It might be early to fully come to a conclusion but we will eventually get one over the years to come and academic integrity of students.

can make you really smart but there are people that dont rely on it at all and still come up with amazing arguments/ papers

I think how it should be, what if your good at one thing but lack in another skill? If you use A.I its going to correct everything and make you believe you are doing it wrong.

they could come up with anything that pops up in their search result and generate content that can be totally false.

another part about what's talked about in this article but in better depth

it may help them, but it won't teach them.

"Studies from the SANRA found A.I to be destructive towards the development of students writing abilities. But can be beneficial if used correctly and sparingly." (Ab)

AI systems often ignore many languages, especially those spoken by Indigenous and minority groups. English is everywhere online, but lots of other languages barely show up. This makes it hard for people who speak these languages to access information and can cause their languages to fade away.

Potentially AI can be a fantastic booster for creativity, but we need to be mindful of how it might centralize power and potentially limit the rich tapestry of human expression.

Some projects, like Papa Reo in New Zealand, are working to add Indigenous knowledge into AI systems

To me this shows education is not just about passing on knowledge; it also plays a crucial role in shaping how individuals perceive their own cultural identity. Moreover, it enhances their ability to appreciate and interact respectfully with other cultures.

To Taylor the VHS tapes are like a secret world. She ties the horror movies to a connection with her father and they foreshadow themes of this work.

Words have power, but they should be backed the power of truth, not by lies and deceit. That singular truth being that each of us is just as human as the next, if not for the "walls" dividing us in the prior line. He is also specifically utilizing the language, and thus words, of the Empire that oppresses his people as a tool to appeal to them.

Frost uses the natural image of the ladder “sticking through a tree” and reaching “toward heaven” to suggest a spiritual or emotional search, which reflects Romantic ideas about finding meaning through nature. The unfinished apples and the barrel he “didn’t fill” symbolize human imperfection and the limits of personal ambition, an inner reflection that Romantic writers valued. His choice to stop apple-picking shows a moment of emotional awareness and self-understanding shaped by his experience in the natural world.

Reason, Nature, and Truth, personified, bring the what the speaker would like to avoid. They bring pain, suffering, and complaining. While imagination brings flowers, associated with happiness, but they are trampled by Truth, bringing our speaker to face their melancholy.

Our speaker is "othered" in these lines. She indicates how she is treated unfairly, but imagination allows her to live her life in peace. We can see how Brontë is reflected in this, a she is often referred to as "reclusive" and "solitary," contributing to the idea that she is more than likely part of the queer community. As Claire O'Callaghan states in her essay about Brontë, "Emily's reserve- ... does not correspond with typical gender norms and implies subversion."

Bronte continues contrast the reality with the one speaker brings to life with the spirit of imagination with light and dark imagery. As the world around her is filled with "danger, and guilt, and darkness" she is able to keep in her "bosom" or heart a "bright, untroubled sky," where the readers can feel warmth versus the coldness that reality holds.

Technique is nothing without inspiration.

Indigenous approaches to organizing knowledge remain underrepresented in mainstream LIS scholarship. This also implicitly situates projects like AIATSIS or Māori Subject Headings as important but not fully transferable models, reinforcing the urgency for North American frameworks grounded in local cultural contexts.

the same as how the husband was killed.

downplaying and demeaning but this ultimately leads to the discovery of evidence.

foreshadow. eluding to the end.

more great evidence showing that AI tools help with childhood literacy development. again it feels like the biggest strength is having a teacher be able to identify student weaknesses faster. it feels like it gives the instructors more reach in the amount of students they can handle and not only helping but improve student literacy development.

We need guardrails on ChatGPT.

saying common ppl are dumb and can be manipulated

proof that common people were not afraid of witches

Textbook source, not journal paper. Good but maybe could add peer reviewed citation. https://pubmed.ncbi.nlm.nih.gov/38649721/

He keep asking for respect, but nobody listens to him. People ignore him and act like he doesn’t exist, which shows how lonely and powerless he feels.

Corliss loves her mother, but her mother often tells lies or exaggerates because of her bipolar disorder. Since these stories usually make Corliss look good, she can’t really hate them.

Once again, studies reveal that bilingual children are performing the same as monolingual children.

AI can write a well structured paper but lacks the knowledge to write a deep understanding of the topic.

AI can make even the most error filled paper sound believable.

If the writing looks well polished but lacks depth or individuality its most likely AI generated.

I wonder if the comparison was accurate with the differing female and male voices.

Tech makes writing easier but also sloppier.

[[Steven Garrity]] coining 'resumability' , where a device just continues on where you were previously. Mentions e-readers as such devices (and paper books with a bookmark), a smartphone and apps like Slack. The latter is not true I think, it scrolls fwd to newest.

Thinking about resumability in terms of notes / pkm. Obsidian is always where I was previously e.g. A type of ratchet for task execution.

Cette partie ........

Provides information but does present it as an invitation.

Quote David Lynch https://en.wikipedia.org/wiki/Catching_the_Big_Fish continued.

Not having a set-up ready when an idea hits means no agency. Mentions festering a type of powerlessness, vgl [[%I Networked Agency]] wrt methods and tools for various things. Also vgl making note of any idea in 3Ideeenkweekkas

David Lynch quoted from https://en.wikipedia.org/wiki/Catching_the_Big_Fish about the necessity of a set-up to have agency and act on an idea.

Source of title Catching the Big Fish. Aside from the meditation angle, this points to practice / reflection, ratchets, and [[Holding questions 20091015123253]] etc.

Bro, how is that? This deflection attempt is so gibberish it's laughable. To be frank, Peta does pick up at games that have little to do with its cause, when they could be, idk, mocking any game that has actual fishing or hunting on it... but the response seems very inmature to me. Perhaps they could have collaborated!

And... there's surprisingly little green food variety. There are cakes but no rice? No legumes? There are no tomatoes!

The second icon, yes, it reminds me of Minecraft hunger bars, which were not represented by energy, but rather by chicken wings.

Not just reading, though, we do things instrumentally, as we are biological machines. Reading is tough, so we scrutinise it severly. Watching TV isn't tough, so the usefulness dilutes and becomes not so present.

Young points out the contradiction: professionals are allowed to use everyday / vernacular language, but students are told they must use “standard English only.” Good evidence for a language + power section.

Example – College writing scholar Kermit Campbell using blended dialect (“fo sho,” “befo”) inside an academic book. This is code meshing in published scholarship and proves that serious academic writing can include home language and still be legitimate.

Young: It’s not the language itself that’s the problem — it’s the attitudes of people in power. Good for explaining how students’ home dialects get treated as defective.

Key term – translanguaging: Here, Alvarez defines translanguaging as the hybrid, flexible ways emergent bilinguals use all their languages together. He frames it as additive (a strength) and says it challenges English-only teaching. This helps my project because it shows how home-language practices aren’t “wrong,” but actually support learning.

Like I said before this a decision between two people as a couple you both need to make decisions together it, they also need to think about their money and how this can affect both of them and their careers. The pros are that the husband is studying more and continuing to grow but a con could be waiting for too long life isnt gonna stop sometimes you need to multitasks you cant stop something for your job once you have a baby your family has to come first.

The issue is that they both work the related issues is that they both want to have a family very soon but one wants to continue their career A requirement in order to solve the issue is to have passion for both you can have a family and continue to study and grow in your career you just have to want to do it

Key source for their critique From this perspective, citizenship is no longer seen as "merely" a status that can be achieved... but it is conceptualized as a "practice"

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Reply to the reviewers

Review report for 'Sterols regulate ciliary membrane dynamics and hedgehog signaling in health and disease', Lamazière et al.

Reviewer #1

In this manuscript, Lamazière et al. address an important understudied aspect of primary cilium biology, namely the sterol composition in the ciliary membrane. It is known that sterols especially play an important role in signal transduction between PTCH1 and SMO, two upstream components of the Hedgehog pathway, at the primary cilium. Moreover, several syndromes linked to cholesterol biosynthesis defects present clinical phenotypes indicative of altered Hh signal transduction. To understand the link between ciliary membrane sterol composition and Hh signal transduction in health and disease, the authors developed a method to isolate primary cilia from MDCK cells and coupled this to quantitative metabolomics. The results were validated using biophysical methods and cellular Hh signaling assays. While this is an interesting study, it is not clear from the presented data how general the findings are: can cilia be isolated from different mammalian cell types using this protocol? Is the sterol composition of MDCK cells expected to the be the same in fibroblasts or other cell types? Without this information, it is difficult to judge whether the conclusions reached in fibroblasts are indeed directly related to the sterol composition detected in MDCK cells. Below is a detailed breakdown of suggested textual changes and experimental validations to strengthen the conclusions of the manuscript.

We would like to thank the reviewer for their helpful comments

Major comments:

• It appears that the comparison has been made between ciliary membranes and the rest of the cell's membranes, which includes many other membranes besides the plasma membrane. This significantly weakens the conclusions on the sterol content specific to the cilium, as it may in fact be highly similar to the rest of the plasma membrane. It is for example known that lathosterol is biosynthesized in the ER, and therefore the non-presence in the cilium may reflect a high abundance in the ER but not necessarily in the plasma membrane.

The reviewer is correct that we compared the sterol composition of the primary ciliary membrane to the average of the remaining cellular membranes. We agree that this broader reference fraction contains multiple intracellular membranes, including ER- and Golgi-derived compartments, and therefore does not isolate the plasma membrane specifically. We would like to emphasize that our study did not aim to compare the cilium directly to the plasma membrane, nor did we claim that the comparison was in any way related to the plasma membrane. It is also worth noting that previous studies in other ciliated organisms have reported a higher cholesterol content in cilia compared to the plasma membrane, suggesting that the two membranes may not be compositionally identical despite their continuity. However, we concur that determining the sterol composition of the MDCK plasma membrane would provide valuable context and enable a comparison with the membrane continuous with the ciliary membrane. Hence, we are willing to try isolating plasma membrane in the same cellular contexts.

• While the protocol to isolate primary cilium from MDCK cells is a valuable addition to the methods available, it would be good to at least include a discussion on its general applicability. Have the authors tried to use this protocol on fibroblasts for example?

Thank you for the reviewer's positive comment on the value of the ciliary isolation protocol. Indeed, we have attempted to apply the same approach to other ciliated cell types, namely IMCD3 and MEF cells. In the case of IMCD3 cells, we were able to isolate primary cilia using the same general strategy; however, we are still refining the preparation, as the overall yield is lower than in MDCK cells and the amount of material obtained is currently insufficient for comprehensive biochemical analyses. With MEF (fibroblast) cells, the procedure proved even more challenging, as the yield of isolated cilia was extremely low. This difficulty is likely due to the shorter length of fibroblast cilia and to their positioning beneath the cell body, which probably makes them more resistant to detachment. Overall, these observations suggest that while the protocol can be adapted to other cell types, its efficiency depends on cellular architecture. We have added a discussion of these aspects in the revised manuscript to clarify the method's current scope and limitations (lines 492-502).

• Some of the conclusions in the introduction (lines 75-80) seem to be incorrectly phrased based on the data: in basal conditions, ciliary membranes are already enriched in cholesterol and desmosterol, and the treatment lowers this in all membranes.

We agree, this was modified in the revised manuscript (lines 75-80).

• There seems to be little effect of simvastatin on overall cholesterol levels. Can the authors comment on this result? How would the membrane fluidity be altered when mimicking simvastatin-induced composition? Since the effect on Hh signaling appears to be the biggest (Figure 5B) under simvastatin treatment, it would be interesting to compare this against that found for AY9944 treatment. Also, the authors conclude that the effects of simvastatin treatment on ciliary membrane sterol composition are the mildest, however, one could argue that they are the strongest as there is a complete lack of desmosterol.

We thank the reviewer for these insightful comments. Regarding the modest overall effect of simvastatin on cholesterol levels, we would like to note that MDCK cells are an immortalized epithelial cell line with high metabolic plasticity. Such cancer-like cell types are known to exhibit enhanced de novo lipogenesis, particularly under culture conditions with ample glucose availability. This compensatory lipid biosynthesis can partially counterbalance pharmacological inhibition of the cholesterol biosynthetic pathway. Because simvastatin acts upstream in the pathway (at HMG-CoA reductase), its inhibition primarily reduces early intermediates rather than fully depleting end-product cholesterol, explaining the relatively mild changes observed in total cholesterol content.

Concerning desmosterol, we agree with the reviewer that its complete loss under simvastatin treatment is a striking finding that deserves further discussion. Interestingly, our data show that simvastatin treatment produces the strongest inhibition of pathway activation (as measured by SMO activation), but the weakest effect on signal transduction downstream of constitutively active SMOM2. This dichotomy suggests that the absence of desmosterol may preferentially affect the activation step of Hedgehog signaling at the ciliary membrane, without equally impacting downstream propagation. We have expanded the Result section to highlight this potential role of desmosterol in the activation phase of Hedgehog signaling and to contrast it with the effects observed under AY9944 treatment (lines 463-469).

It is not clear to me why the authors have chosen to use SAG to activate the Hh pathway, as this is a downstream mode of activation and bypasses PTCH1 (and therefore a potentially sterol-mediated interaction between the two proteins). It would be very informative to compare the effect of sterol modulation on the ability of ShhN vs SAG to activate the pathway.

Our study aims to demonstrate that the sterol composition of the ciliary membrane plays an essential role in the proper functioning of the Hedgehog (Hh) signaling pathway, comparable in importance to that of oxysterols and free cholesterol. Because ShhN itself is covalently modified by cholesterol, and Smoothened (SMO) can be directly activated by both oxysterols and cholesterol, we reasoned that using a non-native SMO agonist such as SAG would allow us to specifically assess defects arising from alterations in membrane-bound sterols. In this way, pathway activation by SAG provides a more direct readout of the functional contribution of ciliary membrane sterols to SMO activity, independent of potential confounding effects related to ShhN processing, secretion, or PTCH1-mediated regulation.

• The conclusions about the effect of tamoxifen on SMO trafficking in MEFs should be validated in human patient cells before being able to conclude that there is a potential off-target effect (line 438). Also, if that is the case, the experiment of tamoxifen treatment of EBP KO cells should give an additional effect on SMO trafficking. Also, could the CDPX2 phenotypes in patients be the result of different cell types being affected than the fibroblast used in this study?

We agree that carrying the proposed experiment would be a good way to assess a potential off-target effect. However, such validation is beyond the scope of the present study, as this comment on off-target effect was aimed primarily to propose a mechanistic hypothesis to explain the differences observed in Hedgehog pathway activation between patient-derived fibroblasts and tamoxifen-treated MEFs. We leaned towards this hypothesis because drug treatments are known for their overall variable specificity, but we agree other hypotheses are possible, and among them the difference in cell type, as both are fibroblasts but from different origin. We rephrased this passage in the revised manuscript (lines 447-448 ).

Regarding the reviewer's third point, we fully agree that the CDPX2 phenotype in patients is unlikely to arise solely from fibroblast dysfunction. Nevertheless, fibroblasts are the only patient-derived cells currently available to us, and they provide a useful model for assessing ciliary signaling. It is reasonable to expect that similar defects could occur in other, more physiologically relevant cell types.

• For the experiments with the SMO-M2 mutant, it would be useful to show the extent of pathway activation by the mutant compared to SAG or ShhN treatment of non-transfected cells. Moreover, it will be necessary to exclude any direct effects of the compound treatment on the ability of this mutant to traffic to the primary cilium, which can easily be done using fluorescence microscopy as the mutant is tagged with mCherry.

The SmoM2 mutant is indeed a well-characterized constitutively active form of Smoothened that has been extensively studied by us and others. It is well established that this mutant correctly localizes to the primary cilium and robustly activates the Hedgehog pathway in MEFs (see Eguether et al., Dev. Cell, 2014 or Eguether et al, mol.biol.cell, 2018). In our study, we have already included supporting evidence for pathway activation in Supplementary Figure S1b, showing Gli1 expression levels in untreated MEFs transfected with SmoM2, which illustrates the extent of its activation compared to ligand-induced conditions.

In line with the reviewer's recommendation, we will additionally include microscopy data showing SmoM2 localization in MEFs treated with the different sterol modulators. These data should confirm that the observed effects are not due to altered ciliary trafficking of the mutant protein but instead reflect changes in downstream signaling or membrane composition.

Minor comments:

Line 74: 'in patients', should be rephrased to 'patient-derived cells'

This was modified in the revised manuscript

Figure 2A: What do the '+/-' indicate? They seem to be erroneously placed.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Figure 2B: no label present for which bar represents cilia/other membranes

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Figure 2C: this representation is slightly deceptive, since the difference between cells and cilia for lanosterol is not significantly different as shown in figure 2A.

This representation has been removed in the revised figures.

Figure 3A: it would be useful to also show where 8-DHC is in the biosynthetic pathway.

This has been modified in the revised figures.

Line 373: the title should be rephrased as it infers that DHCR7 was blocked in model membranes, which is not the case.

This has been modified in the revised manuscript.

Lines 377-384: this paragraph seems to be a mix of methods and some explanation, but should be rephrased for clarity.

We believe the technical information within this paragraph are useful for the understanding of the reader. We would rather leave as is unless recommended by other reviewers or editorial staff.

Line 403: 'which could explain the resulting defects in Hedgehog signaling': how and what defects? At this point in the study no defects in Hh signaling have been shown.

This has been modified in the revised manuscript.

Figure 4D: 'd' is missing

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Line 408: SAG treatment resulted in slightly shorter cilia: this is not the case for just SAG treated cilia, but only for the combination of SAG + AY9944. However, in that condition there appears to be a subpopulation of very short cilia, are those real?

This is correct, this is not the case for untreated cilia, but the short population is real, not only in AY9944 but also in Tamoxifen and Simvastatin. Again, the relevance and significance of minor cilia length change is unclear and we are not trying to draw any other conclusion from this than saying that the ciliary compartment is modified.

Figure 5b: it would be good to add that all conditions contained SAG.

This has been modified in the revised figures.

Figure 5D: Since it is shown in Fig 5C that there are no positive cilia -SAG, there is no point to have empty graphs in Fig 5D on the left side, nor can any statistics be done. Similarly for 5K.

We think this is still worth having in the figure. As the reviewer noted in one of his next comment, there are cases where Smoothened or Patched can be abnormally distributed (see also Eguether et al, mol biol cell, 2018). This shows that we checked all conditions for presence or absence of Smo and that there is no signal to be found. We would rather leave it as is unless asked otherwise by editorial staff.

Figure 5E: it is not clearly indicated what is visualized in the inserts, sometimes it's a box, sometimes a line and they seem randomly integrated into the images.

We apologize for the oversight - the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Figure 5H: is this the intensity in just SMO positive cilia? If yes, this should be indicated, and the line at '0' for WT-SAG should be removed. I am also surprised there is then ns found for WT vs SLO, since in WT there are no positive cilia, but in SLO there are a few, so it appears to be more of a black-white situation. Perhaps it would be useful to split the data from different experiments to see if it consistently the case that there is a low percentage of SMO positive cilia in SLO cells.

Yes, as in the rest of figure 5, the fluorescence intensity of Smo is only taken into account in SMO positive cells. This is now indicated in figure legend (lines 890, 898, 903 ). As for Smo positive, this is a good suggestion. We checked and for cilia in non-activated SLO patients, there are 8 positive cilia over a total of 240 counted cilia, mainly from one of the experiments. We could remove the data or leave as is given that the result is not significant.

Fig S1: panels are inverted compared to mentioning in the text.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Methods-pharmacological treatments: there appear to be large differences in concentrations chosen to treat MDCK versus MEF cells - can the authors comment on these choices and show that the enzymes are indeed inhibited at the indicated concentrations?

We thank the reviewer for this important comment. The concentrations of the pharmacological treatments were optimized separately for MDCK and MEF cells based on cell-type-specific tolerance. For each compound, we used the highest concentration that produced no detectable cytotoxicity or morphological changes. These conditions ensured that the treatments were effective (as seen by changes in sterol composition in MDCK cilia and Hh pathway phenotypes in treated MEFs) and compatible with cell viability and ciliation. Although we did not directly assay enzymatic inhibition in each case, the selected concentrations are consistent with those previously reported to inhibit the targeted enzymes in similar cellular contexts.

Compound

Typical Concentration Range in Mammalian Cell Culture

Typical Exposure Duration

Example Cell Types

Representative Peer-Reviewed References

AY9944 (DHCR7 inhibitor)

1-10 µM widely used; 1 µM for minimal on-target effects; 2.5-10 µM for robust sterol shifts

24-72 h; some sterol studies up to several days

HEK293, fibroblasts, neuronal cells, macrophages

Kim et al., J Biol Chem, 2001 - used 1 µM in dose-response experiments.; Haas et al., Hum Mol Genet, 2007 - 1 µM in cell-based assays.; Recent macrophage sterol study - 2.5-10 µM to induce 7-DHC accumulation.

Simvastatin (HMG-CoA reductase inhibitor)

0.1-10 µM common; 1-10 µM most widely used for robust pathway inhibition

24-72 h

Diverse mammalian lines, including liver, fibroblasts, epithelial cells

Bytautaite et al., Cells (2020) - discusses common in-vitro ranges (1-10 µM).; Mullen et al., 2011 - used 10 µM simvastatin, noting it is a standard in-vitro concentration.

Tamoxifen (modulator of sterol metabolism)

1-20 µM; 1-5 µM for mild/longer treatments; 10-20 µM in cancer/cilia signaling studies

24-72 h (longer treatments often at 1-5 µM)

MDCK, MEFs, MCF-7, diverse epithelial lines

Schlottmann et al., Cells (2022) - used 5-25 µM in sterol-related cell studies.; MCF-7 literature - 0.1-1 µM for estrogenic signaling, higher (5-10 µM) for metabolic/sterol pathway effects.; Additional cancer cell work indicating similar ranges.

This information has been clarified in the revised Methods section (lines 222-224).

(optional): it would be interesting to include a gamma-tubulin staining on the cilium prep to see if there is indeed a presence of the basal body as suggested by the proteomics data.

Thank you, we will try this.

There are many spelling mistakes and inconsistencies throughout the manuscript and its figures (mix of French and English for example) so careful proofreading would be warranted. Moreover, there are many mentionings of 'Hedgehog defects' or 'Hedgehog-linked', where in fact it is a defect in or link to the Hedgehog pathway, not the protein itself. This should be corrected.

We thank the reviewer for noting these issues. We apologize for the inconsistencies observed in the initial submission, as mentioned previously, some of the figures inadvertently included earlier versions, which may have contributed to the errors identified. All figures have now been carefully revised and updated in the resubmitted manuscript.

