cells under osmotic stress do decrease in length, but this is accompanied by an increase in cell width. Because width contributes disproportionately to cell volume in rod-shaped cells, this change results in a modest but reproducible reduction in the SA:Vol ratio relative to WT cells in control medium (Figure 1D). We note that the degree of this change under osmotic stress is small (-0.4%), although statistically significant (p * Likewise, in Figure 2B, they interpret tiny changes in the SA/V. By my estimation, the difference between control and osmotic stress is only 2% (1.195/1.17), less that the wild-type case, which appears to be twice that (which is still pretty modest). The small amplitude of these changes is obscured by the fact that the graphs do not have a baseline at zero, which, as a matter of good data-presentation practice, they should.

*

AUTHOR RESPONSE: We appreciate the reviewer’s distinction between statistical and biological significance and agree that this is an important point to clarify. We now note in the revised text that changes in SA:Vol ratio under osmotic stress are numerically small and should not be overinterpreted. Our revised text now states: “Under oxidative and osmotic stress, the SA:Vol ratio decreased, indicating greater cell volume expansion relative to surface area (Figure 1D). However, we note that the reduction in SA:Vol under osmotic stress, while statistically significant, was modest in magnitude (−0.4%).”

Although small in absolute terms, even subtle geometric changes can be biologically meaningful in fission yeast due to the small size of these cells, where minor shifts in length or width translate into measurable differences in membrane area relative to cytoplasmic volume. Importantly, in Figure 2B, the key observation is not the magnitude of the change but its direction: cdc25-degron-DaMP cells exhibit a ~2% increase in SA:Vol ratio under osmotic stress, in contrast to the decrease observed in WT cells under the same condition. This opposite response reflects altered cell geometry and is supported by corresponding changes in cell length and width. We have revised the Results text to emphasize both the modest magnitude and the directional nature of these effects: “Under osmotic stress, cdc25-degron-DaMP cells exhibited a ~2% increase in SA:Vol ratio, opposite to the modest decrease observed in WT cells. This increase arose from increased cell length and reduced width (Figures 2B-D).”

Regarding data presentation, because SA:Vol ratios vary over a narrow numerical range, setting the y-axis minimum to zero would compress the data and obscure all detectable differences. Instead, we have modifed our SA:Vol ratio graphs in Fig. 1-4 to have consistent axis scaling across panels to accurately convey relative changes while maintaining visual clarity. We are happy to provide full data tables and statistical outputs upon request.

* I am also concerned about the use of manual measurement of width at a single point along the cell. This approach is very sensitive to the choice of width point and to non-cylindrical geometries, several of which are evident in the images presented. MATLAB will return the ??? as well as the length from a mask, but even better, one can more accurately calculate the surface area and volume by assuming rotational symmetry of the mask. Given that surface area and volume calculation need to be redone anyway, as discussed below, I encourage the authors to calculate them directly from the mask, instead of using the cylindrical assumption.*

AUTHOR RESPONSE: In initial experiments to calculate surface area and volume of fission yeast cells for prior work (Miller et al., 2023, Current Biology) we found that automated width measurements by MATLAB or ImageJ were inaccurate for a subset of cells leading to noisy cell surface area and volume values. Measuring cell width by hand and assuming that each cell in a given strain had the same cell radius (average of population) for calculation of cell surface area and volume gave more consistent results and recapitulated established conclusions regarding size control mechanisms.

In this previous work and the current study, abnormally skinny or wide regions of a cell were avoided when drawing a line to measure the cell width by hand. For each strain and condition, an average cell width was determined per independent experiment and used for surface area and volume calculations. Additionally, previous analysis demonstrated that this approach yields results consistent with a rotation method derived directly from cell masks, which does not assume a cylindrical cell shape (Facchetti et al., 2019, Current Biology; Miller et al., 2023, Current Biology).

To test the validity of our size measurements and confirm the robustness of our results in this study we compared the surface area and volume of cells by this rotation method. We have added this additional information to our revised methods section and also added SA:Vol ratio graphs generated from the rotation size measurement to our revised Figure S1 E-J. Importantly, both approaches used to measure cell size gave consistent results and supported the same conclusions.*

The authors also need to be more careful about their claims about size-dependent scaling. The concentration of both Cdc13 and Cdc25 scale with size (perhaps indirectly, in the case of Cdc13), but Cdr2 does not. Cdr2 activity has been proposed to scale with size, and its density at cortical nodes has been reported to scale with size, although that claim has been challenged .*

AUTHOR RESPONSE: We have modified text in the Introduction and Results to address this point. Our revised text in the introduction states: “Recent work has shown that Cdk1 activation integrates size- and time-dependent inputs: the Wee1-inhibitory kinase Cdr2 cortical node density scales with cell surface area (Pan et al., 2014; Facchetti et al., 2019); Cdc25 nuclear accumulation scales with cell volume; and cyclin Cdc13 accumulates over time in the nucleus (Miller et al., 2023) (Figure 1B).” Our revised text in the results section states: “Cdr2 functions as a cortical scaffold that regulates Wee1 activity in relation to cell size, with Cdr2 nodal density reported to scale with cell surface area, enforcing a surface area threshold for mitotic entry (Pan et al., 2014; Allard et al., 2018; Facchetti et al., 2019; Sayyad and Pollard, 2022).”*

Even taking the authors approach at face value, there are observations that do not seem to make sense, which led me to realize that the wrong formulae were used to calculate surface area and volume.

In Figure 1E,F, the KCl-treated cells get shorter and wider; surely, that should result in a lower SA/V ratio. However, as noted above, in Figure 1D, they are shown to have a similar ratio. As a sanity check, I eye-balled the numbers off of the figure (control: 14 µm x 3.6 µm and KCl: 11 µm x 3.8 µm) and calculated their surface area and volume using the formula for a capsule (i.e., a cylinder with hemispheric ends).

SA = the surface area of the two hemispheres + the surface are of the cylinder in between = 4*pi*(width/2)^2 + pi*width*(length-width), the length-width term calculates the side length of the capsule (length without the hemispheres) from the full length of the capsule (length including the hemispheres)

V = the volume of the two hemispheres + the volume of the cylinder in between = 4/3*pi*(width/2)^3 + pi*(width/2)^2*(length-width).

I got SA/V ratios of around 2, which are way off from what is presented in Figure 1D, but my calculated ratio goes down in KCl, as expected, but not as reported.

To make sure I was not doing something wrong, I was going to repeat my calculations with the formulae in Table 1, which made me realize both are incorrect. The stated formula for the cell surface area-2*pi*RL-only represents to surface area of the cylindrical side of the cells, not its hemispherical ends. And it is not even the correct formula for the surface area of the side, because that calls for L to be the length of the side (without the hemispherical ends) not the length of the cell (which includes the hemispherical ends). L here is stated to be cell length (which is what is normally measured in the field, and which is consistent with the reported length of control cells in Figure 1E being 14 µm). The formula for the volume of a capsule in the form use in Table 1 (volume of a cylinder of length L - the volume excluded from the hemispherical ends) is pi*R^2*L - (8-(4/3*pi))*R^3.

Given these problems, I think I spent too much time thinking about the rest of the paper, because all of the calculations, and perhaps their interpretations, need to be redone.*

AUTHOR RESPONSE: The surface area and volume equations for a cylinder with hemispherical ends used in our study and listed in our table are correct and widely used in other work with fission yeast cells (Navarro and Nurse, 2012; Pan et al., 2014; Facchetti et al., 2019; BayBay et al., 2020; and Miller et al., 2023). We write our equations with variables for cell length and radius because these are biologically relevant and measured parameters for fission yeast cells. Cell length (L) refers to the total tip-to-tip length of the cell, including the hemispherical ends, and radius (R) refers to half the measured cell width. We have revised the Methods section to clarify this definition and avoid ambiguity (Please see methods section “Cell geometry measurements”)

Additionally, SA or Vol calculations were performed using the length of each individual cell and the average cell radius of the population. We did not use mean cell length of the population for our calculations like the reviewer assumed in their “sanity check” above. Please see methods section “Cell geometry measurements”. We hope that these clarifications and text revisions improve transparency and reproducibility.

* Minor Points:

Strains should be identified by strain number is the text and figure legends.*

AUTHOR RESPONSE: For clarity and readability, we refer to strains by genotype in the main text and figure legends, which we believe is more informative for readers than strain numbers. All strain numbers corresponding to each genotype are provided in Table S1, ensuring traceability and reproducibility without compromising clarity in data presentation.*

In the Introduction, "Most cell control their size" should be "Most eukaryotic cell control their size".*

• *

AUTHOR RESPONSE: The text has been corrected as suggested.*

Reviewer #2 (Significance (Required)):

Nothing to add.*

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

Summary This manuscript reports that fission yeast cells exhibit distinct cell size and geometry when exposed to osmotic, oxidative, or low-glucose stress. Based on quantitative measurements of cell length and width, the authors propose that different stress conditions trigger specific 'geometric adaptation' patterns, suggesting that cell size homeostasis is flexibly modulated depending on environmental cues. The study provides phenotypic evidence that multiple environmental stresses lead to distinct outcomes in the balance between cell surface area and volume, which the authors interpret as stress-specific modes of size control.

Major comments 1) The authors define the 48-hour time point as the 'long-term response', but no justification is provided for why 48 hours represents a physiologically relevant adaptation phase. It is unclear whether the size-control mode has stabilized by that time, or whether it may continue to change afterward. At minimum, the authors should provide a rationale (e.g., growth recovery dynamics, transcriptional adaptation plateau, or pilot time-course observations) to demonstrate that 48 hours corresponds to the steady-state adaptive phase rather than an arbitrarily selected time point.*

AUTHOR RESPONSE: We thank the reviewer for this important point and agree that the definition of the long-term response should be clarified. We have addressed this with new experiments and revised text. We now incorporate growth curve data and doubling time analyses for all yeast strains grown under control and stress conditions (See new Figure S3). These analyses show that following an initial transient stress-induced cell cycle delay, growth rates stabilize well before 48 hours. Notably, the slowest growth rate observed was in 1M KCl, with a doubling time of ~4 hours across all yeast strains tested. Thus, by 48 hours, cells in this condition have undergone more than 12 generations of growth, while cells in all other conditions with shorter doubling times have undergone even more divisions. So by allowing cells to grow for 48 hours prior to imaging, we are capturing cells that have resumed sustained cell cycle progression following transient stress-induced cell cycle delays. Because cell size control is tightly linked to the cell cycle, we define 48 hours as a physiologically relevant time point where cells have adapted to stress conditions.

Our revised methods now states: “Cultures were incubated at 25°C while shaking at 180 rpm for 48 h prior to imaging. This time point was chosen to ensure that cells had progressed beyond the initial transient stress response and reached a stable, condition-specific growth state, as confirmed by growth curve and doubling time analyses showing stabilization well before 48 h (Figure S3), including in the slowest growing condition (1 M KCl; doubling time ~4 h).”

* 2*）Related to the above comment, the authors propose that different stresses lead to distinct cell size adaptations, yet the rationale for the chosen stress intensities and exposure times is insufficiently described. It remains unclear whether the osmotic, oxidative, and low-glucose conditions used here induce comparable levels of cellular stress. Dose-response and time-course analyses would greatly strengthen the conclusions. Without such analyses, it is difficult to support the interpretation that geometry modulation represents a direct adaptive response.

AUTHOR RESPONSE: * *We selected the specific stress conditions based on previously published work showing that these doses elicit robust responses while preserving overall cell viability and the capacity for recovery. We note that osmotic, oxidative, and low glucose conditions perturb fundamentally different cellular systems (turgor pressure and cell wall mechanics, redox balance, and metabolism etc.) and therefore do not generate directly comparable levels of cellular stress in a quantitative sense. Our goal was not to equalize stress intensity across conditions, but to examine how cells change their geometry in response to distinct classes of stressors.

We have clarified the rationale for specific stress conditions in the revised methods: “These stress intensities were selected based on prior studies demonstrating robust cellular responses while preserving cell viability and the capacity for recovery (Fantes and Nurse, 1977, Shiozaki and Russell, 1995, Degols, et al., 1996; López-Avilés et al., 2008; Sansó et al., 2008; Satioh et al., 2015, Salat-Canela et al., 2021, Bertaux et al., 2023).”

* 3) The authors describe stress-induced size changes as an 'adaptive' response. While this is an appealing hypothesis, the presented data do not demonstrate that the change in cell size itself confers a fitness advantage. Evidence showing that blocking the size change reduces stress survival-or that the altered size improves growth recovery- would be required to support this claim. Without such data, the use of the term 'geometric adaptation' seems overstated.*

AUTHOR RESPONSE: We have revised the text to remove the term “adaptive” and now describe stress-induced size changes in descriptive terms. As discussed further in response to Comment 4, new growth curve and doubling time analyses show that defects in surface area or volume expansion do not uniformly impair growth or survival over the stress exposure examined here, reinforcing the decision to avoid fitness-based language.*

4) The authors conclude that mutants exhibit no major defects in growth or viability during 48-hour stress exposure based on comparable septation index values (Fig. S2). However, septation index alone does not fully capture growth performance or cell-cycle progression and is not sufficient to support claims regarding fitness or robustness of proliferation. If the authors intend to make statements about 'growth', 'viability', or 'cell-cycle progression', additional quantitative measures (e.g., growth curves, doubling time, colony-forming units, or microcolony growth measurements) would be necessary. Alternatively, the claims should be toned down to align with the measurements currently provided.*

AUTHOR RESPONSE: We have addressed this concern with new experiments and revised text. In addition to septation index measurements (now analyzed using chi-square tests of proportions; Figure S2), we performed growth curve experiments and doubling time analyses for all genotypes under control and stress conditions (new Figure S3). These additional data show that growth rates are largely comparable across genotypes in control, oxidative, and low-glucose conditions, with more pronounced genotype-dependent differences emerging under osmotic stress. Defects in surface area or volume expansion did not uniformly correspond to impaired population growth, indicating that geometric remodeling is not strictly required for proliferation over the 48-hour stress exposure examined here. We have refined our conclusion to emphasize that defects in surface area or volume expansion do not uniformly impair growth or survival. See revised Results text under the heading “Defects in surface area or volume expansion do not uniformly compromise growth or survival”.*

5) Related to the above comment, the manuscript does not adequately rule out the possibility that the decreased division size simply results from slower growth or delayed cell-cycle progression rather than a shift in the size-control mechanism. Measurements and normalizations of growth rate are required; without them, the interpretation remains speculative.*

AUTHOR RESPONSE: We agree that changes in growth rate or altered cell cycle timing are important to consider. We have revised our text: “Changes in growth rate or cell cycle progression under stress may influence division size by altering mitotic regulator accumulation. Future studies measuring mitotic regulator dynamics alongside growth rates will be needed to distinguish direct changes in size control mechanisms from growth- or timing-dependent effects.”

* 6) Regarding the phenotypes of wee1-2x cells, it is interesting that they increase the SA:Vol ratio under all stress conditions and show phenotypes distinct from cdr2Δ cells. From these observations, the authors claims that Cdr2 and Wee1 function as a surface-area-sensing module that complements the volume-sensing and time-sensing pathways to maintain geometric homeostasis. To support this interpretation, the authors could consider additional experiments, such as analyzing cdr2Δ + wee1-2x cells under the same stress conditions. Such data would test whether increased Wee1 can rescue or modify the cdr2Δ phenotype, providing functional evidence for the proposed Cdr2-Wee1-Cdk1 regulatory relationship. Measurements of cell length, width, SA:Vol ratio, and, if feasible, Cdk1 activity markers in the strain would greatly strengthen the mechanistic claims.*

AUTHOR RESPONSE: We thank the reviewer for this insightful suggestion. While analysis of a cdr2Δ wee1-2x strain could provide additional mechanistic detail, such experiments address a distinct question beyond the scope of our current study, which focuses on how cell geometry changes under different stress conditions in cells with perturbed surface area-, volume-, or time-sensing pathways. Our conclusions regarding a surface area-sensing role for Cdr2-Wee1 signaling are based on previous studies (Pan et al., 2014; Facchetti et al., 2019; Miller et al., 2023) and the cell geometry phenotypes we observe of cdr2Δ and wee1-2x cells under stress conditions. *

Minor comments 1) The manuscript focuses on adaptation through changes in the surface-to-volume ratio; however, only the ratio is shown. Presenting the underlying values of surface area and volume would clarify which geometric parameter primary contributes to the observed changes.*

AUTHOR RESPONSE: Please see our response to Reviewer 1 major comment 1.*

*2) Statistical analysis for Fig.S2 should be provided.

AUTHOR RESPONSE: We have completed this. See revised Figure S2 and methods.*

3) The paper by Kellog and Levin 2022 is missing from the reference list.*

AUTHOR RESPONSE: Thank you for catching this. This reference has now been added. *

**Referees cross-commenting**

After reading the other reviewer's reports, I recognize that focal points differ, but they appear sequential rather than contradictory.

Reviewer 2 raises concerns regarding the surface area/volume calculations, which-if incorrect-would influence many of the quantitative conclusions. I agree that confirming the validity of these calculations (and recalculating if necessary) should be the top priority before evaluating the biological interpretations.

Reviewer 1 raises more mechanistic biological questions. These are certainly important, but in my view they depend on the robustness of the quantitative analysis highlighted by Reviewer 2.

Therefore, I regard the reports as complementary rather than conflicting. Once the analytical issue pointed out by Reviewer 2 is resolved, the field will be in a better position to assess the significance of the mechanistic points raised by Reviewer 1 (as well as those in my own report).

Reviewer #3 (Significance (Required)):

General assessment One of the major strengths of this manuscript is its quantitative, side-by-side comparison of multiple environmental stresses under a unified experimental and analytical framework. The authors provide well-controlled morphometric measurements, allowing direct comparison of geometry changes that would otherwise be difficult to evaluate across studies. The observation that different stress types generate distinct geometric outcomes is particularly intriguing and has the potential to stimulate new conceptual thinking in the field of size control. However, the strength of the conceptual conclusion is currently limited by several aspects of the experimental design and interpretation. In particular, it remains unclear whether the observed geometry changes represent active adaptive responses rather than non-specific consequences of prolonged or string stress exposure. Demonstrating whether geometry remodeling provides a fitness advantage, clarifying whether the changes reach a steady-state rather than reflecting slow drift over time, or identifying upstream stress pathways that govern the response would substantially strengthen the conceptual advance. Even if additional mechanistic or fitness-related data cannot be added, refining the interpretation so that it remains aligned with the present evidence will enhance the clarity, and impact of the study.

Advance Previous study - including the 2023 publication by the James B. Moseley group - established that fission yeast integrates distinct size-control pathways related to surface area, volume, and time under normal growth conditions. The present manuscript extends this line of work to stressed environments and argues that each stress condition elicits a distinct size-control pattern. To our knowledge, a systematic comparison of cell geometry across multiple stress types in the context of size-control pathways has not been reported, and this represents a potentially valuable conceptual advance. The advance is primarily phenomenological and conceptual rather than mechanistic: the work presents new correlation between stress types and geometry but does not yet elucidate the pathways governing these responses or demonstrate a functional advantage. With additional evidence - or with qualifiers ensuring that claims match the current data - the study could make an important contribution to understanding how cells integrate environmental cues into size-control strategies.

Audience Although the primary audience consists of researchers in the fields of cell growth, cell-cycle control, and stress responses in yeast, the conceptual contribution may interest broader fields such as growth homeostasis, metabolic adaptation, and pathological cell size changes in higher eukaryotes. Beyond yeast biology, the modular view of size regulation proposed here may inspire new investigations in stem cell biology, cancer research, and biotechnology where environmental adaptation and cell size are closely linked.

Expertise: nuclear morphology; cell morphology; cell growth; cell cycle; cytoskeleton*

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript reports that fission yeast cells exhibit distinct cell size and geometry when exposed to osmotic, oxidative, or low-glucose stress. Based on quantitative measurements of cell length and width, the authors propose that different stress conditions trigger specific 'geometric adaptation' patterns, suggesting that cell size homeostasis is flexibly modulated depending on environmental cues. The study provides phenotypic evidence that multiple environmental stresses lead to distinct outcomes in the balance between cell surface area and volume, which the authors interpret as stress-specific modes of size control.

Major comments

1) The authors define the 48-hour time point as the 'long-term response', but no justification is provided for why 48 hours represents a physiologically relevant adaptation phase. It is unclear whether the size-control mode has stabilized by that time, or whether it may continue to change afterward. At minimum, the authors should provide a rationale (e.g., growth recovery dynamics, transcriptional adaptation plateau, or pilot time-course observations) to demonstrate that 48 hours corresponds to the steady-state adaptive phase rather than an arbitrarily selected time point.

2）Related to the above comment, the authors propose that different stresses lead to distinct cell size adaptations, yet the rationale for the chosen stress intensities and exposure times is insufficiently described. It remains unclear whether the osmotic, oxidative, and low-glucose conditions used here induce comparable levels of cellular stress. Dose-response and time-course analyses would greatly strengthen the conclusions. Without such analyses, it is difficult to support the interpretation that geometry modulation represents a direct adaptive response.

3) The authors describe stress-induced size changes as an 'adaptive' response. While this is an appealing hypothesis, the presented data do not demonstrate that the change in cell size itself confers a fitness advantage. Evidence showing that blocking the size change reduces stress survival-or that the altered size improves growth recovery- would be required to support this claim. Without such data, the use of the term 'geometric adaptation' seems overstated.

4) The authors conclude that mutants exhibit no major defects in growth or viability during 48-hour stress exposure based on comparable septation index values (Fig. S2). However, septation index alone does not fully capture growth performance or cell-cycle progression and is not sufficient to support claims regarding fitness or robustness of proliferation. If the authors intend to make statements about 'growth', 'viability', or 'cell-cycle progression', additional quantitative measures (e.g., growth curves, doubling time, colony-forming units, or microcolony growth measurements) would be necessary. Alternatively, the claims should be toned down to align with the measurements currently provided.