Regarding the text, we are surprised to hear about the spelling inconsistencies, as the manuscript was professionally proofread prior to submission (documentation can be provided upon request). Nevertheless, we have conducted an additional round of thorough proofreading to ensure consistency throughout the text and figures.

Finally, we have corrected all instances of "Hedgehog defects" or "Hedgehog-linked" to the more accurate phrasing "Hedgehog pathway defect" or "Hedgehog pathway-linked," as suggested by the reviewer throughout the manuscript.

Reviewer #1 (Significance (Required)):

The study of ciliary membrane composition is highly relevant to understand signal transduction in health and disease. As such, the topic of this manuscript is significant and timely. However, as indicated above, there are limitations to this study, most notably the comparison of ciliary membrane versus all cellular membranes (rather than the plasma membrane), which weakens the conclusions that can be drawn. Moreover, cell-type dependency should be more thoroughly addressed. There certainly is a methodological advance in the form of cilia isolation from MDCK cells, however, it is unclear how broadly applicable this is to other mammalian cell types.

We would like to thank the reviewer for their helpful comments and we appreciate the reviewer's recognition of the relevance and timeliness of studying ciliary membrane composition in the context of signaling regulation. We fully acknowledge that our comparison was made between the primary ciliary membrane and the total cellular membrane fraction, which encompasses multiple intracellular membranes. Our intent, however, was to obtain a global overview of how the ciliary membrane differs from the average membrane environment within the cell, thereby highlighting features that are unique to the cilium as a signaling organelle. This approach provides valuable baseline information that complements, rather than replaces, future targeted comparisons with the plasma membrane. As mentioned in this reply, we aim at carrying out these experiments before publication. Regarding cell-type dependency, we concur that ciliary lipid composition may vary between cell types, reflecting differences in their functional specialization. Our method was intentionally established in MDCK cells, which are epithelial and highly ciliated, to ensure sufficient yield and reproducibility. We have initiated trials with other mammalian cell types, including IMCD3 and MEF cells, and while yields remain limited, preliminary results indicate that the approach is adaptable with further optimization. Thus, our current work establishes a robust and reproducible proof of concept in a mammalian model, providing the first detailed sterol fingerprint of a mammalian primary cilium.

We believe this constitutes a significant methodological and conceptual advance, as it opens the way for systematic exploration of ciliary lipid composition across diverse mammalian systems and pathological contexts.

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

Overview Accumulating evidence suggests that sterols play critical roles in signal transduction within the primary cilium, perhaps most notably in the Hedgehog cascade. However, the precise sterol composition of the primary cilium, and how it may change under distinct biological conditions, remains unknown, in part because of the lack of reproducible, widely accepted procedures to purify primary cilia from mammalian cultured cells. In the present study, the authors have designed a method to isolate the cilium from the MDCK cells efficiently and then utilized this procedure in conjunction with mass spectrometry to systematically analyze the sterol composition of the ciliary membrane, which they then compare to the sterol composition of the cell body. By analyzing this sterol profiling. the authors claim that the cilium has a distinct sterol composition from the cell body, including higher levels of cholesterol and desmosterol but lower levels of 8-DHC and & Lathosterol. This manuscript further demonstrates that alteration of sterol composition within cilia modulates Hedgehog signaling. These results strengthen the link between dysregulated Hedgehog signaling and defects in cholesterol biosynthesis pathways, as observed in SLOS and CDPX2.

While the ability to isolate primary cilia from cultured MDCK cells represents an important technical achievement, the central claim of the manuscript - that cilia have a different sterol composition from the cell body - is not adequately supported by the data, and more rigorous comparisons between the ciliary membrane and key organellar membranes (such as plasma membrane) are required to make this claim. Moreover, although the authors have repeatedly mention that the ciliary sterol composition is "tightly regulated" there is no evidence provided to support such claim. At best, the data suggest that the cilium and cell body may differ in sterol composition (though even that remains uncertain), but no underlying regulatory mechanisms are demonstrated. In addition, much of the 2nd half of the paper represents a rehash of experiments with sterol biosynthesis inhibitors that have already been published in the literature, making the conceptual advance modest at best. Lastly, the link between CDPX2 and defective Hedgehog signaling is tenuous.

We would like to thank the reviewer for their helpful comments

Major comments

Figure 1. C) Although the isolation of cilium from the MDCK cells using dibucaine treatment seems to be very efficient, the quality control of their fractionation procedure to monitor the isolation is limited to a single western blot of the purified cilia vs. cell body samples, with no representative data shown from the sucrose gradient fractionation steps. Given that prior studies (including those from the Marshall lab cited in this manuscript) found that 1) sucrose gradient fractionation was essential to obtain relatively pure ciliary fractions, and 2) the ciliary fractions appear to spread over many sucrose concentrations in those prior studies , the authors should have included the comparison of the fractionation profile from the sucrose gradient while isolating the primary cilium. This additional information would have further clarified and supported the efficiency of their proposed method.

We thank the reviewer for their insightful comments regarding the quality control of our ciliary fractionation. We would like to clarify several important methodological aspects that distinguish our approach from those used in the studies cited (including those from the Marshall lab). In the cited work, the authors used a continuous sucrose gradient ranging from 30 % to 45 %, which allowed visualization of the distribution of ciliary proteins across the gradient. In contrast, we employed a discontinuous sucrose gradient (25 % / 50 %) optimized for higher recovery and reproducibility in our hands. In our preparation, the primary cilia consistently localize at the interface between the 25 % and 50 % layers. We systematically collect five 1 mL fractions from this interface and use fractions 1-3 for downstream analyses, as fractions 4-5 are typically already depleted of ciliary material. This targeted collection ensures good enrichment and low contamination, while avoiding unnecessary dilution of the limited ciliary sample. We also note that the prior studies the reviewer refers to were optimized for proteomic analyses, and therefore used actin as a marker of contamination from the cell body. In our case, the downstream application is lipidomic profiling, for which such protein-based contamination markers are not directly informative, since no reliable lipid marker exists to differentiate between organelle membranes. For this reason, we limited the protein-level validation to a semi-quantitative assessment of ciliary enrichment using ARL13B Western blotting, which robustly reports the presence and enrichment of ciliary membranes. Finally, to complement this targeted validation, we performed proteomic analysis followed by Gene Ontology (GO) Enrichment Analysis using the PANTHER database. This analysis evaluates the overrepresentation of proteins associated with ciliary structures and functions relative to the background frequency in the Canis lupus familiaris proteome. The resulting enrichment profile confirms that the isolated material is highly enriched in ciliary components and somewhat depleted of non-ciliary contaminants, thereby serving as an unbiased and global assessment of sample specificity and purity. We believe that, together, these methodological choices provide a rigorous and quantitative validation of our fractionation efficiency and support the robustness of the cilia isolation protocol used in this study.

1. D) The authors presented proteomic data for the peptides analyzed from the isolated cilia in the form of GO term analysis; however, they did not provide examples of different proteins enriched within their fractionation procedure, aside from Arl13b shown in the blot. Including a summary table with representative proteins identified in the isolated ciliary fraction, along with the relative abundance or percentage distribution of these proteins, would make the data more informative.

We thank the reviewer for this valuable suggestion. As mentioned in the manuscript, our proteomic dataset includes numerous hallmark components of the cilium, such as 18 IFT proteins, 4 BBS proteins, and several Hedgehog pathway components (including SuFu and Arl13b), as well as axonemal (Tubulin, Kinesin, Dynein) and centrosomal proteins (Centrin, CEPs, γ-Tubulin, and associated factors). This composition demonstrates that the isolated fraction is highly enriched in bona fide ciliary components while retaining a small proportion of basal body proteins, which is expected given their physical continuity. Importantly, our dataset shows a 70% overlap with the ciliary proteome published by Ishikawa et al. and a 41% overlap with the CysCilia consortium's list of potential ciliary proteins, which supports both the specificity and reliability of our isolation procedure. Regarding the suggestion to present relative protein abundances, we would like to clarify that defining "relative to what" is challenging in this context. The stoichiometry of ciliary proteins is largely unknown, and relative abundance normalized to total protein content can be misleading, as ciliary structural and signaling components differ greatly in copy number and membrane association. For this reason, we chose to highlight in the text proteins such as BBS and IFTs, which are known to be of low abundance within the cilium; their detection supports the depth and specificity of our proteomic coverage. In addition, we performed an unbiased Gene Ontology (GO) Enrichment Analysis using the PANTHER database, which provides a systematic and quantitative overview of the biological processes and cellular components overrepresented in our dataset relative to the canine proteome. This analysis with regard to purity wa already discussed in the submitted manuscript discussion. To further address the reviewer's comment, we will include as a supplemental table in the revised manuscript, a summary table listing representative ciliary proteins identified in our fraction, including those overlapping with the CysCilia (Gold ans potential lists), CiliaCarta and Ishikawa/Marshall proteomes. This addition should make the dataset more transparent and informative while preserving scientific rigor.

Figure 2.

The authors represented the comparison of sterol content within the cilia versus whole cell (as cell membranes). Since different organelles have a very diverse degree of cholesterol contents within them, for instance plasma membrane itself is around 50 mol% cholesterol levels while organelles like ER have barely any cholesterol. Thus, comparing these two samples and claiming a 2.5-fold increase in cholesterol levels is misleading. A more appropriate comparison would be between isolated primary cilia and isolated plasma membranes (procedures to isolate plasma membranes have been described previously, e.g., Naito et al., eLife 2019; Das et al, PNAS 2013. The absence of such controls makes it difficult to fully validate the reported magnitude of sterols enrichment in cilia relative to the cell surface.

As already discussed above for reviewer 1, we would like to emphasize that our study did not aim to compare the cilium directly to the plasma membrane, nor did we claim that the comparison was in any way related to the plasma membrane. Our intent, was to obtain a global overview of how the ciliary membrane differs from the average membrane environment within the cell, thereby highlighting features that are unique to the cilium as a signaling organelle. This approach provides valuable baseline information that complements, rather than replaces, future targeted comparisons with the plasma membrane. However, we concur that determining the sterol composition of the MDCK plasma membrane would provide valuable context and enable a comparison with the membrane continuous with the ciliary membrane. Hence, we are willing to try isolating plasma membrane in the same cellular contexts, and we thank the reviewer for the proposed literature.

Also, because dibucaine was used here to isolate MDCK cilia, a control experiment to exclude possible effects of the dibucaine treatment on sterol biosynthesis would be helpful.

Thank you for this comment, we will verify this point by quantifying by GC-MS the sterol content of whole MDCK cells with and without 15 minutes-dibucaine treatments.

Figure 3.

Tamoxifen is a potent drug for nuclear hormone receptor activity and thus can independently influence various cellular processes. As several experiments in the later sections of the manuscript rely on tamoxifen treatment of cells, it is important that the authors include appropriate controls for tamoxifen treatment, to confirm that the observed effects do not stem from effects on nuclear hormone receptor activity. This would ensure that the observed effects can be confidently attributed to the experimental manipulation rather than to the intrinsic effects of tamoxifen.

The reviewer is right, tamoxifen, like many drugs, has pleiotropic effects in different cell processes. Aware of this possible issue, we turned to a genetic model creating a CRISPR-CAS9 mediated knock down of EBP, the enzyme targeted by tamoxifen. We showed in figure 5 that the results between tamoxifen treated cells and CRIPSR EBP cells were in accordance with one another, showing that, for hedgehog signaling, the effect of tamoxifen recapitulates the effect of the enzyme KO.

Figure4. The authors present the results of spectroscopy studies to analyze generalized polarization (GP) of liposomes in vitro , but only processed data are shown, and the raw spectra are not provided. The authors need to present representative spectra to enable the readers to interact the raw data from the experiments.

This has been added to new supplemental figure 1 and corresponding figure legend (lines 898-904)

Figure5. B) The experiment shown Gli1 mRNA levels following treatment with inhibitors of cholesterol biosynthesis, but similar findings have already been reported previously (e.g., Cooper et al, Nature Genetics 2003; Blassberg et al, Hum Mol Genet 2016), and the present results do not provide a significant conceptual advance over those earlier studies.

We thank the reviewer for this comment and for highlighting the importance of earlier studies on Hedgehog (Hh) signaling and cholesterol metabolism. While we fully agree that confirming and extending established findings has intrinsic scientific value, we respectfully disagree with the assertion that our work does not provide conceptual novelty.

The seminal work by Cooper et al. (Nature Genetics, 2003) indeed laid the foundation for linking sterol metabolism to Hedgehog signaling, and we cite it as such. However, that study was conducted in chick embryos, a model that is relatively distant from mammalian systems and human pathophysiology. Moreover, their approach relied heavily on cyclodextrin-mediated cholesterol depletion, which is non-specific and extracts multiple sterols from membranes (discussed in this article lines 512-516). In contrast, our study employs pharmacological inhibitors targeting specific enzymes in the sterol biosynthetic pathway, thereby allowing us to modulate distinct steps and intermediates in a controlled and mechanistically informative manner. We also extend these analyses to patient-derived fibroblasts and CRISPR-engineered cells, providing direct human and genetic validation of the observed effects. Importantly, we complement these cellular studies with biochemical characterization of isolated ciliary membranes from MDCK cells, enabling a direct assessment of how specific sterol alterations affect ciliary composition and Hh pathway function - an angle not addressed in prior work.

Regarding Blassberg et al. (Hum. Mol. Genet., 2016), we agree that part of our findings recapitulates their observations on SMO-related signaling defects, which we view as an important confirmation of reproducibility. However, their study primarily sought to distinguish whether Hh pathway impairment in SLOS results from 7-DHC accumulation or cholesterol depletion, concluding that cholesterol deficiency was the main cause. Our results expand on this by demonstrating that perturbations extend beyond these two sterols, and that additional intermediates in the biosynthetic pathway also impact ciliary membrane composition and signaling competence. Furthermore, our experiments using the constitutively active SmoM2 mutant show that Hh signaling defects are not restricted to SMO activation per se, revealing a broader disruption of the signaling machinery within the cilium.

Finally, neither of the above studies examined CDPX2 patient-derived cells or the consequences of EBP enzyme deficiency on Hh signaling. Our finding that this pathway is altered in this genetic context represents, to our knowledge, a novel link between CDPX2 and Hedgehog pathway dysfunction.

Taken together, our work builds upon and extends previous findings by integrating cell-type-specific, biochemical, and patient-based analyses to provide a more comprehensive and mechanistically detailed view of how sterol composition of the ciliary membrane regulates Hedgehog signaling.

In addition, the authors analyze the effect of these inhibitors on SAG stimulation, but the experiment lacks the control for Gli mRNA levels in the absence of SAG treatment. Without this control, it is impossible to know where the baseline in the experiment is and how large the effects in question really are.

Below, we provide the data expressed using the ΔΔCt method (NT + SAG normalized to NT - SAG), which more clearly illustrates the magnitude of the effect in question. As similar qPCR-based Hedgehog pathway activation assays in MEFs have been published previously (see Eguether et al., Dev. Cell 2014; Eguether et al., Mol. Biol. Cell 2018), our goal here was not to re-establish the assay itself but to highlight the comparative effects across experimental conditions. In addition, one of the datasets was obtained using a new batch of SAG, which exhibited stronger pathway activation across all conditions (visible as higher overall expression levels). To ensure valid statistical comparisons across experiments and to focus on relative rather than absolute activation, we therefore chose to present the data as fold change values, which provides a more robust and statistically consistent measure for cross-condition analysis.

J-K) The data represented in these panels for SAG treatment as fraction of Smo and its fluorescence intensity for the same sample appears to be inconsistent between the two graphs. Under SAG treatment for EBP mutants shows higher Smo fluorescence intensity while Smo positive cilia seems to be less than the wild type control cells. If the number of Smo+ cilia (quantified by eye) differs between conditions, shouldn't the quantification of Smo intensity within cilia show a similar difference?

We thank the reviewer for this careful observation. The apparent discrepancy arises because the two panels quantify different parameters. In panel (j), we counted the percentage of cilia positive for SMO (i.e., cilia in which SMO was detected above background). In contrast, panel (k) reports the fluorescence intensity of SMO, but this measurement was performed only within the SMO-positive cilia identified in panel (j). This distinction has now been explicitly clarified in the figure legend, as also suggested by Reviewer 1.

Taken together, these two analyses indicate that although fewer cilia display detectable SMO accumulation in the EBP mutant cells, the amount of SMO present within those cilia that do recruit it is comparable to wild-type levels (as reflected by the non-significant difference in fluorescence intensity). This interpretation helps explain the partial functional preservation of Hedgehog signaling in this condition and contrasts with cases such as AY9944 treatment, where both the number of SMO-positive cilia and the SMO intensity are reduced.

1. I) The rationale for using SmoM2 in the analysis of cholesterol metabolism-related diseases such as SLOS and CDPX2 is unclear. The SmoM2 variant is primarily associated with cancer rather than cholesterol biosynthesis defects and its relevance either of these disorders is not immediately apparent.

We thank the reviewer for this pertinent observation. We fully agree that SmoM2 was originally identified as an oncogenic mutation and is not directly associated with cholesterol biosynthesis disorders. However, our rationale for using this mutant was mechanistic rather than pathological. SmoM2 is a constitutively active form of SMO that triggers pathway activation independently of upstream components such as PTCH1 or ligand-mediated regulation.

By using SmoM2, we aimed to determine whether the signaling defects observed under conditions that alter sterol metabolism (e.g., treatment with AY9944 or tamoxifen) occur upstream or downstream of SMO activation. The results demonstrate that, even when SMO is constitutively active, the Hedgehog pathway remains impaired under AY9944 treatment-and to a lesser extent with tamoxifen-indicating that these sterol perturbations disrupt the pathway beyond the level of SMO activation itself. In contrast, cells treated with simvastatin maintain normal pathway responsiveness, reinforcing the specificity of this effect.

This experiment is therefore central to our study, as it reveals that sterol imbalance can hinder Hedgehog signaling even in the presence of an active SMO, providing new insight into how membrane composition influences downstream signaling competence.

Minor corrections

1. Line 385 seems to be a bit confusing which mentions cilia were treated with AY9944 - do the authors mean that cells were been treated with the drugs before isolation of cilia, or were the purified cilia actually treated with the drugs?

Thank you, this has been modified in the revised manuscript

The authors should add proper label in Figure 2 panel b for the bars representing the cilia and cell membranes.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Panels in Figure S1 should be re-arranged according to the figure legend and figure reference in line 450.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Legend for the Figure S1b should be corrected as data sets in graph represents 7 points while technical replicates in legend shows 6 experimental values.

Thank you, this has been modified in the revised manuscript

The labels for drug in Figure 3 and 5 should be corrected from tamoxifene to tamoxifen and simvastatine to simvastatin.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

Reviewer #2 (Significance (Required)):

In the present study, the authors have designed a method to isolate the cilium from the MDCK cells efficiently and then utilized this procedure in conjunction with mass spectrometry to systematically analyze the sterol composition of the ciliary membrane, which they then compare to the sterol composition of the cell body. By analyzing this sterol profiling. the authors claim that the cilium has a distinct sterol composition from the cell body, including higher levels of cholesterol and desmosterol but lower levels of 8-DHC and & Lathosterol. This manuscript further demonstrates that alteration of sterol composition within cilia modulates Hedgehog signaling. These results strengthen the link between dysregulated Hedgehog signaling and defects in cholesterol biosynthesis pathways, as observed in SLOS and CDPX2.

While the ability to isolate primary cilia from cultured MDCK cells represents an important technical achievement, the central claim of the manuscript - that cilia have a different sterol composition from the cell body - is not adequately supported by the data, and more rigorous comparisons between the ciliary membrane and key organellar membranes (such as plasma membrane) are required to make this claim. Moreover, although the authors have repeatedly mention that the ciliary sterol composition is "tightly regulated" there is no evidence provided to support such claim. At best, the data suggest that the cilium and cell body may differ in sterol composition (though even that remains uncertain), but no underlying regulatory mechanisms are demonstrated. In addition, much of the 2nd half of the paper represents a rehash of experiments with sterol biosynthesis inhibitors that have already been published in the literature, making the conceptual advance modest at best. Lastly, the link between CDPX2 and defective Hedgehog signaling is tenuous.

We thank the reviewer for this detailed summary and for acknowledging the technical advance represented by our method for isolating primary cilia from MDCK cells. However, we respectfully disagree with several aspects of the reviewer's assessment of our work.

As we elaborated in our responses to earlier comments, particularly regarding Figure 5, we disagree with the characterization of part of our study as a "rehash", a somewhat derogatory word, of previously published experiments. Our approach differs from earlier studies by relying on specific pharmacological modulation of defined enzymes in the sterol biosynthesis pathway, rather than using non-specific agents such as cyclodextrins, and by linking these manipulations to direct biochemical measurements of ciliary sterol composition. This strategy allows, for the first time, a targeted and physiologically relevant examination of how specific sterol perturbations affect Hedgehog signaling.

Regarding our statement that ciliary sterol composition is "tightly regulated," we acknowledge that we have not yet explored the underlying molecular mechanisms of this regulation. Nevertheless, the experimental evidence supporting this statement lies in the variation of ciliary sterol composition across multiple treatments that strongly perturb cellular sterols. Despite broad cellular changes, the ciliary sterol profile remains very resilient for some parameters, an observation that, in our view, strongly supports the idea of a selective or regulated process maintaining ciliary sterol identity. This conclusion does not depend on comparison with other membrane compartments.

We also respectfully disagree that the observed differences between cilia and the cell body (which doesn't equal to plasma membrane) are "uncertain." The consistent enrichment in cholesterol and desmosterol, combined with the relative depletion in 8-DHC and lathosterol, were detected across independent replicates using robust lipidomic profiling and are statistically supported. These findings are, to our knowledge, the first quantitative demonstration of a sterol fingerprint specific to a mammalian cilium.

Finally, while we agree that the mechanistic link between CDPX2 and defective Hedgehog signaling warrants further exploration, the data we present, combining pharmacological inhibition (tamoxifen), CRISPR-mediated EBP knockout, and SMOM2 activation assays, all consistently indicate a functional impairment of the Hedgehog pathway under EBP deficiency. This is further reinforced by clinical reports describing Hedgehog-related phenotypes in CDPX2 patients. We therefore believe that our work provides a solid experimental and conceptual basis for connecting EBP dysfunction to Hedgehog signaling defects.

In summary, our study introduces a validated and reproducible method for mammalian cilia isolation, provides the first detailed sterol composition profile of primary cilia, and establishes a functional link between ciliary sterol imbalance and Hedgehog pathway modulation. We believe these findings represent a meaningful conceptual advance and a valuable resource for the field

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

Lamaziere et al. describe an improved protocol for isolating primary cilia from MDCK cells for downstream lipidomics analysis. Using this protocol, they characterize sterol profile of MDCK cilia membrane under standard growth conditions and following pharmacological perturbations that are meant to mimic SLOS and CDPX2 disorders in humans. The authors then assess the impact of the same pharmacological manipulations on Shh pathway activity and validate their findings from these experiments using orthogonal genetic approaches. Major and minor concerns that require attention prior to publication are outlined below.

We would like to thank the reviewer for their comments

Major 1.Since the extent of contamination of the cilia preps with non-cilia membranes is unclear, and variability between replicates is not reported, it makes interpretation of changes in cilia membrane sterol composition in response to pharmacological manipulations somewhat difficult to interpret. Discussing reproducibility of cilia sterol composition between replicates (and including corresponding data) could alleviate these concerns to some extent.

We thank the reviewer for this comment. We would like to clarify that variability between replicates is indeed reported throughout the manuscript. In Figures 2 and 3, all data are presented as mean {plus minus} SEM, as indicated in the figure legends. Specifically, the data in Figure 2 are derived from six independent experiments, reflecting the central dataset used for comparative analyses, while the data in Figure 3 are based on three independent experiments.

We also note that the overall variability between replicates is low, further supporting the reproducibility of our ciliary sterol composition measurements. This consistency across independent biological replicates provides confidence that the differences observed between cilia and the cell body are robust and not due to stochastic contamination or technical variation.

2.An abundant non-ciliary membrane protein (rather than GAPDH) may be a more appropriate loading control in Fig. 1C.

This is a valuable comment and we will find a non-ciliary membrane protein to complement this experiment.

3.Fig. 2b - which bar corresponds to cells and which one to cilia? What do numbers inside bars represent? Please label accordingly.

We apologize for the oversight, the figures initially submitted with the manuscript inadvertently included some earlier versions, which explains several of the discrepancies noted by the reviewers. This issue has been corrected in the revised submission, and all figures have now been updated to reflect the finalized data.

4.Fig. 3b-d, right panels - please define what numbers inside bars represent

Thank you, this was done in the revised manuscript. The numbers are reports of absolute quantification.

5.The font in Figs 2, 3, and 4 is very small and difficult to read. Please make the font and/or panels bigger to improve readability.

We did our best to enlarge font despite space limitations, but we are willing to work with editorial staff to improve readability as suggested.

6.It would help to have a diagram of the key steps in the cholesterol synthesis pathway for reference early in the paper rather than in figure 3.

We thank the reviewer for his comment, but we don't understand why this would be helpful as we only use sterol modulators involving the pathway's enzyme in fig3. We are open to discussion with editorial staff about moving it up to fig2. If they feel this is needed

7.The authors need to discuss why/how global inhibition of enzymes (e.g. via AY9944 treatment) in a cell could cause reduction in cholesterol levels only in the cilium and not in other cell membranes (see also point 1). Yet, tamoxifen treatment lowers cholesterol across the board.

We thank the reviewer for these insightful comments. Regarding the modest overall effect of simvastatin on cholesterol levels, we would like to note that MDCK cells are an immortalized epithelial cell line with high metabolic plasticity. Such cancer-like cell types are known to exhibit enhanced de novo lipogenesis, particularly under culture conditions with ample glucose availability. This compensatory lipid biosynthesis can partially counterbalance pharmacological inhibition of the cholesterol biosynthetic pathway. Because simvastatin acts upstream in the pathway (at HMG-CoA reductase), its inhibition primarily reduces early intermediates rather than fully depleting end-product cholesterol, explaining the relatively mild changes observed in total cholesterol content. . This has been added in a new paragraph in the revised manuscript (lines 371-378).

8.Fig. 5c, g, and j - statistical analyses are missing and need to be added in support of conclusions drawn in the text of the manuscript.

Thank you, this has been done in the revised manuscript

9.The decrease in the fraction of Smo+ cilia observed in EBP KO cells is mild (panel j, no statistics), and there is possibly a clone-specific effect here as well (statistical analysis is needed to determine if EBP139 is indeed different from WT and whether EBP139 and 141 are different from each other). Similarly, Smo fluorescence intensity after SAG treatment (panel k) is the same in WT and EBP KO cells, while there is a marked difference in intraciliary Smo intensity after tamoxifen treatment. The author's conclusion "...we were able to show that results with human cells aligned with our tamoxifen experiments" (line 436) should be modified to more accurately reflect the presented data. Ditto conclusions on lines 440-442, 530-531. In fact, it is the lack of Hh phenotypes in CDPX2 patients that is consistent with the EBP KO data presented in the paper.

We thank the reviewer for this detailed comment. We have now performed the requested statistical analyses and incorporated them into the revised manuscript.

The new analyses confirm that both EBP139 and EBP141 CRISPR KO clones show a statistically significant reduction in the fraction of Smo⁺ cilia compared to WT cells. They also reveal that the two clones differ significantly from each other, consistent with the expected clonal variability inherent to independently derived CRISPR lines.

Despite this variability, several lines of evidence support our conclusion that the EBP KO phenotypes align with the effects observed after tamoxifen treatment:

1- Directionally consistent reduction in Smo⁺ cilia:

Although the magnitude of the decrease differs between clones, both clones display a significant reduction compared to WT, paralleling the reduction observed in tamoxifen-treated cells. This directional consistency is the key point for comparing pharmacological and genetic perturbations.

2-Converging evidence from SmoM2 experiments:

Tamoxifen treatment also reduces pathway output in the context of SmoM2 overexpression. This supports the interpretation that both EBP inhibition (tamoxifen) and EBP loss (CRISPR KO) impair Hedgehog signaling at the level of ciliary function, albeit more mildly than AY9944/SLOS-like perturbations.

3-Interpretation of Smo intensity (panel k):

As clarified in the revised text, the fluorescence intensities in panel K correspond only to cilia that are Smo-positive. The absence of a difference in intensity therefore does not contradict the observed reduction in the number of Smo⁺ cilia. Rather, it explains why the phenotype is milder than that observed for SLOS/AY9944: when Smo is able to enter the cilium, its enrichment level is comparable to WT.

4- Clinical relevance for CDPX2:

While Hedgehog-related phenotypes in CDPX2 patients may be milder or under-reported, several documented features, such as polydactyly (10% of cases), as well as syndactyly and clubfoot, are classically associated with ciliary/Hedgehog signaling defects. This clinical pattern is consistent with the milder yet detectable defects we observe in EBP KO cells.

Minor •Line 310: 'intraflagellar' rather than 'intraciliary' transport particle B is a more conventional term

We agree that intraflagellar is more conventional than intraciliary, but in this case, this is how the GO term is labeled in the database. In our opinion, it should stay as is.

• Fig. 2c - typos in the color key, is grey meant to be "cells" and blue "cilia"? Individual panels are not referenced in the text

This panel has been removed thanks to comment from reviewer 1 and 3 finding it misleading.

• Lines 357-358: "Notably, AY9944 treatment led to a greater reduction in cholesterol content as well as a greater increase in 7-DHC and 8-DHC in cilia than in the other cell membranes" - the authors need to support this statement with appropriate statistical analysis

We respectfully believe there may be a misunderstanding in the reviewer's concern. In all cases, our comparisons are made between treated vs. untreated conditions within each compartment (cell bulk vs. ciliary membrane), and the statistical significance of these differences is already reported as determined by a Mann-Whitney test. In every case, the changes observed are greater in cilia than in the cell body. The statement in the manuscript simply summarizes this quantitative observation. However, if the reviewer feels that an additional statistical test directly comparing the magnitude of the two compartment-specific changes would strengthen the claim, we are willing to include this analysis. Alternatively, if preferred, we can remove the sentence entirely, as the comparison is already clearly visible in Figure 3b.

• Line 473 - unclear what is meant by "olfactory cilia are mainly sensory and not primary". Primary cilia are sensory.

We agree, primary cilia are sensory, but still different from cilia belonging to sensory epithelia like retina photoreceptors or olfactory cilia. Nevertheless, this statement was modified in revised manuscript

• Line 551: 'data not shown'. Please include the data that you would like to discuss or remove discussion of these data from the manuscript.

The data is not shown because there is nothing to show, as we discussed in that sentence, use of cholesterol probe resulted in the disappearance of primary cilia altogether. We are willing to work with editorial staff to find a better way of expressing this idea.

Reviewer #3 (Significance (Required)):

Overall, the manuscript expands our knowledge of cilia membrane composition and reports an interesting link between SLOS and Shh signaling defects, which could at least in part explain SLOS patients' symptoms. The findings reported in the manuscript could be of interest to a broad audience of cell biologists and geneticists.

We would like to thank the reviewer for his recognition of the importance of this work

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Referee #2

Evidence, reproducibility and clarity

Overview

Accumulating evidence suggests that sterols play critical roles in signal transduction within the primary cilium, perhaps most notably in the Hedgehog cascade. However, the precise sterol composition of the primary cilium, and how it may change under distinct biological conditions, remains unknown, in part because of the lack of reproducible, widely accepted procedures to purify primary cilia from mammalian cultured cells. In the present study, the authors have designed a method to isolate the cilium from the MDCK cells efficiently and then utilized this procedure in conjunction with mass spectrometry to systematically analyze the sterol composition of the ciliary membrane, which they then compare to the sterol composition of the cell body. By analyzing this sterol profiling. the authors claim that the cilium has a distinct sterol composition from the cell body, including higher levels of cholesterol and desmosterol but lower levels of 8-DHC and & Lathosterol. This manuscript further demonstrates that alteration of sterol composition within cilia modulates Hedgehog signaling. These results strengthen the link between dysregulated Hedgehog signaling and defects in cholesterol biosynthesis pathways, as observed in SLOS and CDPX2.

While the ability to isolate primary cilia from cultured MDCK cells represents an important technical achievement, the central claim of the manuscript - that cilia have a different sterol composition from the cell body - is not adequately supported by the data, and more rigorous comparisons between the ciliary membrane and key organellar membranes (such as plasma membrane) are required to make this claim. Moreover, although the authors have repeatedly mention that the ciliary sterol composition is "tightly regulated" there is no evidence provided to support such claim. At best, the data suggest that the cilium and cell body may differ in sterol composition (though even that remains uncertain), but no underlying regulatory mechanisms are demonstrated. In addition, much of the 2nd half of the paper represents a rehash of experiments with sterol biosynthesis inhibitors that have already been published in the literature, making the conceptual advance modest at best. Lastly, the link between CDPX2 and defective Hedgehog signaling is tenuous.

Major comments

Figure 1.

C) Although the isolation of cilium from the MDCK cells using dibucaine treatment seems to be very efficient, the quality control of their fractionation procedure to monitor the isolation is limited to a single western blot of the purified cilia vs. cell body samples, with no representative data shown from the sucrose gradient fractionation steps. Given that prior studies (including those from the Marshall lab cited in this manuscript) found that 1) sucrose gradient fractionation was essential to obtain relatively pure ciliary fractions, and 2) the ciliary fractions appear to spread over many sucrose concentrations in those prior studies , the authors should have included the comparison of the fractionation profile from the sucrose gradient while isolating the primary cilium. This additional information would have further clarified and supported the efficiency of their proposed method. D) The authors presented proteomic data for the peptides analyzed from the isolated cilia in the form of GO term analysis; however, they did not provide examples of different proteins enriched within their fractionation procedure, aside from Arl13b shown in the blot. Including a summary table with representative proteins identified in the isolated ciliary fraction, along with the relative abundance or percentage distribution of these proteins, would make the data more informative.

Figure 2.

The authors represented the comparison of sterol content within the cilia versus whole cell (as cell membranes). Since different organelles have a very diverse degree of cholesterol contents within them, for instance plasma membrane itself is around 50 mol% cholesterol levels while organelles like ER have barely any cholesterol. Thus, comparing these two samples and claiming a 2.5-fold increase in cholesterol levels is misleading. A more appropriate comparison would be between isolated primary cilia and isolated plasma membranes (procedures to isolate plasma membranes have been described previously, e.g., Naito et al., eLife 2019; Das et al, PNAS 2013. The absence of such controls makes it difficult to fully validate the reported magnitude of sterols enrichment in cilia relative to the cell surface. Also, because dibucaine was used here to isolate MDCK cilia, a control experiment to exclude possible effects of the dibucaine treatment on sterol biosynthesis would be helpful.

Figure 3.

Tamoxifen is a potent drug for nuclear hormone receptor activity and thus can independently influence various cellular processes. As several experiments in the later sections of the manuscript rely on tamoxifen treatment of cells, it is important that the authors include appropriate controls for tamoxifen treatment, to confirm that the observed effects do not stem from effects on nuclear hormone receptor activity. This would ensure that the observed effects can be confidently attributed to the experimental manipulation rather than to the intrinsic effects of tamoxifen.

Figure4.

The authors present the results of spectroscopy studies to analyze generalized polarization (GP) of liposomes in vitro , but only processed data are shown, and the raw spectra are not provided. The authors need to present representative spectra to enable the readers to interact the raw data from the experiments.

Figure5.

B) The experiment shown Gli1 mRNA levels following treatment with inhibitors of cholesterol biosynthesis, but similar findings have already been reported previously (e.g., Cooper et al, Nature Genetics 2003; Blassberg et al, Hum Mol Genet 2016), and the present results do not provide a significant conceptual advance over those earlier studies. In addition, the authors analyze the effect of these inhibitors on SAG stimulation, but the experiment lacks the control for Gli mRNA levels in the absence of SAG treatment. Without this control, it is impossible to know where the baseline in the experiment is and how large the effects in question really are. J-K) The data represented in these panels for SAG treatment as fraction of Smo and its fluorescence intensity for the same sample appears to be inconsistent between the two graphs. Under SAG treatment for EBP mutants shows higher Smo fluorescence intensity while Smo positive cilia seems to be less than the wild type control cells. If the number of Smo+ cilia (quantified by eye) differs between conditions, shouldn't the quantification of Smo intensity within cilia show a similar difference? I) The rationale for using SmoM2 in the analysis of cholesterol metabolism-related diseases such as SLOS and CDPX2 is unclear. The SmoM2 variant is primarily associated with cancer rather than cholesterol biosynthesis defects and its relevance either of these disorders is not immediately apparent.

Minor corrections

1. Line 385 seems to be a bit confusing which mentions cilia were treated with AY9944 - do the authors mean that cells were been treated with the drugs before isolation of cilia, or were the purified cilia actually treated with the drugs?
2. The authors should add proper label in Figure 2 panel b for the bars representing the cilia and cell membranes.
3. Panels in Figure S1 should be re-arranged according to the figure legend and figure reference in line 450.
4. Legend for the Figure S1b should be corrected as data sets in graph represents 7 points while technical replicates in legend shows 6 experimental values.
5. The labels for drug in Figure 3 and 5 should be corrected from tamoxifene to tamoxifen and simvastatine to simvastatin.

Significance

In the present study, the authors have designed a method to isolate the cilium from the MDCK cells efficiently and then utilized this procedure in conjunction with mass spectrometry to systematically analyze the sterol composition of the ciliary membrane, which they then compare to the sterol composition of the cell body. By analyzing this sterol profiling. the authors claim that the cilium has a distinct sterol composition from the cell body, including higher levels of cholesterol and desmosterol but lower levels of 8-DHC and & Lathosterol. This manuscript further demonstrates that alteration of sterol composition within cilia modulates Hedgehog signaling. These results strengthen the link between dysregulated Hedgehog signaling and defects in cholesterol biosynthesis pathways, as observed in SLOS and CDPX2.

While the ability to isolate primary cilia from cultured MDCK cells represents an important technical achievement, the central claim of the manuscript - that cilia have a different sterol composition from the cell body - is not adequately supported by the data, and more rigorous comparisons between the ciliary membrane and key organellar membranes (such as plasma membrane) are required to make this claim. Moreover, although the authors have repeatedly mention that the ciliary sterol composition is "tightly regulated" there is no evidence provided to support such claim. At best, the data suggest that the cilium and cell body may differ in sterol composition (though even that remains uncertain), but no underlying regulatory mechanisms are demonstrated. In addition, much of the 2nd half of the paper represents a rehash of experiments with sterol biosynthesis inhibitors that have already been published in the literature, making the conceptual advance modest at best. Lastly, the link between CDPX2 and defective Hedgehog signaling is tenuous.

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Referee #1

Evidence, reproducibility and clarity

Review report for 'Sterols regulate ciliary membrane dynamics and hedgehog signaling in health and disease', Lamazière et al.

In this manuscript, Lamazière et al. address an important understudied aspect of primary cilium biology, namely the sterol composition in the ciliary membrane. It is known that sterols especially play an important role in signal transduction between PTCH1 and SMO, two upstream components of the Hedgehog pathway, at the primary cilium. Moreover, several syndromes linked to cholesterol biosynthesis defects present clinical phenotypes indicative of altered Hh signal transduction. To understand the link between ciliary membrane sterol composition and Hh signal transduction in health and disease, the authors developed a method to isolate primary cilia from MDCK cells and coupled this to quantitative metabolomics. The results were validated using biophysical methods and cellular Hh signaling assays. While this is an interesting study, it is not clear from the presented data how general the findings are: can cilia be isolated from different mammalian cell types using this protocol? Is the sterol composition of MDCK cells expected to the be the same in fibroblasts or other cell types? Without this information, it is difficult to judge whether the conclusions reached in fibroblasts are indeed directly related to the sterol composition detected in MDCK cells. Below is a detailed breakdown of suggested textual changes and experimental validations to strengthen the conclusions of the manuscript.

Major comments:

• It appears that the comparison has been made between ciliary membranes and the rest of the cell's membranes, which includes many other membranes besides the plasma membrane. This significantly weakens the conclusions on the sterol content specific to the cilium, as it may in fact be highly similar to the rest of the plasma membrane. It is for example known that lathosterol is biosynthesized in the ER, and therefore the non-presence in the cilium may reflect a high abundance in the ER but not necessarily in the plasma membrane.
• While the protocol to isolate primary cilium from MDCK cells is a valuable addition to the methods available, it would be good to at least include a discussion on its general applicability. Have the authors tried to use this protocol on fibroblasts for example?
• Some of the conclusions in the introduction (lines 75-80) seem to be incorrectly phrased based on the data: in basal conditions, ciliary membranes are already enriched in cholesterol and desmosterol, and the treatment lowers this in all membranes.
• There seems to be little effect of simvastatin on overall cholesterol levels. Can the authors comment on this result? How would the membrane fluidity be altered when mimicking simvastatin-induced composition? Since the effect on Hh signaling appears to be the biggest (Figure 5B) under simvastatin treatment, it would be interesting to compare this against that found for AY9944 treatment. Also, the authors conclude that the effects of simvastatin treatment on ciliary membrane sterol composition are the mildest, however, one could argue that they are the strongest as there is a complete lack of desmosterol.
• It is not clear to me why the authors have chosen to use SAG to activate the Hh pathway, as this is a downstream mode of activation and bypasses PTCH1 (and therefore a potentially sterol-mediated interaction between the two proteins). It would be very informative to compare the effect of sterol modulation on the ability of ShhN vs SAG to activate the pathway.
• The conclusions about the effect of tamoxifen on SMO trafficking in MEFs should be validated in human patient cells before being able to conclude that there is a potential off-target effect (line 438). Also, if that is the case, the experiment of tamoxifen treatment of EBP KO cells should give an additional effect on SMO trafficking. Also, could the CDPX2 phenotypes in patients be the result of different cell types being affected than the fibroblast used in this study?
• For the experiments with the SMO-M2 mutant, it would be useful to show the extent of pathway activation by the mutant compared to SAG or ShhN treatment of non-transfected cells. Moreover, it will be necessary to exclude any direct effects of the compound treatment on the ability of this mutant to traffic to the primary cilium, which can easily be done using fluorescence microscopy as the mutant is tagged with mCherry.

Minor comments:

Line 74: 'in patients', should be rephrased to 'patient-derived cells'

Figure 2A: What do the '+/-' indicate? They seem to be erroneously placed.

Figure 2B: no label present for which bar represents cilia/other membranes

Figure 2C: this representation is slightly deceptive, since the difference between cells and cilia for lanosterol is not significantly different as shown in figure 2A.

Figure 3A: it would be useful to also show where 8-DHC is in the biosynthetic pathway.

Line 373: the title should be rephrased as it infers that DHCR7 was blocked in model membranes, which is not the case.

Lines 377-384: this paragraph seems to be a mix of methods and some explanation, but should be rephrased for clarity.

Line 403: 'which could explain the resulting defects in Hedgehog signaling': how and what defects? At this point in the study no defects in Hh signaling have been shown.

Figure 4D: 'd' is missing

Line 408: SAG treatment resulted in slightly shorter cilia: this is not the case for just SAG treated cilia, but only for the combination of SAG + AY9944. However, in that condition there appears to be a subpopulation of very short cilia, are those real?

Figure 5b: it would be good to add that all conditions contained SAG.

Figure 5D: Since it is shown in Fig 5C that there are no positive cilia -SAG, there is no point to have empty graphs in Fig 5D on the left side, nor can any statistics be done. Similarly for 5K.

Figure 5E: it is not clearly indicated what is visualized in the inserts, sometimes it's a box, sometimes a line and they seem randomly integrated into the images.

Figure 5H: is this the intensity in just SMO positive cilia? If yes, this should be indicated, and the line at '0' for WT-SAG should be removed. I am also surprised there is then ns found for WT vs SLO, since in WT there are no positive cilia, but in SLO there are a few, so it appears to be more of a black-white situation. Perhaps it would be useful to split the data from different experiments to see if it consistently the case that there is a low percentage of SMO positive cilia in SLO cells. Fig S1: panels are inverted compared to mentioning in the text.

Methods-pharmacological treatments: there appear to be large differences in concentrations chosen to treat MDCK versus MEF cells - can the authors comment on these choices and show that the enzymes are indeed inhibited at the indicated concentrations?

(optional): it would be interesting to include a gamma-tubulin staining on the cilium prep to see if there is indeed a presence of the basal body as suggested by the proteomics data.

There are many spelling mistakes and inconsistencies throughout the manuscript and its figures (mix of French and English for example) so careful proofreading would be warranted. Moreover, there are many mentionings of 'Hedgehog defects' or 'Hedgehog-linked', where in fact it is a defect in or link to the Hedgehog pathway, not the protein itself. This should be corrected.