5) Related to the above comment, the manuscript does not adequately rule out the possibility that the decreased division size simply results from slower growth or delayed cell-cycle progression rather than a shift in the size-control mechanism. Measurements and normalizations of growth rate are required; without them, the interpretation remains speculative.

6) Regarding the phenotypes of wee1-2x cells, it is interesting that they increase the SA:Vol ratio under all stress conditions and show phenotypes distinct from cdr2Δ cells. From these observations, the authors claims that Cdr2 and Wee1 function as a surface-area-sensing module that complements the volume-sensing and time-sensing pathways to maintain geometric homeostasis. To support this interpretation, the authors could consider additional experiments, such as analyzing cdr2Δ + wee1-2x cells under the same stress conditions. Such data would test whether increased Wee1 can rescue or modify the cdr2Δ phenotype, providing functional evidence for the proposed Cdr2-Wee1-Cdk1 regulatory relationship. Measurements of cell length, width, SA:Vol ratio, and, if feasible, Cdk1 activity markers in the strain would greatly strengthen the mechanistic claims.

Minor comments

1) The manuscript focuses on adaptation through changes in the surface-to-volume ratio; however, only the ratio is shown. Presenting the underlying values of surface area and volume would clarify which geometric parameter primary contributes to the observed changes.

2) Statistical analysis for Fig.S2 should be provided.

3) The paper by Kellog and Levin 2022 is missing from the reference list.

Referees cross-commenting

After reading the other reviewer's reports, I recognize that focal points differ, but they appear sequential rather than contradictory.

Reviewer 2 raises concerns regarding the surface area/volume calculations, which-if incorrect-would influence many of the quantitative conclusions. I agree that confirming the validity of these calculations (and recalculating if necessary) should be the top priority before evaluating the biological interpretations.

Reviewer 1 raises more mechanistic biological questions. These are certainly important, but in my view they depend on the robustness of the quantitative analysis highlighted by Reviewer 2.

Therefore, I regard the reports as complementary rather than conflicting. Once the analytical issue pointed out by Reviewer 2 is resolved, the field will be in a better position to assess the significance of the mechanistic points raised by Reviewer 1 (as well as those in my own report).

Significance

General assessment

One of the major strengths of this manuscript is its quantitative, side-by-side comparison of multiple environmental stresses under a unified experimental and analytical framework. The authors provide well-controlled morphometric measurements, allowing direct comparison of geometry changes that would otherwise be difficult to evaluate across studies. The observation that different stress types generate distinct geometric outcomes is particularly intriguing and has the potential to stimulate new conceptual thinking in the field of size control. However, the strength of the conceptual conclusion is currently limited by several aspects of the experimental design and interpretation. In particular, it remains unclear whether the observed geometry changes represent active adaptive responses rather than non-specific consequences of prolonged or string stress exposure. Demonstrating whether geometry remodeling provides a fitness advantage, clarifying whether the changes reach a steady-state rather than reflecting slow drift over time, or identifying upstream stress pathways that govern the response would substantially strengthen the conceptual advance. Even if additional mechanistic or fitness-related data cannot be added, refining the interpretation so that it remains aligned with the present evidence will enhance the clarity, and impact of the study.

Advance

Previous study - including the 2023 publication by the James B. Moseley group - established that fission yeast integrates distinct size-control pathways related to surface area, volume, and time under normal growth conditions. The present manuscript extends this line of work to stressed environments and argues that each stress condition elicits a distinct size-control pattern. To our knowledge, a systematic comparison of cell geometry across multiple stress types in the context of size-control pathways has not been reported, and this represents a potentially valuable conceptual advance. The advance is primarily phenomenological and conceptual rather than mechanistic: the work presents new correlation between stress types and geometry but does not yet elucidate the pathways governing these responses or demonstrate a functional advantage. With additional evidence - or with qualifiers ensuring that claims match the current data - the study could make an important contribution to understanding how cells integrate environmental cues into size-control strategies.

Audience

Although the primary audience consists of researchers in the fields of cell growth, cell-cycle control, and stress responses in yeast, the conceptual contribution may interest broader fields such as growth homeostasis, metabolic adaptation, and pathological cell size changes in higher eukaryotes. Beyond yeast biology, the modular view of size regulation proposed here may inspire new investigations in stem cell biology, cancer research, and biotechnology where environmental adaptation and cell size are closely linked.

Expertise: nuclear morphology; cell morphology; cell growth; cell cycle; cytoskeleton.

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Referee #2

Evidence, reproducibility and clarity

Cabral et al. present a analysis of the effects of environmental stress of cellular geometry in the fission yeast S. pombe. The stresses they study-oxidative, osmotic and nutritional-have previously been shown to affect cell size in fission yeast. Here, the authors do a more sophisticated analysis, measuring surface area as well as volume (for which length had previously been used as a proxy, assuming fission yeast cells are cylinders of constant width). In addition, they investigate the effect of mutations in three cell-cycle control proteins that have been proposed to regulate cell geometry: Cdc13, Cdc25 and Cdr2. It is an interesting study that could provide insight into cell-size control and environmental-stress response in fission yeast. However, I have serious concerns about the analysis of the data. In fact, as I was writing up my concerns, I noticed that the formulae in Table 1 for surface area and volume are incorrect, so the whole paper appears to require reanalysis.

One general problem is that the authors seem to confuse statistical significance with biological significance. They claim that both oxidative and osmotic stress cause a reduction in SA/V ratio. For oxidative stress, the difference is evident, but the control and KCl-treated cells look to have indistinguishable distributions. Perhaps there is a significant statistical difference between the, but I am skeptical. (I would ask for the data table to try out the stats myself, but given the revelation below that the number will all need to be recalculated, that point is moot). In any case, the difference is certainly not biologically significant.

Likewise, in Figure 2B, they interpret tiny changes in the SA/V. By my estimation, the difference between control and osmotic stress is only 2% (1.195/1.17), less that the wild-type case, which appears to be twice that (which is still pretty modest). The small amplitude of these changes is obscured by the fact that the graphs do not have a baseline at zero, which, as a matter of good data-presentation practice, they should.

I am also concerned about the use of manual measurement of width at a single point along the cell. This approach is very sensitive to the choice of width point and to non-cylindrical geometries, several of which are evident in the images presented. MATLAB will return the ??? as well as the length from a mask, but even better, one can more accurately calculate the surface area and volume by assuming rotational symmetry of the mask. Given that surface area and volume calculation need to be redone anyway, as discussed below, I encourage the authors to calculate them directly from the mask, instead of using the cylindrical assumption.

The authors also need to be more careful about their claims about size-dependent scaling. The concentration of both Cdc13 and Cdc25 scale with size (perhaps indirectly, in the case of Cdc13), but Cdr2 does not. Cdr2 activity has been proposed to scale with size, and its density at cortical nodes has been reported to scale with size, although that claim has been challenged <https://pubmed.ncbi.nlm.nih.gov/36093997>.

Even taking the authors approach at face value, there are observations that do not seem to make sense, which led me to realize that the wrong formulae were used to calculate surface area and volume.

In Figure 1E,F, the KCl-treated cells get shorter and wider; surely, that should result in a lower SA/V ratio. However, as noted above, in Figure 1D, they are shown to have a similar ratio. As a sanity check, I eye-balled the numbers off of the figure (control: 14 µm x 3.6 µm and KCl: 11 µm x 3.8 µm) and calculated their surface area and volume using the formula for a capsule (i.e., a cylinder with hemispheric ends).

SA = the surface area of the two hemispheres + the surface are of the cylinder in between = 4pi(width/2)^2 + piwidth(length-width), the length-width term calculates the side length of the capsule (length without the hemispheres) from the full length of the capsule (length including the hemispheres)

V = the volume of the two hemispheres + the volume of the cylinder in between = 4/3pi(width/2)^3 + pi(width/2)^2(length-width).

I got SA/V ratios of around 2, which are way off from what is presented in Figure 1D, but my calculated ratio goes down in KCl, as expected, but not as reported.

To make sure I was not doing something wrong, I was going to repeat my calculations with the formulae in Table 1, which made me realize both are incorrect. The stated formula for the cell surface area-2piRL-only represents to surface area of the cylindrical side of the cells, not its hemispherical ends. And it is not even the correct formula for the surface area of the side, because that calls for L to be the length of the side (without the hemispherical ends) not the length of the cell (which includes the hemispherical ends). L here is stated to be cell length (which is what is normally measured in the field, and which is consistent with the reported length of control cells in Figure 1E being 14 µm). The formula for the volume of a capsule in the form use in Table 1 (volume of a cylinder of length L - the volume excluded from the hemispherical ends) is piR^2L - (8-(4/3pi))R^3.

Given these problems, I think I spent too much time thinking about the rest of the paper, because all of the calculations, and perhaps their interpretations, need to be redone.

Minor Points:

Strains should be identified by strain number is the text and figure legends.

In the Introduction, "Most cell control their size" should be "Most eukaryotic cell control their size".

Significance

Nothing to add.

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Referee #1

Evidence, reproducibility and clarity

Using genetics and microscopy approaches, Cabral et al. investigate how fission yeast regulates its length and width in response to osmotic, oxidative, or low glucose stress. Miller et al. have recently found that the cell cycle regulators Cdc25, Cdc13 and Cdr2 integrate information about cell volume, time and cell surface area into the cellular decision when to divide. Cabral now build on this work and test how disruption of these regulators affects cell size adaptation. They find that each stress condition shows a distinct dependence on the individual regulators, suggesting that the complex size control network enables optimized size adaptation for each condition. Overall, the manuscript is clear and the detailed methods ensure that the experiments can be replicated.

Major comments:

1. It would be much easier to follow the authors' conclusions, if in addition to surface area to volume ratio, length and width, they would also plot cell volume at division in Figs. 1-4.
2. To me, it seems that maybe even more than upon osmotic stress, the cdc13-2x strain differs qualitatively from WT in low glucose conditions, where the increased SA-V ratio is almost completely abolished.
3. It is not entirely clear to me why two copies of Cdc13 would qualitatively affect the responses. Shouldn't the extra copy behave similarly to the endogenous one and therefore only lead to quantitative changes? Maybe the authors can discuss this more clearly or even test a strain in which Cdc13 function is qualitatively disrupted.
4. I don't see why the authors come to the conclusion that under osmotic stress cells would maximize cell volume. It leads to a decreased cell length, doesn't it?

Significance

Fission yeast has long been used as a model for eukaryotic cell size regulation. So far, this research has been mostly focused on steady state size regulation. While it has long been clear that cells across organisms adapt their size in response to environmental changes, little is known about how these external inputs are processed through the size control network. Dissecting how disruption of the various branches of the size control network affects size adaptation is an important step towards a mechanistic understanding of this process. Future studies will have to build on these observations and investigate how each stress mechanistically affects the respective regulator(s). While the details of the molecular players and their contribution to size adaptation are likely specific to fission yeast, the concept of stress type-specific size adaptation that is mediated through different regulators is likely conserved and thus of broader relevance.

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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' __

Response to Reviewer#1 manuscript structural changes 1-5: This reviewer considers the findings related to rhoptry biology as the most significant aspect of the study and suggests rewriting the manuscript to emphasize these findings specifically. Doing so might make the key findings easier to interpret. However, in our view, this approach could misrepresent how the study originated and what we see as the most important outcomes. We did not develop MoTissU-ExM specifically to investigate rhoptry biology. Instead, this technique was created independently of any particular biological question, and once established, we asked what questions it could answer, using rhoptry biology as a proof of concept. Given the authors' previous work and available resources, we chose to focus on rhoptry biology. Since this was driven by basic research rather than a specific hypothesis, it's important to acknowledge this in the manuscript. While we agree that the findings related to rhoptry biology are valuable, we believe that highlighting the technique's ability to observe organelles, structures, and phenotypes with unprecedented ease and detail is more important than emphasizing the rhoptry findings alone. For these reasons, we have decided not to restructure the manuscript as suggested.

Reviewer #2

Minor text changes (Reviewer #2)

1. __The 'image Z-depth' value indicated in the figures is ambiguous. It is not clear whether this refers to the distance from the coverslip surface or the starting point of the z-stack image acquisition. A precise definition of this parameter would be beneficial. __

In the legend of Figure 1, the image Z-depth has been clarified as "sum distance of Z-slices in max intensity projection". 2.

__Paragraph 3 of the introduction - line 7, "handful or proteins" should be handful of proteins __

This has been corrected. 3.

__Paragraph 5 of the introduction - line 7, "also able to observed" should be observe __

This has been changed. 4.

__In the final paragraph of the introduction - line 1, "leverage this new understand" should be understanding __

This has been fixed. 5.

__The first paragraph of the discussion summary contains an incomplete sentence on line 7, "PbRON11ctrl-infected SGs." __

This has been removed. 6.

__The second paragraph of the discussion - line 10, "until cytokinesis beings" should be begins __

This mistake has been corrected. 7.

__One minor point that author suggest that oocyst diameter is not appropriate for the development of sporozoite develop. This is not so true as oocyst diameter tells between cell division and cell growth so it is important parameter especially where the proliferation with oocyst does not take place but the growth of oocyst takes place. __

We agree that this was not highlighted enough in the text. The final sentence of the results section about this now reads:

"While diameter is a useful readout for oocyst development in the early stages of its growth, this suggests that diameter is a poor readout for oocyst development once sporozoite formation has begun and highlights the usefulness of the segmentation score as an alternative.", and the final sentence of the discussion section about this now reads "Considering that oocyst size does not plateau until cytokinesis begins4, measuring oocyst diameter may represent a useful biological clock specifically when investigating the early stages of oocyst development." 8.

__How is the apical polarity different to merozoite as some conoid genes are present in ookinete and sporozoite but not in merozoite. __

Our hypothesis is that apical polarity is established by the positioning and attachment of the centriolar plaque to the parasite plasma membrane in both forming merozoites and sporozoites. While the apical polar ring proteins are obviously present at the apical end, and have important functions, we think that they themselves are unlikely to regulate polarity establishment directly. Additionally, it seems that the apical polar rings are visible in forming sporozoites far before the comparable stages of merozoite formation. An important note here is that at this point, this is largely inferences based on observational differences and there is relatively little functional data on proteins that regulate polarity establishment at any stage of the Plasmodium 9.

__Therefore, I think that electron microscopy remains essential for the observation of such ultra-fine structures __

We have added a paragraph in the discussion that provides a more clear comparison between MoTissU-ExM and other imaging modalities previously applied on mosquito-stage parasites (see response to Reviewer#1 (Minor text changes) comment #17). 10.

__The author have not mentioned that sometimes the stage oocyst development is also dependent on the age of mosquito and it vary between different mosquito gut even if the blood feed is done on same day. __

In our opinion this can be inferred through the more general statement that "development of each oocyst within a midgut is asynchronous..."

Figure changes (Reviewer #2)

1. __Fig 3B: stage 2 and 6 does not show the DNA cyan, it would-be good show the sate of DNA at that particular stage, especially at stage 2 when APR is visible. And box the segment in the parent picture whose subset is enlarged below it. __

We completely agree with the reviewer that the stage 2 image would benefit from the addition of a DNA stain. Many of the images in Figure 3b were done on samples that did not have a DNA stain and so in these * yoelii samples we did not find examples of all segmentation scores with the DNA stain. Examples of segmentation score 2 and 6 for P. berghei, and 6 for P. falciparum* can be found with DNA stains in Figure S8. 2.

__For clarity, it would be helpful to add indicators for the centriolar plaques in Figure 1b, as their locations are not immediately obvious. __

The CPs in Figure 1a and 1b have been circled on the NHS ester only panel for clarity. +

__Regarding Figure 1c, the authors state that 'the rootlet fiber is visible'. However, such a structure cannot be confirmed from the provided NHS ester image. Can the authors present a clearer image where the rootlet fibre is more distinct? Furthermore, please provide the basis for identifying this structure as a rootlet fiber based on the NHS ester observation alone. __

The image in Figure 1c has been replaced with one that more clearly shows the rootlet fibre.

Based on electron microscopy studies, the rootlet fibre has been defined as a protein dense structure that connects the centriolar plaque to the apical polar rings (PMID: 17908361). Through NHS ester and tubulin staining, we could identify the apical polar rings and centriolar plaque as sites on the apical end of the parasite and nucleus that microtubules are nucleated from. There is a protein dense fibre that connects these two structures. Based on the fact that the protein density of this structure was previously considered sufficient for its identification by electron microscopy, we consider its visualisation by NHS ester staining sufficient for its identification by U-ExM.

__Fig 1B - could the tubulin image in the hemispindle panel be made brighter? __

The tubulin staining in this panel was not saturated, and so this change has been made.

__Fig 4A - the green text in the first image panel is not visible. Also, the cyan text in the 3rd image in Fig 1A is also difficult to see. There's a few places where this is the case __

We have made all microscopy labels legible at least when printed in A4/Letter size.

__Fig 6A - how do the authors know ron11 expression is reduced by 99%? Did they test this themselves or rely on data from the lab that gifted them the construct? Also please provide mention the number of oocyst and sporozoites were observed. __

The way Figure 6a was previously designed and described was an oversight, that wrongly suggested we had quantified a >99% reduction in *ron11 * The 99% reduction has been removed from Figure 6a and the corresponding part of the figure legend has been rewritten to emphasise that this was previously established:

"(a) Schematic showing previously established Ron11Ctrl and Ron11cKD parasite lines where ron11 expression was reduced by >99%9."

As to the second part of the question, we did not independently test either protein or RNA level expression of RON11, but we were gifted the clonal parasite lines established by Prof. Ishino's lab in PMID: 31247198 not just the genetic constructs.

__Fig 6E - are the data point colours the wrong way round on this graph? Just looking at the graph it looks as though the RON11cKD has more rhoptries than the control which does not match what is said in the text. __

Thank you for pointing out this mistake, the colours have now been corrected.

__Fig S8C, PbRON11 ctrl, pie chart shows 89.7 % spz are present in the secretory cavity while the text shows 100 %, 35/35 __

The text saying 100% (35/35) only considered salivary glands that were infected (ie. Uninfected SGs were removed from the count. The two sentences that report this data have been clarified to reflect this better:

"Of *PbRON11ctrl SGs that were infected (35/39), 100% (35/35) contained sporozoites in the secretory cavity (Figure S8c). Conversely of infected PbRON11cKD SGs (59/82), only 24% (14/59) contained sporozoites within the secretory cavity (Figure S9d)."

*

__Fig S9D shows that RON11 ckd contains 17.1% sporozoites in secretory cavity while the text says 24%. __

Please see the response to Reviewer#2 Figure Changes Comment #8 where this was addressed.

Experimental changes (Reviewer #2)

1. __Why do the congruent rhoptries have similar lengths to each other, while the dimorphic rhoptries have different lengths? Is this morphological difference related to the function of these rhoptries? __

We hypothesise that this morphological difference arises because the congruent rhoptries are 'used' during SG invasion, while the dimorphic rhoptries are utilized during hepatocyte invasion. It is not straightforward to test this functionally at this point, as no protein is known to have differential localization between the two. Additionally, RON11 is likely directly involved in both SG and hepatocyte invasion through a secreted portion of the protein (as seen in RBC invasion). Therefore, RON11cKD sporozoites may have combined defects, meaning we cannot assume any defect is solely due to the absence of two rhoptries. Determining this functionally is of high interest to our research groups and remains an area of ongoing study, but it is beyond the scope of this study. 2.

Would it be possible to show whether RON11 localises to the dimorphic rhoptries, the congruent rhoptries, or both, by using expansion microscopy and a parasite line that expresses RON11 tagged with GFP or a peptide tag?

__ __We do not have access to a parasite line that expresses a tagged copy of RON11, or anti-PbRON11 antibodies. Based on previously published localisation data, however, it seems likely that RON11 localises to both sets of rhoptries. Below are excerpts from Figure 1c of PMID: 31247198, where RON11 (in green) seems to have a more basally-extended localisation in midgut (MG) sporozoites than in salivary gland (SG) sporozoites. From this we infer that in the MG sporozoite you're seeing RON11 in both pairs of rhoptries, but only the one remaining pair in the SG sporozoite.

__The knockdown of RON11 disrupts the rhoptry structure, making the dimorphic and congruent rhoptries indistinguishable. Does this suggest that RON11 is important for the formation of both types of rhoptries? I believe that it would be crucial to confirm whether RON11 localises to all rhoptries or is restricted to specific rhoptries for a more precise discussion of RON11's function. __

Based on our analysis, it does indeed seem that RON11 is important for both types of rhoptries as when RON11 isn't expressed sporozoites still have both apical and cytoplasmic rhoptries (ie. Not just one pair is lost; see Reviewer #1 Experimental changes comment #1).

__The authors state that 64% of RON11cKD SG sporozoites contained no rhoptries at all. Does this mean RON11cKD SG sporozoites used up all rhoptries corresponding to the dimorphic and congruent pairs during SG invasion? If so, this contradicts your claims that sporozoites are 'leaving the dimorphic rhoptries for hepatocyte invasion' and that 'rhoptry pairs are specialized for different invasion events'. If that is not the case, does it mean that RON11cKD sporozoites failed to form the rhoptries corresponding to the dimorphic pair? A more detailed discussion would be needed on this point and, as I mentioned above, on the specific role of RON11 in the formation of each rhoptry pair. __

We do not agree that this constitutes a contradiction; instead, more nuance is needed to fully explain the phenotype. As shown in the new graph added in response to Reviewer#1 Figure changes comment #1 in RON11cKD oocyst sporozoites, 64% of all rhoptries are located at the apical end. Our hypothesis is that these rhoptries are used for SG invasion and, therefore, would not be present in RON11cKD SG sporozoites. Consequently, the fact that 64% of RON11cKD sporozoites lack rhoptries is exactly what we would expect. Essentially, we predict three slightly different 'pathways' for RON11cKD sporozoites: If they had 2 apical rhoptries in the oocyst, we predict they would have zero rhoptries in the SG. If they had 2 cytoplasmic rhoptries in the oocyst, we predict they would have two rhoptries in the SG. If they had one apical and one cytoplasmic rhoptry in the oocyst, we predict they would have one rhoptry in the SG. In any case, we expect the apical rhoptries to be 'used up,' which appears to be supported by the data.