Significance

The study of ciliary membrane composition is highly relevant to understand signal transduction in health and disease. As such, the topic of this manuscript is significant and timely. However, as indicated above, there are limitations to this study, most notably the comparison of ciliary membrane versus all cellular membranes (rather than the plasma membrane), which weakens the conclusions that can be drawn. Moreover, cell-type dependency should be more thoroughly addressed. There certainly is a methodological advance in the form of cilia isolation from MDCK cells, however, it is unclear how broadly applicable this is to other mammalian cell types.

"Story as theory" - not just data, but a way of knowing

Students who aren't able to "master" code-switching as easily and conform to SAE won't excel the way other students do thus merging linguistic segregation and physical segregation.

https://reddit.com/r/typewriters/comments/1p42tr1/typewriter_ribbon/

It's a small metal ring/hub that fits onto the ribbon spindle. You can call around to repair shops for replacements (which may be the cheapest route) https://site.xavier.edu/polt/typewriters/tw-repair.html. Ribbons Unlimited https://ribbonsunlimited.com also sells these hubs with ribbon attached, but it's more expensive to do this, but once you've got them, you can buy ribbon by itself for much cheaper in the future and just wind the new ribbon onto existing spool hubs.

Here's some useful videos which might help you out: - https://www.youtube.com/watch?v=iTFM54VKKc4 - https://www.youtube.com/watch?v=xWQTa4b7jPs (This one has some advice about using a Remington without the spools.)

English is the second language in the country?

Funny. Cryptographers club held elections, but cannot access results as one of the three keys needed to see results was lost by one of the people involved. They did not design for human failure / lapses in operational precision. Typical. Vgl the cartoon with laptop w unbreakable login and person taking a bat to the one who knows the login.

Yes! key part of social filtering. Recommendations and source, in ones network is a key piece of metadata. I think it's not just likable but necessary.

Passport show expertise

Jorge Arango talks about his writing process. He actually co-authored a book on Information Architecture in 2015. This vid more about his latest. uses lots of paper notebooks Mentions 3 (obvious) phases in his non-fiction writing research structuring writing Says all three req diff tools. (he uses Obsidian f research)

Stage 1 research, vague idea about what topic, (s paper notebooks, index/sequence them) His book duly noted is on this phase.

Stage 2 structuring. mistake to go directly to writing. (vgl [[A System for Writing by Bob Doto]] ) Mentions author Robert Caro who had book structure on his wall story book like, vgl what I do when writing reports w wall of post its for structure. Limitation is size of wall. But physcial movement helpt. He does this type of wall in [[Tinderbox]] !!!! canvas, with the sticky notes having metadata. His chapter and heading structure emerges from it! Prevents getting lost in the details. Shows him what is missing too (looping back to research phase sometimes). It's not writing but getting a sense of the narrative flow of the entire thing. Seems like outlining of talks, but a book is bigger and thus the outlining is more filled out with links to material

What question would a reader have entering chapter 2 after reading chapter 1, and go from there. Has opening story/anecdote for each chapter. Mwah. Uses the story board view like how the periodic table suggested the existence of atoms that had not been discovered yet. Dmitri Mendleev.

Stage 3 writing After structuring the writing tools come into play. He used Scrivener, avoiding having a monolithic text. Now Ulysses, in markdown. Uses word count targets in these tools for sections/chapters

set up supportive environments for each pahse structure first but keep flexible, don't make it a linear process, but structure ulnocks the writing swith modalities - walking, free form in [[Tinderbox]] or another tool, to avoid getting stuck.

Lymph isn’t actively pumped by the heart but due to pressure gradient caused by skeletal muscle contraction and breathing. This pressure gradient causes the vessels to open

Recognizing how your environment affects your emotions allows you to make small adjustments or temporary changes to test whether a bigger shift is needed, but if altering your surroundings or relationships isn't enough, professional treatment may still be necessary.

Sometimes, when cultures or values are not shared between people, one can feel isolated and even depressed. But sometimes, this differences can also make one more aware and accepting.

I think this sentence is really strong and it connect the topic of hip-hop to the world and the people in it, but also shows how hip-hop is an amalgamation of different cultures and meanings.

the term "Dusty feet" philosophers might be an odd phrase but it's meant to represent the discovery of knowledge and insight from places that you might not expect. and in a way you can almost look at it the same way Ashanti Young explains code meshing, the "Dusty feet" philosopher is code meshing in a way, for example, African American Standard (AASE) English might look odd to someone who was taught American standard English (ASE) for years might looks at AASE and think there doing it wrong but grammatically and structurally they both follow the same rules and are both just as good, much like a "Dusty foot philosopher" who might look rough on the outside but is well educated and just as good as any other person.

Overall, gender didn't significantly influence restoration (H1 not supported), but juniors (H2 supported) and environmental majors (H3 partially supported) showed notably stronger physiological and psychological recovery from natural landscapes than freshmen and non-majors.

Gender and grade level had no effect on systolic BP recovery. The only major-related difference was that landscape/environmental majors showed a significantly larger SBP reduction than non-environment majors when viewing desert landscapes, but not for any other landscape type.

This doesn't seem to me to be a tiny event at all, but I see what they mean. The appearance of these presses opening up possibilities that were not even considered before, which is exciting.

I found out that apparently a punctum is "a small, distinct point," or according to Oxford Reference "A term used by Barthes to refer to an incidental but personally poignant detail in a photograph which ‘pierces’ or ‘pricks’ a particular viewer, constituting a private meaning unrelated to any cultural code." I like this a lot as a press name!

Reiterating point above but this is highly interesting and aligns with what were thinking of talking about

This shows a major concern: AI-generated advice can appear correct but actually mislead writers, which is why human judgment remains central in ethical AI use.

"Issues with AI assisted writing" margin note Usefulness vs. risk: AI can help, but only if humans critically evaluate and revise the content.

Medical context: These issues are especially serious in healthcare writing, where misinformation could cause harm.

Citation danger: AI is weakest at references, with extremely high error/fabrication rates.

Ethical responsibility: Humans remain fully accountable for verifying accuracy and ensuring originality.

AI can sound confident even when it is completely wrong. This is especially dangerous in medical writing, where accuracy is essential.

"What do the journals and publishers say?" Margin notes: Hybrid research approach: Authors combine literature search + ChatGPT to gather initial perspectives. Shows real-world use of AI in research.

Publishers’ priorities: Integrity, ethical practice, and preventing misconduct shape AI guidelines.

Central principle = transparency: Full disclosure of AI use is essential; hiding it is unethical.

AI ≠ author: AI can create content but cannot take accountability → cannot qualify as an author.

Human creativity still primary: AI can support technical tasks but cannot replace intellectual contribution.

Evolving policies: AI guidelines are new and changing; scholars must stay informed.

This sentence reinforces one of the strongest uniform rules across journals: AI cannot be listed as an author. It can assist, but it cannot take responsibility or be accountable for the work.

This was most likely a prevalent thing in ancient times, as simply having the access to the tools to learn was the difference in social class

If English gets to a point where only people with advanced educational resources can fluently understand it, it is at risk of dissolving

Personally, I love this; Image annotations.

This can be used as an effective analysis tool. Visual stimulus is powerful and for many individuals constitutes a deeper connection to fundamental learning. Balanced learning across the three basic modes; written, auditory and visual is implied in academics and the workplace but the reality is that one mode is dominant. Recognizing that mode and enhancing reaps far more advantage than forcing an inferior mode. @Byrnesz

im fine with you guys keeping these outputs but ideally they should go into some other nicer looking table

this output isn't awful but since you're reporting the findings already i would say there's no need for this

"Discussion" Margin Notes: Benefits: AI enhances efficiency and quality but is framed as a complement to human work.

Drawbacks/Risks: Potential for plagiarism, misuse, misinformation, and bias if ethical guidelines are ignored.

Relevancy to paper: Strong support for discussing both ethical obligations and practical applications of AI in writing.

This quote is saying that AI improves scientific writing but also introduces risks that require strong human oversight.

Reviewer #1 (Public review):

Summary:

In this study, participants completed two different tasks. A perceptual choice task in which they compared the sizes of pairs of items and a value-different task in which they identified the higher value option among pairs of items with the two tasks involving the same stimuli. Based on previous fMRI research, the authors sought to determine whether the superior frontal sulcus (SFS) is involved in both perceptual and value-based decisions or just one or the other. Initial fMRI analyses were devised to isolate brain regions that were activated for both types of choices and also regions that were unique to each. Transcranial magnetic stimulation was applied to the SFS in between fMRI sessions and it was found to lead to a significant decrease in accuracy and RT on the perceptual choice task but only a decrease in RT on the value-different task. Hierarchical drift diffusion modelling of the data indicated that the TMS had led to a lowering of decision boundaries in the perceptual task and a lower of non-decision times on the value-based task. Additional analyses show that SFS covaries with model derived estimates of cumulative evidence, that this relationship is weakened by TMS.

Strengths:

The paper has many strengths, including the rigorous multi-pronged approach of causal manipulation, fMRI and computational modelling, which offers a fresh perspective on the neural drivers of decision making. Some additional strengths include the careful paradigm design, which ensured that the two types of tasks were matched for their perceptual content while orthogonalizing trial-to-trial variations in choice difficulty. The paper also lays out a number of specific hypotheses at the outset regarding the behavioural outcomes that are tied to decision model parameters and well justified.

Weaknesses:

In my previous comments (1.3.1 and 1.3.2) I noted that key results could be potentially explained by cTBS leading to faster perceptual decision making in both the perceptual and value-based tasks. The authors responded that if this were the case then we would expect either a reduction in NDT in both tasks or a reduction in decision boundaries in both tasks (whereas they observed a lowering of boundaries in the perceptual task and a shortening of NDT in the value task). I disagree with this statement. First, it is important to note that the perceptual decision that must be completed before the value-based choice process can even be initiated (i.e. the identification of the two stimuli) is no less trivial than that involved in the perceptual choice task (comparison of stimulus size). Given that the perceptual choice must be completed before the value comparison can begin, it would be expected that the model would capture any variations in RT due to the perceptual choice in the NDT parameter and not as the authors suggest in the bound or drift rate parameters since they are designed to account for the strength and final quantity of value evidence specifically. If, in fact, cTBS causes a general lowering of decision boundaries for perceptual decisions (and hence speeding of RTs) then it would be predicted that this would manifest as a short NDT in the value task model, which is what the authors see.

Reviewer #2 (Public review):

Summary:

The authors set out to test whether a TMS-induced reduction in excitability of the left Superior Frontal Sulcus influenced evidence integration in perceptual and value-based decisions. They directly compared behaviour-including fits to a computational decision process model---and fMRI pre and post TMS in one of each type of decision-making task. Their goal was to test domain-specific theories of the prefrontal cortex by examining whether the proposed role of the SFS in evidence integration was selective for perceptual but not value-based evidence.

Strengths:

The paper presents multiple credible sources of evidence for the role of the left SFS in perceptual decision making, finding similar mechanisms to prior literature and a nuanced discussion of where they diverge from prior findings. The value-based and perceptual decision-making tasks were carefully matched in terms of stimulus display and motor response, making their comparison credible.

Weaknesses:

-I was confused about the model specification in terms of the relationship between evidence level and drift rate. While the methods (and e.g. supplementary figure 3) specify a linear relationship between evidence level and drift rate, suggesting, unless I misunderstood, that only a single drift rate parameter (kappa) is fit. However, the drift rate parameter estimates in the supplementary tables (and response to reviewers) do not scale linearly with evidence level.

-The fit quality for the value-based decision task is not as good as that for the PDM, and this would be worth commenting on in the paper.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public Review):

Summary:

In this study, participants completed two different tasks. A perceptual choice task in which they compared the sizes of pairs of items and a value-different task in which they identified the higher value option among pairs of items with the two tasks involving the same stimuli. Based on previous fMRI research, the authors sought to determine whether the superior frontal sulcus (SFS) is involved in both perceptual and value-based decisions or just one or the other. Initial fMRI analyses were devised to isolate brain regions that were activated for both types of choices and also regions that were unique to each. Transcranial magnetic stimulation was applied to the SFS in between fMRI sessions and it was found to lead to a significant decrease in accuracy and RT on the perceptual choice task but only a decrease in RT on the value-different task. Hierarchical drift-diffusion modelling of the data indicated that the TMS had led to a lowering of decision boundaries in the perceptual task and a lower of non-decision times on the value-based task. Additional analyses show that SFS covaries with model-derived estimates of cumulative evidence and that this relationship is weakened by TMS.

Strengths:

The paper has many strengths including the rigorous multi-pronged approach of causal manipulation, fMRI and computational modelling which offers a fresh perspective on the neural drivers of decision making. Some additional strengths include the careful paradigm design which ensured that the two types of tasks were matched for their perceptual content while orthogonalizing trial-to-trial variations in choice difficulty. The paper also lays out a number of specific hypotheses at the outset regarding the behavioural outcomes that are tied to decision model parameters and are well justified.

Weaknesses:

(1.1) Unless I have missed it, the SFS does not actually appear in the list of brain areas significantly activated by the perceptual and value tasks in Supplementary Tables 1 and 2. Its presence or absence from the list of significant activations is not mentioned by the authors when outlining these results in the main text. What are we to make of the fact that it is not showing significant activation in these initial analyses?

You are right that the left SFS does not appear in our initial task-level contrasts. Those first analyses were deliberately agnostic to evidence accumulation (i.e., average BOLD by task, irrespective of trial-by-trial evidence). Consistent with prior work, SFS emerges only when we model the parametric variation in accumulated perceptual evidence.

Accordingly, we ran a second-level GLM that included trial-wise accumulated evidence (aE) as a parametric modulator. In that analysis, the left SFS shows significant aE-related activity specifically during perceptual decisions, but not during value-based decisions (SVC in a 10-mm sphere around x = −24, y = 24, z = 36).

To avoid confusion, we now:

(i) explicitly separate and label the two analysis levels in the Results; (ii) state up front that SFS is not expected to appear in the task-average contrast; and (iii) add a short pointer that SFS appears once aE is included as a parametric modulator. We also edited Methods to spell out precisely how aE is constructed and entered into GLM2. This should make the logic of the two-stage analysis clearer and aligns the manuscript with the literature where SFS typically emerges only in parametric evidence models.

(1.2) The value difference task also requires identification of the stimuli, and therefore perceptual decision-making. In light of this, the initial fMRI analyses do not seem terribly informative for the present purposes as areas that are activated for both types of tasks could conceivably be specifically supporting perceptual decision-making only. I would have thought brain areas that are playing a particular role in evidence accumulation would be best identified based on whether their BOLD response scaled with evidence strength in each condition which would make it more likely that areas particular to each type of choice can be identified. The rationale for the authors' approach could be better justified.

We agree that both tasks require early sensory identification of the items, but the decision-relevant evidence differs by design (size difference vs. value difference), and our modelling is targeted at the evidence integration stage rather than initial identification.

To address your concern empirically, we: (i) added session-wise plots of mean RTs showing a general speed-up across the experiment (now in the Supplement); (ii) fit a hierarchical DDM to jointly explain accuracy and RT. The DDM dissociates decision time (evidence integration) from non-decision time (encoding/response execution).

After cTBS, perceptual decisions show a selective reduction of the decision boundary (lower accuracy, faster RTs; no drift-rate change), whereas value-based decisions show no change to boundary/drift but a decrease in non-decision time, consistent with faster sensorimotor processing or task familiarity. Thus, the TMS effect in SFS is specific to the criterion for perceptual evidence accumulation, while the RT speed-up in the value task reflects decision-irrelevant processes. We now state this explicitly in the Results and add the RT-by-run figure for transparency.

(1.2.1) The value difference task also requires identification of the stimuli, and therefore perceptual decision-making. In light of this, the initial fMRI analyses do not seem terribly informative for the present purposes as areas that are activated for both types of tasks could conceivably be specifically supporting perceptual decision-making only.

Thank you for prompting this clarification.

The key point is what changes with cTBS. If SFS supported generic identification, we would expect parallel cTBS effects on drift rate (or boundary) in both tasks. Instead, we find: (a) boundary decreases selectively in perceptual decisions (consistent with SFS setting the amount of perceptual evidence required), and (b) non-decision time decreases selectively in the value task (consistent with speed-ups in encoding/response stages). Moreover, trial-by-trial SFS BOLD predicts perceptual accuracy (controlling for evidence), and neural-DDM model comparison shows SFS activity modulates boundary, not drift, during perceptual choices.

Together, these converging behavioral, computational, and neural results argue that SFS specifically supports the criterion for perceptual evidence accumulation rather than generic visual identification.

(1.2.2) I would have thought brain areas that are playing a particular role in evidence accumulation would be best identified based on whether their BOLD response scaled with evidence strength in each condition which would make it more likely that areas particular to each type of choice can be identified. The rationale for the authors' approach could be better justified.

We now more explicitly justify the two-level fMRI approach. The task-average contrast addresses which networks are generally more engaged by each domain (e.g., posterior parietal for PDM; vmPFC/PCC for VDM), given identical stimuli and motor outputs. This complements, but does not substitute for, the parametric evidence analysis, which is where one expects accumulation-related regions such as SFS to emerge. We added text clarifying that the first analysis establishes domain-specific recruitment at the task level, whereas the second isolates evidence-dependent signals (aE) and reveals that left SFS tracks accumulated evidence only for perceptual choices. We also added explicit references to the literature using similar two-step logic and noted that SFS typically appears only in parametric evidence models.

(1.3) TMS led to reductions in RT in the value-difference as well as the perceptual choice task. DDM modelling indicated that in the case of the value task, the effect was attributable to reduced non-decision time which the authors attribute to task learning. The reasoning here is a little unclear.

(1.3.1) Comment: If task learning is the cause, then why are similar non-decision time effects not observed in the perceptual choice task?

Great point. The DDM addresses exactly this: RT comprises decision time (DT) plus non-decision time (nDT). With cTBS, PDM shows reduced DT (via a lower boundary) but stable nDT; VDM shows reduced nDT with no change to boundary/drift. Hence, the superficially similar RT speed-ups in both tasks are explained by different latent processes: decision-relevant in PDM (lower criterion → faster decisions, lower accuracy) and decision-irrelevant in VDM (faster encoding/response). We added explicit language and a supplemental figure showing RT across runs, and we clarified in the text that only the PDM speed-up reflects a change to evidence integration.

(1.3.2) Given that the value-task actually requires perceptual decision-making, is it not possible that SFS disruption impacted the speed with which the items could be identified, hence delaying the onset of the value-comparison choice?

We agree there is a brief perceptual encoding phase at the start of both tasks. If cTBS impaired visual identification per se, we would expect longer nDT in both tasks or a decrease in drift rate. Instead, nDT decreases in the value task and is unchanged in the perceptual task; drift is unchanged in both. Thus, cTBS over SFS does not slow identification; rather, it lowers the criterion for perceptual accumulation (PDM) and, separately, we observe faster non-decision components in VDM (likely familiarity or motor preparation). We added a clarifying sentence noting that item identification was easy and highly overlearned (static, large food pictures), and we cite that nDT is the appropriate locus for identification effects in the DDM framework; our data do not show the pattern expected of impaired identification.

(1.4) The sample size is relatively small. The authors state that 20 subjects is 'in the acceptable range' but it is not clear what is meant by this.

We have clarified what we mean and provided citations. The sample (n = 20) matches or exceeds many prior causal TMS/fMRI studies targeting perceptual decision circuitry (e.g., Philiastides et al., 2011; Rahnev et al., 2016; Jackson et al., 2021; van der Plas et al., 2021; Murd et al., 2021). Importantly, we (i) use within-subject, pre/post cTBS differences-in-differences with matched tasks; (ii) estimate hierarchical models that borrow strength across participants; and (iii) converge across behavior, latent parameters, regional BOLD, and connectivity. We now replace the vague phrase with a concrete statement and references, and we report precision (HDIs/SEs) for all main effects.

Reviewer #2 (Public Review):

Summary:

The authors set out to test whether a TMS-induced reduction in excitability of the left Superior Frontal Sulcus influenced evidence integration in perceptual and value-based decisions. They directly compared behaviour - including fits to a computational decision process model - and fMRI pre and post-TMS in one of each type of decision-making task. Their goal was to test domain-specific theories of the prefrontal cortex by examining whether the proposed role of the SFS in evidence integration was selective for perceptual but not value-based evidence.

Strengths:

The paper presents multiple credible sources of evidence for the role of the left SFS in perceptual decision-making, finding similar mechanisms to prior literature and a nuanced discussion of where they diverge from prior findings. The value-based and perceptual decision-making tasks were carefully matched in terms of stimulus display and motor response, making their comparison credible.

Weaknesses:

(2.1) More information on the task and details of the behavioural modelling would be helpful for interpreting the results.

Thank you for this request for clarity. In the revision we explicitly state, up front, how the two tasks differ and how the modelling maps onto those differences.

(1) Task separability and “evidence.” We now define task-relevant evidence as size difference (SD) for perceptual decisions (PDM) and value difference (VD) for value-based decisions (VDM). Stimuli and motor mappings are identical across tasks; only the evidence to be integrated changes.

(2) Behavioural separability that mirrors task design. As reported, mixed-effects regressions show PDM accuracy increases with SD (β=0.560, p<0.001) but not VD (β=0.023, p=0.178), and PDM RTs shorten with SD (β=−0.057, p<0.001) but not VD (β=0.002, p=0.281). Conversely, VDM accuracy increases with VD (β=0.249, p<0.001) but not SD (β=0.005, p=0.826), and VDM RTs shorten with VD (β=−0.016, p=0.011) but not SD (β=−0.003, p=0.419).

(3 How the HDDM reflects this. The hierarchical DDM fits the joint accuracy–RT distributions with task-specific evidence (SD or VD) as the predictor of drift. The model separates decision time from non-decision time (nDT), which is essential for interpreting the different RT patterns across tasks without assuming differences in the accumulation process when accuracy is unchanged.

These clarifications are integrated in the Methods (Experimental paradigm; HDDM) and in Results (“Behaviour: validity of task-relevant pre-requisites” and “Modelling: faster RTs during value-based decisions is related to non-decision-related sensorimotor processes”).

(2.2) The evidence for a choice and 'accuracy' of that choice in both tasks was determined by a rating task that was done in advance of the main testing blocks (twice for each stimulus). For the perceptual decisions, this involved asking participants to quantify a size metric for the stimuli, but the veracity of these ratings was not reported, nor was the consistency of the value-based ones. It is my understanding that the size ratings were used to define the amount of perceptual evidence in a trial, rather than the true size differences, and without seeing more data the reliability of this approach is unclear. More concerning was the effect of 'evidence level' on behaviour in the value-based task (Figure 3a). While the 'proportion correct' increases monotonically with the evidence level for the perceptual decisions, for the value-based task it increases from the lowest evidence level and then appears to plateau at just above 80%. This difference in behaviour between the two tasks brings into question the validity of the DDM which is used to fit the data, which assumes that the drift rate increases linearly in proportion to the level of evidence.

We thank the reviewer for raising these concerns, and we address each of them point by point:

2.2.1. Comment: It is my understanding that the size ratings were used to define the amount of perceptual evidence in a trial, rather than the true size differences, and without seeing more data the reliability of this approach is unclear.

That is correct—we used participants’ area/size ratings to construct perceptual evidence (SD).

To validate this choice, we compared those ratings against an objective image-based size measure (proportion of non-black pixels within the bounding box). As shown in Author response image 3, perceptual size ratings are highly correlated with objective size across participants (Pearson r values predominantly ≈0.8 or higher; all p<0.001). Importantly, value ratings do not correlate with objective size (Author response image 2), confirming that the two rating scales capture distinct constructs. These checks support using participants’ size ratings as the participant-specific ground truth for defining SD in the PDM trials.

Author response image 1.

Objective size and value ratings are unrelated. Scatterplots show, for each participant, the correlation between objective image size (x-axis; proportion of non-black pixels within the item box) and value-based ratings (y-axis; 0–100 scale). Each dot is one food item (ratings averaged over the two value-rating repetitions). Across participants, value ratings do not track objective size, confirming that value and size are distinct constructs.

Author response image 2.

Perceptual size ratings closely track objective size. Scatterplots show, for each participant, the correlation between objective image size (x-axis) and perceptual area/size ratings (y-axis; 0–100 scale). Each dot is one food item (ratings averaged over the two perceptual ratings). Perceptual ratings are strongly correlated with objective size for nearly all participants (see main text), validating the use of these ratings to construct size-difference evidence (SD).

(2.2.2) More concerning was the effect of 'evidence level' on behaviour in the value-based task (Figure 3a). While the 'proportion correct' increases monotonically with the evidence level for the perceptual decisions, for the value-based task it increases from the lowest evidence level and then appears to plateau at just above 80%. This difference in behaviour between the two tasks brings into question the validity of the DDM which is used to fit the data, which assumes that the drift rate increases linearly in proportion to the level of evidence.

We agree that accuracy appears to asymptote in VDM, but the DDM fits indicate that the drift rate still increases monotonically with evidence in both tasks. In Supplementary figure 11, drift (δ) rises across the four evidence levels for PDM and for VDM (panels showing all data and pre/post-TMS). The apparent plateau in proportion correct during VDM reflects higher choice variability at stronger preference differences, not a failure of the drift–evidence mapping. Crucially, the model captures both the accuracy patterns and the RT distributions (see posterior predictive checks in Supplementary figures 11-16), indicating that a monotonic evidence–drift relation is sufficient to account for the data in each task.

Author response image 3.

HDDM parameters by evidence level. Group-level posterior means (± posterior SD) for drift (δ), boundary (α), and non-decision time (τ) across the four evidence levels, shown (a) collapsed across TMS sessions, (b) for PDM (blue) pre- vs post-TMS (light vs dark), and (c) for VDM (orange) pre- vs post-TMS. Crucially, drift increases monotonically with evidence in both tasks, while TMS selectively lowers α in PDM and reduces τ in VDM (see Supplementary Tables for numerical estimates).

(2.3) The paper provides very little information on the model fits (no parameter estimates, goodness of fit values or simulated behavioural predictions). The paper finds that TMS reduced the decision bound for perceptual decisions but only affected non-decision time for value-based decisions. It would aid the interpretation of this finding if the relative reliability of the fits for the two tasks was presented.

We appreciate the suggestion and have made the quantitative fit information explicit:

(1) Parameter estimates. Group-level means/SDs for drift (δ), boundary (α), and nDT (τ) are reported for PDM and VDM overall, by evidence level, pre- vs post-TMS, and per subject (see Supplementary Tables 8-11).

(2) Goodness of fit and predictive adequacy. DIC values accompany each fit in the tables. Posterior predictive checks demonstrate close correspondence between simulated and observed accuracy and RT distributions overall, by evidence level, and across subjects (Supplementary Figures 11-16).

Together, these materials document that the HDDM provides reliable fits in both tasks and accurately recovers the qualitative and quantitative patterns that underlie our inferences (reduced α for PDM only; selective τ reduction in VDM).

(2.4) Behaviourally, the perceptual task produced decreased response times and accuracy post-TMS, consistent with a reduced bound and consistent with some prior literature. Based on the results of the computational modelling, the authors conclude that RT differences in the value-based task are due to task-related learning, while those in the perceptual task are 'decision relevant'. It is not fully clear why there would be such significantly greater task-related learning in the value-based task relative to the perceptual one. And if such learning is occurring, could it potentially also tend to increase the consistency of choices, thereby counteracting any possible TMS-induced reduction of consistency?

Thank you for pointing out the need for a clearer framing. We have removed the speculative label “task-related learning” and now describe the pattern strictly in terms of the HDDM decomposition and neural results already reported:

(1) VDM: Post-TMS RTs are faster while accuracy is unchanged. The HDDM attributes this to a selective reduction in non-decision time (τ), with no change in decision-relevant parameters (α, δ) for VDM (see Supplementary Figure 11 and Supplementary Tables). Consistent with this, left SFS BOLD is not reduced for VDM, and trialwise SFS activity does not predict VDM accuracy—both observations argue against a change in VDM decision formation within left SFS.

(2) PDM: Post-TMS accuracy decreases and RTs shorten, which the HDDM captures as a lower decision boundary (α) with no change in drift (δ). Here, left SFS BOLD scales with accumulated evidence and decreases post-TMS, and trialwise SFS activity predicts PDM accuracy, all consistent with a decision-relevant effect in PDM.

Regarding the possibility that faster VDM RTs should increase choice consistency: empirically, consistency did not change in VDM, and the HDDM finds no decision-parameter shifts there. Thus, there is no hidden counteracting increase in VDM accuracy that could mask a TMS effect—the absence of a VDM accuracy change is itself informative and aligns with the modelling and fMRI.

Reviewer #3 (Public Review):

Summary:

Garcia et al., investigated whether the human left superior frontal sulcus (SFS) is involved in integrating evidence for decisions across either perceptual and/or value-based decision-making. Specifically, they had 20 participants perform two decision-making tasks (with matched stimuli and motor responses) in an fMRI scanner both before and after they received continuous theta burst transcranial magnetic stimulation (TMS) of the left SFS. The stimulation thought to decrease neural activity in the targeted region, led to reduced accuracy on the perceptual decision task only. The pattern of results across both model-free and model-based (Drift diffusion model) behavioural and fMRI analyses suggests that the left SLS plays a critical role in perceptual decisions only, with no equivalent effects found for value-based decisions. The DDM-based analyses revealed that the role of the left SLS in perceptual evidence accumulation is likely to be one of decision boundary setting. Hence the authors conclude that the left SFS plays a domain-specific causal role in the accumulation of evidence for perceptual decisions. These results are likely to add importance to the literature regarding the neural correlates of decision-making.

Strengths:

The use of TMS strengthens the evidence for the left SFS playing a causal role in the evidence accumulation process. By combining TMS with fMRI and advanced computational modelling of behaviour, the authors go beyond previous correlational studies in the field and provide converging behavioural, computational, and neural evidence of the specific role that the left SFS may play.

Sophisticated and rigorous analysis approaches are used throughout.

Weaknesses:

(3.1) Though the stimuli and motor responses were equalised between the perception and value-based decision tasks, reaction times (according to Figure 1) and potential difficulty (Figure 2) were not matched. Hence, differences in task difficulty might represent an alternative explanation for the effects being specific to the perception task rather than domain-specificity per se.

We agree that RTs cannot be matched a priori, and we did not intend them to be. Instead, we equated the inputs to the decision process and verified that each task relied exclusively on its task-relevant evidence. As reported in Results—Behaviour: validity of task-relevant pre-requisites (Fig. 1b–c), accuracy and RTs vary monotonically with the appropriate evidence regressor (SD for PDM; VD for VDM), with no effect of the task-irrelevant regressor. This separability check addresses differences in baseline RTs by showing that, for both tasks, behaviour tracks evidence as designed.

To rule out a generic difficulty account of the TMS effect, we relied on the within-subject differences-in-differences (DID) framework described in Methods (Differences-in-differences). The key Task × TMS interaction compares the pre→post change in PDM with the pre→post change in VDM while controlling for trialwise evidence and RT covariates. Any time-on-task or unspecific difficulty drift shared by both tasks is subtracted out by this contrast. Using this specification, TMS selectively reduced accuracy for PDM but not VDM (Fig. 3a; Supplementary Fig. 2a,c; Supplementary Tables 5–7).

Finally, the hierarchical DDM (already in the paper) dissociates latent mechanisms. The post-TMS boundary reduction appears only in PDM, whereas VDM shows a change in non-decision time without a decision-relevant parameter change (Fig. 3c; Supplementary Figs. 4–5). If unmatched difficulty were the sole driver, we would expect parallel effects across tasks, which we do not observe.

(3.2) No within- or between-participants sham/control TMS condition was employed. This would have strengthened the inference that the apparent TMS effects on behavioural and neural measures can truly be attributed to the left SFS stimulation and not to non-specific peripheral stimulation and/or time-on-task effects.

We agree that a sham/control condition would further strengthen causal attribution and note this as a limitation. In mitigation, our design incorporates several safeguards already reported in the manuscript:

· Within-subject pre/post with alternating task blocks and DID modelling (Methods) to difference out non-specific time-on-task effects.

· Task specificity across levels of analysis: behaviour (PDM accuracy reduction only), computational (boundary reduction only in PDM; no drift change), BOLD (reduced left-SFS accumulated-evidence signal for PDM but not VDM; Fig. 4a–c), and functional coupling (SFS–occipital PPI increase during PDM only; Fig. 5).

· Matched stimuli and motor outputs across tasks, so any peripheral sensations or general arousal effects should have influenced both tasks similarly; they did not.

Together, these converging task-selective effects reduce the likelihood that the results reflect non-specific stimulation or time-on-task. We will add an explicit statement in the Limitations noting the absence of sham/control and outlining it as a priority for future work.

(3.3) No a priori power analysis is presented.

We appreciate this point. Our sample size (n = 20) matched prior causal TMS and combined TMS–fMRI studies using similar paradigms and analyses (e.g., Philiastides et al., 2011; Rahnev et al., 2016; Jackson et al., 2021; van der Plas et al., 2021; Murd et al., 2021), and was chosen a priori on that basis and the practical constraints of cTBS + fMRI. The within-subject DID approach and hierarchical modelling further improve efficiency by leveraging all trials.

To address the reviewer’s request for transparency, we will (i) state this rationale in Methods—Participants, and (ii) ensure that all primary effects are reported with 95% CIs or posterior probabilities (already provided for the HDDM as pmcmcp_{\mathrm{mcmc}}pmcmc). We also note that the design was sensitive enough to detect RT changes in both tasks and a selective accuracy change in PDM, arguing against a blanket lack of power as an explanation for null VDM accuracy effects. We will nevertheless flag the absence of a formal prospective power analysis in the Limitations.

Recommendations for the Authors:

Reviewer #1 (Recommendations For The Authors):

Some important elements of the methods are missing. How was the site for targeting the SFS with TMS identified? The methods described how M1 was located but not SFS.

Thank you for catching this omission. In the revised Methods we explicitly describe how the left SFS target was localized. Briefly, we used each participant’s T1-weighted anatomical scan and frameless neuronavigation to place a 10-mm sphere at the a priori MNI coordinates (x = −24, y = 24, z = 36) derived from prior work (Heekeren et al., 2004; Philiastides et al., 2011). This sphere was transformed to native space for each participant. The coil was positioned tangentially with the handle pointing posterior-lateral, and coil placement was continuously monitored with neuronavigation throughout stimulation. (All of these procedures mirror what we already report for M1 and are now stated for SFS as well.)

Where to revise the manuscript:

Methods → Stimulation protocol. After the first sentence naming cTBS, insert:<br /> “The left SFS target was localized on each participant’s T1-weighted anatomical image using frameless neuronavigation. A 10-mm radius sphere was centered at the a priori MNI coordinates x = −24, y = 24, z = 36 (Heekeren et al., 2004; Philiastides et al., 2011), then transformed to native space. The MR-compatible figure-of-eight coil was positioned tangentially over the target with the handle oriented posterior-laterally, and its position was tracked and maintained with neuronavigation during stimulation.”

It is not clear how participants were instructed that they should perform the value-difference task. Were they told that they should choose based on their original item value ratings or was it left up to them?

We agree the instruction should be explicit. Participants were told_: “In value-based blocks, choose the item you would prefer to eat at the end of the experiment.”_ They were informed that one VDM trial would be randomly selected for actual consumption, ensuring incentive-compatibility. We did not ask them to recall or follow their earlier ratings; those ratings were used only to construct evidence (value difference) and to define choice consistency offline.

Where to revise the manuscript:

Methods → Experimental paradigm.

Add a sentence to the VDM instruction paragraph:

“In value-based (LIKE) blocks, participants were instructed to choose the item they would prefer to consume at the end of the experiment; one VDM trial was randomly selected and implemented, making choices incentive-compatible. Prior ratings were used solely to construct value-difference evidence and to score choice consistency; participants were not asked to recall or match their earlier ratings.”

Line 86 Introduction, some previous studies were conducted on animals. Why it is problematic that the studies were conducted in animals is not stated. I assume the authors mean that we do not know if their findings will translate to the human brain? I think in fairness to those working with animals it might be worth an extra sentence to briefly expand on this point.

We appreciate this and will clarify that animal work is invaluable for circuit-level causality, but species differences and putative non-homologous areas (e.g., human SFS vs. rodent FOF) limit direct translation. Our point is not that animal studies are problematic, but that establishing causal roles in humans remains necessary.

Revision:

Introduction (paragraph discussing prior animal work). Replace the current sentence beginning “However, prior studies were largely correlational”

“Animal studies provide critical causal insights, yet direct translation to humans can be limited by species-specific anatomy and potential non-homologies (e.g., human SFS vs. frontal orienting fields in rodents). Therefore, establishing causal contributions in the human brain remains essential.”

Line 100-101: "or whether its involvement is peripheral and merely functionally supporting a larger system" - it is not clear what you mean by 'supporting a larger system'

We meant that observed SFS activity might reflect upstream/downstream support processes (e.g., attentional control or working-memory maintenance) rather than the computation of evidence accumulation itself. We have rephrased to avoid ambiguity.

Revision:

Introduction. Replace the phrase with:

“or whether its observed activity reflects upstream or downstream support processes (e.g., attention or working-memory maintenance) rather than the accumulation computation per se.”

The authors do have to make certain assumptions about the BOLD patterns that would be expected of an evidence accumulation region. These assumptions are reasonable and have been adopted in several previous neuroimaging studies. Nevertheless, it should be acknowledged that alternative possibilities exist and this is an inevitable limitation of using fMRI to study decision making. For example, if it turns out that participants collapse their boundaries as time elapses, then the assumption that trials with weaker evidence should have larger BOLD responses may not hold - the effect of more prolonged activity could be cancelled out by the lower boundaries. Again, I think this is just a limitation that could be acknowledged in the Discussion, my opinion is that this is the best effort yet to identify choice-relevant regions with fMRI and the authors deserve much credit for their rigorous approach.

Agreed. We already ground our BOLD regressors in the DDM literature, but acknowledge that alternative mechanisms (e.g., time-dependent boundaries) can alter expected BOLD–evidence relations. We now add a short limitation paragraph stating this explicitly.

Revision:

Discussion (limitations paragraph). Add:

“Our fMRI inferences rest on model-based assumptions linking accumulated evidence to BOLD amplitude. Alternative mechanisms—such as time-dependent (collapsing) boundaries—could attenuate the prediction that weaker-evidence trials yield longer accumulation and larger BOLD signals. While our behavioural and neural results converge under the DDM framework, we acknowledge this as a general limitation of model-based fMRI.”

Reviewer #2 (Recommendations For The Authors):

Minor points

I suggest the proportion of missed trials should be reported.

Thank you for the suggestion. In our preprocessing we excluded trials with no response within the task’s response window and any trials failing a priori validity checks. Because non-response trials contain neither a choice nor an RT, they are not entered into the DDM fits or the fMRI GLMs and, by design, carry no weight in the reported results. To keep the focus on the data that informed all analyses, we now (i) state the trial-inclusion criteria explicitly and (ii) report the number of analysed (valid) trials per task and run. This conveys the effective sample size contributing to each condition without altering the analysis set.

Revision:

Methods → (at the end of “Experimental paradigm”): “Analyses were conducted on valid trials only, defined as trials with a registered response within the task’s response window and passing pre-specified validity checks; trials without a response were excluded and not analysed.”

Results → “Behaviour: validity of task-relevant pre-requisites” (add one sentence at the end of the first paragraph): “All behavioural and fMRI analyses were performed on valid trials only (see Methods for inclusion criteria).”

Figure 4 c is very confusing. Is the legend or caption backwards?

Thanks for flagging. We corrected the Figure 4c caption to match the colouring and contrasts used in the panel (perceptual = blue/green overlays; value-based = orange/red; ‘post–pre’ contrasts explicitly labeled). No data or analyses were changed, just the wording to remove ambiguity.

Revision:

Figure 4 caption (panel c sentence). Replace with:

“(c) Post–pre contrasts for the trialwise accumulated-evidence regressor show reduced left-SFS BOLD during perceptual decisions (green overlay), with a significantly stronger reduction for perceptual vs value-based decisions (blue overlay). No reduction is observed for value-based decisions.”

Even if not statistically significant it may be of interest to add the results for Value-based decision making on SFS in Supplementary Table 3.

Done. We now include the SFS small-volume results for VDM (trialwise accumulated-evidence regressor) alongside the PDM values in the same table, with exact peak, cluster size, and statistics.

Revision:

Supplementary Table 3 (title):

“Regions encoding trialwise accumulated evidence (parametric modulation) during perceptual and value-based decisions, including SFS SVC results for both tasks.”

Model comparisons: please explain how model complexity is accounted for.

We clarify that model evidence was compared using the Deviance Information Criterion (DIC), which penalizes model fit by an effective number of parameters (pD). Lower DIC indicates better out-of-sample predictive performance after accounting for model complexity.

Revision:

Methods → Hierarchical Bayesian neural-DDM (last paragraph). Add:

“Model comparison used the Deviance Information Criterion (DIC = D̄ + pD), where pD is the effective number of parameters; thus DIC penalizes model complexity. Lower DIC denotes better predictive accuracy after accounting for complexity.”

Reviewer #3 (Recommendations For The Authors):

The following issues would benefit from clarification in the manuscript:

- It is stated that "Our sample size is well within acceptable range, similar to that of previous TMS studies." The sample size being similar to previous studies does not mean it is within an acceptable range. Whether the sample size is acceptable or not depends on the expected effect size. It is perfectly possible that the previous studies cited were all underpowered. What implications might the lack of an a priori power analysis have for the interpretation of the results?

We agree and have revised our wording. We did not conduct an a priori power analysis. Instead, we relied on a within-participant design that typically yields higher sensitivity in TMS–fMRI settings and on convergence across behavioural, computational, and neural measures. We now acknowledge that the absence of formal power calculations limits claims about small effects (particularly for null findings in VDM), and we frame those null results cautiously.

Revision:

Discussion (limitations). Add:

“The within-participant design enhances statistical sensitivity, yet the absence of an a priori power analysis constrains our ability to rule out small effects, particularly for null results in VDM.”

- I was confused when trying to match the results described in the 'Behaviour: validity of task-relevant pre-requisites' section on page 6 to what is presented in Figure 1. Specifically, Figure 1C is cited 4 times but I believe two of these should be citing Figure 1B?

Thank you—this was a citation mix-up. The two places that referenced “Fig. 1C” but described accuracy should in fact point to Fig. 1B. We corrected both citations.

Revision:

Results → Behaviour: validity… Change the two incorrect “Fig. 1C” references (when describing accuracy) to “Fig. 1B”.

- Also, where is the 'SD' coefficient of -0.254 (p-value = 0.123) coming from in line 211? I can't match this to the figure.

This was a typographical error in an earlier draft. The correct coefficients are those shown in the figure and reported elsewhere in the text (evidence-specific effects: for PDM RTs, SD β = −0.057, p < 0.001; for VDM RTs, VD β = −0.016, p = 0.011; non-relevant evidence terms are n.s.). We removed the erroneous value.

Revision:

Results → Behaviour: validity… (sentence with −0.254). Delete the incorrect value and retain the evidence-specific coefficients consistent with Fig. 1B–C.

- It is reported that reaction times were significantly faster for the perceptual relative to the value-based decision task. Was overall accuracy also significantly different between the two tasks? It appears from Figure 3 that it might be, But I couldn't find this reported in the text.

To avoid conflating task with evidence composition, we did not emphasize between-task accuracy averages. Our primary tests examine evidence-specific effects and TMS-induced changes within task. For completeness, we now report descriptive mean accuracies by task and point readers to the figure panels that display accuracy as a function of evidence (which is the meaningful comparison in our matched-evidence design). We refrain from additional hypothesis testing here to keep the analyses aligned with our preregistered focus.

Revision:

Results → Behaviour: validity… Add:

“For completeness, group-mean accuracies by task are provided descriptively in Fig. 3a; inferential tests in the manuscript focus on evidence-specific effects and TMS-induced changes within task.”

This could be a good thing, and allowable in certain contexts. Marketing sites for example. Often brand wants to push a DS beyond its stated definitions, and as such, this 'abuse' of 'cn' could be considered acceptable practice in these bleeding-edge cases of marketing/brand expression

This article is a little outdated but as per my read through, the only aspect I have found that is truly 'out of date' is the way forms are implemented as that has been recently changed. The method mentioned in the article is still valid but being sunsetted as of the time I'm making this comment.

Starting from so-called 'Headless UI components' seems to me a 'no-brainer' especially when tools like ShadCN is not only built on top of tech that Agentic dev tools are familiar with, ShadCN itself is also something Agents (in my experience) are well versed in.

Great work overall! But still need some small changes to make it better.