__Out of pure curiosity, is it possible to measure the length and number of subpellicular microtubules in the sporozoites observed in this study using expansion microscopy? __

We have performed an analysis of subpellicular microtubules which is now included as Supplementary Figure 2. We could not always distinguish every SPMT from each other and so have not quantified SPMT number. We have, however, quantified their absolute length on both the 'long side' and 'short side', their relative length (as % sporozoite length) and the degree to which they are polyglutamylated.

A description of this analysis is now found in the results section as follows: "*We quantified the length and degree of polyglutamylation of SPMTs on the 'long side' and 'short side' of the sporozoite (Figure S2). 'Short side' SPMTs were on average 33% shorter (mean = 3.6 µm {plus minus}SD 1.0 µm) than 'long side' SPMTs (mean = 5.3 µm {plus minus}SD 1.5 µm) and extended 17.4% less of the total sporozoite length. While 'short side' SPMTs were significantly shorter, a greater proportion of their length (87.9% {plus minus}SD 11.2%) was polyglutamylated compared to 'long side' SPMTs (69.4% {plus minus}SD 13.8%)." *

Supplementary Figure 2: Analysis of sporozoite subpellicular microtubules. Isolated P. yoelii salivary gland sporozoites were prepared by U-ExM and stained with anti-tubulin (microtubules) and anti-PolyE (polyglutamylated SPMTs) antibodies. SPMTs were defined as being on either the 'long side' (nucleus distant from plasma membrane) or 'short side' (nucleus close to plasma membrane) of the sporozoite as depicted in Figure 1f. (a) SPMT length along with (b) SPMT length as a proportion of sporozoite length were both measured. (c) Additionally, the proportion of the SPMT that was polyglutamylated was measured. Analysis comprises 25 SPMTs (11 long side, 14 short side) from 6 SG sporozoites. ** = p The following section has also been added to the methods to describe this analysis: * "Subpellicular microtubule measurement

• To measure subpellicular microtubule length and polyglutamylation maximum intensity projections were made of sporozoites stained with NHS Ester, anti-tubulin and anti-PolyE antibodies, and SYTOX Deep Red. The side where the nucleus was closest to the parasite plasma membrane was defined as the 'short side', while the side where the nucleus was furthest from the parasite plasma membrane was defined as the 'long side'. Subpellicular microtubules were then measured using a spline contour from the apical end of the sporozoite to the basal-most end of the microtubule with fluorescence intensity across the contour plotted (Zeiss ZEN 3.8). Sporozoite length was defined as the distance from the sporozoite apical polar rings to the basal complex, measuring through the centre of the cytoplasm. The percentage of the subpellicular microtubule that was polyglutamylated was determined by assessing when along the subpellicular microtubule contour the anti-PolyE fluorescence intensity last dropped below a pre-defined threshold."

*

__In addition to the previous point, in the text accompanying Figure 7a, the authors claim that "64% of PbRON11cKD SG sporozoites contained no rhoptries at all, while 9% contained 1 rhoptry and 27% contained 2 rhoptries". Could this data be used to infer which rhoptry pair are missing from the RON11cKD oocyst sporozoites? Can it be inferred that the 64% of salivary gland sporozoites that had no rhoptries in fact had 2 congruent rhoptries in the oocyst sporozoite stage and that these have been discharged already? __

Please see the response to Reviewer #2 Experimental Changes Comment #4.

__Is it possible that the dimorphic rhoptries are simply precursors to the congruent rhoptries? Could it be that after the congruent rhoptries are used for SG invasion, new congruent rhoptries are formed from the dimorphic ones and are then used for the next invasion?____ Would it be possible to investigate this by isolating sporozoites some time after they have invaded the SG and performing expansion microscopy? This would allow you to confirm whether the dimorphic rhoptries truly remain in the same form, or if new congruent rhoptries have been formed, or if there have been any other changes to the morphology of the dimorphic rhoptries. __

In theory, it is possible that the dimorphic rhoptries are precursors to the uniform rhoptries, specifically how the larger one of the two in the dimorphic pair might be a precursor. Maybe the smaller one is, but we have no evidence to suggest that this rhoptry lengthens after SG invasion. We are interested in isolating sporozoites from SGs to add a temporal perspective, but currently, this isn't feasible. When sporozoites are isolated from SGs, they are collected at all stages of invasion. Additionally, we don't know how long each step of SG invasion takes, so a time-based method might not be effective either. We are developing an assay to better determine the timing of events during SG invasion with MoTissU-ExM, but this is beyond the scope of this study.

__In the section titled "Presence of PbRON11cKD sporozoites in the SG intercellular space", the authors state that "the majority of PbRON11cKD-infected mosquitoes contained some sporozoites in their SGs, but these sporozoites were rarely inside either the SG epithelial cell or secretory cavity". - this is suggestive of an invasion defect as the authors suggest. Could the authors collect these sporozoites and see if liver hepatocyte infection can be established by the mutant sporozoites? They previously speculate that the two different types of rhoptries (congruent and dimorphic) may be specific to the two invasion events (salivary gland epithelial cell and liver cell infection). __

It has already been shown that RON11cKD sporozoites fail hepatocyte invasion (PMID: 31247198), even when isolated from the haemolymph and so it seems very unlikely that they would be invasive following SG isolation. As mentioned in the discussion, RON11 in merozoites has a 'dual-function' where it is partially secreted during merozoite invasion in addition to its rhoptry biogenesis functions. Assuming this is also the case in sporozoites, using the RON11cKD parasite line we cannot differentiate these two functions and therefore cannot ascribe invasion defects purely to issues with rhoptry biogenesis. In order to answer this question functionally, we would need to identify a protein that only has roles in rhoptry biogenesis and not invasion directly.

Reviewer #3

Minor text changes (Reviewer #3)

1. __Page 3 last paragraph: ...the molecular mechanisms underlying SG (invasion?) are poorly understood. __

This has been corrected 2.

__The term "APR" does not refer to a tubulin structure per se, but rather to the proteinaceous structure to which tubulin anchors. Are there any specific APR markers that can be used in Figure 1C? If not, I recommend avoiding the use of "APR" in this context. __

The text does not state that the APR is a tubulin structure. Given that it is a proteinaceous structure, we visualise the APRs through protein density (NHS Ester). It has been standard for decades to define APRs by protein density using electron microscopy, and it has previously been sufficient in Plasmodium using expansion microscopy (PMIDs: 41542479, 33705377) so it is unclear why it should not be done so in this study. 3.

__I politely disagree with the bold statements ‚ Little is known about cell biology of sporozoite formation.....from electron microscopy studies now decades old' (p.3, 2nd paragraph); ‚To date, only a handful of (instead of ‚or') proteins have been implicated in SG invasion' (p. 4, 1st paragraph). These claims may overlook existing studies; a more thorough review of the literature is recommended. __

This study includes at least 50 references from papers broadly related to sporozoite biology, covering publications from every decade since the 1970s. The most recent review that discusses salivary gland invasion cites 11 proteins involved in SG invasion. We have replaced "handful" with a more precise term, as it is not the best adjective, but it is hardly an exaggeration.

Figure changes (Reviewer #3)

1. __The hypothesis that Plasmodium utilizes two distinct rhoptry pairs for invading the salivary gland and liver cells is intriguing but remains clearly speculative. Are the "cytoplasmic pair" and "docked pair" composed of the same secretory proteins? Are the paired rhoptries identical? How does the parasite determine which pair to use for salivary gland versus liver cell invasion? Is there any experimental evidence showing that the second pair is activated upon successful liver cell invasion? Without such data this hypothesis seems rather premature. __

We are unaware of any direct protein localisation evidence suggesting that the rhoptry pairs may carry different cargo. However, only a few proteins have been localised in a way that would allow us to determine if they are associated with distinct rhoptry pairs, so this possibility cannot be ruled out either. It seems unlikely that the parasite 'selects' a specific pair, as rhoptries are typically always found at the apical end. What appears more plausible is that the "docked pair" forms first and immediately occupies the apical docking site, preventing the cytoplasmic pair from docking there. Regarding any evidence that the second pair is activated during liver cell invasion, it has been well documented over decades that rhoptries are involved in hepatocyte invasion. If the dimorphic rhoptries are the only ones present in the parasite during hepatocyte invasion, then they must be used for this process. 2.

__The quality of the "Roolet fibre" image is not good and resembles background noise from PolyE staining. Additional or alternative images should be provided to convincingly demonstrate that PolyE staining indeed visualizes the Roolet fibre. It is puzzling that the structure is visible with PolyE staining but not with tubulin staining. __

This is a logical misinterpretation based on the image provided in Figure 1c. Our intention was not to imply that PolyE staining enables us to see the rootlet fibre but that PolyE and tubulin allow us to see the APR to which the rootlet fibre is connected. There is some PolyE staining that likely corresponds to the early SPMTs that in 1c appears to run along the rootlet fibre but this is a product of the max-intensity projection. Please see Reviwer#2 Figure Changes Comment #3 for the updated Figure 1c. 3.

__More arrows should be added to Figures 6b and 6c to guide readers and improve clarity. __

We have added arrows to Figure 6b and 6c which point out what we have defined as normal and aberrant rhoptries more clearly. These panels now look like this: 4.

__Figure 2a zoomed image of P. yoelii infected SG is different than the highligted square. __

We agree that the highlighted square and the zoomed area appear different, but this is due to the differing amounts of light captured by the objectives used in these two panels. The entire SG panel was captured with a 5x objective, while the zoomed panel was captured with a 63x objective. Because of this difference, the plane of focus of the zoomed area is hard to distinguish in the whole SG image. The zoomed image is on the 'top' of the SG (closest to the coverslip), while most of the signal you see in the whole SG image comes from the 'middle' of the SG. To demonstrate this more clearly, we have provided the exact region of interest shown in the 63x image alongside a 5x image and an additional 20x image, all of which are clearly superimposable.__

__ 5.

__Figure 3 legend: "P. yoelii infected midguts harvested on day 15" should be corrected. More general, yes, "...development of each oocyst within a single midgut is asynchronous." but it is still required to provide the dissection days. __

We are unsure what the suggested change here is. We do not know what is wrong with the statement about day 15 post infection, that is when these midguts were dissected. __ Experimental Changes (Reviewer #3)__

1. __The proposed role of AOR in rhoptry biogenesis appears highly speculative. It is unclear how the authors conclude that "AORs carry rhoptry cargo" solely based on the presence of RON4 within the structure. Inclusion of additional markers to characterize the content of AOR and rhoptries will be essential to substantiate the hypothesis that this enigmatic structure supports rhoptry biogenesis. __

It is important to note that the hypothesis that AORs, or rhoptry anlagen, carry rhoptry cargo and serve as vehicles of rhoptry biogenesis was proposed long before this study (PMID: 17908361). In that study, it was assumed that structures now called AORs or rhoptry anlagen were developing rhoptries. Although often visualised by EM and presumed to carry rhoptry cargo (PMID: 33600048, 26565797, 25438048), it was only more recently that AORs became the subject of dedicated investigation (PMID: 31805442), where the authors stated that "...AORs could be immature rhoptr[ies]...". Our observation that AORs contain the rhoptry protein RON4, which is not known to localize to any other organelle, we therefore consider sufficient to conclude that AORs carry rhoptry cargo and are thus vehicles for rhoptry biogenesis. 2.

__The study of RON11 appears to be a continuation of previous work by a collaborator in the same group. However, neither this study nor the previous one adequately addresses the evolutionary context or structural characteristics of RON11. Notably, the presence of an EF-hand motif is an important feature, especially considering the critical role of calcium signaling in parasite stage conversion. Given the absence of a clear ortholog, it would be interesting to know whether other Apicomplexan parasites harbor rhoptry proteins with transmembrane domains and EF-hand motifs, and if these proteins might respond similarly to calcium stimulation. Investigating mutations within the EF-hand domain could provide valuable functional insights into RON11. __

We are unsure what suggests that RON11 lacks a clear orthologue. RON11 is conserved across all apicomplexans and is also present in Vitrella brassicaformis (OrthoMCL orthogroup: OG7_0028843). A phylogenetic comparison of RON11 across apicomplexans has previously been performed (PMID: 31247198), and this study provides a structural prediction of PbRON11 with the dual EF-hand domains annotated (Supplementary Figure 9). 3.

__The study cannot directly confirm that membrane fusion occurs between rhoptries and AORs. __

This is already stated verbatim in the results "Our data cannot directly confirm that membrane fusion occurs between rhoptries and AORs..." 4.

__It is unclear what leads to the formation of the aberrant rhoptries observed in RON11cKD sporozoites. Since mosquitoes were not screened for infection prior to salivary gland dissection, The defect reports and revisited of RON11 knockdown does not aid in interpreting rhoptry pair specialization, as there was no consistent trend as to which rhoptry pair was missing in RON11cKD oocyst sporozoites. The notion that RON11cKD parasites likely have ‚combinatorial defects that effect both rhoptry biogenesis and invasion' poses challenges to understand the molecular role(s) of RON11 on biogenesis versus invasion. Of note, RON11 also plays a role in merozoite invasion. __

We are unclear about the comment or suggestion here, as the claims that RON11cKD does not help interpret rhoptry pair specialization, and that these parasites have combined defects, are both directly stated in the manuscript. 5.

__Do all SG PbRON11cKD sporozoites lose their reduced number of rhoptries during SG invasion as in Figure 7a (no rhoptries)? __

Not all RON11cKD SG sporozoites 'use up' their rhoptries during SG invasion. This is quantified in both Figure 7a and the text, which states: "64% of *PbRON11cKD SG sporozoites contained no rhoptries at all, while 9% contained 1 rhoptry and 27% contained 2 rhoptries."

* 6.

Different mosquito species/strains are used for P. yoelii, P. berghei, and P. falciparum. Does it effect oocyst sizes/stages? Is it ok to compare?

__ __We agree that a direct comparison between for example * yoelii and P. berghei *oocyst size would be inappropriate, however Figure 3c and Supplementary Figure 4 are not direct comparisons between two species, but a summation of all oocysts measured in this study to indicate that the trends we observe transcend parasite/mosquito species differences. Our study was not set up with the experimental power to determine if mosquito host species alter oocyst size. 7.

__While I acknowledge that UExM has significantly advanced resolution capabilities in parasite studies, the value of standard microscopy technique should not be overlooked. Particularly, when discussing the function of RON11, relevant IFA and electron microscopy (EM) images should be included to support claims about RON11's role in rhoptry biogenesis. This would complement the UExM data and substantially strengthen the conclusions. Importantly, UExM can sometimes produce unexpected localization patterns due to the denaturation process, which warrants caution. __

The purpose of this study is not to discredit, undermine, or supersede other imaging techniques. It is simply to use U-ExM to answer biological questions that cannot or have not been answered using other techniques. Please refer to Reviewer # 1 Minor text changes comment#17 to see the new paragraph "Comparison of MoTissU-ExM and other imaging modalities" that addresses this

Both conventional IFA and immunoEM have already been performed on RON11 in sporozoites before (PMID: 31247198). When assessing defects caused by RON11 knockdown, conventional IFA isn't especially helpful because it doesn't allow visualization of individual rhoptries. Thin-section TEM also doesn't provide the whole-cell view needed to draw these kinds of conclusions. Volume EM could likely support these observations, but we don't have access to or expertise in this technique, and we believe it is beyond the scope of this study. It's also important to note that for the defect we observe-missing or abnormal rhoptries-the visualization with NHS ester isn't significantly different from what would be seen with EM-based techniques, where rhoptries are easily identified based on their protein density.

The statement that "UExM can sometimes produce unexpected localisation patterns due to the denaturation process..." is partially correct but lacks important nuance in this context. Based on our extensive experience with U-ExM, there are two main reasons why the localisation of a single protein may look different when comparing U-ExM and traditional IFA images. First, denaturation: in conventional IFAs, antibodies need to recognize conformational epitopes to bind to their target, whereas in U-ExM, antibodies must recognize linear epitopes. This doesn't mean the target protein's localisation changes, only that the antibody's ability to recognize it does. Second, antibody complexes seem unable to freely diffuse out of the gel, which can result in highly fluorescent signals not related to the target protein appearing in the image, as we have previously reported (PMID: 36993603). Importantly, neither of these factors applies to our phenotypic analysis of RON11 knockdown. All phenotypes described are based solely on NHS Ester (total protein) staining, so the considerations about changes in the localisation of individual proteins are not relevant.

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Referee #3

Evidence, reproducibility and clarity

Overall, the manuscript is well-written and -structured. However, I would like to raise several major points for consideration:

1. While I acknowledge that UExM has significantly advanced resolution capabilities in parasite studies, the value of standard microscopy technique should not be overlooked. Particularly, when discussing the function of RON11, relevant IFA and electron microscopy (EM) images should be included to support claims about RON11's role in rhoptry biogenesis. This would complement the UExM data and substantially strengthen the conclusions. Importantly, UExM can sometimes produce unexpected localization patterns due to the denaturation process, which warrants caution.
2. The proposed role of AOR in rhoptry biogenesis appears highly speculative. It is unclear how the authors conclude that "AORs carry rhoptry cargo" solely based on the presence of RON4 within the structure. Inclusion of additional markers to characterize the content of AOR and rhoptries will be essential to substantiate the hypothesis that this enigmatic structure supports rhoptry biogenesis.
3. The hypothesis that Plasmodium utilizes two distinct rhoptry pairs for invading the salivary gland and liver cells is intriguing but remains clearly speculative. Are the "cytoplasmic pair" and "docked pair" composed of the same secretory proteins? Are the paired rhoptries identical? How does the parasite determine which pair to use for salivary gland versus liver cell invasion? Is there any experimental evidence showing that the second pair is activated upon successful liver cell invasion? Without such data this hypothesis seems rather premature.
4. The study of RON11 appears to be a continuation of previous work by a collaborator in the same group. However, neither this study nor the previous one adequately addresses the evolutionary context or structural characteristics of RON11. Notably, the presence of an EF-hand motif is an important feature, especially considering the critical role of calcium signaling in parasite stage conversion. Given the absence of a clear ortholog, it would be interesting to know whether other Apicomplexan parasites harbor rhoptry proteins with transmembrane domains and EF-hand motifs, and if these proteins might respond similarly to calcium stimulation. Investigating mutations within the EF-hand domain could provide valuable functional insights into RON11.
5. The study cannot directly confirm that membrane fusion occurs between rhoptries and AORs.
6. It is unclear what leads to the formation of the aberrant rhoptries observed in RON11cKD sporozoites. Since mosquitoes were not screened for infection prior to salivary gland dissection, The defect reports and revisited of RON11 knockdown does not aid in interpreting rhoptry pair specialization, as there was no consistent trend as to which rhoptry pair was missing in RON11cKD oocyst sporozoites. The notion that RON11cKD parasites likely have ‚combinatorial defects that effect both rhoptry biogenesis and invasion' poses challenges to understand the molecular role(s) of RON11 on biogenesis versus invasion. Of note, RON11 also plays a role in merozoite invasion. I like the introduction of a segmentation score to Plasmodium oocyst maturation.

Minor comments:

1. The term "APR" does not refer to a tubulin structure per se, but rather to the proteinaceous structure to which tubulin anchors. Are there any specific APR markers that can be used in Figure 1C? If not, I recommend avoiding the use of "APR" in this context.
2. The quality of the "Roolet fibre" image is not good and resembles background noise from PolyE staining. Additional or alternative images should be provided to convincingly demonstrate that PolyE staining indeed visualizes the Roolet fibre. It is puzzling that the structure is visible with PolyE staining but not with tubulin staining.
3. Figure 2a zoomed image of P. yoelii infected SG is different than the highligted square.
4. Figure 3 legend: "P. yoelii infected midguts harvested on day 15" should be corrected. More general, yes, "...development of each oocyst within a single midgut is asynchronous." but it is still required to provide the dissection days.
5. More arrows should be added to Figures 6b and 6c to guide readers and improve clarity.
6. Do all SG PbRON11cKD sporozoites lose their reduced number of rhoptries during SG invasion as in Figure 7a (no rhoptries)?
7. Different mosquito species/strains are used for P. yoelii, P. berghei, and P. falciparum. Does it effect oocyst sizes/stages? Is it ok to compare?
8. I politely disagree with the bold statements ‚ Little is known about cell biology of sporozoite formation.....from electron microscopy studies now decades old' (p.3, 2nd paragraph); ‚To date, only a handful of (instead of ‚or') proteins have been implicated in SG invasion' (p. 4, 1st paragraph). These claims may overlook existing studies; a more thorough review of the literature is recommended.
9. Page 3 last paragraph: ...the molecular mechanisms underlying SG (invasion?) are poorly understood.

Significance

In this study, the authors explore Ultrastructure Expansion Microscopy (U-ExM) in Plasmodium-infected mosquito tissue with the aim to enhance the visualization of parasite ultrastructure. For this purpose, they revisit sporogony, the maturation of sporozoites inside oocysts, and sporozoite invasion of salivary glands, which has been studied both by cell biological methods and experimental genetics over four decades. They focus their analysis on the biogenesis and function of key secretory organelles, termed rhoptries, which are central to parasite invasion and, again, have been studied extensively.

This study is a follow-up of a previous study by the same authors (Ref. 19). In the former study the authors showed that U-ExM allows to visualize subcellular structures in sporozoites, including the nucleus, rhoptries, Golgi, apical polar rings (APR), and basal complex, as well as midgut-associated oocysts with developing sporozoites. Here, the authors claim a new finding by stating that sporozoites possess two distinct rhoptry pairs. Supposedly, only one pair is utilized during salivary gland invasion. The authors suggest specialization of rhoptries for different cell invasion events. The authors also revisit a RON11 knock-down parasite line, which was previously shown to be deficient in salivary gland invasion, host cell attachment, gliding locomotion, and liver invasion (Ref. 14).