I don't know what this part is doing, I assume you want to returns a matrix of p-values, but I don't think you need p-values in a matrix table. Cause I can tell from your plot, If p < .05, it show the correlation, but If p > .05, it won't show anything.

If your goal is to evaluate the relationships between all variables, it may be more informative to display the full correlation matrix without masking non-significant values. In that case, you can remove the significance filter so the plot shows every correlation.

if you want, you can add another layer "geom_jitter()", adds a small amount of random variation to the location of each point, so we can clearly visualizes data density.

(But maybe ask Dr.Shane before you add this)

This is the thesis. The nursery is the villain from this perspective. This Thesis also aligns with my own essay in terms of emotional detachment from the parents.

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

The manuscript by Yin and colleagues addresses a long-standing question in the field of cortical morphogenesis, regarding factors that determine differential cortical folding across species and individuals with cortical malformations. The authors present work based on a computational model of cortical folding evaluated alongside a physical model that makes use of gel swelling to investigate the role of a two-layer model for cortical morphogenesis. The study assesses these models against empirically derived cortical surfaces based on MRI data from ferret, macaque monkey, and human brains.

The manuscript is clearly written and presented, and the experimental work (physical gel modeling as well as numerical simulations) and analyses (subsequent morphometric evaluations) are conducted at the highest methodological standards. It constitutes an exemplary use of interdisciplinary approaches for addressing the question of cortical morphogenesis by bringing together well-tuned computational modeling with physical gel models. In addition, the comparative approaches used in this paper establish a foundation for broad-ranging future lines of work that investigate the impact of perturbations or abnormalities during cortical development.

The cross-species approach taken in this study is a major strength of the work. However, correspondence across the two methodologies did not appear to be equally consistent in predicting brain folding across all three species. The results presented in Figures 4 (and Figures S3 and S4) show broad correspondence in shape index and major sulci landmarks across all three species. Nevertheless, the results presented for the human brain lack the same degree of clear correspondence for the gel model results as observed in the macaque and ferret. While this study clearly establishes a strong foundation for comparative cortical anatomy across species and the impact of perturbations on individual morphogenesis, further work that fine-tunes physical modeling of complex morphologies, such as that of the human cortex, may help to further understand the factors that determine cortical functionalization and pathologies.

We thank the reviewer for positive opinions and helpful comments. Yes, the physical gel model of the human brain has a lower similarity index with the real brain. There are several reasons.

First, the highly convoluted human cortex has a few major folds (primary sulci) and a very large number of minor folds associated with secondary or tertiary sulci (on scales of order comparable to the cortical thickness), relative to the ferret and macaque cerebral cortex. In our gel model, the exact shapes, positions, and orientations of these minor folds are stochastic, which makes it hard to have a very high similarity index of the gel models when compared with the brain of a single individual.

Second, in real human brains, these minor folds evolve dynamically with age and show differences among individuals. In experiments with the gel brain, multiscale folds form and eventually disappear as the swelling progresses through the thickness. Our physical model results are snapshots during this dynamical process, which makes it hard to have a concrete one-to-one correspondence between the instantaneous shapes of the swelling gel and the growing human brain.

Third, the growth of the brain cortex is inhomogeneous in space and varying with time, whereas, in the gel model, swelling is relatively homogeneous.

We agree that further systematic work, based on our proposed methods, with more fine-tuned gel geometries and properties, might provide a deeper understanding of the relations between brain geometry, and growth-induced folds and their functionalization and pathologies. Further analysis of cortical pathologies using computational and physical gel models can be found in our companion paper (Choi et al., 2025), also published in eLife:

G. P. T. Choi, C. Liu, S. Yin, G. Séjourné, R. S. Smith, C. A. Walsh, L. Mahadevan, Biophysical basis for brain folding and misfolding patterns in ferrets and humans. eLife, 14, RP107141, 2025. doi:10.7554/eLife.107141

Reviewer# 2 (Public review):

This manuscript explores the mechanisms underlying cerebral cortical folding using a combination of physical modelling, computational simulations, and geometric morphometrics. The authors extend their prior work on human brain development (Tallinen et al., 2014; 2016) to a comparative framework involving three mammalian species: ferrets (Carnivora), macaques (Old World monkeys), and humans (Hominoidea). By integrating swelling gel experiments with mathematical differential growth models, they simulate sulcification instability and recapitulate key features of brain folding across species. The authors make commendable use of publicly available datasets to construct 3D models of fetal and neonatal brain surfaces: fetal macaque (ref. [26]), newborn ferret (ref. [11]), and fetal human (ref. [22]).

Using a combination of physical models and numerical simulations, the authors compare the resulting folding morphologies to real brain surfaces using morphometric analysis. Their results show qualitative and quantitative concordance with observed cortical folding patterns, supporting the view that differential tangential growth of the cortex relative to the subcortical substrate is sufficient to account for much of the diversity in cortical folding. This is a very important point in our field, and can be used in the teaching of medical students.

Brain folding remains a topic of ongoing debate. While some regard it as a critical specialization linked to higher cognitive function, others consider it an epiphenomenon of expansion and constrained geometry. This divergence was evident in discussions during the Strungmann Forum on cortical development (Silver¨ et al., 2019). Though folding abnormalities are reliable indicators of disrupted neurodevelopmental processes (e.g., neurogenesis, migration), their relationship to functional architecture remains unclear. Recent evidence suggests that the absolute number of neurons varies significantly with position-sulcus versus gyrus-with potential implications for local processing capacity (e.g., https://doi.org/10.1002/cne.25626). The field is thus in need of comparative, mechanistic studies like the present one.

This paper offers an elegant and timely contribution by combining gel-based morphogenesis, numerical modelling, and morphometric analysis to examine cortical folding across species. The experimental design - constructing two-layer PDMS models from 3D MRI data and immersing them in organic solvents to induce differential swelling - is well-established in prior literature. The authors further complement this with a continuum mechanics model simulating folding as a result of differential growth, as well as a comparative analysis of surface morphologies derived from in vivo, in vitro, and in silico brains.

We thank the reviewer for the very positive comments.

I offer a few suggestions here for clarification and further exploration:

Major Comments

(1) Choice of Developmental Stages and Initial Conditions

The authors should provide a clearer justification for the specific developmental stages chosen (e.g., G85 for macaque, GW23 for human). How sensitive are the resulting folding patterns to the initial surface geometry of the gel models? Given that folding is a nonlinear process, early geometric perturbations may propagate into divergent morphologies. Exploring this sensitivity-either through simulations or reference to prior work-would enhance the robustness of the findings.

The initial geometry is one of the important factors that decides the final folding pattern. The smooth brain in the early developmental stage shows a broad consistency across individuals, and we expect the main folds to form similarly across species and individuals.

Generally, we choose the initial geometry when the brain cortex is still relatively smooth. For the human, this corresponds approximately to GW23, as the major folds such as the Rolandic fissure (central sulcus), arise during this developmental stage. For the macaque brain, we chose developmental stage G85, primarily because of the availability of the dataset corresponding to this time, which also corresponds to the least folded.

We expect that large-scale folding patterns are strongly sensitive to the initial geometry but fine-scale features are not. Since our goal is to explain the large-scale features, we expect sensitivity to the initial shape.

Below are some references of other researchers that are consistent with this idea. Figure 4 from Wang et al. shows some images of simulations obtained by perturbing the geometry of a sphere to an ellipsoid. We see that the growth-induced folds mostly maintain their width (wavelength), but change their orientations.

Reference:

Wang, X., Lefévre, J., Bohi, A., Harrach, M.A., Dinomais, M. and Rousseau, F., 2021. The influence of biophysical parameters in a biomechanical model of cortical folding patterns. Scientific Reports, 11(1), p.7686.

Related results from the same group show that slight perturbations of brain geometry, cause these folds also tend to change their orientations but not width/wavelength (Bohi et al., 2019).

Reference:

Bohi, A., Wang, X., Harrach, M., Dinomais, M., Rousseau, F. and Lefévre, J., 2019, July. Global perturbation of initial geometry in a biomechanical model of cortical morphogenesis. In 2019 41st Annual International Conference of the IEEE Engineering in Medicine and Biology Society (EMBC) (pp. 442-445). IEEE.

Finally, a systematic discussion of the role of perturbations on the initial geometries and physical properties can be seen in our work on understanding a different system, gut morphogenesis (Gill et al., 2024).

We have added the discussion about geometric sensitivity in the section Methods-Numerical Simulations:

“Small perturbations on initial geometry would affect minor folds, but the main features of major folds, such as orientations, width, and depth, are expected to be conserved across individuals [49, 50]. For simplicity, we do not perturb the fetal brain geometry obtained from datasets.”

(2) Parameter Space and Breakdown Points

The numerical model assumes homogeneous growth profiles and simplifies several aspects of cortical mechanics. Parameters such as cortical thickness, modulus ratios, and growth ratios are described in Table II. It would be informative to discuss the range of parameter values for which the model remains valid, and under what conditions the physical and computational models diverge. This would help delineate the boundaries of the current modelling framework and indicate directions for refinement.

Exploring the valid parameter space is a key problem. We have tested a series of growth parameters and will state them explicitly in our revision. In the current version, we chose the ones that yield a relatively high similarity index to the animal brains. More generally, folding patterns are largely regulated by geometry as well as physical parameters, such as cortical thickness, modulus ratios, growth ratios, and inhomogeneity. In our previous work on a different system, gut morphogenesis, where similar folding patterns are seen, we have explored these features (Gill et al., 2024).

Reference:

Gill, H.K., Yin, S., Nerurkar, N.L., Lawlor, J.C., Lee, C., Huycke, T.R., Mahadevan, L. and Tabin, C.J., 2024. Hox gene activity directs physical forces to differentially shape chick small and large intestinal epithelia. Developmental Cell, 59(21), pp.2834-2849.

(3) Neglected Regional Features: The Occipital Pole of the Macaque

One conspicuous omission is the lack of attention to the occipital pole of the macaque, which is known to remain smooth even at later gestational stages and has an unusually high neuronal density (2.5× higher than adjacent cortex). This feature is not reproduced in the gel or numerical models, nor is it discussed. Acknowledging this discrepancy-and speculating on possible developmental or mechanical explanationswould add depth to the comparative analysis. The authors may wish to include this as a limitation or a target for future work.

Yes, we have added that the omission of the Occipital Pole of the macaque is one of our paper’s limitations. Our main aim in this paper is to explore the formation of large-scale folds, so the smooth region is not discussed. But future work could include this to make the model more complete.

The main text has been modified in Methods, Numerical simulations:

“To focus on fold formation, we did not discuss the relatively smooth region, such as the Occipital Pole of the macaque.”

and also in the caption of Figure 4: “... The occipital pole region of macaque brains remains smooth in real and simulated brains.”

(4) Spatio-Temporal Growth Rates and Available Human Data

The authors note that accurate, species-specific spatio-temporal growth data are lacking, limiting the ability to model inhomogeneous cortical expansion. While this may be true for ferret and macaque, there are high-quality datasets available for human fetal development, now extended through ultrasound imaging (e.g., https://doi.org/10.1038/s41586-023-06630-3). Incorporating or at least referencing such data could improve the fidelity of the human model and expand the applicability of the approach to clinical or pathological scenarios.

We thank the reviewer for pointing out the very useful datasets that exist for the exploration of inhomogeneous growth driven folding patterns. We have referred to this paper to provide suggestions for further work in exploring the role of growth inhomogeneities.

We have referred to this high-quality dataset in our main text, Discussion:

“...the effect of inhomogeneous growth needs to be further investigated by incorporating regional growth of the gray and white matter not only in human brains [29, 31] based on public datasets [45], but also in other species.”

A few works have tried to incorporate inhomogeneous growth in simulating human brain folding by separating the central sulcus area into several lobes (e.g., lobe parcellation method, Wang, PhD Thesis, 2021). Since our goal in this paper is to explain the large-scale features of folding in a minimal setting, we have kept our model simple and show that it is still capable of capturing the main features of folding in a range of mammalian brains.

Reference:

Xiaoyu Wang. Modélisation et caractérisation du plissement cortical. Signal and Image Processing. Ecole nationale superieure Mines-Télécom Atlantique, 2021. English. 〈NNT : 2021IMTA0248〉.

(5) Future Applications: The Inverse Problem and Fossil Brains

The authors suggest that their morphometric framework could be extended to solve the inverse growth problem-reconstructing fetal geometries from adult brains. This speculative but intriguing direction has implications for evolutionary neuroscience, particularly the interpretation of fossil endocasts. Although beyond the scope of this paper, I encourage the authors to elaborate briefly on how such a framework might be practically implemented and validated.

For the inverse problem, we could use the following strategies:

a. Perform systematic simulations using different geometries and physical parameters to obtain the variation in morphologies as a function of parameters.

b. Using either supervised training or unsupervised training (physics-informed neural networks, PINNs) to learn these characteristic morphologies and classify their dependence on the parameters using neural networks. These can then be trained to determine the possible range of geometrical and physical parameters that yield buckled patterns seen in the systematic simulations.

c. Reconstruct the 3D surface from fossil endocasts. Using the well-trained neural network, it should be possible to predict the initial shape of the smooth brain cortex, growth profile, and stiffness ratio of the gray and white matter.

As an example in this direction, supervised neural networks have been used recently to solve the forward problem to predict the buckling pattern of a growing two-layer system (Chavoshnejad et al., 2023). The inverse problem can then be solved using machine-learning methods when the training datasets are the folded shape, which are then used to predict the initial geometry and physical properties.

Reference:

Chavoshnejad, P., Chen, L., Yu, X., Hou, J., Filla, N., Zhu, D., Liu, T., Li, G., Razavi, M.J. and Wang, X., 2023. An integrated finite element method and machine learning algorithm for brain morphology prediction. Cerebral Cortex, 33(15), pp.9354-9366.

Conclusion

This is a well-executed and creative study that integrates diverse methodologies to address a longstanding question in developmental neurobiology. While a few aspects-such as regional folding peculiarities, sensitivity to initial conditions, and available human data-could be further elaborated, they do not detract from the overall quality and novelty of the work. I enthusiastically support this paper and believe that it will be of broad interest to the neuroscience, biomechanics, and developmental biology communities.

Note: The paper mentions a companion paper [reference 11] that explores the cellular and anatomical changes in the ferret cortex. I did not have access to this manuscript, but judging from the title, this paper might further strengthen the conclusions.

The companion paper (Choi et al., 2025) has also been submitted to eLife and can be found here:

G. P. T. Choi, C. Liu, S. Yin, G. Séjourné, R. S. Smith, C. A. Walsh, L. Mahadevan, Biophysical basis for brain folding and misfolding patterns in ferrets and humans. eLife, 14, RP107141, 2025. doi:10.7554/eLife.107141

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

This study was conducted and presented to the highest methodological standards. It is clearly written, and the results are thoroughly presented in the main manuscript and supplementary materials. Nevertheless, I would present the following minor points and comments for consideration by the authors prior to finalizing their work:

We thank the reviewer for positive opinions and helpful comments.

(1) Where did the MRI-based cortical surface data come from? Specifically, it would be helpful to include more information regarding whether the surfaces were reconstructed based on individual- or group-level data. It appears the surfaces were group-level, and, if so, accounting for individual-level cortical folding may be a fruitful direction for future work.

The surface data come from public database, which are stated in the Methods Section. “We used a publicly available database for all our 3d reconstructions: fetal macaque brain surfaces are obtained from Liu et al. (2020); newborn ferret brain surfaces are obtained from Choi et al. (2025); and fetal human brain surfaces are obtained from Tallinen et al. (2016).”

These surfaces are reconstructed based on group-level data. Specifically, the macaque atlas images are constructed for brains at gestational ages of 85 days (G85, N \=18_, 9 females), 110 days (G110, _N \=10_, 7 females) and 135 days (G135, _N \=16_,_ 7 females). And yes, future work may focus on individual-level cortical folding, and we expect that more specific results could be found.

(2) One methodological approach for assessing consistency of cortical folding within species might be an evaluation of cross-hemispheric symmetry. I would find this particularly interesting with respect to the gel models, as it could complement the quantification of variation with respect to the computationally derived and real surfaces.

Yes, the cross-hemispheric symmetry comparison can be done by our morphometric analysis method. We have added the results of ferret brain’s left-right symmetry for gel models, simulations, and real surfaces in the supplementary material. A typical conformal mapping figure and the similarity index table are shown here.

(3) Was there a specific reason to reorder the histogram plots in Figure 4c to macaque, ferret, human rather than to maintain the order presented in Figure 4a/b of ferret, macaque, human? I appreciate that this is a minor concern, and all subplots are indeed properly titled, but consistent order may improve clarity.

We have reordered the histogram plots to make all the figure orders consistent.

Reviewer #2 (Recommendations for the authors):

(1) Please consider revising the caption of Figure 1 (or equivalent figures) to explicitly state whether features such as the macaque occipital flatness were reproduced or not.

We thank the reviewer for pointing out the macaque occipital flatness.

Author response table 1.

Left-right similarity index evaluated by comparing the shape index of ferret brains, calculated with vector P-NORM p\=2,

Author response image 1.

Left-right similarity index of ferret brains

Occipital Pole of the macaque remains relatively smooth in both real brains and computational models. But our main aim in this paper is to explore the large-scale folds formation, so the smooth region is not discussed in depth. But future work could include this to make the model more complete.

(2) Some figures could benefit from clearer labelling to distinguish between in vivo, in vitro, and in silico results.

We have supplemented some texts in panels to make the labelling clearer.

(3) The manuscript would benefit from a short paragraph in the Discussion reflecting on how future incorporation of regional heterogeneities might improve model fidelity.

We have added a sentence in the Discussion Section about improving the model fidelity by considering regional heterogeneities.

“Future more accurate models incorporating spatio-temporal inhomogeneous growth profiles and mechanical properties, such as varying stiffness, would make the folding pattern closer to the real cortical folding. This relies on more in vivo measurements of the brain’s physical properties and cortical expansion.”

(4) Suggestions for improved or additional experiments, data, or analyses.

(5) Clarify and justify the selection of developmental stages: The authors should explain why particular gestational stages (e.g., G85 for macaque, GW23 for human) were chosen as starting points for the physical and computational models. A discussion of how sensitive the folding patterns are to the initial geometry would help assess the robustness of the model. If feasible, a brief sensitivity analysis-varying initial age or surface geometry-would strengthen the conclusions.

The initial geometry is one of the important factors that decides the final folding pattern. The smooth brain in the early developmental stage shows a broad consistency across individuals, and we expect the main folds to form similarly across species and individuals.

Generally, we choose the initial geometry when the brain cortex is still relatively smooth. For the human, this corresponds approximately to GW23, as the major folds such as the Rolandic fissure (central sulcus), arise during this developmental stage. For the macaque brain, we chose developmental stage G85, primarily because of the availability of the dataset corresponding to this time, which also corresponds to the least folded.

We expect that large-scale folding patterns are strongly sensitive to the initial geometry but fine-scale features are not. Since our goal is to explain the large-scale features, we expect sensitivity to the initial shape.

We have added the discussion about geometric sensitivity in the section Methods-Numerical Simulations: “Small perturbations on initial geometry would affect minor folds, but the main features of major folds, such as orientations, width, and depth, are expected to be conserved across individuals [49, 50]. For simplicity, we do not perturb the fetal brain geometry obtained from datasets.”

(6) Explore parameter boundaries more explicitly: The paper would benefit from a clearer account of the ranges of mechanical and geometric parameters (e.g., growth ratios, cortical thickness) for which the model holds. Are there specific conditions under which the physical and numerical models diverge? Identifying breakdown points would help readers understand the model’s limitations and applicability.

Exploring the valid parameter space is a key problem. We have tested a series of growth parameters and will state them explicitly in our revision. In the current version, we chose the ones that yield a relatively high similarity index to the animal brains. More generally, folding patterns are largely regulated by geometry as well as physical parameters, such as cortical thickness, modulus ratios, and growth ratios and inhomogeneity. In our previous work on a different system, gut morphogenesis, where similar folding patterns are seen, we have explored these features (Gill et al., 2024).

(7) Address species-specific cortical peculiarities: A striking omission is the flat occipital pole of the macaque, which is not reproduced in the physical or computational models. Given its known anatomical and cellular distinctiveness, this discrepancy warrants discussion. Even if not explored experimentally, the authors could speculate on what developmental or mechanical conditions would be needed to reproduce such regional smoothness.

Please refer to our answer to the public reviewer 2, question (3). From our results, the formation of smooth Occipital Pole might indicate that the spatio-temporal growth rate of gray and white matter are consistent in this region, such that there’s no much differential growth.

(8) Consider integration of available human growth data: While the authors note the lack of spatiotemporal growth data across species, such datasets exist for human fetal brain development, including those from MRI and ultrasound studies (e.g., Nature 2023). Incorporating these into the human model-or at least discussing their implications-would enhance biological relevance.

Yes, some datasets for fetal human brains have provided very comprehensive measurements on brain shapes at many developmental stages. This can surely be implemented in our current model by calculating the spatio-temporal growth rate from regional cortical shapes at different stages.

(9) Recommendations for improving the writing and presentation:

a) The manuscript is generally well-written, but certain sections would benefit from more explicit linksbetween the biological phenomena and the modeling framework. For instance, the Introduction and Discussion could more clearly articulate how mechanical principles interface with genetic or cellular processes, especially in the context of evolution and developmental variation.

We have briefly discussed the gene-regulated cellular process and the induced changes of mechanical properties and growth rules in SI, table S1. In the main text, to be clearer, we have added a sentence:

“Many malformations are related to gene-regulated abnormal cellular processes and mechanical properties, which are discussed in SI”

b) The Discussion could better acknowledge limitations and future directions, including regional dif-ferences in folding, inter-individual variability, and the model’s assumptions of homogeneous material properties and growth.

In the discussion section, we have pointed out four main limitations and open directions based on our current model, including the discussion on spatiotemporal growth and property. To be more complete, we have supplemented other limitations on the regional differences in folding and the interindividual variability. In the main text, we added the following sentence:

“In addition to the homogeneity assumption, we have not investigated the inter-individual variability and regional differences in folding. More accurate and specific work is expected to focus on these directions.”

c) The authors briefly mention the potential for addressing the inverse growth problem. Expanding this idea in a short paragraph - perhaps with hypothetical applications to fossil brain reconstructions-would broaden the paper’s appeal to evolutionary neuroscientists.

We have stated general steps in the response to public reviewer 2, question (5).