I find it difficult to estimate the significance. Obviously, attention will be limited to Plasmodium researchers only, as this study is descriptive and revisits a well-studied aspect of the Plasmodium life cycle in the Anopheles vector.

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Referee #2

Evidence, reproducibility and clarity

The manuscript by Liffner et al have used the modified expansion microscopy as they term Mosquito Tissue Ultrastructure Expansion Microscopy (MoTissU-ExM) to study a cell biology of temporal development of malaria parasite sporozoite biogenesis within mosquito host. They employed three different malaria parasite models Plasmodium yoelii, P.beghei and P falciparum and infected them in mosquito host.

The application of MoTissU-ExM to infected mosquito tissues is a significant technical advance, enabling visualizations previously only achievable with electron microscopy.

The major conclusion and advances are as following

• The establishment of a "segmentation score" as a great tool for staging asynchronous oocyst development.
• The location of Centriolar plaques, rootlet and other structures which are difficult to analyse
• The first detailed timeline for sporozoite rhoptry biogenesis.
• Clear quantification showing that sporozoites possess four rhoptries and utilise two during salivary gland (SG) invasion.
• A characterization of the RON11 knockout phenotype, linking it to defects in rhoptry biogenesis and a specific block in SG epithelial cell invasion. The following points are intended to further strengthen the paper for publication.

Points for Revision

1. For clarity, it would be helpful to add indicators for the centriolar plaques in Figure 1b, as their locations are not immediately obvious.
2. The 'image Z-depth' value indicated in the figures is ambiguous. It is not clear whether this refers to the distance from the coverslip surface or the starting point of the z-stack image acquisition. A precise definition of this parameter would be beneficial.
3. Regarding Figure 1c, the authors state that 'the rootlet fiber is visible'. However, such a structure cannot be confirmed from the provided NHS ester image. Can the authors present a clearer image where the rootlet fibre is more distinct? Furthermore, please provide the basis for identifying this structure as a rootlet fiber based on the NHS ester observation alone.
4. Why do the congruent rhoptries have similar lengths to each other, while the dimorphic rhoptries have different lengths? Is this morphological difference related to the function of these rhoptries?
5. Would it be possible to show whether RON11 localises to the dimorphic rhoptries, the congruent rhoptries, or both, by using expansion microscopy and a parasite line that expresses RON11 tagged with GFP or a peptide tag?
6. The knockdown of RON11 disrupts the rhoptry structure, making the dimorphic and congruent rhoptries indistinguishable. Does this suggest that RON11 is important for the formation of both types of rhoptries? I believe that it would be crucial to confirm whether RON11 localises to all rhoptries or is restricted to specific rhoptries for a more precise discussion of RON11's function.
7. The authors state that 64% of RON11cKD SG sporozoites contained no rhoptries at all. Does this mean RON11cKD SG sporozoites used up all rhoptries corresponding to the dimorphic and congruent pairs during SG invasion? If so, this contradicts your claims that sporozoites are 'leaving the dimorphic rhoptries for hepatocyte invasion' and that 'rhoptry pairs are specialized for different invasion events'. If that is not the case, does it mean that RON11cKD sporozoites failed to form the rhoptries corresponding to the dimorphic pair? A more detailed discussion would be needed on this point and, as I mentioned above, on the specific role of RON11 in the formation of each rhoptry pair.
8. Out of pure curiosity, is it possible to measure the length and number of subpellicular microtubules in the sporozoites observed in this study using expansion microscopy?
9. Is it possible that the dimorphic rhoptries are simply precursors to the congruent rhoptries? Could it be that after the congruent rhoptries are used for SG invasion, new congruent rhoptries are formed from the dimorphic ones and are then used for the next invasion? Would it be possible to investigate this by isolating sporozoites some time after they have invaded the SG and performing expansion microscopy? This would allow you to confirm whether the dimorphic rhoptries truly remain in the same form, or if new congruent rhoptries have been formed, or if there have been any other changes to the morphology of the dimorphic rhoptries.
10. In addition to the previous point, in the text accompanying Figure 7a, the authors claim that "64% of PbRON11cKD SG sporozoites contained no rhoptries at all, while 9% contained 1 rhoptry and 27% contained 2 rhoptries". Could this data be used to infer which rhoptry pair are missing from the RON11cKD oocyst sporozoites? Can it be inferred that the 64% of salivary gland sporozoites that had no rhoptries in fact had 2 congruent rhoptries in the oocyst sporozoite stage and that these have been discharged already?
11. In the section titled "Presence of PbRON11cKD sporozoites in the SG intercellular space", the authors state that "the majority of PbRON11cKD-infected mosquitoes contained some sporozoites in their SGs, but these sporozoites were rarely inside either the SG epithelial cell or secretory cavity". - this is suggestive of an invasion defect as the authors suggest. Could the authors collect these sporozoites and see if liver hepatocyte infection can be established by the mutant sporozoites? They previously speculate that the two different types of rhoptries (congruent and dimorphic) may be specific to the two invasion events (salivary gland epithelial cell and liver cell infection).

There are a few typing errors in the document:

1. Paragraph 3 of the introduction - line 7, "handful or proteins" should be handful of proteins
2. Paragraph 5 of the introduction - line 7, "also able to observed" should be observe
3. In the final paragraph of the introduction - line 1, "leverage this new understand" should be understanding
4. The first paragraph of the discussion summary contains an incomplete sentence on line 7, "PbRON11ctrl-infected SGs."
5. The second paragraph of the discussion - line 10, "until cytokinesis beings" should be begins

Some suggestions for figures

Fig 1B - could the tubulin image in the hemispindle panel be made brighter?

Fig 3B: stage 2 and 6 does not show the DNA cyan, it would-be good show the sate of DNA at that particular stage, especially at stage 2 when APR is visible. And box the segment in the parent picture whose subset is enlarged below it.

Fig 4A - the green text in the first image panel is not visible. Also, the cyan text in the 3rd image in Fig 1A is also difficult to see. There's a few places where this is the case

Fig 6A - how do the authors know ron11 expression is reduced by 99%? Did they test this themselves or rely on data from the lab that gifted them the construct? Also please provide mention the number of oocyst and sporozoites were observed.

Fig 6E - are the data point colours the wrong way round on this graph? Just looking at the graph it looks as though the RON11cKD has more rhoptries than the control which does not match what is said in the text.

Fig S8C, PbRON11 ctrl, pie chart shows 89.7 % spz are present in the secretory cavity while the text shows 100 %, 35/35

Fig S9D shows that RON11 ckd contains 17.1% sporozoites in secretory cavity while the text says 24%.

Some point to discuss

1.One minor point that author suggest that oocyst diameter is not appropriate for the development of sporozoite develop. This is not so true as oocyst diameter tells between cell division and cell growth so it is important parameter especially where the proliferation with oocyst does not take place but the growth of oocyst takes place.<br /> 2. The author have not mentioned that sometimes the stage oocyst development is also dependent on the age of mosquito and it vary between different mosquito gut even if the blood feed is done on same day. 3. How is the apical polarity different to merozoite as some conoid genes are present in ookinete and sporozoite but not in merozoite.

Significance

The following aspects are important:

This is novel and more cell biology approach to study the challenging stage of malaria parasite within mosquito. By using MoTissU-ExM, the authors have enabled the three-dimensional observation of ultrastructures of oocyst-sporozoite development that were previously difficult to observe with conventional electron microscopy alone. This includes the developmental process and entire ultrastructure of oocysts and sporozoites, and even the tissue architecture of the mosquito salivary gland and its epithelia cells.

Advances:

By observing sporozoites formation within the oocyst and the overall ultrastructure of the sporozoite with MoTissU-ExM, the authors have provided detailed descriptions of the complete structure and three-dimensional spatial relationships of the rhoptries, rootlet fibre, nucleus, and other organelles. Furthermore, their detailed localisation analysis of sporozoites within the salivary gland is also a great achievement. Considering that such observations were technically and laboriously very difficult with conventional electron microscopy, enabling these analyses with higher efficiency and relatively lower difficulty represents a major contribution to the future advancement of oocyst-sporozoite biology. The development of the 'segmentation score' for sporozoite formation within the oocyst is another major advance. I think this will enable detailed descriptions of structural changes at each developmental stage and of the molecular mechanisms involved in the development of oocysts-sporozoites This has its advantages if antibodies can be used and somewhat reduces the need for immuno-EM. Secondly, in terms of sporozoite rhoptry biology, the Schrevel et al Parasitology 2007 seems to only focus on oocyst sporozoite rhoptries as they say that the sporozoites have 4 rhoptries. This study on the other hand also looks at salivary gland sporozoites and shows that there are potentially important differences between the two - namely the reduction from 4 rhoptries to two. This also leads to further questions about the different types of rhoptries in oocyst sporozoites and whether they're adapted to invasion of different cell types (sal gland epithelial cells or liver hepatocytes)

Limitation

It would be that expansion microscopy alone still has its limits when it comes to observing ultra-fine structures. For example, visualising the small vesicular structures that Schrevel et al. observed in detail with electron microscopy, or seeing ultra-high resolution details such as the fusion of membrane structures and their interactions with structures like the rootlet fibre and microtubules. Therefore, I think that electron microscopy remains essential for the observation of such ultra-fine structures The real impact of this work is mostly cell biologist working with malaria parasite and more in mosquito stages. But the approaches can be applied to any material from any species where temporal dynamics need to be studied with tissue related structures and where UExM can be applied. I am parasite cell biologist working with parasites stages within mosquito vector host.

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Referee #1

Evidence, reproducibility and clarity

In this paper the authors use ultrastructure expansion microscopy to investigate the mosquito stages of the malaria parasite, specifically the stage called oocyst and the process of sporozoite development. They report a number of observations of which the ones concerning rhoptries are the most interesting. There are four of these organelles in the first form of sporozoites in the oocyst and only two in the mature form in the salivary gland. Using a gene knockout of a protein that was reported to be important for rhoprty formation in merozoites, the parasites invading into human red blood cells, they found that fewer rhoptries are formed also in sporozoites and that these cannot enter into the salivary gland cells any more. The presented data are in my view conclusive and no additional experiments are needed for this work to be published. The described experiments should be readily reproducible and have a high statistical power. The text is mostly clearly written but could be improved to make it more concise and more precise and to avoid overstatements. Some references could be added. It would have helped to have line numbers in the manuscript. My suggestions are as following:

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

Add reference on page 3 after 'disrupted parasites' Change 'the basal compelx at the leading edge' - this seems counterintuitive Change 'mechanisms underlying SG are poorly' - what mechanisms? of invasion or infection? On page 4: 'handful of proteins' '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. what are the 'three microtubule spindle structures'? '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. 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? change 'rhoptries golgi-derived, made de novo' change 'new understand to' 'rhoptry malformations' seem to be similar in sporozoites and merozoites. Is that surprising/new? 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? On page change/specify: 'wide range of parasite structures' On page 7: is Airyscan2 a particular method or a specific microscope? what are the dark lines in panel E? in panel G: Are the dense granules not micronemes? What are the dark lines? Rhoptries?? 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. Figure 2 seems to add little extra compared to the following figures and could in my view go to the supplement. 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. 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. Text on page 12 could be condensed to highlight the new data of ron4 staining of the AOR. 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. On page 16 the authors state that different rhoptries might have different function. This is an interesting hyopthesis/result that could be mentioned in the abstract. how large is RON11? On page 19: do the parasites with the RON11 knockout only have the cytoplasmic or only the apical rhoptries? Page 23: I suggest to delete the first sentence and focus on the functional aspects and the discoveries. There is no causal link between ookinete invasion and oocyst developmental asynchrony 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 On page 25 or before the vast number of electron microscopy studies should be discussed and compared with the authors new data. First sentence on page 27: there are many studies on parasite proteins involved in salivary gland invasion that could be mentioned/discussed. 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'

Significance

This interesting study investigates the development of malaria parasites in the mosquito using ultrastructure expansion microscopy adapted to mosquito tissue. It provides new and beautiful views of the process of sporozoite formation. The authors discovered that four secretory vesicles called rhoptires are formed in the sporozoites with two pairs being important for distinct functions, one pair functions during invasion of the salivary glands of the mosquito and the other in liver infection, although the latter is not shown but inferred from prior data.

This study will thus be of interest to scientists investigating malaria parasites in the mosquito as well as to scientist working on vesicle secretion and invasion in these parasites.

The authors use a previously generated parasite line that lack a protein to investigate its function in rhoptry biogenesis and find that its absence leads to fewer rhoptries which impacts the capacity of the parasite to enter into salivary gland cells. This is a nice functional addition to an otherwise largely descriptive study, but mimics largely the previously reported results from the blood stages. It is not clear to this reviewer how much the study advances the field over the many previous electron microscopy studies. This could be better elaborated in the text.

Strength of the study: beautiful microscopy, new insights into rhoptry formation and function, new technique to study malaria parasites in the mosquito

Weakness of the study: Some loose ends in the description of spindles and CSP layers, text could be more focussed on the key advancements reported

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Reply to the reviewers

Reviewer #1 Reviewer 1 Point 1- The authors describe cortical neuronal counts across several mammalian species, which is quite impressive, but the information on the methods of counting is lacking: how representative are the data used / shown; how many individuals / brains / sections were used for each species considered? Much more detailed description of the quantifications should be provided to judge the validity of this first conclusion.

Response: We sincerely thank the reviewer for this insightful and constructive suggestion. We agree that the methodological description of our comparative histological analysis, which is the fundamental basis of this study, was insufficient in the original manuscript. Following the reviewer’s advice, we have extensively revised the Materials and Methods section entitled “Nissl staining and neuronal cell number count” (Page 32, Line 15).

Reviewer 1 Point 2- The authors use several markers of cortical neuron identity to confirm their neuron number measurements, but from the data shown in Figure 1D,E it seems that only some markers (Satb2) show species-differences while others do not (CTIP2 / Tbr1). How do the authors explain this discrepancy - does this mean that it is mainly Satb2 neurons that are increased in number? But if so how to explain the relative increase in subcortical projections shown in Figure S7?

Response: We appreciate the reviewer’s insightful comments regarding the marker expression patterns. Upon re-evaluating our data in light of your feedback, we agree that the species differences in deep-layer (DL) markers such as Ctip2 and Tbr1 in the adult stage appear relatively modest compared to the robust differences observed in Satb2 and the projection data shown in Figure S8.

To address this point, we have incorporated a comparison between the adult data (Figure 1) and our findings from P7 (Figure S2). As shown in the revised manuscript, the species differences for all markers are significantly more pronounced at P7 than in the adult. Notably, in the lower layers, rats exhibit a significantly higher number of marker-positive cells across all markers, including those newly added in this revision, compared to mice.

We offer the following interpretation regarding these temporal differences:

1. Developmental Relevance: The marker molecules analyzed are well-established regulators of neuronal subtype fate and projection identity during development. Their critical fate-determining functions are primarily exercised during the migration and maturation phases of nascent neurons.
2. Postnatal Expression Shifts: Whether these molecules maintain functional roles in the fully matured adult brain remains less certain. It is plausible that marker expression may diminish in certain neuronal populations during late postnatal development, leading to the attenuated species differences observed in adults. Consequently, we believe the strong correlation between P7 quantitative data and projection fate provides a biologically sound validation of our hypothesis.

While we have kept the discussion in the main text concise to maintain focus for the general reader, we have provided comprehensive data in Figure 1 and Figure S2. This ensures that the necessary evidence is readily available for specialists interested in these developmental dynamics.

Reviewer 1 Point 3- The authors focus their study almost exclusively on somatosensory cortex, but can they comment on other areas (motor, visual for instance)? It would be nice to provide additional comparative data on other areas, at least for some of the parameters examined across mouse and rat. Alternatively the authors should be more explicit in the abstract and description of the study that it is limited to a single area.

Response: We sincerely appreciate the reviewer’s insightful comment. As suggested, we have revised the Abstract to explicitly state that our current analysis is focused on the somatosensory cortex. Furthermore, as demonstrated in Figure 1B, we have added a discussion regarding the possibility that the species differences observed in the primary somatosensory cortex may be a general feature shared across the entire cerebral cortex, as follows: “This DL-biased thickening in rats was evident in the primary somatosensory area, but is consistently observed throughout the rostral-caudal cortical regions. (Page 19, Lines 29-31)“

Reviewer 1 Point 4- The authors provide convincing evidence of increased Wnt signaling pathway in the rat. They should show more explicitly how other classical pathways of neurogenic balance / temporal patterning are expressed in their mouse and rat transcriptome data sets. These would include Notch, FGF, BMP, for which all the data should be available to provide meaningful species comparison.

Response: We sincerely thank the reviewer for this insightful suggestion. Following your advice, we have newly included comparative data on key signaling pathways essential for cortical development—namely Wnt, FGF, NOTCH, mTOR, SHH, and BMP—across different species. These results are now presented in Figure S17. Rat progenitors show comparable patterns to other species for FGF, mTOR, and Notch signaling, but elevated Wnt and BMP expression, especially at early stages. A detailed heatmap of raw Wnt pathway gene expression across species is also included in the same supplementary figure. We believe these additions provide a more comprehensive evolutionary perspective and significantly strengthen our findings.

Reviewer 1 Point 5- The alignment of mouse and rat trajectories is very nicely showing a delay at early-mid-corticogenesis. But there is also heterochronic transcriptome at latest stages (end of 5). How can this be interpreted? Does this mean potentially prolonged astrogliogenesis in the rat cortex?

Response: We sincerely appreciate the reviewer’s insightful comment and the meticulous attention given to our data. Regarding the heterochronic shift observed at Day 5, we agree that this point was not sufficiently addressed in the original manuscript.

We would like to clarify the two primary reasons for this omission, which are inherent to the current study’s design:

1. Resolution of Stage Alignment at Temporal Extremes: In our developmental stage alignment analysis, corresponding stages are defined by pairs showing the highest transcriptomic similarity within the sampled range. By definition, the precision of this alignment tends to decrease at the earliest and latest time points of a dataset. Since the "true" biological equivalent might lie outside our sampling window, we must be cautious in interpreting shifts at these temporal boundaries.
2. Difference in Validation Rigor: Our study prioritized the early stages of deep-layer (DL) neuron production. Consequently, we rigorously defined the onset of neurogenesis in rats (Day 1) using multiple independent methods, including clonal analysis, immunohistochemistry, and gene expression. In contrast, Day 5 was defined simply as five days post-initiation of neurogenesis, without equivalent multi-modal validation. Given that our primary focus is the early phase of neurogenesis, the precision of the transition from late neurogenesis to gliogenesis is relatively lower. For these reasons, we believe that an in-depth discussion of the heterochronic shift at Day 5 might lead to over-interpretation. To reflect this more accurately and avoid misleading the reader, we have revised Figure 6F to de-emphasize the Day 5 shift. In addition, we revised the manuscript as “Importantly, while this analysis identified stage pairs with the highest similarity, the correspondence at the edges of the temporal sampling window is inherently less certain than at the center. Consequently, we focus on the notable reflection point at the center of our dataset. (Page 13, Lines 37-39)”.

We believe these changes more faithfully represent the biological scope of our data while maintaining the scientific integrity of our primary conclusions.

Reviewer 1 Point 6- Figure 7: description implies that module 3 is a subset of module 4, but this is not obvious at all from the panels shown. Please clarify.

Response: We sincerely appreciate the reviewer’s careful reading of our manuscript. As suggested, we have revised Figure 7 to clarify the hierarchical relationship between Module 3 and Module 4, ensuring that their inclusion is now explicitly presented.

Reviewer #2 Reviewer 2 Point 1. The introduction lacks sufficient background and fails to convey the significance of the study. Specifically, why the research was undertaken, what knowledge gap it addresses, and how the findings could be applied. Addressing these questions already in the introduction would enhance the impact of the work and broaden its readership.

Response: We sincerely appreciate the reviewer’s insightful comment on this point. Our study reports evolutionary insights gained through an unconventional approach: a single-cell level comparison between mice and rats. We agree that clarifying the necessity of this specific approach is crucial for the manuscript. Accordingly, we have added the following two points to the Introduction:

1. At the end of the first paragraph, we emphasized the current lack of research on the evolutionary adaptation of cortical circuits, despite the established functional importance of evolutionarily conserved circuits. (Page 3, Lines 7-10); “Paradoxically, despite the importance of these variations, research has predominantly focused on the conserved aspects of cortical architecture. Consequently, the degree of evolutionary plasticity inherent in these circuits and the cell-intrinsic mechanisms driving their modification remain profoundly enigmatic.”)
2. At the end of the third paragraph, we revised and added text (Page3, Lines 26-27; “This lack of comparative insight represents a significant gap in our understanding of how conserved developmental programs give rise to species-specific brain architectures.”).

Reviewer 2 Point 2. In figure 5 the authors conclude that "differences in cell cycle kinetics and indirect neurogenesis are unlikely to be the primary factors driving the species-specific variation in DL neuron production. Instead, the temporal regulation of progenitor neurogenic competence, which determines the duration of the DL production phase, provides a more plausible explanation for the greater number of DL subtypes observed in rats". It is not clear to this reviewer how the authors come to this conclusion. Authors observe a significant proportion of mitotic cells in rat VZ from day 1, and a higher constant proportion of mitotic progenitors in SVZ rats compared to mouse (Figure 5C). This points to an early difference in mitotic progenitors that may also lead to increased IP numbers, and potentially an increased number in DL cells, even before day 1. In addition, the higher abundance of IPs in the G2/S phase (statistically significant in 4 of the 7 time points) (Figure 5F), would suggest that this difference might play a role in the species-specific variation of DL neuron production. The authors should estimate cell cycle length instead of just measuring proportions to conclude something about cell cycle kinetics. They can then model growth curves to predict the effect caused if there were differences in cell cycle length between equivalent cell types across species.

Response: We sincerely thank the reviewer for their careful reading of our manuscript and for pointing out the overstatements in our original descriptions. We agree that a more nuanced interpretation of the data was necessary. In response to these constructive suggestions, we have made the following revisions:

1. Refinement of Descriptions: We have revised the text to more accurately reflect our findings, specifically noting that the increase in RG division on Day 1 and IP proliferation throughout the neurogenic period showed a significant trend. These features are now described more fairly and cautiously in the revised manuscript. (Page 11, Lines 42-46; “Remarkably, while the temporal dynamics of mitotic density were strikingly conserved between the two species, subtle yet discernible species-specific signatures emerged. Specifically, rats exhibited a higher ratio of mitotic cells in the VZ at the onset of neurogenesis, the precise period when DL subtypes are generated in both species. Further assessment of G2/S-phase cells via pulse-EdU labeling (Figure 5D, E) “)
2. Inclusion of Time-lapse Imaging Data: The reviewer is correct that measuring the proportions of M and G2/S phases provides only a limited snapshot of cell cycle dynamics. To gain a more precise insight, we performed primary cultures of neural progenitor cells (NPCs) from Day 1 and conducted live-cell time-lapse imaging. This allowed us to directly quantify the cell cycle duration of mouse and rat NPCs (Figure S9A-C).
3. Comparative Analysis and Mathematical Modeling: Our new data revealed that the cell cycle lengths of the two species are remarkably similar, with no significant differences observed under these culture conditions. Furthermore, to validate the impact of these findings on overall brain development, we developed a mathematical model based on our experimental data. This model predicts the total number of cells produced over the five-day neurogenic period, providing a more robust theoretical framework for our conclusions (Figure S9D). We believe these additions significantly strengthen the manuscript and address the reviewer's concerns regarding the physiological relevance of our observations.

Reviewer 2 Point 3. In Figure 6 the authors focus only on the mouse and rat datasets. Given the availability of datasets from primates that the author used already for Figure 7, it would give the reader a broader prospective if also these datasets would be integrated in the analysis done for Figure 6, particularly it would be interesting to integrate them in the pseudotime alignment of cortical progenitor. How do human and/or macaque early and late neurogenic phase would compare to mouse and rat in this model?

Response: We sincerely appreciate the reviewer’s insightful suggestion. In accordance with this comment, we have now incorporated pseudotime alignments of cortical progenitors between primates (human, macaque) and rodents (mouse, rat), presented as pairwise gene expression distance matrices with dynamic time warping in Figure S13. These heatmaps illustrate temporal compression or stretching in progenitor gene expression progression across species. Notably, macaque progenitors show no definitive deviations from rodents, whereas human progenitors exhibit distinct protraction relative to rats and even more so to mice. These additions provide a more comprehensive cross-species perspective without altering the study's core conclusions.

Reviewer 2 Point 4. In Figures 6C and 6D, the authors distinguish between cycling and non-cycling NECs and RGCs. Could the authors clarify the rationale behind making this distinction? Could the authors comment on how they interpret the impact of cycling versus non-cycling states on species-specific non-uniform scaling? Do they consider the observed non-linear correspondences to be driven by differences in cell cycle activity?

Response: We are grateful to the reviewer for their insightful observation. We agree that our initial classification of neural progenitor cell (NPC) populations based on proliferation marker expression levels followed a convention used in other studies but was, in the context of this work, unnecessary and potentially misleading. To avoid further confusion and focus on the core biological question, we have re-organized the data by pooling these populations into a single group. Regarding the concern about species differences in cell cycle kinetics, we believe there is no significant divergence between mice and rats that could explain the observed developmental patterns in temporal progression of neurogenesis. This is supported by two lines of evidence:

1. Quantitative analysis of pH3-positive cells (Figure 5).
2. New time-lapse imaging data of primary cultured NPCs, which shows no substantial difference in cell cycle length between the two species (Figure S9). These results indicate that the species-specific differences in deep-layer (DL) neuron production are not driven by cell division kinetics. Consequently, we conclude that the non-linear developmental progression of NPCs occurs independently of cell cycle regulation.

Reviewer 2 Point 5. For the non-uniform scaling in Figure 6F, the authors identify critical inflection points and mention that "the largest delay in rat progenitors occurring where Day 1 and Day 3 progenitors overlapped". It would be good if the authors could discuss what they think all the inflection points represents. How much can it be explained by the heterogeneity within progenitors per time point? There is a clear higher spread of histograms at days 3 and 5, and the histogram at day 5 almost overlaps with day 1. I wonder if the same conclusion about non-uniform scaling would be detected if the distance matrix was built separately for specific cell types, for example only looking at NECs or RGCs.

Response: We sincerely appreciate the reviewer’s insightful perspective on this point. In alignment with the suggestions from both this reviewer and Reviewer 1 (Point 5), we have updated the manuscript to discuss all identified inflection points. Specifically, we have clarified why our discussion focuses on the correspondence between Mouse D1 and Rat Day 3.

A recognized limitation of our current analytical approach is that it identifies the closest matching expression profiles within the specific timeframes sampled for each species. For stages at the beginning or end of our sampling window, the "true" corresponding stage in the other species may lie outside our sampled range, which naturally limits the strength of any conclusions regarding those boundary points. Consequently, while we can confidently confirm the correspondence between Mouse Day 1 and Rat Day 3—both of which sit centrally within our sampled window—we have intentionally avoided over-interpreting data near the temporal boundaries.

Regarding the cell types analyzed, this specific analysis was conducted exclusively on NECs and RGs (now shown in Figure 6F). Extensive prior research (Susan McConnell lab, Sally Temple lab, Fumio Matsuzaki lab, Dennis Jabaudon lab, and more) has established that the time-dependent mechanisms governing the fate determination of cortical excitatory neuron subtypes are encoded within RGs. Therefore, we focused our investigation on these lineages and did not include other cell types in this study. We believe this focused approach maintains the highest degree of biological relevance for our conclusions.

Reviewer 2 Point 6. The authors conclude that the elevated and prolonged expression of Wnt-ligand genes in rat RGs extend the DL neurogenic window and contribute to rat-specific expansion of deep cortical layer. In order to validate this finding it would be good for the authors to perform a perturbation experiment and reduce Wnt signalling/ Axin 2 levels in rats or depleted the Lmx1a and Lhx2 double-positive population. Response: __We thank the reviewer for this insightful suggestion. We agree that providing direct experimental evidence is crucial to demonstrating that elevated Wnt signaling in RG progenitors drives the production of DL subtype neurons in rats. To address this, we performed a functional intervention on Day 3, a stage when Wnt signaling (indicated by Axin2 expression) is significantly higher in rats than in mice (__Figure 7C, D). By introducing a dominant-negative form of TCF7L2 (dnTCF7L2) to inhibit Wnt signaling specifically in RG progenitors, we tracked the fate of the resulting neurons (Figure 7I, J). Our results showed a clear reduction in the proportion of DL neurons, accompanied by a reciprocal increase in upper-layer (UL) neurons. These findings demonstrate that maintained high levels of Wnt signaling are essential for the prolonged neurogenic capacity for DL neurons in rats. This new data has been incorporated into Figure 7.

Reviewer 2 Point 7. The authors conclude that Wnt signaling is a rat specific effect since they did not observe any clear temporal change in wnt receptors in gyrencephalic species, and only a subset of RG in rats co-express Lmx1a and Lhx2. However, specific Wntligands and receptors (Wnt5a, Fzd and Lrp6) seem to be upregulated in human as well (Fig 7G), non RG cells could act as wnt ligand inducers in other species, and it has not been demonstrated that Lmx1a and Lhx2 are the source for Wntligand production. I wonder if the authors can completely rule out a role for Wnt in the protracted neurogenesis of other species.

Response: We sincerely appreciate the reviewer’s insightful and broad perspective regarding Wnt signaling dynamics across diverse species. In this study, our primary focus was to elucidate the specific mechanisms underlying the differences between mice and rats. Consequently, we did not initially explore Wnt dynamics in other species or their roles in developmental timing in great depth in the original manuscript. We fully acknowledge that lineage-specific adaptations occur at the individual gene level; for instance, Silver and colleagues have reported that human-specific upregulation of Wnt receptor gene FZD8 modulates neural progenitor behavior (Boyd et al., Current Biology 2008, Liu et al., Nature 2025). However, our comparative analysis of five mammalian species—carefully aligned by developmental stage—reveals a distinct global trend. While individual gene variations exist like human FZD8, the expression levels of multiple Wnt-related genes, particularly ligands, are markedly higher in rats than in the other four species.

Following the reviewer’s insightful suggestion, we examined the potential role of Lmx1a in activating Wnt ligand transcription in rat cortical progenitors by analyzing their expression correlation at the single-cell level. Our analysis revealed that several Wnt ligand genes are co-expressed with Lmx1a with a remarkably strong positive correlation. While we have not yet experimentally demonstrated the direct transcriptional activation of Wnt ligands by Lmx1a in these cells, this robust correlation at single-cell resolution strongly suggests that Lmx1a regulates Wnt ligand expression. These new findings are now included in Figure 7 and Figure S16, and the corresponding results section (Page 15, Lines 42-44) has been revised accordingly.

__Reviewer 2 Point 8 __Minor comments: The RNAscope experiment is currently qualitative. Is it the mRNA copy number per cell equal in both species but more cells are positive in rat, or are there differences in number of mRNA molecules as well? It is not indicated if the RNAscopeprobes are the same for mouse and rat.

Response: We sincerely thank the reviewer for this insightful suggestion. Following the comment, we performed RNAscope analysis for Axin2 in both mice and rats and quantified the results (now included in Figure 7D). The new data successfully validate the species differences initially observed in our scRNAseq analysis: specifically, the period of high-level Axin2 expression is significantly extended in rats compared to mice. These findings provide histological evidence that reinforces our conclusions regarding the distinct temporal dynamics between the two species.

Regarding probe design, the Axin2 RNAscope probes target conserved and corresponding sequences between mouse and rat, with species-specific probes optimized for each organism to ensure maximal specificity and sensitivity. We have updated the Methods section ("Fluorescent in situ hybridization with RNAscope") to include these details.

Reviewer #3

Reviewer 3 Point 1. Satb2 is also widely recognized as a deep layer marker. The authors need to perform analysis and quantification in Figs 1 and 4 with other II/III and IV markers such as Cux1 and Rorb.

Response: We thank the reviewer for their insightful comments regarding the marker specificity. We fully agree that while Satb2 is a robust marker for callosal projection identity, its broad distribution across both deep and upper layers limits its utility as a layer-specific marker. As the reviewer suggested, Cux1 (Layers 2/3) and Rorb (Layer 4) are indeed superior markers for defining laminar identity.

To address this, we have incorporated new immunohistochemical data for these markers in both the quantification of somatosensory cortical neurons (Figure S2) and the birth-dating analysis (Figure 4).

Our new findings are as follows:

1. Layer Quantification (Figure S2): By utilizing Cux1 and Rorb as more specific upper-layer (UL) markers, we confirmed that there are no significant differences in the number of these neurons between mice and rats.
2. Birth-dating Analysis (Figure 4): These markers allowed us to more precisely define the timing of Cux1/Rorb-positive cell generation, revealing subtle but important differences between the two species. While these additions do not alter the fundamental narrative of the original manuscript, they have significantly enhanced the precision and rigor of our analysis. We are grateful to the reviewer for guiding us toward this more robust validation.

Reviewer 3 Point 2. Rats have larger cortices. Therefore, quantification of neurons should also be normalized to cortical thickness in Fig 1E and also represented with individual data points.

Response: We sincerely appreciate the reviewer’s constructive suggestion. We agree that normalizing the number of cortical neurons by thickness provides a more rigorous comparison. Accordingly, we have calculated the neuronal density (cell count per unit thickness) for Tbr1- and Ctip2-positive cells and included these data in Figure S2C. Our analysis confirms that these populations are distributed at a significantly higher density in mice compared to rats.

Furthermore, we have updated the visualization in Figure 1E to display individual data points, ensuring full transparency of the underlying distribution. We believe these revisions, prompted by the reviewer’s insight, have substantially strengthened the clarity and persuasiveness of our manuscript.

Reviewer 3 Point 3. The clonal analysis in Figs 2 and 3 quantifies GFP and RFP and reports these as neurons. However, without using cell-specific markers, it seems the authors cannot exclude that some progeny are also glia derived from a radial glial progeny. I don't expect all experiments to have this but they must have some measures of both populations to address this possibility. This needs to be addressed to build confidence in the conclusion that there is clonal production of neurons.

Related to this, the relationship between position and fate is not always 1 to 1. The data summarized in Fig 2G are based on position and not using subtype markers. They should include assessment of markers as they do in Fig 4.

Response: We sincerely thank the reviewer for this insightful comment. We agree that a clear definition of cell types is essential for the accuracy of clonal analysis.

In this study, we primarily identified neurons based on their distinct morphological characteristics and performed measurements specifically on these cells. To validate this approach, we confirmed that the vast majority of cells identified as neurons were positive for NeuN and cortical excitatory neuron markers, while remaining negative for glial markers such as Olig2 and SOX9. (Notably, at postnatal day 7, most cells in the glial lineage exist as undifferentiated Olig2-positive progenitors). These observations support our conclusion that the cells analyzed based on morphology are indeed cortical excitatory neurons.

As the reviewer rightly pointed out, evaluating cell composition using fate-specific marker expression is the ideal approach. However, our current experimental setup required multiple fluorescence channels for DAPI staining (to assess tissue architecture) and immunostaining for GFP and RFP (to identify labeled clones). Due to these technical constraints regarding available detection channels and host species compatibility, we relied on morphological criteria for the primary analysis.

To address this concern and ensure the reliability of our findings, we performed additional analyses using a subset of samples. By co-staining retrovirally labeled neurons with cell-fate markers, we obtained results consistent with our other data (Figures 1 and 4) regarding laminar position and marker expression. Based on this consistency, we are confident that our classification based on morphology and laminar position does not alter the fundamental conclusions of this study.

Reviewer 3 Point 4. In Fig 5, the authors use PH3 as well as EdU to measure differences in indirect neurogenesis. Using EdU and Tbr2 they report more dividing IPs. However they need to measure this over the total number of Tbr2 cells as it is not normalized to differences in Tbr2 cells between species. Are there total differences in Tbr2+ cells when normalized to DAPI as well? Moreover, little analyses is performed to measure any impact on radial glia. As no striking differences were observed in IPs this leaves the cellular mechanism a bit unclear and begs the impact on radial glia. Measuring PH3+ cells in VZ and SVZ is not cell specific nor does it yield information to support the prolonged neurogenesis.

Response: We sincerely thank the reviewer for this insightful suggestion. We agree that quantifying Tbr2+/EdU+ double-positive cells alone was insufficient to fully capture the IP dynamics. Following the reviewer’s advice, we have now quantified the total population of Tbr2+ cells, normalized to the number of DAPI-stained nuclei. This new analysis reveals that mice and rats exhibit nearly indistinguishable temporal dynamics (Figure S10). When integrated with the original Tbr2+/EdU+ data in Figure 5, these findings suggest that rats maintain a slightly higher IP pool throughout the neurogenic period. This implies that the increased neuronal production in rats is not restricted to a specific phase, but rather occurs consistently across all developmental stages. We believe these additional data significantly strengthen our conclusions.

Reviewer 3 Point 5. The sc-seq is done in rat and compared to published mouse data from corresponding stages. They conclude species specific differences in progenitor gene expression. I am unsure how appropriate this is. Are similar sequencing platforms used? Can they find similar results if using multiple dataset? There are other datasets that may be used to validate these findings beyond DiBella et al.

Response: We sincerely thank the reviewer for this insightful comment. We agree that establishing the validity of our analytical approach is crucial for the reader’s confidence in our findings. To address this, we have explicitly stated in the revised manuscript that both our rat scRNAseq data and the publicly available datasets were generated using consistent experimental platforms. This ensures that the integration process is technically sound.

Revised text (Page 13, Lines 16-18): “After quality control, we integrated these profiles with previously published mouse cortical cell data from corresponding neurogenic stages, which is prepared using the consistent platform with ours (35) (Figure S11).”

Furthermore, to ensure the robustness of our comparative analysis, we have incorporated an additional independent dataset (Ruan et al., PNAS 2021) in addition to the Di Bella et al. Nature 2021 data used in the original manuscript. We confirmed that the results obtained using this second dataset are highly consistent with our initial findings, further validating our conclusions across different studies (Figure S13A).

Reviewer 3 Point 6. Wnt ligand analysis requires validation in situ across developmental stages, to support their conclusions. Ideally they might consider doing some manipulations to provide context to this observation.

Response: We sincerely thank the reviewer for these insightful suggestions. We agree that validating the spatial expression patterns of Wnt ligands and confirming their expression in rat-specific RG, as suggested by our scRNAseq data, is crucial for strengthening our conclusions.

Regarding the expression of Wnt3a, a key ligand in cortical development: although immunohistochemical analysis clearly identified Wnt3a expression in the cortical hem, the expression levels in RG within the cortical area were substantially lower than those in the hem, making definitive visualization challenging. To complement these findings and provide more robust evidence, we performed the following additional experiments:

1. Validation of Wnt signaling levels: Using RNAscope-based in situ hybridization for Axin2, we successfully confirmed the elevated Wnt signaling levels in rat-specific RG (Figure 7C, D), consistent with our scRNAseq findings.
2. Elucidating strikingly high correlated expressions of Lmx1a and Wnt ligand genes in the rat cortical progenitors in our scRNAseq dataset (Figure S16B).
3. Functional analysis: To test the functional significance of this signaling, we inhibited Wnt signaling by electroporating dominant-negative TCF7L2 into rat RG at E15.5. This manipulation resulted in a subtype shift of the generated neurons toward an upper-layer identity (Figure 7I, J). These new results demonstrate that the rat-specific extension of high Wnt signaling levels serves as a fundamental mechanism for the prolonged production of deep-layer (DL) neurons. We are grateful to the reviewer for these suggestions; these additional data have significantly strengthened our core argument that the heterochronic regulation of Wnt signaling states drives the evolution of cortical neuronal composition.

__Reviewer 3 Point 7 __Minor concerns-1

Please separate images in Fig 1D it is very strange to have them all on top of each other.

Response: We sincerely thank the reviewer for this suggestion. As requested, we have provided individual channel images alongside the merged multicolor panels. We agree that this modification significantly enhances the clarity of our data and makes the results much easier to interpret.

__Reviewer 3 Point 8 __Minor concerns-2

Are data in Fig 4E Edu+Tbr1+EdU+? This should be clarified and would be most accurate.

Response: We appreciate the reviewer’s suggestion. We added the label of Y axes of the plots in Figure 4E-K. The procedure of cell count in these analyses are documented in the caption of Figure 4E-K, “Normalized counts of neurons colabeled for EdU and projection-specific markers, relative to the peak of EdU+ and marker+ cells.”.

__Reviewer 3 Point 9 __Minor concerns-3

Fig 4 graphs only have titles without Y axis. Please adjust location of title or repeat for clarity.

Response: We thank the reviewer for this helpful suggestion. To clarify the definition of the Y-axis, we have now added a descriptive label to the axis in the revised figure.

__Reviewer 3 Point 10 __Minor concerns-4

Fig 4A implies cumulative incorporation which I don't think is being performed here. They should clarify this in the figure.

Response: We appreciate the reviewer’s insightful comment. To avoid any potential misunderstanding regarding the additivity of the effect, we have revised the illustration in Figure 4A for greater clarity.

__Reviewer 3 Point 11 __Minor concerns-5

Fig 5 needs labels for the actual stages assayed, as illustrated in Fig 4A.

Response: We thank the reviewer for this helpful suggestion. Following your comment, we have added the developmental stage information (expressed as embryonic days) for both mice and rats in the revised manuscript.

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Referee #3

Evidence, reproducibility and clarity

In this study the authors investigate differences between two closely related species, rats and mice, in terms of cortical development and neuronal composition. They first perform comparative analysis of cortical layers which revealed the density and markers of deep layer neurons of rats is disproportionately larger compared to adult mice. They then use retroviruses for lineage analysis from embryonic stages to P7. They find in general that there are temporal differences in when mice and rats produce upper versus deep layer neurons, with the process being protracted in rats. EdU injections were used to report differences in the timing of cortical neuron generation between species and they note no striking differences in IPs. Sc-sequencing of rat cortices at different stages was then used to measure temporal changes in gene expression and compared to published mouse data. They note that rats have sustained Wnt ligand expression in radial glia highlighting that as a potential mechanism of action.

Major concerns 1. Satb2 is also widely recognized as a deep layer marker. The authors need to perform analysis and quantification in Figs 1 and 4 with other II/III and IV markers such as Cux1 and Rorb. 2. Rats have larger cortices. Therefore, quantification of neurons should also be normalized to cortical thickness in Fig 1E and also represented with individual data points. 3. The clonal analysis in Figs 2 and 3 quantifies GFP and RFP and reports these as neurons. However, without using cell-specific markers, it seems the authors cannot exclude that some progeny are also glia derived from a radial glial progney. I don't expect all experiments to have this but they must have some measures of both populations to address this possibility. This needs to be addressed to build confidence in the conclusion that there is clonal production of neurons. Related to this, the relationship between position and fate is not always 1 to 1. The data summarized in Fig 2G are based on position and not using subtype markers. They should include assessment of markers as they do in Fig 4. 4. In Fig 5, the authors use PH3 as well as EdU to measure differences in indirect neurogenesis. Using EdU and Tbr2 they report more dividing IPs. However they need to measure this over the total number of Tbr2 cells as it is not normalized to differences in Tbr2 cells between species. Are there total differences in Tbr2+ cells when normalized to DAPI as well? Moreover, little analyses is performed to measure any impact on radial glia. As no striking differences were observed in IPs this leaves the cellular mechanism a bit unclear and begs the impact on radial glia. Measuring PH3+ cells in VZ and SVZ is not cell specific nor does it yield information to support the prolonged neurogenesis. 5. The sc-seq is done in rat and compared to published mouse data from corresponding stages. They conclude species specific differences in progenitor gene expression. I am unsure how appropriate this is. Are similar sequencing platforms used? Can they find similar results if using multiple dataset? There are other datasets that may be used to validate these findings beyond DiBella et al. 6. Wnt ligand analysis requires validation in situ across developmental stages, to support their conclusions. Ideally they might consider doing some manipulations to provide context to this observation.