(10) Minor corrections to the text and figures:

a) Figures:

Label figures more clearly to distinguish between in vivo, in vitro, and in silico brain representations.– Ensure that the occipital pole of the macaque is visible or annotated, especially if it lacks the expected smoothness.

Add scale bars where missing for clarity in morphometric comparisons.

We thank the reviewer for suggestions to improve the readability of our manuscript.

The in vivo (real), in vitro (gel), and in silico (simulated) results are both distinguished by their labels and different color scheme: gray-white for real brain, pink-white for gel model, and blue-white for simulations, respectively.

The occipital pole of the macaque brain remains relatively smooth in our computational model but notin our physical gel model. We have clarified this in the main text: “To focus on fold formation, we did not discuss the relatively smooth region, such as the Occipital Pole of the macaque.”

All the brain models are rescaled to the same size, where the distance between the anterior-most pointof the frontal lobe and the posterior-most point of the occipital lobe is two units.

b) Text:

Consider revising figure captions to explicitly mention whether specific regional features (e.g., flatoccipital pole) were observed or absent in models.

In Table II (and relevant text), ensure parameter definitions are consistent and explained clearly for across-disciplinary audience.

Add citations to recent human fetal growth imaging work (e.g., ultrasound-based studies) to support claims about available data.

We have added some descriptions of the characters of the folding pattern in the caption of Figure 4,including major folds and smooth regions.

“Three or four major folds of each brain model are highlighted and served as landmarks. The occipital pole region of macaque brains remains smooth in real and simulated brains.”

We have clarified the definition of growth ratio gMsub>g</sub>/g_w and stiffness ratio µ_g/µ_w between gray matter and white matter, and the normalized cortical thickness h/L in Table 2.

We have referred to a high-quality dataset of fetal brain imaging work, the ultrasound-imaging method(Namburete et al. 2023), in our main text, Discussion:

“...the effect of inhomogeneous growth needs to be further investigated by incorporating regional growth of the gray and white matter not only in human brains [29, 31] based on public datasets [45], but also in other species.”

Reviewer #2 (Public review):

Summary:

This study aims to show how structural and functional brain organization develops during childhood and adolescence using two large neuroimaging datasets. It addresses whether core principles of brain organization are stable across development, how they change over time, and how these changes relate to cognition and psychopathology. The study finds that brain organization is established early and remains stable but undergoes gradual refinement, particularly in higher-order networks. Structural-functional coupling is linked to better working memory but shows no clear relationship with psychopathology.

Comments on revisions:

Follow-up: I would like to thank the authors for their thoughtful and comprehensive revisions. The additional analyses addressing developmental differences in structure-function coupling between CALM and NKI are valuable and clearly strengthen the manuscript. I particularly appreciate the inclusion of the neurotypical subgroup within CALM to disentangle neurotypicality from potential site-related effects, as well as the expanded discussion of these findings in the context of individual variability and equifinality.

Regarding my earlier comment on the use of COMBAT, I realize that "exclusion" may have been a poor choice of wording. What I meant was that harmonization procedures like COMBAT can, in some cases, weaken extremes or reduce variability by shrinking values toward the mean, rather than literally excluding participants from the analysis. Nevertheless, I appreciate the authors' careful consideration of this point and their additional analysis examining sample coverage following motion-based exclusions.

Overall, I am satisfied with the revisions, and I believe the manuscript has been substantially improved.

Author response:

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

Reviewer #1 (Public review):

Lack of Sensitivity Analyses for some Key Methodological Decisions: Certain methodological choices in this manuscript diverge from approaches used in previous works. In these cases, I recommend the following: (i) The authors could provide a clear and detailed justification for these deviations from established methods, and (ii) supplementary sensitivity analyses could be included to ensure the robustness of the findings, demonstrating that the results are not driven primarily by these methodological changes. Below, I outline the main areas where such evaluations are needed:

This detailed guidance is incredibly valuable, and we are grateful. Work of this kind is in its relative infancy, and there are so many design choices depending on the data available, questions being addressed, and so on. Help us navigate that has been extremely useful. In our revised manuscript we are very happy to add additional justification for design choices made, and wherever possible test the impact of those choices. It is certainly the case that different approaches have been used across the handful of papers published in this space, and, unlike in other areas of systems neuroscience, we have yet to reach the point where any of these approaches are established. We agree with the reviewer that wherever possible these design choices should be tested. 

Use of Communicability Matrices for Structural Connectivity Gradients: The authors chose to construct structural connectivity gradients using communicability matrices, arguing that diffusion map embedding "requires a smooth, fully connected matrix." However, by definition, the creation of the affinity matrix already involves smoothing and ensures full connectedness. I recommend that the authors include an analysis of what happens when the communicability matrix step is omitted. This sensitivity test is crucial, as it would help determine whether the main findings hold under a simpler construction of the affinity matrix. If the results significantly change, it could indicate that the observations are sensitive to this design choice, thereby raising concerns about the robustness of the conclusions. Additionally, if the concern is related to the large range of weights in the raw structural connectivity (SC) matrix, a more conventional approach is to apply a log-transformation to the SC weights (e.g., log(1+𝑆𝐶_𝑖𝑗)), which may yield a more reliable affinity matrix without the need for communicability measures.

The reason we used communicability is indeed partly because we wanted to guarantee a smooth fully connected matrix, but also because our end goal for this project was to explore structure-function coupling in these low-dimensional manifolds.  Structural communicability – like standard metrics of functional connectivity – includes both direct and indirect pathways, whereas streamline counts only capture direct communication. In essence we wanted to capture not only how information might be routed from one location to another, but also the more likely situation in which information propagates through the system. 

In the revised manuscript we have given a clearer justification for why we wanted to use communicability as our structural measure (Page 4, Line 179):

“To capture both direct and indirect paths of connectivity and communication, we generated weighted communicability matrices using SIFT2-weighted fibre bundle capacity (FBC). These communicability matrices reflect a graph theory measure of information transfer previously shown to maximally predict functional connectivity (Esfahlani et al., 2022; Seguin et al., 2022). This also foreshadowed our structure-function coupling analyses, whereby network communication models have been shown to increase coupling strength relative to streamline counts (Seguin et al., 2020)”.

We have also referred the reader to a new section of the Results that includes the structural gradients based on the streamline counts (Page 7, line 316):

“Finally, as a sensitivity analysis, to determine the effect of communicability on the gradients, we derived affinity matrices for both datasets using a simpler measure: the log of raw streamline counts. The first 3 components derived from streamline counts compared to communicability were highly consistent across both NKI  (r_s = 0.791, r_s = 0.866, r_s = 0.761) and the referred subset of CALM (r_s = 0.951, r_s = 0.809, r_s = 0.861), suggesting that in practice the organisational gradients are highly similar regardless of the SC metric used to construct the affinity matrices”. 

Methodological ambiguity/lack of clarity in the description of certain evaluation steps: Some aspects of the manuscript’s methodological description are ambiguous, making it challenging for future readers to fully reproduce the analyses based on the information provided. I believe the following sections would benefit from additional detail and clarification:

Computation of Manifold Eccentricity: The description of how eccentricity was computed (both in the results and methods sections) is unclear and may be problematic. The main ambiguity lies in how the group manifold origin was defined or computed. (1) In the results section, it appears that separate manifold origins were calculated for the NKI and CALM groups, suggesting a dataset-specific approach. (2) Conversely, the methods section implies that a single manifold origin was obtained by somehow combining the group origins across the three datasets, which seems contradictory. Moreover, including neurodivergent individuals in defining the central group manifold origin in conceptually problematic. Given that neurodivergent participants might exhibit atypical brain organization, as suggested by Figure 1, this inclusion could skew the definition of what should represent a typical or normative brain manifold. A more appropriate approach might involve constructing the group manifold origin using only the neurotypical participants from both the NKI and CALM datasets. Given the reported similarity between group-level manifolds of neurotypical individuals in CALM and NKI, it would be reasonable to expect that this combined origin should be close to the origin computed within neurotypical samples of either NKI or CALM. As a sanity check, I recommend reporting the distance of the combined neurotypical manifold origin to the centres of the neurotypical manifolds in each dataset. Moreover, if the manifold origin was constructed while utilizing all samples (including neurodivergent samples) I think this needs to be reconsidered. 

This is a great point, and we are very happy to clarify. Separate manifolds were calculated for the NKI and CALM participants, hence a dataset-specific approach. Indeed, in the long-run our goal was to explore individual differences in these manifolds, relative to the respective group-level origins, and their intersection across modalities, so manifold eccentricity was calculated at an individual level for subsequent analyses. At the group level, for each modality, we computed 3 manifold origins: one for NKI, one for the referred subset of CALM, and another for the neurotypical portion of CALM. Crucially, because the manifolds are always normal, in each case the manifold origin point is near-zero (extremely near-zero, to the 6^th or 7^th decimal place). In other words, we do indeed calculate the origin separately each time we calculate the gradients, but the origin is zero in every case. As a result, differences in the origin point cannot be the source of any differences we observe in manifold eccentricity between groups or individuals. We have updated the Methods section with the manifold origin points for each dataset and clarified our rationale (Page 16, Line 1296):

“Note that we used a dataset-specific approach when we computed manifold eccentricity for each of the three groups relative to their group-level origin: neurotypical CALM (SC origin = -7.698 x 10^-7, FC origin = 6.724 x 10^-7), neurodivergent CALM (SC origin = -6.422 x 10 , FC origin = 1.363 x 10 ), and NKI (SC origin = -7.434 x 10 , FC origin = 4.308 x 10^-6). Eccentricity is a relative measure and thus normalised relative to the origin. Because of this normalisation, each time gradients are constructed the manifold origin is necessarily near-zero, meaning that differences in manifold eccentricity of individual nodes, either between groups or individuals, are stem from the eccentricity of that node rather than a difference in origin point”. 

We clarified the computation of the respective manifold origins within the Results section, and referred the reader to the relevant Methods section (Page 9, line 446):

“For each modality (2 levels: SC and FC) and dataset (3 levels: neurotypical CALM, neurodivergent CALM, and NKI), we computed the group manifold origin as the mean of their respective first three gradients. Because of the normal nature of the manifolds this necessarily means that these origin points will be very near-zero, but we include the exact values in the ‘Manifold Eccentricity’ methodology sub-section”. 

Individual-Level Gradients vs. Group-Level Gradients: Unlike previous studies that examined alterations in principal gradients (e.g., Xia et al., 2022; Dong et al., 2021), this manuscript focuses on gradients derived directly from individual-level data. In contrast, earlier works have typically computed gradients based on grouped data, such as using a moving window of individuals based on age (Xia et al.) or evaluating two distinct age groups (Dong et al.). I believe it is essential to assess the sensitivity of the findings to this methodological choice. Such an evaluation could clarify whether the observed discrepancies with previous reports are due to true biological differences or simply a result of different analytical strategies.

This is a brilliant point. The central purpose of our project was to test how individual differences in these gradients, and their intersection across modalities, related to differences in phenotype (e.g. cognitive difficulties). These necessitated calculating gradients at the level of individuals and building a pipeline to do so, given that we could find no other examples. Nonetheless, despite this different goal and thus approach, we had expected to replicate a couple of other key findings, most prominently the ‘swapping’ of gradients shown by Dong et al. (2021). We were also surprised that we did not find this changing in order. The reviewer is right and there could be several design features that produce the difference, and in the revised manuscript we test several of them. We have added the following text to the manuscript as a sensitivity analysis for the Results sub-section titled “Stability of individual-level gradients across developmental time” (Page 7, Line 344 onwards):

“One possibility is that our observation of gradient stability – rather than a swapping of the order for the first two gradients (Dong et al., 2021) – is because we calculated them at an individual level. To test this, we created subgroups and contrasted the first two group-level structural and functional gradients derived from children (younger than 12 years old) versus those from adolescents (12 years old and above), using the same age groupings as prior work (Dong et al., 2021). If our use of individually calculated gradients produces the stability, then we should observe the swapping of gradients in this sensitivity analysis. Using baseline scans from NKI, the primary structural gradient in childhood (N = 99) as shown in Figure 1f, this was highly correlated (r_s = 0.995) with those derived from adolescents (N = 123). Likewise, the secondary structural gradient in childhood was highly consistent in adolescence (r_s = 0.988). In terms of functional connectivity, the principal gradient in childhood (N = 88) was highly consistent in adolescence (r_s = 0.990, N = 125). The secondary gradient in childhood was again highly similar in adolescence (r_s = 0.984). The same result occurred in the CALM dataset: In the baseline referred subset of CALM, the primary and secondary communicability gradients derived from children (N = 258) and adolescents (N = 53) were near-identical (r_s = 0.991 and r_s = 0.967, respectively). Alignment for the primary and secondary functional gradients derived from children (N = 130) and adolescents (N = 43) were also near-identical (r_s = 0.972 and r_s = 0.983, respectively). These consistencies across development suggest that gradients of communicability and functional connectivity established in childhood are the same as those in adolescence, irrespective of group-level or individual-level analysis. Put simply, our failure to replicate the swapping of gradient order in Dong et al. (2021) is not the result of calculating gradients at the level of individual participants.”

Procrustes Transformation: It is unclear why the authors opted to include a Procrustes transformation in this analysis, especially given that previous related studies (e.g., Dong et al.) did not apply this step. I believe it is crucial to evaluate whether this methodological choice influences the results, particularly in the context of developmental changes in organizational gradients. Specifically, the Procrustes transformation may maximize alignment to the group-level gradients, potentially masking individual-level differences. This could result in a reordering of the gradients (e.g., swapping the first and second gradients), which might obscure true developmental alterations. It would be informative to include an analysis showing the impact of performing vs. omitting the Procrustes transformation, as this could help clarify whether the observed effects are robust or an artifact of the alignment procedure. (Please also refer to my comment on adding a subplot to Figure 1). Additionally, clarifying how exactly the transformation was applied to align gradients across hemispheres, individuals, and/or datasets would help resolve ambiguity. 

The current study investigated individual differences in connectome organisation, rather than group-level trends (Dong et al., 2021). This necessitates aligning individual gradients to the corresponding group-level template using a Procrustes rotation. Without a rotation, there is no way of knowing if you are comparing  ‘like with like’: the manifold eccentricity of a given node may appear to change across individuals simply due to subtle differences in the arbitrary orientation of the underlying manifolds. We also note that prior work examining individual differences in principal alignment have used Procrustes (Xia et al., 2022), who demonstrated emergence of the principal gradient across development, albeit with much smaller effects than Dong and colleagues (2021). Nonetheless, we agree, the Procrustes rotation could be another source of the differences we observed with the previous paper (Dong et al. 2021). We explored the impact of the Procrustes rotation on individual gradients as our next sensitivity analysis. We recalculated everyone’s gradients without Procrustes rotation. We then tested the alignment of each participant with the group-level gradients using Spearman’s correlations, followed by a series of generalised linear models to predict principal gradient alignment using head motion, age, and sex. The expected swapping of the first and second functional gradient (Dong et al., 2021) would be represented by a decrease in the spatial similarity of each child’s principal functional gradient to the principal childhood group-level gradient, at the onset of adolescence (~age 12). However, there is no age effect on this unrotated alignment, suggesting that the lack of gradient swapping in our data does not appear to be the result of the Procrustes rotation. When you use unrotated individual gradients the alignment is remarkably consistent across childhood and adolescence. Alignment is, however, related to head motion, which is often related to age. To emphasise the importance of motion, particularly in relation to development, we conducted a mediation analysis between the relationship between age and principal alignment (without correcting for motion), with motion as a mediator, within the NKI dataset. Before accounting for motion, the relationship between age and principal alignment is significant, but this can be entirely accounted for by motion. In our revised manuscript we have included this additional analysis in the Results sub-section titled “Stability of individual-level gradients across developmental time”, following on from the above point about the effect of group-level versus individual-level analysis (Page 8, Line 400):

“A second possible discrepancy between our results and that of prior work examining developmental change in group-level functional gradients (Dong et al., 2021) was the use of Procrustes alignment. Such alignment of individual-level gradients to group-level templates is a necessary step to ensure valid comparisons between corresponding gradients across individuals, and has been implemented in sliding-window developmental work tracking functional gradient development (Xia et al., 2022). Nonetheless, we tested whether our observation of stable principal functional and communicability gradients may be an artefact of the Procrustes rotation. We did this by modelling how individual-level alignment without Procrustes rotation to the group-level templates varies with age, head motion, and sex, as a series of generalised linear models. We included head motion as the magnitude of the Procrustes rotation has been shown to be positively correlated with mean framewise displacement (Sasse et al., 2024), and prior group-level work (Dong et al., 2021) included an absolute motion threshold rather than continuous motion estimates. Using the baseline referred CALM sample, there was no significant relationship between alignment and age (β = -0.044, 95% CI = [-0.154, 0.066], p = 0.432) after accounting for head motion and sex. Interestingly, however head motion was significantly associated with alignment ( β = -0.318, 95% CI = [-0.428, -.207], p = 1.731 x 10^-8), such that greater head motion was linked to weaker alignment. Note that older children tended to have exhibit less motion for their structural scans (r_s = 0.335, p < 0.001). We observed similar trends in functional alignment, whereby tighter alignment was significantly predicted by lower head motion (β = -0.370, 95% CI = [-0.509, -0.231], p = 1.857 x 10^-7), but not by age (β= 0.049, 95% CI = [-0.090, 0.187], p = 0.490). Note that age and head motion for functional scans were not significantly related (r_s = -0.112, p = 0.137). When repeated for the baseline scans of NKI, alignment with the principal structural gradient was not significantly predicted by either scan age (β = 0.019, 95% CI = [-0.124, 0.163], p = 0.792) or head motion (β = -0.133, 95% CI = [-0.175, 0.009], p = 0.067) together in a single model, where age and motion were negatively correlated (r_s = -0.355, p < 0.001). Alignment with the principal functional gradient was significantly predicted by head motion (β = -0.183, 95% CI = [-0.329, -0.036], p = 0.014) but not by age (β= 0.066, 95% CI = [-0.081, 0.213], p = 0.377), where age and motion were also negatively correlated (r_s = -0.412, p < 0.001). Across modalities and datasets, alignment with the principal functional gradient in NKI was the only example in which there was a significant correlation between alignment and age (r_s = 0.164, p = 0.017) before accounting for head motion and sex. This suggests that apparent developmental effects on alignment are minimal, and where they do exist they are removed after accounting for head motion. Put together this suggests that the lack of order swapping for the first two gradients is not the result of the Procrustes rotation – even without the rotation there is no evidence for swapping”.

“To emphasise the importance of head motion in the appearance of developmental change in alignment, we examined whether accounting for head motion removes any apparent developmental change within NKI. Specifically, we tested whether head motion mediates the relationship between age and alignment (Figure 1X), controlling for sex, given that higher motion is associated with younger children (β= -0.429, 95% CI = [0.552, -0.305], p = 7.957 x 10^-11), and stronger alignment is associated with reduced motion (β = -0.211, 95% CI = [-0.344, -0.078], p = 2.017 x 10^-3). Motion mediated the relationship between age and alignment (β = 0.078, 95% CI = [0.006, 0.146], p = 1.200 x 10^-2), accounting for 38.5% variance in the age-alignment relationship, such that the link between age and alignment became non-significant after accounting for motion (β = 0.066, 95% CI = [-0.081, 0.214], p = 0.378). This firstly confirms our GLM analyses, where we control for motion and find no age associations. Moreover, this suggests that caution is required when associations between age and gradients are observed. In our analyses, because we calculate individual gradients, we can correct for individual differences in head motion in all our analyses. However, other than using an absolute motion threshold and motion-matched child and adolescent groups, individual differences in motion were not accounted for by prior work which demonstrated a flipping of the principal functional gradients with age (Dong et al., 2021)”. 

We further clarify the use of Procrustes rotation as a separate sub-section within the Methods (Page 25, Line 1273):

“Procrustes Rotation

For group-level analysis, for each hemisphere we constructed an affinity matrix using a normalized angle kernel and applied diffusion-map embedding. The left hemisphere was then aligned to the right using a Procrustes rotation. For individual-level analysis, eigenvectors for the left hemisphere were aligned with the corresponding group-level rotated eigenvectors. No alignment was applied across datasets. The only exception to this was for structural gradients derived from the referred CALM cohort. Specifically, we aligned the principal gradient of the left hemisphere to the secondary gradient of the right hemisphere: this was due to the first and second gradients explaining a very similar amount of variance, and hence their order was switched”. 

SC-FC Coupling Metric: The approach used to quantify nodal SC-FC coupling in this study appears to deviate from previously established methods in the field. The manuscript describes coupling as the "Spearman-rank correlation between Euclidean distances between each node and all others within structural and functional manifolds," but this description is unclear and lacks sufficient detail. Furthermore, this differs from what is typically referred to as SC-FC coupling in the literature. For instance, the cited study by Park et al. (2022) utilizes a multiple linear regression framework, where communicability, Euclidean distance, and shortest path length are independent variables predicting functional connectivity (FC), with the adjusted R-squared score serving as the coupling index for each node. On the other hand, the Baum et al. (2020) study, also cited, uses Spearman correlation, but between raw structural connectivity (SC) and FC values. If the authors opt to introduce a novel coupling metric, it is essential to demonstrate its similarity to these previous indices. I recommend providing an analysis (supplementary) showing the correlation between their chosen metric and those used in previous studies (e.g., the adjusted R-squared scores from Park et al. or the SC-FC correlation from Baum et al.). Furthermore, if the metrics are not similar and results are sensitive to this alternative metric, it raises concerns about the robustness of the findings. A sensitivity analysis would therefore be helpful (in case the novel coupling metric is not like previous ones) to determine whether the reported effects hold true across different coupling indices.