Minor concerns 1. Please separate images in Fig 1D it is very strange to have them all on top of each other. 2. Are data in Fig 4E Edu+Tbr1+EdU+? This should be clarified and would be most accurate. 3. Fig 4 graphs only have titles without Y axis. Please adjust location of title or repeat for clarity. 4. Fig 4A implies cumulative incorporation which I don't think is being performed here. They should clarify this in the figure. 5. Fig 5 needs labels for the actual stages assayed, as illustrated in Fig 4A.

Significance

Strengths:

The finding that there are differences in cortical composition between rats and mice and that this is linked to prolonged neurogenesis in rats Use of careful and detailed lineage analysis to define differences in temporal production of neurons Inclusion of single cell sequencing

Limitations:

Largely descriptive Requires additional investigation to support some conclusions about neurons Concerns about inferring too much from single cell sequencing done by the authors but compared to publication

Advance: Finding that there are differences in neurogenesis between closely related species is interesting and provides insight into mechanisms of cortical evolution.

Audience: Evolution, cortical development

Expertise: Cortical development, evolution

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Referee #2

Evidence, reproducibility and clarity

Summary:

Yamauchi et al. performed a comparative anatomical analysis of the layer architecture in the primary somatosensory cortex across 8 mammalian species. Unlike primates, which show an expansion of upper layers (UL), rodents, especially rats, display a pronounced thickening of deep layers (DL). In this study they focus on comparing rats and mice, given the higher abundance of DL neuron subtypes in rats. Using histological analysis, they showed that rats possess significantly more DL neurons per cortical column than mice, while UL neuron counts remain similar. Clonal lineage tracing showed that rat radial glial (RG) progenitors generate more DL neurons, indicating species-specific differences in progenitor neurogenic activity. Birth dating assays confirmed an extended DL neurogenesis phase in rats, followed by a conserved UL generation phase. Single-cell RNA sequencing further revealed that rats maintain an early progenitor state longer than mice, marked by sustained expression of DL-associated genes. Specifically, rat RG progenitors exhibit prolonged and elevated expression of Wnt signaling genes, particularly Wnt ligands. Comparative analysis of published single-cell RNA-Seq across species highlighted that this extended Wnt-high period in rats is exceptional, suggesting a species-specific extension of a conserved neurogenic program.

Major comments:

This reviewer thinks the topic is exciting, and the experiments elegant, insightful and well described. The paper is well written and follows a very logical flow, the conclusion for each experiment is supported by the data and they are carefully stated. This reviewer really appreciated the summary illustration included as a panel in each figure, they think that this greatly enhanced the clarity and accessibility of the data presented, especially because species comparison can be difficult to follow.

In this reviewer's opinion, there are some aspects of the findings that the authors would need to clarify/address to explain in clarify the phenotype observed and to enhance the overall significance of this very well-made paper: 1. The introduction lacks sufficient background and fails to convey the significance of the study. Specifically, why the research was undertaken, what knowledge gap it addresses, and how the findings could be applied. Addressing these questions already in the introduction would enhance the impact of the work and broaden its readership. 2. In figure 5 the authors conclude that "differences in cell cycle kinetics and indirect neurogenesis are unlikely to be the primary factors driving the species-specific variation in DL neuron production. Instead, the temporal regulation of progenitor neurogenic competence, which determines the duration of the DL production phase, provides a more plausible explanation for the greater number of DL subtypes observed in rats". It is not clear to this reviewer how the authors come to this conclusion. Authors observe a significant proportion of mitotic cells in rat VZ from day 1, and a higher constant proportion of mitotic progenitors in SVZ rats compared to mouse (Figure 5C). This points to an early difference in mitotic progenitors that may also lead to increased IP numbers, and potentially an increased number in DL cells, even before day 1. In addition, the higher abundance of IPs in the G2/S phase (statistically significant in 4 of the 7 time points) (Figure 5F), would suggest that this difference might play a role in the species-specific variation of DL neuron production. The authors should estimate cell cycle length instead of just measuring proportions to conclude something about cell cycle kinetics. They can then model growth curves to predict the effect caused if there were differences in cell cycle length between equivalent cell types across species. 3. In Figure 6 the authors focus only on the mouse and rat datasets. Given the availability of datasets from primates that the author used already for Figure 7, it would give the reader a broader prospective if also these datasets would be integrated in the analysis done for Figure 6, particularly it would be interesting to integrate them in the pseudotime alignment of cortical progenitor. How do human and/or macaque early and late neurogenic phase would compare to mouse and rat in this model? 4. In Figures 6C and 6D, the authors distinguish between cycling and non-cycling NECs and RGCs. Could the authors clarify the rationale behind making this distinction? Could the authors comment on how they interpret the impact of cycling versus non-cycling states on species-specific non-uniform scaling? Do they consider the observed non-linear correspondences to be driven by differences in cell cycle activity? 5. For the non-uniform scaling in Figure 6F, the authors identify critical inflection points and mention that "the largest delay in rat progenitors occurring where Day 1 and Day 3 progenitors overlapped". It would be good if the authors could discuss what they think all the inflection points represents. How much can it be explained by the heterogeneity within progenitors per time point? There is a clear higher spread of histograms at days 3 and 5, and the histogram at day 5 almost overlaps with day 1. I wonder if the same conclusion about non-uniform scaling would be detected if the distance matrix was built separately for specific cell types, for example only looking at NECs or RGCs. 6. The authors conclude that the elevated and prolonged expression of Wnt-ligand genes in rat RGs extend the DL neurogenic window and contribute to rat-specific expansion of deep cortical layer. In order to validate this finding it would be good for the authors to perform a perturbation experiment and reduce Wnt signalling/ Axin 2 levels in rats or depleted the Lmx1a and Lhx2 double-positive population. 7. The authors conclude that Wnt signaling is a rat specific effect since they did not observe any clear temporal change in wnt receptors in gyrencephalic species, and only a subset of RG in rats co-express Lmx1a and Lhx2. However, specific Wnt ligands and receptors (Wnt5a, Fzd and Lrp6) seem to be upregulated in human as well (Fig 7G), non RG cells could act as wnt ligand inducers in other species, and it has not been demonstrated that Lmx1a and Lhx2 are the source for Wnt ligand production. I wonder if the authors can completely rule out a role for Wnt in the protracted neurogenesis of other species.

Minor comments:

The RNAscope experiment is currently qualitative. Is it the mRNA copy number per cell equal in both species but more cells are positive in rat, or are there differences in number of mRNA molecules as well? It is not indicated if the RNAscope probes are the same for mouse and rat.

Significance

How different species achieve such remarkable differences in brain shape and size remains poorly understood. A critical aspect of this process is the duration of the neurogenic phase: the period during which neural progenitors generate neurons. This phase tends to be extended in species with larger brains and contains multiple neuronal stem cell types in varying proportions. It is thought that this accounts for their increased neuronal numbers. In their search for mechanisms that prolong neurogenesis across species, the authors propose a rat-specific role for Wnt ligands in expanding the neurogenic period in the rat brain. Importantly, they rule out that this mechanism operates in other species, such as primates or ferrets, to achieve similar extensions.

The study is of high quality, incorporating rigorous lineage-tracing experiments in two species and single-cell RNA sequencing. Previous work established a role for Wnt signaling in regulating early neurogenesis in mice. Here, the authors characterize a novel population of radial glial cells (Lmx1a and Lhx2 double-positive) that may explain increased Wnt ligand secretion in rats. However, functional validation of this mechanism is still lacking. To strengthen its evolutionary relevance, it would be important to determine whether similar effects occur during earlier neural stages in other species (such as neuroepithelium thickening), or whether other cell types have co-opted the proposed Lmx1a-Lhx2 regulatory module in other species.

From the perspective of a researcher with a stem cell and developmental background focused on neural evo-devo, this manuscript represents a solid and novel contribution. The proposed model of a rat-specific mechanism for extending the neurogenic phase contrasts with the prevailing concept of convergence in mechanisms underlying species-specific cortical development. This raises intriguing questions about how multiple molecular pathways have been co-opted to achieve similar developmental outcomes. Furthermore, we know very little about what determines the duration of specific developmental processes. This work suggests that extended Wnt signaling may account for prolonged neurogenesis in rats compared to mice. Future studies should aim to validate the proposed rat-specific co-option of an Lmx1a-Wnt ligand cascade in cortical radial glia, potentially through relief of Lhx2-mediated repression of Lmx1a.

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Referee #1

Evidence, reproducibility and clarity

Yamauchi and colleagues explore how species-specific differences in timing of neurogenesis may contribute to cell composition in the mature brain, using rat and mouse cortex as a main model of study. They first estimate and compare among 8 mammalian species the number of cortical neurons corresponding to deep layer (DL) and upper layer (UL) neurons. They find a species-specific relative increase of DL/UL neurons in rats, compared with all other species tested. They then explore the cellular mechanisms underlying these differences in mouse and rat, using retrovirus-based clonal analyses and EdU nuclear labeling, as well as axonal projection retrograde tracing. They conclude that the increased number of DL neurons in the rat is correlated with an increase in the period of DL neuron generation at early stages of corticogenesis. They also report a lack of obvious difference in cell cycle kinetics and indirect vs direct neurogenesis that could explain the DL/UL differences. Finally, they perform comparative scRNAseq analysis in mouse vs rat embryonic cortical cells. This first confirms at the transcriptomic level an apparent prolonged period of early neurogenesis in the rat cortex. Moreover they find among modules of co-expression detectable at these stages an increase in genes corresponding to Wnt signalling, a pathway previously linked to increased self-renewal and delayed differentiation of radial glial progenitors. They thus conclude that the species-differences in neuronal number in the rat is linked to increased Wnt signaling at a critical time of corticogenesis.

Overall this is a thorough and elegant study focused on a timely and interesting topic. The data shown are convincing and carefully interpreted. I have however a couple of comments and questions to make the study fully clear and convincing.

• The authors describe cortical neuronal counts across several mammalian species, which is quite impressive, but the information on the methods of counting is lacking: how representative are the data used / shown; how many individuals / brains / sections were used for each species considered? Much more detailed description of the quantifications should be provicded to judge the validity of this first conclusion.
• The authors use several markers of cortical neuron identity to confirm their neuron number measurements, but from the data shown in Figure 1D,E it seems that only some markers (Satb2) show species-differences while others do not (CTIP2 / Tbr1). How do the authors explain this discrepancy - does this mean that it is mainly Satb2 neurons that are increased in number? But if so how to explain the relative increase in subcortical projections shown in Figure S7?
• The authors focus their study almost exclusively on somatosensory cortex, but can they comment on other areas (motor, visual for instance)? It would be nice to provide additional comparative data on other areas, at least for some of the parameters examined acros mouse and rat. Alternatively the authors should be more explicit in the abstract and description of the study that it is limited to a single area.
• The authors provide convincing evidence of increased Wnt signaling pathway in the rat. They should show more explicitely how other classical pathways of neurogenic balance / temporal patterning are expressed in their mouse and rat transcriptome data sets. These would include Notch, FGF, BMP, for which all the data should be available to provide meaningful species comparison.
• The alignment of mouse and rat trajectories is very nicely showing a delay at early-mid-corticogenesis. But there is also heterochronic transcriptome at latest stages (end of 5). How can this be interpreted? Does this mean potentially prolonged astrogliogenesis in the rat cortex?
• Figure 7: description implies that module 3 is a subset of module 4, but this is not obvious at all from the panels shown. Please clarify.

Significance

The topic of the study if of general interest and original, and the conclusions original and important. The approaches used are state of the art and applied in an elegant fashion to the topic. This study should be of broad interest to developmental neurobiologists, but also developmental biologists interesting in temporal patterning and developmental timing across species.

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Reply to the reviewers

We thank the reviewers and editors for their careful evaluation of our manuscript and their positive comments on the importance and rigor of the work. Below you will find our point-by-point response to each reviewer's suggestions. We believe that we have addressed (in the response and the revised manuscript) all of the concerns. Please note that in some cases, we have numbered a reviewer's comments for clarity, however beyond this, we have not altered any of the reviewers' text.

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

Lo et al., report a high-throughput functional profiling study on the gene encoding for argininosuccinate synthase (ASS1), done in a yeast experimental system. The study design is robust (see lines 141-143, main text, Methods), whereby "approximately three to four independent transformants of each variant would be isolated and assayed." (lines 140 - 141, main text, Methods). Such a manner of analysis will allow for uncertainty of the functional readout for the tested variants to be accounted for.

This is an outstanding study providing insights on the functional landscape of ASS1. Functionally impaired ASS1 may cause citrullinemia type I, and disease severity varies according to the degree of enzyme impairment (line 30, main text; Abstract). Data from this study forms a valuable resource in allowing for functional interpretation of protein-altering ASS1 variants that could be newly identified from large-scale whole-genome sequencing efforts done in biobanks or national precision medicine programs. I have some suggestions for the Authors to consider:

1. The specific function of ASS1 is to condense L-citrulline and L-aspartate to form argininosuccinate. Instead of measuring either depletion of substrate or formation of product, the Authors elected to study 'growth' of the yeast cells. This is a broader phenotype which could be determined by other factors outside of ASS1. Whereas i agree that the experiments were beautifully done, the selection of an indirect phenotype such as ability of the yeast cells to grow could be more vigorously discussed.

We appreciate the reviewer's point regarding the indirect nature of growth as a functional readout. In our system, yeast growth is tightly and specifically coupled to ASS enzymatic activity. The strains used are isogenic and lack the native yeast argininosuccinate synthetase, such that arginine biosynthesis, and therefore yeast replication on minimal medium lacking arginine, depends exclusively on the activity of human ASS1. Under these defined and limiting conditions, growth provides a quantitative proxy for ASS1 function. However, we acknowledge that this assay does not resolve specific molecular mechanisms underlying reduced function, such as altered catalytic activity versus effects on protein stability. We have updated the text to clarify these points.

"While growth is an indirect phenotype relative to direct measurement of substrate turnover or product formation, it is tightly coupled to ASS enzymatic activity in this system and is expected to be impaired by amino acid substitutions that reduce catalytic activity or protein stability. Therefore, growth on minimal medium lacking arginine is a quantitative measure of ASS enzyme function, allowing the impact of ASS1 missense variants to be assessed at scale through a high-throughput growth assay, in a single isogenic strain background, under controlled, defined conditions that limit confounding factors unrelated to ASS1 activity. We expect that the assay will detect reductions in both catalytic activity and protein stability but will not distinguish between these mechanisms."

1. One of the key reasons why studies such as this one are valuable is due to the limitations of current variant classification methods that rely on 'conservation' status of amino acid residues to predict which variants might be 'pathogenic' and which variants might be 'likely benign'. However, there are serious limitations, and Figures 2 and 6 in the main text shows this clearly. Specifically, there is an appreciable number of variants that, despite being classified as "ClinVar Pathogenic", were shown by the assay to unlikely be functionally impaired. This should be discussed vigorously. Could these inconsistencies be potentially due to the read out (growth instead of a more direct evaluation of ASS1 function)?

We interpret this discrepancy as reflecting a sensitivity limitation of the growth-based readout rather than a fundamental disagreement between functional effect and clinical annotation. Specifically, we believe that our assay is unable to resolve the very mildest hypomorphic variants from true wild type, i.e., the residual activity of these variants is sufficient to fully support yeast growth under the conditions used. On this basis, we have chosen not to treat wild-type-like growth in our assay as informative for benignity; conversely, reduced growth provides evidence supporting pathogenicity (all clinically validated variants examined in this range are pathogenic).

We have revised the manuscript to clarify this point explicitly and to frame these variants as lying outside the effective resolution limit of the assay rather than representing true false positives. Additional discussion of this limitation and its implications is provided in our responses to Reviewer 2 (points 1 and 4) along with specific changes made to the text.

1. Figure 3 is very interesting, showing a continuum of functional readout ranging from 'wild-type' to 'null'. It is very interesting that the Authors used a threshold of less than 0.85 as functionally hypomorphic. What does this mean? It would be very nice if they have data from patients carrying two hypomorphic ASS1 alleles, and correlate their functional readout with severity of clinical presentation. The reader might be curious as to the clinical presentation of individuals carrying, for example, two ASS1 alleles with normalized growth of 0.7 to 0.8.

I hope you will find these suggestions helpful.

We thank the reviewer for this thoughtful comment. Figure 3 indeed illustrates a continuum of functional effects, and we agree that careful interpretation of the thresholds used is important. To clarify the rationale for the hypomorphic threshold, the interpretation of intermediate growth values, and to emphasize that these labels reflect only behavior in the functional assay, we have rewritten the relevant section of the Results:

"The normalized growth scores of the 2,193 variants tested in our functional assay form a clear bimodal distribution (Figure 3), with two distinct peaks corresponding to functional extremes, as is commonly reported in large-scale functional assays of protein function [9, 10]. The smaller peak, centered around the null control (normalized growth = 0), represents variants that fail to support growth in the assay (growth 0.85). Variants with growth values falling between these two peak-based thresholds display partial functional impairment and are classified as functionally hypomorphic (n = 323). Crucially, these classifications are entirely derived from the observed peaks in the distribution of growth values and reflect differences in functional activity under the assay conditions. They do not provide direct evidence for clinical pathogenicity or benignity and should not be used for clinical variant interpretation without proper benchmarking against clinical reference datasets, as implemented below within an OddsPath framework."

We agree with the reviewer that correlating functional measurements with clinical severity in individuals carrying two hypomorphic ASS1 alleles would be highly informative, particularly given that ASS1 deficiency is an autosomal recessive disorder. While mild hypomorphic variants (for example, variants with normalized growth values of 0.7-0.8 in our assay) could plausibly contribute to disease when paired with a complete loss-of-function allele, systematic analysis of combinatorial genotype effects and genotype-phenotype correlations is beyond the scope of the present study, which focuses on the functional effects of individual variants. We view this as an important direction for future work.

Reviewer #1 (Significance (Required)):

This is an outstanding study providing insights on the functional landscape of ASS1. Functionally impaired ASS1 may cause citrullinemia type I, and disease severity varies according to the degree of enzyme impairment (line 30, main text; Abstract). Data from this study forms a valuable resource in allowing for functional interpretation of protein-altering ASS1 variants that could be newly identified from large-scale whole-genome sequencing efforts done in biobanks or national precision medicine programs.

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

In this manuscript, Lo et al characterize the phenotypic effect of ~90% of all possible ASS1 missense mutations using an elegant yeast-based system, and use this dataset to aid the interpretation of clinical ASS1 variants. Overall, the manuscript is well-written and the experimental data are interpretated rigorously. Of particular interest is the identification of pairs of deleterious alleles that rescue ASS1 activity in trans. My comments mainly pertain to the relevance of using a yeast screening methodology to infer functional effects of human ASS1 mutations.

1. Since human ASS1 is heterologously expressed in yeast for this mutational screen, direct comparison of native expression levels between human cells and yeast is not possible. Could the expression level of human ASS1 (driven by the pARG1 promoter) in yeast alter the measured fitness defect of each variant? For instance, if ASS1 expression in yeast is sufficiently high to mask modest reductions in catalytic activity, such variants may be misclassified as hypomorphic rather than amorphic. Conversely, if expression is intrinsically low, even mild catalytic impairments could appear deleterious. While it is helpful that the authors used non-human primate SNV data to calibrate their assay, experiments could be performed to directly address this possibility.

The nature of the relationship between yeast growth and availability of functional ASS1 could also influence the interpretation of results from the yeast-based screen. Does yeast growth scale proportionately with ASS1 enzymatic activity?

We completely agree that the expression level of human ASS1 in yeast could influence the measured fitness effects of individual variants. We expect the rank ordering of variants in our growth assay to reflect their relative enzymatic activity (i.e. a monotonic relationship) but acknowledge that the precise mapping between activity and growth is unknown and may include ceiling and floor effects that limit the assay's dynamic range. As the reviewer notes, under high expression conditions moderate loss-of-function variants could appear indistinguishable from wild type (ceiling effect), whereas under lower expression the same variants could behave closer to the null control (floor effect).

In our system, ASS1 is expressed from the pARG1 promoter, chosen under the assumption that the native expression level of ARG1 (the yeast ASS1 ortholog) is appropriately tuned for yeast growth. Crucially, rather than assuming a fixed mapping from assay growth to clinical pathogenicity (given potential nonlinearities in the relationship between ASS function and growth) we benchmark the assay against external data, including known pathogenic and benign variants and non-human primate SNVs, to calibrate thresholds and guide interpretation within an OddsPath framework. This benchmarking indicates that ceiling effects are likely present, with some mild loss-of-function pathogenic variants appearing indistinguishable from wild type in the growth assay. We explicitly account for this by not using high-growth scores as evidence toward benignity. We have made the following changes the manuscript:

"A subset of clinically pathogenic ASS1 variants exhibit near-wild-type growth in our yeast assay. In general, we expect a monotonic relationship between ASS function and yeast growth, but with the potential for floor and ceiling effects that constrain the assay's dynamic range. In this context, we interpret high-growth pathogenic variants as likely causing mild loss of function that cannot be distinguished from wild type in our assay"

"Based on these findings and given that 22/56 pathogenic variants show >85% growth, we conclude that growth above this threshold should not be used as evidence toward benignity."

1. It would be helpful to add an additional diagram to Figure 1A explaining how the screen was performed, in particular: when genotype and phenotype were measured, relative to plating on selective vs non-selective media? This is described in "Variant library sequence confirmation" and "Measuring the growth of individual isolates" of the Methods section but could also be distilled into a diagram.

We thank the reviewer for this helpful suggestion. We have updated Figure 1 by adding a new schematic panel (Figure 1C) that distills the experimental workflow into a visual overview. This diagram is intended to complement the detailed descriptions in the Methods and improve clarity for the reader.

1. The authors rationalize the biochemical consequences of ASS1 mutations in the context of ASS1 per se - for example, mutations in the active site pocket impair substrate binding and therefore catalytic activity, which is expected. Does ASS1 physically interact with other proteins in human cells, and could these interactions be altered in the presence of specific ASS1 mutations? Such effects may not be captured by performing mutational scanning in yeast.

We are not aware of any specific protein-protein interactions involving ASS that are required for its enzymatic function. However, we agree that ASS could engage in non-essential interactions with other human proteins that might be altered by specific missense variants and that such interactions would not necessarily be captured in a yeast-based assay.

Importantly, our complementation system depends on human ASS providing the essential enzymatic activity required for arginine biosynthesis in yeast. If ASS1 required obligate human-specific protein interactions to function, even the wild-type enzyme would fail to support yeast growth, which is clearly not the case. We therefore conclude that the assay robustly reports on the intrinsic enzymatic activity of ASS, while acknowledging that non-essential human-specific interactions may not be assessed. We have updated the manuscript to reflect this point.

"Importantly, successful functional complementation indicates that ASS enzymatic activity does not depend on any obligate human-specific protein interactions."

1. The authors note that only a small number (2/11) of mutations at the ASS1 monomer-monomer interface lead to growth defects in yeast. It would be helpful for the authors to discuss this further.

As discussed in response to the reviewer's comments on the relationship between ASS activity and yeast growth (point 1 above), we expect growth to be a monotonic but nonlinear function of enzymatic activity, with potential ceiling effects at high activity. Under this model, variants causing weak or moderate loss of function may remain indistinguishable from wild type when residual activity is sufficient to support normal growth. We favor this explanation for the observation that only 2/11 interface variants show reduced growth, as many pathogenic interface substitutions are associated with milder disease presentations, consistent with higher residual enzyme function. Consistent with this interpretation, variants affecting the active site, where substitutions are expected to cause large reductions in catalytic activity, are readily detected by the assay.

Although we cannot exclude partial buffering of dimerization defects in yeast, we interpret the reduced sensitivity to interface variants primarily as a general limitation of growth-based assays. Accordingly, our decision not to use growth >85% as evidence toward benignity is conservative relative to approaches that would classify high-growth variants as benign except at the monomer-monomer interface, avoiding reliance on structural subclassification and minimizing the risk of false benign interpretation. Reduced growth, by contrast, provides strong evidence of loss of ASS1 function and pathogenicity, validated under the OddsPath framework.

We have updated the Results and Discussion sections to clarify these points (also see response to the reviewer's point 1).

"A subset of clinically pathogenic ASS1 variants exhibit near-wild-type growth in our yeast assay. In general, we expect a monotonic relationship between ASS function and yeast growth, but with the potential for floor and ceiling effects that constrain the assay's dynamic range. In this context, we interpret high-growth pathogenic variants as likely causing mild loss of function that cannot be distinguished from wild type in our assay. Consistent with this view, many pathogenic variants with high assay growth are located at the monomer-monomer interface rather than the active site, and are associated with milder or later-onset clinical presentations, suggesting partial enzymatic impairment that is clinically relevant in humans but not resolved by the yeast assay."

"Based on these findings and given that 22/56 pathogenic variants show >85% growth, we conclude that growth above this threshold should not be used as evidence toward benignity. Notably, this approach is conservative relative to treating high-growth variants as benign except at the monomer-monomer interface, avoiding reliance on structural subclassification and minimizing the risk of false benign interpretation arising from assay ceiling effects. Conversely, the variants with

Reviewer #2 (Significance (Required)):

This study presents the first comprehensive mutational profiling of human ASS1 and would be of broad interest to clinical geneticists as well as those seeking biochemical insights into the enzymology of ASS1. The authors' use of a yeast system to profile human mutations would be particularly useful for researchers performing deep mutational scans, given that it provides functional insights in a rapid and inexpensive manner.

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

Section 1 - Evidence, reproducibility, and clarity Summary This manuscript presents a comprehensive functional profiling of 2,193 ASS1 missense variants using a yeast complementation assay, providing valuable data for variant interpretation in the rare disease citrullinemia type I. The dataset is extensive, technically sound, and clinically relevant. The demonstration of intragenic complementation in ASS1 is novel and conceptually important. Overall, the study represents a substantial contribution to functional genomics and rare disease variant interpretation.

Major comments 1. This is an exciting paper as it can provide support to clinicians to make actionable decisions when diagnosing infants. I have a few major comments, but I want to emphasize the label of "functionally unimpaired" variants to be misleading. The authors explain that there are several pathogenic ClinVar variants that fall into this category (above the >.85 growth threshold) but I think this category needs a more specific name and I would ask the authors to reiterate the shortcomings of the assay again in the Discussion section.

We thank the reviewer for raising this important point. We agree that the label "functionally unimpaired" could be misleading if interpreted as implying clinical benignity rather than assay behavior. We have therefore clarified that this designation refers strictly to variant behavior in the yeast growth assay and does not imply absence of pathogenicity.

In addition, we have expanded the Discussion to explicitly address the existence of clinically pathogenic variants with high growth scores (>0.85), emphasizing that these likely reflect a ceiling effect of the assay and represent a key limitation for interpretation. This clarification reiterates that high-growth scores should not be used as evidence toward benignity, while reduced growth provides strong functional evidence of pathogenicity. Relevant revisions are described in our responses to Reviewers 1 and 2.

1. I think there's an important discussion to be had here, is the assay detecting variants that alter the function of ASS or is it detecting a complete ablation of enzymatic activity? The results might be strengthened with a follow-up experiment that identifies stably expressed ASS1 variants.

We agree with the review that distinguishing between stability and enzyme activity would be valuable information. Unfortunately, we do not currently have the resources to perform this type of large-scale study. We have acknowledged in the text that our assay does not distinguish between enzyme activity and protein stability:

"We expect that the assay will detect reductions in both catalytic activity and protein stability, but will not distinguish between these mechanisms."

At the very least, it would be great to see the authors replicate some of their interesting results from the high-throughput screen by down-selecting to ~12 variants of uncertain significance that could be newly considered pathogenic.

We have included new analysis of all 25 VUS variants falling in the pathogenic range of our assay (Supplemental Table S7). Reclassification under current guidelines (in the absence of our data) shifts six variants to Pathogenic/Likely Pathogenic and 11 more are reclassified to Likely Pathogenic with the application of our functional data as PS3_Supporting. The remaining eight VUS are all reclassified to Likely Pathogenic when inclusion of homozygous PrimateAI-benign variants allows the assay to satisfy full PS3 criteria.

1. I would ask the authors to provide more citations of the literature in the introduction of the manuscript. I would be especially interested in knowing more about human ASS being identified as a homolog of yeast ARG1, as they share little sequence similarity (27.5%) at the protein level. That said, I find the yeast complementation assay exciting.

We thank the reviewer for this suggestion. Human ASS and yeast Arg1 catalyze the same biochemical reaction and share approximately 49% amino acid sequence identity. We have revised the Introduction to clarify this relationship and to note explicitly that the Saccharomyces Genome Database (SGD) identifies the human gene encoding argininosuccinate synthase (ASS1) as the ortholog of yeast ARG1. An appropriate citation has been added to support this statement. The protein alignments have been provided as File S2.

"This assay is based on the ability of human ASS to functionally replace (complement) its yeast ortholog (Arg1) in S. cerevisiae (Saccharomyces Genome Database, 2026). Importantly, successful functional complementation indicates that ASS enzymatic activity does not depend on any obligate human-specific protein interactions. At the protein level, human ASS and yeast Arg1 display 49% sequence identity (File S2) and share identical enzymatic roles in converting citrulline and aspartate into argininisuccinate."

1. I appreciate the efforts made by the authors to share their work and make this study more reproducible, such as sharing the hASS1 and yASS1 plasmids being shared on NCBI Genbank (Line 121) and publishing the ONT reads on SRA (Line 154). I made a requests for additional data to be shared, such as the custom method/code for codon optimization and a table of Twist variant cassettes that were ordered. I would also love to see these results shared on MaveDB.org.

We thank the reviewer for these suggestions regarding data sharing and reproducibility. As requested, we have provided the custom codon optimization script as File S1 and the amino acid alignment used to perform codon harmonization as File S2. The sequence of the underlying variant cassette is included in the corresponding GenBank entry, and we have clarified this point in the legend of Figure 1. For each amino acid substitution, Twist Bioscience used a yeast-specific codon scheme with a single consistent codon per amino acid; accordingly, the sequence of each variant cassette can be inferred from the base construct and the specified amino acid change. A complete list of variant amino acid substitutions used in this study is provided in Table S3.

1. I find this manuscript very exciting as the authors have a compelling assay that identifies pathogenic variants, but I was generally disappointed by the quality and organization of the figures. For example, Figure 4 provides very little insight, but could be dramatically improved with an overlay of the normalized growth score data or highlighting variants surrounding the substrate or ATP interfaces. There are some very interesting aspects of this manuscript that could be shine through with some polished figures.

We thank the reviewer for this feedback and agree that clear and well-organized figures are essential for conveying the key results of the study. In response, we have substantially revised Figure 4 by adding colored overlays showing residue conservation and median normalized growth scores (new panels Figure 4C and 4D), which more directly link structural context to functional outcomes and highlight patterns surrounding the active site and substrate interfaces.

I would also encourage the authors to generate a heatmap of the data represented in Figure 2 (see Fowler and Fields 2014 PMID 25075907, Figure 2), this would be more helpful reference to the readers.

The reviewer also suggested that a heatmap representation, similar to that used in Fowler and Fields (2014), might aid interpretation of the data shown in Figure 2. Because our dataset consists of sparse single-amino acid substitutions rather than a complete mutational scan, such heatmaps are inherently less dense and less effective at conveying patterns than in saturation mutagenesis studies. Nevertheless, to aid readers who may find this visualization useful, we have generated and included a single-nucleotide variant heatmap as Supplemental Figure S1.

My major comments are as follows: 6. Citations needed - especially in the introduction and for establishing that hASS is a homolog of yARG1

We have added the requested citations and clarified the ASS1-ARG1 orthology in the Introduction, as described in our response to point 3 above.

1. Generally, the authors do a nice job distinguishing the ASS1 gene from the ASS enzyme, though I found some ambiguities (Line 685). Please double-check the use of each throughout the manuscript.

We have edited the manuscript to ensure consistent and unambiguous use of gene and enzyme nomenclature throughout.

1. Generally, I'm confused about what strain was used for integrating all these variants, was is the arg1 knock-out strain from the yeast knockout collection or was it FY4? I think FY4 was used for the preliminary experiments, then the KO collection strain was used for making the variant library but I think this could be made more clear in the text and figures. Lines 226-229 describes introducing the hASS1 and yASS1 sequences into the native ARG1 locus in strain FY4, but the Fig1A image depicts the ASS1 variants going into arg1 KO locus. Fig1A should be moved to Fig2.

We agree that the strain construction steps were not described as clearly as they could have been. We have therefore clarified the strain construction workflow in the Materials & Methods and Results sections, as well as in the Figure 1 legend, to explicitly distinguish preliminary experiments performed in strain FY4 from construction of the variant library in the arg1 knockout background.

As we have also added an additional panel to Figure 1 that schematically explains how the screen was performed (per Reviewer #2's request), we believe that Figure 1A is appropriately placed and should remain in Figure 1.

1. Line 303 - "We classify these variants as 'functionally unimpaired'", this is not an accurate description of these variants as Figure 2 highlights 24 pathogenic ClinVar variants that would fall into this category of "functionally unimpaired". The yeast growth assay appears to capture pathogenic variants, but there is likely some nuance of human ASS functionality that is not being assessed here. I would make the language more specific, e.g. "complementary to Arg1" or "growth-compatible".

We agree that the label "functionally unimpaired" could be misinterpreted if read as implying clinical benignity. We have therefore clarified within the manuscript that this designation refers strictly to variant behavior in the yeast growth assay (i.e., wild-type-like growth under assay conditions) and does not imply absence of pathogenicity. We also expanded the Discussion to explicitly address the subset of clinically pathogenic variants with high growth scores (>0.85), consistent with a ceiling effect of the assay and a key limitation for interpretation. See response to reviewer #3 point 1. Relevant revisions are also discussed in our responses to Reviewers #1 and #2.

1. Lines 345-355 - It is interesting that there are variants that appear functional at the substrate interfacing sites. Is there anything common across these variants? Are they maintaining the polarity or hydrophobicity of the WT residue? Are any of these variants included in ClinVar or gnomAD? Are pathogenic variants found at any of these sites

Yes. For highly sensitive active-site residues that have few permissible variants, the vast majority of amino acid substitutions that do retain activity preserve key physicochemical properties of the wild-type residue, such as hydrophobicity or charge. We have added this important observation to the manuscript:

"Any variants at these sensitive residues that are permissive for activity in our assay retain hydrophobicity or charged states relative to the original amino acid side chain (Figure 5A & Table S5)."

None of these variants are present in ClinVar. Only L15V and E191D are present in gnomAD (Table S4).

1. Lines 423-430 - The OddsPath calculation would seem to rely heavily on the thresholds of .85 for normalized growth. The OddsPath calculation could be bolstered with some additional analysis that emphasizes the robustness to alternative thresholds.

We agree that the sensitivity of the OddsPath calculation to the choice of growth thresholds is an important consideration. In our assay, benign ClinVar variants and non-human primate variants are observed exclusively within the peak centered on wild-type growth, whereas clinically annotated variants falling below this peak are exclusively pathogenic. On this basis, we defined the upper boundary of the assay range interpreted as supporting pathogenicity as the lower boundary of the wild-type-centered peak in the growth distribution (as defined in Figure 3), rather than selecting a cutoff by direct optimization of the OddsPath. This choice reflects the observed concordance, in our dataset, between the onset of measurable functional impairment in the assay and clinical pathogenic annotation. Importantly, in practice the OddsPath value is locally robust to the precise placement of this boundary, remaining invariant across the range 0.82-0.88. Supporting our chosen threshold of 0.85, the lowest-growth benign or primate variant observed has a normalized growth value of 0.88, while the lowest growth observed among variants present as homozygotes in gnomAD was 0.86. We have clarified this rationale and analysis in the revised manuscript.

"Notably, the "Among all nine of the human ASS1 missense variants observed as homozygotes in gnomAD which were tested as amino acid substitutions in our assay, the lowest observed growth value was 0.86 (Ala258Val) consistent with the lower boundary of the PrimateAI variants which was a growth value of 0.87 (Ala81Thr) (Figure 6) and with our use of a 0.85 classification threshold."

"If we treat PrimateAI variants as benign (solely for OddsPath calculation purposes), the OddsPath for growth

1. Lines 432-441 - This is an interesting idea to use variants observed in primates, has ACMG weighed in on this? I understand that CTLN1 is an autosomal recessive disorder but I'd still be interested in seeing how the observed ASS1 missense variants in gnomAD perform in your growth assay, possibly a supplemental figure?

To our knowledge, the ACMG/AMP guidelines do not currently address the use of homozygous missense variants observed in non-human primates. We are currently in discussion with two ClinGen working groups to discuss the possibility of formalizing the use of this data source.

We agree that comparison with human population data is also important. Accordingly, total gnomAD allele counts and homozygous counts for all applicable ASS1 missense variants are provided in Table S4, and the growth behavior of ASS1 missense variants observed in the homozygous state in gnomAD is shown in Figure 6. These homozygous variants uniformly exhibit high growth in our assay, consistent with the absence of strong loss-of-function effects. We have updated the manuscript text to clarify these points.

Minor comments 1. Lines 53-59 - This paragraph needs to cite the literature, especially lines 56, 57, and 59 2. Line 61 - no need to repeat "citrullinemia type I", just use the abbreviation as it was introduced in the paragraph above 3. Lines 61-71 - again, this paragraph needs more literature citations 4. Line 62 - change to "results"

The changes suggested in points 1-4 have all been implemented in the revised manuscript.

1. Line 74-75 - "RUSP" acronym not needed as it's never used in the manuscript, the same goes for "HHS"

We agree that the acronyms "RUSP" and "HHS" are not reused elsewhere in the manuscript. We have nevertheless retained them at first mention, alongside the expanded names, because these acronyms are commonly used in newborn screening and public health policy contexts and may be more familiar to some readers than the expanded terms. We would be happy to remove the acronyms if preferred.

1. Line 86 - "ASS1" I think is referring to the enzyme and should just be "ASS"? If referring to the gene then italicize to "ASS1"
2. Lines 91-93 - It would be helpful to mention this is a functional screen in yeast
3. Line 101 - It would be helpful to the readers to define SD before using the acronym, consider changing to "minimal synthetic defined (SD) medium" and afterwards can refer to as "SD medium"
4. 109-114 - It would be great if you could share your method for designing the codon-harmonized yASS1 gene, consider sharing as a supplemental script or creating a GitHub repository linked to a Zenodo DOI for publication.

The changes suggested in points 6-9 have all been implemented in the revised manuscript. The codon harmonization script has been provided as File S1.

1. Lines 135-137 - I think it's helpful to provide a full table of the cassettes ordered from Twist as well as the primers used to amplify them, consider a supplemental table.

Details of Twist cassette and the primer sequences used for amplification have been added to the Materials & Methods.

1. Line 138 - "standard methods" is a bit vague, I'm guessing this is a Geitz and Schiestl 2007 LiAc/ssDNA protocol (PMID 17401334)? Also, was ClonNAT used to select for natMX colonies?

The reviewer is correct about which protocol was used, and we have added the citation. We have also clarified that selection was carried out based on resistance to nourseothricin.

1. Line 150 - change to "sequence the entire open reading frame, as previously described [4]."
2. Line 222-223 - remove "replace" and just use "complement" (and remove the parenthesis)
3. Line 249 - It would be great to see a supplemental alignment of the hASS1 and yASS1 sequences.
4. Line 261 - spelling "citrullemia" should be corrected to "citrullinemia"
5. Line 280 - "using Oxford Nanopore sequencing" is a bit vague, I suggest specifying the equipment used (e.g. Oxford Nanopore Technologies MinION platform) or simplify to "via long-read sequencing (see Materials & Methods)"

The changes suggested in points 12-16 have all been implemented in the revised manuscript. An alignment of the ASS and Arg1 protein sequences has been provided as File S2.

1. Line 287-289 - It would be great to see the average number of isolates per variant, as well as a plot of the variant growth estimate vs individual isolate growth.

We agree with the reviewer that conveying measurement precision is important. The number of isolates assayed per variant is provided in Table S4, and we have added explicit mention of this in the text. Because variants were assayed with a mixture of 1, 2, or {greater than or equal to}3 independent isolates, a scatterplot of variant-level growth estimates versus individual isolate measurements would be difficult to interpret and potentially misleading. Instead, we report standard error estimates for each variant in Table S4, derived from the linear model used to estimate growth effects, which more appropriately summarizes measurement uncertainty given the experimental design.

1. Lines 324-25 - consider removing the last sentence of this paragraph, it is redundant as the following paragraph starts with the same statement.

We have removed this sentence.

1. Lines 327-335 - This is interesting and would benefit from its own subpanel or plot in which the normalized growth score is plotted against variants that are at conserved or diverse residues in human ASS, and see if there's a statistical difference in score between the two groupings.

As suggested by the reviewer, we have added Supplemental Figure 2 (Figure S2) in which the normalized growth score of each variant is plotted against the conservation of the corresponding residue, as measured by ConSurf. The manuscript already includes a statistical analysis of the relationship between residue conservation and functional impact, showing that amorphic variants occur significantly more frequently at highly conserved residues than unimpaired variants do (one-sided Fisher's exact test). We now refer to this new supplemental figure in the relevant Results section.

1. Lines 339-341 - As written, it is unclear if aspartate interacts with all of the same residues as citrulline or just Asn123 and Thr119.
2. Lines 345-355 - As with my above comment, I find this interesting and would
3. Line 353 - add a period to "al" in "Diez-Fernandex et al."

The issues raised in points 20 and 22 have all addressed. Point 21 appears to be truncated.

1. Figure 1 a. Remove "Figure" from the subpanels and show just "A" and "B" (as you do for Figure 4) and combine the two images into a single image. Also make this correction to Figure 5 and Figure 8. b. Panel A - I thought the hASS1 and yASS1 were dropped into FY4, not the arg1 KO strain. This needs clarification. c. Panel A - I'm assuming the natMX cassette contains its own promoter, you could use a right-angled arrow to indicate where the promotors are in your construct. d. Panel B - I'm not sure the bar graph is necessary, it would be more helpful to see calculations of the colony size (or growth curves for each strain) and plot the raw values (maybe pixel counts?) for each replicate rather than normalizing to yeast ARG1. I would be great to have a supplemental figure showing all the replicates side-by-side. e. Panel B - Would be helpful to denote the pathogenic and benign ClinVar variants with an icon or colored text.

f. Figure 1 Caption - make "A)" and "B)" bold.

We have implemented the requested changes in Figure 1 with the following exceptions. We have retained panels A and B as separate subfigures because they illustrate distinct experimental concepts. In addition, we respectfully disagree with point (d). The bar graph is intended to provide a clear, high-level comparison of functional complementation by hASS1 versus yASS1 and to illustrate the gross differences in growth between benign and pathogenic proof-of-principle variants. As the bar graph includes error bars for standard deviations, presenting raw colony size measurements or growth curves for individual replicates would substantially complicate the figure without materially improving interpretability for this purpose.

1. Figure 2 a. "Shown in magenta are amino acid substitutions corresponding to ClinVar pathogenic, pathogenic/likely pathogenic, and likely pathogenic variants" is repeated in the figure caption. b. "Shown in green are amino acid substitutions corresponding to ClinVar benign and likely benign variants." I don't see any green points. c. Identify the colors used for ASS1 substrate binding residues. d. This plot would benefit from a depiction of the human ASS secondary structure and any protein domains (nucleotide-binding domain, synthase domain, and C-terminal helix from Fig4B)

e. Line 685 675 - "ASS1" is being used in reference to the enzyme, is this correct or should it be "ASS"?

We have made the requested changes to Figure 2. The repeated caption text has been removed, and references to green points have been corrected to orange points to match the figure. The colors used to indicate ASS substrate-binding residues are explicitly described in the figure key. Secondary structure annotations have been added. References to the enzyme have been corrected to "ASS" rather than "ASS1" where appropriate.

1. Figure 3 a. Rename the "unimpaired" category as there are several pathogenic ClinVar variants that fall into this category.

To address this point, we have clarified the labeling by adding "in our yeast assay" to the figure legend, making explicit that the "unimpaired" category refers only to wild-type-like behavior under assay conditions and does not imply clinical benignity. See also response to Reviewer #3, Major Comment 1.

1. Figure 4 a. List the PDB or AlphaFold accession used for this structure b. Panel A - state which colors are used for to depict each monomer. It is confusing to see several shades of pink/purple used to depict a single monomer in Panel A. c. It is very difficult to make out the aspartate and citrulline substrates in the catalytic binding activity, consider making an inset zooming-in on this domain and displaying a ribbon diagram of the structure rather than the surface. d. Generally, it would be more helpful here to label any particular residues that were identified as pathogenic from your screen, or to overlay average grow scores per residue data onto the structure

We have implemented the requested changes to Figure 4. The relevant PDB/AlphaFold accession is now listed, and the colors used to depict each monomer in Panel A are clarified in the figure legend. An inset focusing on the active site has been added to improve visualization of the citrulline and aspartate substrates. In addition, we have added new panels (Figure 4C and 4D) overlaying pathogenic residues and average growth scores onto the structure to more directly link structural context with functional data.

1. Figure 5 a. Line 716 - Insert a page break to place Figure 5 on its own page b. I suggest using a heatmap for this type of plot, as it is very difficult to track which color corresponds to which residue.

c. Fig5A - This plot could be improved by identifying which residue positions interface with which substrate.

We have placed Figure 5 on its own page and added information to the legend identifying which residue positions interface with each substrate. We have retained the active-site variant strip charts raised in point (b), as we believe they effectively illustrate how the distribution of variant effects differs between residues. In addition, we have provided a supplemental heatmap showing variant growth across the entire protein (Figure S1), and individual variant scores for all residues are provided in Table S4.

1. Figure 7 a. Line 735 - Insert page break to place figure on a new page

List the PDB accession used for these images. c. For clarity I would mention "human ASS" in the figure title d. State the colors of the substrates e. Panels A and B could be combined into a single panel, making it easier to distinguish the active site and dimerization variants.

f. Could be interesting to get SASA scores for the ClinVar structural variants to determine if they are surface-accessible

We have implemented the requested changes in Figure 7 with the following exceptions. For point (e), there is no single orientation of the structure that allows a clear simultaneous view of both active-site and dimerization variants; accordingly, we have retained panels A and B as separate subfigures to preserve clarity. With respect to point (f), we agree that solvent accessibility analysis could be informative in other contexts. However, such an analysis does not integrate naturally with the functional and assay-based framework of the present study and was therefore not included.

1. Figure 8 a. Panel B - overlay a square frame in the larger protein structure that depicts where the below inset is focused, and frame inset image as well.

We have framed the inset image as requested. We did not add a corresponding frame to the full protein structure, as doing so obscured structural details in the region of interest.

Reviewer #3 (Significance (Required)):

Section 2 - Significance This study represents a substantial technical, functional, and translational advance in the interpretation of missense variation in ASS1, a gene of high clinical relevance for the rare disease citrullinemia type I. Its principal strength lies in the generation of an experimentally validated functional atlas of ASS1 missense variants that covers ~90% of all SNV-accessible substitutions. The scale, internal reproducibility, and careful benchmarking of the yeast complementation assay against known pathogenic and benign variants provide a robust foundation for identifying pathogenic ASS1 variants. Particularly strong aspects include the rigorous quality control of variant identities, the quantitative nature of the functional readout, and the thoughtful integration of results into the ACMG/AMP OddsPath framework. The discovery of intragenic complementation between variants affecting distinct structural regions of the enzyme is a notable conceptual and mechanistic contribution. Limitations include the assay's reduced sensitivity to variants impacting oligomerization or subtle folding defects, and the use of yeast as a heterologous system, which may mask disease-relevant mechanisms as several pathogenic ClinVar variants were found to be "functionally unimpaired". Future work extending functional testing to additional cellular contexts or expanding genotype-level combinatorial analyses would further enhance clinical applicability. Relative to prior studies, which have relied on small numbers of patient-derived variants or low-throughput biochemical assays, this work extends the field decisively by delivering a comprehensive, variant-resolved functional map for ASS1. To the best of my current knowledge, this is the first systematic functional screen of ASS1 at this scale and the first direct experimental demonstration that ASS active sites span multiple subunits, enabling intragenic complementation consistent with Crick and Orgel's classic variant sequestration model. As such, the advance is simultaneously technical (high-throughput functional genomics), mechanistic (defining structural contributors to catalysis and epistasis), and clinical (enabling evidence-based reclassification of VUS). I find the use of homozygous non-human primate variants as an orthogonal benign calibration set both creative and controversial, my hope would be that this manuscript will prompt a productive discussion.

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript presents a comprehensive functional profiling of 2,193 ASS1 missense variants using a yeast complementation assay, providing valuable data for variant interpretation in the rare disease citrullinemia type I. The dataset is extensive, technically sound, and clinically relevant. The demonstration of intragenic complementation in ASS1 is novel and conceptually important. Overall, the study represents a substantial contribution to functional genomics and rare disease variant interpretation.

Major comments

This is an exciting paper as it can provide support to clinicians to make actionable decisions when diagnosing infants. I have a few major comments, but I want to emphasize the label of "functionally unimpaired" variants to be misleading. The authors explain that there are several pathogenic ClinVar variants that fall into this category (above the >.85 growth threshold) but I think this category needs a more specific name and I would ask the authors to reiterate the shortcomings of the assay again in the Discussion section. I think there's an important discussion to be had here, is the assay detecting variants that alter the function of ASS or is it detecting a complete ablation of enzymatic activity? The results might be strengthened with a follow-up experiment that identifies stably expressed ASS1 variants. At the very least, it would be great to see the authors replicate some of their interesting results from the high-throughput screen by down-selecting to ~12 variants of uncertain significance that could be newly considered pathogenic. I would ask the authors to provide more citations of the literature in the introduction of the manuscript. I would be especially interested in knowing more about human ASS being identified as a homolog of yeast ARG1, as they share little sequence similarity (27.5%) at the protein level. That said, I find the yeast complementation assay exciting. I appreciate the efforts made by the authors to share their work and make this study more reproducible, such as sharing the hASS1 and yASS1 plasmids being shared on NCBI Genbank (Line 121) and publishing the ONT reads on SRA (Line 154). I made a requests for additional data to be shared, such as the custom method/code for codon optimization and a table of Twist variant cassettes that were ordered. I would also love to see these results shared on MaveDB.org. I find this manuscript very exciting as the authors have a compelling assay that identifies pathogenic variants, but I was generally disappointed by the quality and organization of the figures. For example, Figure 4 provides very little insight, but could be dramatically improved with an overlay of the normalized growth score data or highlighting variants surrounding the substrate or ATP interfaces. There are some very interesting aspects of this manuscript that could be shine through with some polished figures. I would also encourage the authors to generate a heatmap of the data represented in Figure 2 (see Fowler and Fields 2014 PMID 25075907, Figure 2), this would be more helpful reference to the readers.

My major comments are as follows:

1. Citations needed - especially in the introduction and for establishing that hASS is a homolog of yARG1
2. Generally, the authors do a nice job distinguishing the ASS1 gene from the ASS enzyme, though I found some ambiguities (Line 685). Please double-check the use of each throughout the manuscript
3. Generally, I'm confused about what strain was used for integrating all these variants, was is the arg1 knock-out strain from the yeast knockout collection or was it FY4? I think FY4 was used for the preliminary experiments, then the KO collection strain was used for making the variant library but I think this could be made more clear in the text and figures. Lines 226-229 describes introducing the hASS1 and yASS1 sequences into the native ARG1 locus in strain FY4, but the Fig1A image depicts the ASS1 variants going into arg1 KO locus. Fig1A should be moved to Fig2.
4. Line 303 - "We classify these variants as 'functionally unimpaired'", this is not an accurate description of these variants as Figure 2 highlights 24 pathogenic ClinVar variants that would fall into this category of "functionally unimpaired". The yeast growth assay appears to capture pathogenic variants, but there is likely some nuance of human ASS functionality that is not being assessed here. I would make the language more specific, e.g. "complementary to Arg1" or "growth-compatible".
5. Lines 345-355 - It is interesting that there are variants that appear functional at the substrate interfacing sites. Is there anything common across these variants? Are they maintaining the polarity or hydrophobicity of the WT residue? Are any of these variants included in ClinVar or gnomAD? Are pathogenic variants found at any of these sites
6. Lines 423-430 - The OddsPath calculation would seem to rely heavily on the thresholds of <.05 and >.85 for normalized growth. The OddsPath calculation could be bolstered with some additional analysis that emphasizes the robustness to alternative thresholds.
7. Lines 432-441 - This is an interesting idea to use variants observed in primates, has ACMG weighed in on this? I understand that CTLN1 is an autosomal recessive disorder but I'd still be interested in seeing how the observed ASS1 missense variants in gnomAD perform in your growth assay, possibly a supplemental figure?

Minor comments

1. Lines 53-59 - This paragraph needs to cite the literature, especially lines 56, 57, and 59
2. Line 61 - no need to repeat "citrullinemia type I", just use the abbreviation as it was introduced in the paragraph above
3. Lines 61-71 - again, this paragraph needs more literature citations
4. Line 62 - change to "results"
5. Line 74-75 - "RUSP" acronym not needed as it's never used in the manuscript, the same goes for "HHS"
6. Line 86 - "ASS1" I think is referring to the enzyme and should just be "ASS"? If referring to the gene then italicize to "ASS1"
7. Lines 91-93 - It would be helpful to mention this is a functional screen in yeast
8. Line 101 - It would be helpful to the readers to define SD before using the acronym, consider changing to "minimal synthetic defined (SD) medium" and afterwards can refer to as "SD medium"
9. 109-114 - It would be great if you could share your method for designing the codon-harmonized yASS1 gene, consider sharing as a supplemental script or creating a GitHub repository linked to a Zenodo DOI for publication.
10. Lines 135-137 - I think it's helpful to provide a full table of the cassettes ordered from Twist as well as the primers used to amplify them, consider a supplemental table
11. Line 138 - "standard methods" is a bit vague, I'm guessing this is a Geitz and Schiestl 2007 LiAc/ssDNA protocol (PMID 17401334)? Also, was ClonNAT used to select for natMX colonies?
12. Line 150 - change to "sequence the entire open reading frame, as previously described [4]."
13. Line 222-223 - remove "replace" and just use "complement" (and remove the parenthesis)
14. Line 249 - It would be great to see a supplemental alignment of the hASS1 and yASS1 sequences
15. Line 261 - spelling "citrullemia" should be corrected to "citrullinemia"
16. Line 280 - "using Oxford Nanopore sequencing" is a bit vague, I suggest specifying the equipment used (e.g. Oxford Nanopore Technologies MinION platform) or simplify to "via long-read sequencing (see Materials & Methods)"
17. Line 287-289 - It would be great to see the average number of isolates per variant, as well as a plot of the variant growth estimate vs individual isolate growth
18. Lines 324-25 - consider removing the last sentence of this paragraph, it is redundant as the following paragraph starts with the same statement
19. Lines 327-335 - This is interesting and would benefit from its own subpanel or plot in which the normalized growth score is plotted against variants that are at conserved or diverse residues in human ASS, and see if there's a statistical difference in score between the two groupings
20. Lines 339-341 - As written, it is unclear if aspartate interacts with all of the same residues as citrulline or just Asn123 and Thr119.
21. Lines 345-355 - As with my above comment, I find this interesting and would
22. Line 353 - add a period to "al" in "Diez-Fernandex et al."
23. Figure 1

a. Remove "Figure" from the subpanels and show just "A" and "B" (as you do for Figure 4) and combine the two images into a single image. Also make this correction to Figure 5 and Figure 8

b. Panel A - I thought the hASS1 and yASS1 were dropped into FY4, not the arg1 KO strain. This needs clarification

c. Panel A - I'm assuming the natMX cassette contains its own promoter, you could use a right-angled arrow to indicate where the promotors are in your construct

d. Panel B - I'm not sure the bar graph is necessary, it would be more helpful to see calculations of the colony size (or growth curves for each strain) and plot the raw values (maybe pixel counts?) for each replicate rather than normalizing to yeast ARG1. I would be great to have a supplemental figure showing all the replicates side-by-side

e. Panel B - Would be helpful to denote the pathogenic and benign ClinVar variants with an icon or colored text

f. Figure 1 Caption - make "A)" and "B)" bold 24. Figure 2

a. "Shown in magenta are amino acid substitutions corresponding to ClinVar pathogenic, pathogenic/likely pathogenic, and likely pathogenic variants" is repeated in the figure caption

b. "Shown in green are amino acid substitutions corresponding to ClinVar benign and likely benign variants." I don't see any green points

c. Identify the colors used for ASS1 substrate binding residues

d. This plot would benefit from a depiction of the human ASS secondary structure and any protein domains (nucleotide-binding domain, synthase domain, and C-terminal helix from Fig4B)

e. Line 685 - "ASS1" is being used in reference to the enzyme, is this correct or should it be "ASS"? 25. Figure 3

a. Rename the "unimpaired" category as there are several pathogenic ClinVar variants that fall into this category 26. Figure 4

a. List the PDB or AlphaFold accession used for this structure

b. Panel A - state which colors are used for to depict each monomer. It is confusing to see several shades of pink/purple used to depict a single monomer in Panel A

c. It is very difficult to make out the aspartate and citrulline substrates in the catalytic binding activity, consider making an inset zooming-in on this domain and displaying a ribbon diagram of the structure rather than the surface.

d. Generally, it would be more helpful here to label any particular residues that were identified as pathogenic from your screen, or to overlay average grow scores per residue data onto the structure 27. Figure 5

a. Line 716 - Insert a page break to place Figure 5 on its own page

b. I suggest using a heatmap for this type of plot, as it is very difficult to track which color corresponds to which residue

c. Fig5A - This plot could be improved by identifying which residue positions interface with which substrate 28. Figure 7

a. Line 735 - Insert page break to place figure on a new page

b. List the PDB accession used for these images

c. For clarity I would mention "human ASS" in the figure title

d. State the colors of the substrates

e. Panels A and B could be combined into a single panel, making it easier to distinguish the active site and dimerization variants

f. Could be interesting to get SASA scores for the ClinVar structural variants to determine if they are surface-accessible 29. Figure 8

a. Panel B - overlay a square frame in the larger protein structure that depicts where the below inset is focused, and frame inset image as well.

Significance

This study represents a substantial technical, functional, and translational advance in the interpretation of missense variation in ASS1, a gene of high clinical relevance for the rare disease citrullinemia type I. Its principal strength lies in the generation of an experimentally validated functional atlas of ASS1 missense variants that covers ~90% of all SNV-accessible substitutions. The scale, internal reproducibility, and careful benchmarking of the yeast complementation assay against known pathogenic and benign variants provide a robust foundation for identifying pathogenic ASS1 variants. Particularly strong aspects include the rigorous quality control of variant identities, the quantitative nature of the functional readout, and the thoughtful integration of results into the ACMG/AMP OddsPath framework. The discovery of intragenic complementation between variants affecting distinct structural regions of the enzyme is a notable conceptual and mechanistic contribution. Limitations include the assay's reduced sensitivity to variants impacting oligomerization or subtle folding defects, and the use of yeast as a heterologous system, which may mask disease-relevant mechanisms as several pathogenic ClinVar variants were found to be "functionally unimpaired". Future work extending functional testing to additional cellular contexts or expanding genotype-level combinatorial analyses would further enhance clinical applicability.

Relative to prior studies, which have relied on small numbers of patient-derived variants or low-throughput biochemical assays, this work extends the field decisively by delivering a comprehensive, variant-resolved functional map for ASS1. To the best of my current knowledge, this is the first systematic functional screen of ASS1 at this scale and the first direct experimental demonstration that ASS active sites span multiple subunits, enabling intragenic complementation consistent with Crick and Orgel's classic variant sequestration model. As such, the advance is simultaneously technical (high-throughput functional genomics), mechanistic (defining structural contributors to catalysis and epistasis), and clinical (enabling evidence-based reclassification of VUS). I find the use of homozygous non-human primate variants as an orthogonal benign calibration set both creative and controversial, my hope would be that this manuscript will prompt a productive discussion.

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Lo et al characterize the phenotypic effect of ~90% of all possible ASS1 missense mutations using an elegant yeast-based system, and use this dataset to aid the interpretation of clinical ASS1 variants. Overall, the manuscript is well-written and the experimental data are interpretated rigorously. Of particular interest is the identification of pairs of deleterious alleles that rescue ASS1 activity in trans. My comments mainly pertain to the relevance of using a yeast screening methodology to infer functional effects of human ASS1 mutations.

• Since human ASS1 is heterologously expressed in yeast for this mutational screen, direct comparison of native expression levels between human cells and yeast is not possible. Could the expression level of human ASS1 (driven by the pARG1 promoter) in yeast alter the measured fitness defect of each variant? For instance, if ASS1 expression in yeast is sufficiently high to mask modest reductions in catalytic activity, such variants may be misclassified as hypomorphic rather than amorphic. Conversely, if expression is intrinsically low, even mild catalytic impairments could appear deleterious. While it is helpful that the authors used non-human primate SNV data to calibrate their assay, experiments could be performed to directly address this possibility.
• The nature of the relationship between yeast growth and availability of functional ASS1 could also influence the interpretation of results from the yeast-based screen. Does yeast growth scale proportionately with ASS1 enzymatic activity?
• It would be helpful to add an additional diagram to Figure 1A explaining how the screen was performed, in particular: when genotype and phenotype were measured, relative to plating on selective vs non-selective media? This is described in "Variant library sequence confirmation" and "Measuring the growth of individual isolates" of the Methods section but could also be distilled into a diagram.
• The authors rationalize the biochemical consequences of ASS1 mutations in the context of ASS1 per se - for example, mutations in the active site pocket impair substrate binding and therefore catalytic activity, which is expected. Does ASS1 physically interact with other proteins in human cells, and could these interactions be altered in the presence of specific ASS1 mutations? Such effects may not be captured by performing mutational scanning in yeast.
• The authors note that only a small number (2/11) of mutations at the ASS1 monomer-monomer interface lead to growth defects in yeast. It would be helpful for the authors to discuss this further.

Significance

This study presents the first comprehensive mutational profiling of human ASS1 and would be of broad interest to clinical geneticists as well as those seeking biochemical insights into the enzymology of ASS1. The authors' use of a yeast system to profile human mutations would be particularly useful for researchers performing deep mutational scans, given that it provides functional insights in a rapid and inexpensive manner.

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Referee #1

Evidence, reproducibility and clarity

Lo et al., report a high-throughput functional profiling study on the gene encoding for argininosuccinate synthase (ASS1), done in a yeast experimental system. The study design is robust (see lines 141-143, main text, Methods), whereby "approximately three to four independent transformants of each variant would be isolated and assayed." (lines 140 - 141, main text, Methods). Such a manner of analysis will allow for uncertainty of the functional readout for the tested variants to be accounted for.

This is an outstanding study providing insights on the functional landscape of ASS1. Functionally impaired ASS1 may cause citrullinemia type I, and disease severity varies according to the degree of enzyme impairment (line 30, main text; Abstract). Data from this study forms a valuable resource in allowing for functional interpretation of protein-altering ASS1 variants that could be newly identified from large-scale whole-genome sequencing efforts done in biobanks or national precision medicine programs. I have some suggestions for the Authors to consider:

1. The specific function of ASS1 is to condense L-citrulline and L-aspartate to form argininosuccinate. Instead of measuring either depletion of substrate or formation of product, the Authors elected to study 'growth' of the yeast cells. This is a broader phenotype which could be determined by other factors outside of ASS1. Whereas i agree that the experiments were beautifully done, the selection of an indirect phenotype such as ability of the yeast cells to grow could be more vigorously discussed.
2. One of the key reasons why studies such as this one are valuable is due to the limitations of current variant classification methods that rely on 'conservation' status of amino acid residues to predict which variants might be 'pathogenic' and which variants might be 'likely benign'. However, there are serious limitations, and Figures 2 and 6 in the main text shows this clearly. Specifically, there is an appreciable number of variants that, despite being classified as "ClinVar Pathogenic", were shown by the assay to unlikely be functionally impaired. This should be discussed vigorously. Could these inconsistencies be potentially due to the read out (growth instead of a more direct evaluation of ASS1 function)?
3. Figure 3 is very interesting, showing a continuum of functional readout ranging from 'wild-type' to 'null'. It is very interesting that the Authors used a threshold of less than 0.85 as functionally hypomorphic. What does this mean? It would be very nice if they have data from patients carrying two hypomorphic ASS1 alleles, and correlate their functional readout with severity of clinical presentation. The reader might be curious as to the clinical presentation of individuals carrying, for example, two ASS1 alleles with normalized growth of 0.7 to 0.8.

I hope you will find these suggestions helpful.

Significance

This is an outstanding study providing insights on the functional landscape of ASS1. Functionally impaired ASS1 may cause citrullinemia type I, and disease severity varies according to the degree of enzyme impairment (line 30, main text; Abstract). Data from this study forms a valuable resource in allowing for functional interpretation of protein-altering ASS1 variants that could be newly identified from large-scale whole-genome sequencing efforts done in biobanks or national precision medicine programs.