This is a great point, and we are happy to take the reviewer’s recommendation. There are multiple different ways of calculating structure-function coupling. For our set of questions, it was important that our metric incorporated information about the structural and functional manifolds, rather than being a separate approach that is unrelated to these low-dimensional embeddings. Put simply, we wanted our coupling measure to be about the manifolds and gradients outlined in the early sections of the results. We note that the multiple linear regression framework was developed by Vázquez-Rodríguez and colleagues (2019), whilst the structure-function coupling computed in manifold space by Park and colleagues (2022) was operationalised as a linear correlation between z-transformed functional connectomes and structural differentiation eigenvectors. To clarify how this coupling was calculated, and to justify why we developed a new coupling method based on manifolds rather than borrow an existing approach from the literature, we have revised the manuscript to make this far clearer for readers (Page 13, line 604):

“To examine the relationship between each node’s relative position in structural and functional manifold space, we turned our attention to structure-function coupling. Whilst prior work typically computed coupling using raw streamline counts and functional connectivity matrices, either as a correlation (Baum et al., 2020) or through a multiple linear regression framework (Vázquez-Rodríguez et al., 2019), we opted to directly incorporate low-dimensional embeddings within our coupling framework. Specifically, as opposed to correlating row-wise raw functional connectivity with structural connectivity eigenvectors (Park et al., 2022), our metric directly incorporates the relative position of each node in low-dimensional structural and functional manifold spaces. Each node was situated in a low-dimensional 3D space, the axes of which were each participant’s gradients, specific to each modality. For each participant and each node, we computed the Euclidean distance with all other nodes within structural and functional manifolds separately, producing a vector of size 200 x 1 per modality. The nodal coupling coefficient was the Spearman correlation between each node’s Euclidean distance to all other nodes in structural manifold space, and that in functional manifold space. Put simply, a strong nodal coupling coefficient suggests that that node occupies a similar location in structural space, relative to all other nodes, as it does in functional space”. 

We also agree with the reviewer’s recommendation to compare this to some of the more standard ways of calculating coupling. We compare our metric with 3 others (Baum et al., 2020; Park et al., 2022; VázquezRodríguez et al., 2019), and find that all metrics capture the core developmental sensorimotor-to-association axis (Sydnor et al., 2021). Interestingly, manifold-based coupling measures captured this axis more strongly than non-manifold measures. We have updated the Results accordingly (Page 14, Line 638):

“To evaluate our novel coupling metric, we compared its cortical spatial distribution to three others (Baum et al., 2020; Park et al., 2022; Vázquez-Rodríguez et al., 2019), using the group-level thresholded structural and functional connectomes from the referred CALM cohort. As shown in Figure 4c, our novel metric was moderately positively correlated to that of a multi-linear regression framework (r_s = 0.494, p_spin = 0.004; Vázquez-Rodríguez et al., 2019) and nodal correlations of streamline counts and functional connectivity (r_s = 0.470, p_spin = 0.005; Baum et al., 2020). As expected, our novel metric was strongly positively correlated to the manifold-derived coupling measure (r_s = 0.661, p_spin < 0.001; Park et al., 2022), more so than the first (Z(198) = 3.669, p < 0.001) and second measure (Z(198) = 4.012, p < 0.001). Structure-function coupling is thought to be patterned along a sensorimotor-association axis (Sydnor et al., 2021): all four metrics displayed weak-tomoderate alignment (Figure 4c). Interestingly, the manifold-based measures appeared most strongly aligned with the sensorimotor-association axis: the novel metric was more strongly aligned than the multi-linear regression framework (Z(198) = -11.564, p < 0.001) and the raw connectomic nodal correlation approach (Z(198) = -10.724, p < 0.001), but the previously-implemented structural manifold approach was more strongly aligned than the novel metric  (Z(198) = -12.242, p < 0.001). This suggests that our novel metric exhibits the expected spatial distribution of structure-function coupling, and the manifold approach more accurately recapitulates the sensorimotor-association axis than approaches based on raw connectomic measures”.

We also added the following to the legend of Figure 4 on page 15:

“d. The inset Spearman correlation plot of the 4 coupling measures shows moderate-to-strong correlations (p_spin < 0.005 for all spatial correlations). The accompanying lollypop plot shows the alignment between the sensorimotor-to-association axis and each of the 4 coupling measures, with the novel measure coloured in light purple (p_spin < 0.007 for all spatial correlations)”. 

Prediction vs. Association Analysis: The term “prediction” is used throughout the manuscript to describe what appear to be in-sample association tests. This terminology may be misleading, as prediction generally implies an out-of-sample evaluation where models trained on a subset of data are tested on a separate, unseen dataset. If the goal of the analyses is to assess associations rather than make true predictions, I recommend refraining from the term “prediction” and instead clarifying the nature of the analysis. Alternatively, if prediction is indeed the intended aim (which would be more compelling), I suggest conducting the evaluations using a k-fold cross-validation framework. This would involve training the Generalized Additive Mixed Models (GAMMs) on a portion of the data and training their predictive accuracy on a held-out sample (i.e. different individuals). Additionally, the current design appears to focus on predicting SC-FC coupling using cognitive or pathological dimensions. This is contrary to the more conventional approach of predicting behavioural or pathological outcomes from brain markers like coupling. Could the authors clarify why this reverse direction of analysis was chosen? Understanding this choice is crucial, as it impacts the interpretation and potential implications of the findings. 

We have replaced “prediction” with “association” across the manuscript. However, for analyses corresponding to Figure 5, which we believe to be the most compelling, we conducted a stratified 5-fold cross-validation procedure, outlined below, repeated 100 times to account for random variation in the train-test splits. To assess whether prediction accuracy in the test splits was significantly greater than chance, we compared our results to those derived from a null dataset in which cognitive factor 2 scores had been permuted across participants. To account for the time-series element and block design of our data, in that some participants had 2 or more observations, we permuted entire participant blocks of cognitive factor 2 scores, keeping all other variables, including covariates, the same. Included in our manuscript are methodological details and results pertaining to this procedure. Specifically, the following has been added to the Results (Page 16, Line 758):

“To examine the predictive value of the second cognitive factor for global and network-level structure-function coupling, operationalised as a Spearman rank correlation coefficient, we implemented a stratified 5-fold crossvalidation framework, and predictive accuracy compared with that of a null data frame with cognitive factor 2 scores permuted across participant blocks (see ‘GAMM cross-validation’ in the Methods). This procedure was repeated 100 times to account for randomness in the train-test splits, using the same model specification as above. Therefore, for each of the 5 network partitions in which an interaction between the second cognitive factor and age was a significant predictor of structure-function coupling (global, visual, somato-motor, dorsal attention, and default-mode), we conducted a Welch’s independent-sample t-test to compare 500 empirical prediction accuracies with 500 null prediction accuracies. Across all 5 network partitions, predictive accuracy of coupling was significantly higher than that of models trained on permuted cognitive factor 2 scores (all p < 0.001). We observed the largest difference between empirical (M = 0.029, SD = 0.076) and null (M = -0.052, SD = 0.087) prediction accuracy in the somato-motor network [t (980.791) = 15.748, p < 0.001, Cohen’s d = 0.996], and the smallest difference between empirical (M = 0.080, SD = 0.082) and null (M = 0.047, SD = 0.081) prediction accuracy in the dorsal attention network [t (997.720) = 6.378, p < 0.001, Cohen’s d = 0.403]. To compare relative prediction accuracies, we ordered networks by descending mean accuracy and conducted a series of Welch’s independent sample t-tests, followed by FDR correction (Figure 5X). Prediction accuracy was highest in the default-mode network (M = 0.265, SD = 0.085), two-fold that of global coupling (t(992.824) = 25.777, p_FDR = 5.457 x 10^-112, Cohen’s d = 1.630, M = 0.131, SD = 0.079). Global prediction accuracy was significantly higher than the visual network (t (992.644) = 9.273, p_FDR = 1.462 x 10^-19, Cohen’s d = 0.586, M = 0.083, SD = 0.085), but visual prediction accuracy was not significantly higher than within the dorsal attention network (t (997.064) = 0.554, p_FDR = 0.580, Cohen’s d = 0.035, M = 0.080, SD = 0.082). Finally, prediction accuracy within the dorsal attention network was significantly stronger than that of the somato-motor network [t (991.566) = 10.158, p_FDR = 7.879 x 10^-23, Cohen’s d = 0.642 M = 0.029, SD = 0.076]. Together, this suggests that out-of-sample developmental predictive accuracy for structure-function coupling, using the second cognitive factor, is strongest in the higher-order default-mode network, and lowest in the lower-order somatosensory network”. 

We have added a separate section for GAMM cross-validation in the Methods (Page 27, Line 1361):

GAMM cross-validation

“We implemented a 5-fold cross validation procedure, stratified by dataset (2 levels: CALM or NKI). All observations from any given participant were assigned to either the testing or training fold, to prevent data leakage, and the cross-validation procedure was repeated 100 times, to account for randomness in data splits. The outcome was predicted global or network-level structure-function coupling across all test splits, operationalised as the Spearman rank correlation coefficient. To assess whether prediction accuracy exceeded chance, we compared empirical prediction accuracy with that of GAMMs trained and tested on null data in which cognitive factor 2 scores were permuted across subjects. The number of observations formed 3 exchangeability blocks (N = 320 with one observation, N = 105 with two observations, and N = 33 with three observations), whereby scores from a participant with two observations were replaced by scores from another participant with two observations, with participant-level scores kept together, and so on for all numbers of observations. We compared empirical and null prediction accuracies using independent sample t-tests as, although the same participants were examined, the shuffling meant that the relative ordering of participants within both distributions was not preserved. For parallelisation and better stability when estimating models fit on permuted data, we used the bam function from the mgcv R package (Wood, 2017)”. 

We also added a justification for why we predicted coupling using behaviour or psychopathology, rather than vice versa (Page 27, Line 1349):

“When using our GAMMs to test for the relationship between cognition and psychopathology and our coupling metrics, we opted to predict structure-function coupling using cognitive or psychopathological dimensions, rather than vice versa, to minimise multiple comparisons. In the current framework, we corrected for 8 multiple comparisons within each domain. This would have increased to 16 multiple comparison corrections for predicting two cognitive dimensions using network-level coupling, and 24 multiple comparison corrections for predicting three psychopathology dimensions. Incorporating multiple networks as predictors within the same regression framework introduces collinearity, whilst the behavioural dimensions were orthogonal: for example, coupling is strongly correlated between the somato-motor and ventral attention networks (r_s = 0.721), between the default-mode and frontoparietal networks (r_s = 0.670), and between the dorsal attention and fronto-parietal networks (r_s = 0.650)”. 

Finally, we noticed a rounding error in the ages of the data frame containing the structure-function coupling values and the cognitive/psychopathology dimensions. We rectified this and replaced the GAMM results, which largely remained the same. 

In typical applications of diffusion map embedding, sparsification (e.g., retaining only the top 10  of the strongest connections) is often employed at the vertex-level resolution to ensure computational feasibility. However, since the present study performs the embedding at the level of 200 brain regions (a considerably coarser resolution), this step may not be necessary or justifiable. Specifically, for FC, it might be more appropriate to retain all positive connections rather than applying sparsification, which could inadvertently eliminate valuable information about lower-strength connections. Whereas for SC, as the values are strictly non-negative, retaining all connections should be feasible and would provide a more complete representation of the structural connectivity patterns. Given this, it would be helpful if the authors could clarify why they chose to include sparsification despite the coarser regional resolution, and whether they considered this alternative approach (using all available positive connections for FC and all non-zero values for SC). It would be interesting if the authors could provide their thoughts on whether the decision to run evaluations at the resolution of brain regions could itself impact the functional and structural manifolds, their alteration with age, and or their stability (in contrast to Dong et al. which tested alterations in highresolution gradients).

This is another great point. We could retain all connections, but we usually implement some form of sparsification to reduce noise, particularly in the case of functional connectivity. But we nonetheless agree with the reviewer’s point. We should check what impact this is having on the analysis. In brief, we found minimal effects of thresholding, suggesting that the strongest connections are driving the gradient (Page 7, Line 304):

“To assess the effect of sparsity on the derived gradients, we examined group-level structural (N = 222) and functional (N = 213) connectomes from the baseline session of NKI. The first three functional connectivity gradients derived using the full connectivity matrix (density = 92%) were highly consistent with those obtained from retaining the strongest 10% of connections in each row (r₁ = 0.999, r₂ = 0.998, r₃ < 0.999, all p < 0.001). Likewise, the first three communicability gradients derived from retaining all streamline counts (density = 83%) were almost identical to those obtained from 10% row-wise thresholding (r₁ = 0.994, r₂ = 0.963, r₃ = 0.955, all p < 0.001). This suggests that the reported gradients are driven by the strongest or most consistent connections within the connectomes, with minimal additional information provided by weaker connections. In terms of functional connectivity, such consistency reinforces past work demonstrating that the sensorimotor-toassociation axis, the major axis within the principal functional connectivity gradient, emerges across both the top- and bottom-ranked functional connections (Nenning et al., 2023)”.

Furthermore, we appreciate the nudge to share our thoughts on whether the difference between vertex versus nodal metrics could be important here, particularly regarding thresholds. To combine this point with R2’s recommendation to expand the Discussion, we have added the following paragraph (Page 19, Line 861): 

“We consider the role of thresholding, cortical resolution, and head motion as avenues to reconcile the present results with select reports in the literature (Dong et al., 2021; Xia et al., 2022). We would suggest that thresholding has a greater effect on vertex-level data, rather than parcel-level. For example, a recent study revealed that the emergence of principal vertex-level functional connectivity gradients in childhood and adolescence are indeed threshold-dependent (Dong et al., 2024). Specifically, the characteristic unimodal organisation for children and transmodal organisation for adolescents only emerged at the 90% threshold: a 95% threshold produced a unimodal organisation in both groups, whilst an 85% threshold produced a transmodal organisation in both groups. Put simply, the ‘swapping’ of gradient orders only occurs at certain thresholds. Furthermore, our results are not necessarily contradictory to this prior report (Dong et al., 2021): developmental changes in high-resolution gradients may be supported by a stable low-dimensional coarse manifold. Indeed, our decision to use parcellated connectomes was partly driven by recent work which demonstrated that vertex-level functional gradients may be derived using biologically-plausible but random data with sufficient spatial smoothing, whilst this effect is minimal at coarser resolutions (Watson & Andrews, 2023). We observed a gradual increase in the variance of individual connectomes accounted for by the principal functional connectivity gradient in the referred subset of CALM, in line with prior vertex-level work demonstrating a gradual emergence of the sensorimotor-association axis as the principal axis of connectivity (Xia et al., 2022), as opposed to a sudden shift. It is also possible that vertex-level data is more prone to motion artefacts in the context of developmental work. Transitioning from vertex-level to parcel-level data involves smoothing over short-range connectivity, thus greater variability in short-range connectivity can be observed in vertex-level data. However, motion artefacts are known to increase short-range connectivity and decrease long-range connectivity, mimicking developmental changes (Satterthwaite et al., 2013). Thus, whilst vertexlevel data offers greater spatial resolution in representation of short-range connectivity relative to parcel-level data, it is possible that this may come at the cost of making our estimates of the gradients more prone to motion”.

Evaluating the consistency of gradients across development: the results shown in Figure 1e are used as evidence suggesting that gradients are consistent across ages. However, I believe additional analyses are required to identify potential sources of the observed inconsistency compared to previous works. The claim that the principal gradient explains a similar degree of variance across ages does not necessarily imply that the spatial structure remains the same. The observed variance explanation is hence not enough to ascertain inconsistency with findings from Dong et al., as the spatial configuration of gradients may still change over time. I suggest the following additional analyses to strengthen this claim. Alignment to group-level gradients: Assess how much of the variance in individual FC matrices is explained by each of the group-level gradients (G1, G2, and G3, for both FC and SC). This analysis could be visualized similarly to Figure 1e, with age on the x-axis and variance explained on the y-axis. If the explained variance varies as a function of age, it may indicate that the gradients are not as consistent as currently suggested. 

This is another great suggestion. In the additional analyses above (new group-level analyses and unrotated gradient analyses) we rule-out a couple of the potential causes of the different developmental trends we observe in our data – namely the stability of the gradients over time. The suggested additional analysis is a great idea, and we have implemented it as follows (Page 8, Line 363):

“To evaluate the consistency of gradients across development, across baseline participants with functional connectomes from the referred CALM cohort (N = 177), we calculated the proportion of variance in individuallevel connectomes accounted for by group-level functional gradients. Specifically, we calculated the proportion of variance in an adjacency matrix A accounted for by the vector v_i as the fraction of the square of the scalar projection of v_i onto A, over the Frobenius norm of A. Using a generalised linear model, we then tested whether the proportion of variance explained varies systematically with age, controlling for sex and headmotion. The variance in individual-level functional connectomes accounted for by the group-level principal functional gradient gradually increased with development (β= 0.111, 95% CI = [0.022, 0.199], p = 1.452 x 10^-2, Cohen’s d = 0.367), as shown in Figure 1g, and decreased with higher head motion ( β = -10.041, 95% CI = [12.379, -7.702], p = 3.900 x 10^-17), with no effect of sex (β= 0.071, 95% CI = [-0.380, 0.523], p = 0.757). We observed no developmental effects on the variance explained by the second (r_s = 0.112, p = 0.139) or third (r_s = 0.053, p = 0.482) group-level functional gradient. When repeated with the baseline functional connectivity for NKI (N = 213), we observed no developmental effects (β = 0.097, 95% CI = [-0.035, 0.228], p = 0.150) on the variance explained by the principal functional gradient after accounting for motion (β= -3.376, 95% CI = [8.281, 1.528], p = 0.177) and sex (β = -0.368, 95% CI = [-1.078, 0.342], p = 0.309). However, we observed significant developmental correlations between age and variance (r_s = 0.137, p = 0.046) explained before accounting for head motion and sex. We observed no developmental effects on the variance explained by the second functional gradient (r_s = -0.066, p = 0.338), but a weak negative developmental effect on the variance explained by the third functional gradient (r_s = -0.189, p = 0.006). Note, however, the magnitude of the variance accounted for by the third functional gradient was very small (all < 1%). When applied to communicability matrices in CALM, the proportion of variance accounted for by the group-level communicability gradient was negligible (all < 1%), precluding analysis of developmental change”. 

“To further probe the consistency of gradients across development, we examined developmental changes in the standard deviation of gradient values, corresponding to heterogeneity, following prior work examining morphological (He et al., 2025) and functional connectivity gradients (Xia et al., 2022). Using a series of generalised linear models within the baseline referred subset of CALM, correcting for head motion and sex, we found that gradient variation for the principal functional gradient increased across development (= 0.219, 95% CI = [0.091, 0.347], p = 0.001, Cohen’s d = 0.504), indicating greater heterogeneity (Figure 1h), whilst gradient variation for the principal communicability gradient decreased across development (β = -0.154, 95% CI = [-0.267, -0.040], p = 0.008, Cohen’s d = -0.301), indicating greater homogeneity (Figure 1h). Note, a paired t-test on the 173 common participants demonstrated a significant effect of modality on gradient variability (t(172) = -56.639, p = 3.663 x 10^-113), such that the mean variability of communicability gradients (M = 0.033, SD = 0.001) was less than half that of functional connectivity (M = 0.076, SD = 0.010). Together, this suggests that principal functional connectivity and communicability gradients are established early in childhood and display age-related refinement, but not replacement”. 

The Issue of Abstraction and Benefits of the Gradient-Based View: The manuscript interprets the eccentricity findings as reflecting changes along the segregation-integration spectrum. Given this, it is unclear why a more straightforward analysis using established graph-theory metrics of segregationintegration was not pursued instead. Mapping gradients and computing eccentricity adds layers of abstraction and complexity. If similar interpretations can be derived directly from simpler graph metrics, what additional insights does the gradient-based framework offer? While the manuscript argues that this approach provides “a more unifying account of cortical reorganization”, it is not evident why this abstraction is necessary or advantageous over traditional graph metrics. Clarifying these benefits would strengthen the rationale for using this method. 

This is a great point, and something we spent quite a bit of time considering when designing the analysis. The central goal of our project was to identify gradients of brain organisation across different datasets and modalities and then test how the organisational principles of those modalities align. In other words, how do structural and functional ‘spaces’ intersect, and does this vary across the cortex? That for us was the primary motivation for operationalising organisation as nodal location within a low-dimensional manifold space (Bethlehem et al., 2020; Gale et al., 2022; Park et al., 2021), using a simple composite measure to achieve compression, rather than as a series of graph metrics. The reason we subsequently calculated those graph metrics and tested for their association was simply to help us interpret what eccentricity within that lowdimensional space means. Manifold eccentricity was moderately positively correlated to graph-theory metrics of integration, leaving a substantial portion of variance unaccounted for, but that association we think is nonetheless helpful for readers trying to interpret eccentricity. However, since ME tells us about the relative position of a node in that low-dimensional space, it is also likely capturing elements of multiple graph theory measures. Following the Reviewer’s question, this is something we decided to test. Specifically, using 4 measures of segregation, including two new metrics requested by the Reviewer in a minor point (weighted clustering coefficient and normalized degree centrality), we conducted a dominance analysis (Budescu, 1993) with normalized manifold eccentricity of the group-level referred CALM structural connectome. We also detail the use of gradient measures in developmental contexts, and how they can be complementary to traditional graph theory metrics. 

We have added the following to the Results section (Page 10, Lines 472 onwards): 

“To further contextualise manifold eccentricity in terms of integration and segregation beyond simple correlations, we conducted a multivariate dominance analysis (Budescu, 1993) of four graph theory metrics of segregation as predictors of nodal normalized manifold eccentricity within the group-level referred CALM structural and functional connectomes (Figure 2c). A dominance analysis assesses the relative importance of each predictor in a multilinear regression framework by fitting 2ⁿ – 1 models (where n is the number of predictors) and calculating the relative increase in adjusted R2 caused by adding each predictor to the model across both main effects and interactions. A multilinear regression model including weighted clustering coefficient, within-module degree Z-score, participation coefficient and normalized degree centrality accounted for 59% of variance in nodal manifold eccentricity in the group-level CALM structural connectome. Withinmodule degree Z score was the most important predictor (40.31% dominance), almost twice that of the participation coefficient (24.03% dominance) and normalized degree centrality (24.05% dominance) which made roughly equal contributions. The least important predictor was the weighted clustering coefficient (11.62% dominance). When the same approach was applied for the group-level referred CALM functional connectome, the 4 predictors accounted for 52% variability. However, in contrast to the structural connectome, functional manifold eccentricity seemed to incorporate the same graph theory metrics in different proportions. Normalized degree centrality was the most important predictor (47.41% dominance), followed by withinmodule degree Z-score (24.27%), and then the participation coefficient (15.57%) and weighted clustering coefficient (12.76%) which made approximately equal contributions. Thus, whilst structural manifold eccentricity was dominated most by within-module degree Z-score and least by the weighted clustering coefficient, functional manifold eccentricity was dominated most by normalized degree centrality and least by the weighted clustering coefficient. This suggests that manifold mapping techniques incorporate different aspects of integration dependent on modality. Together, manifold eccentricity acts as a composite measure of segregation, being differentially sensitive to different aspects of segregation, without necessitating a priori specification of graph theory metrics. Further discussion of the value of gradient-based metrics in developmental contexts and as a supplement to traditional graph theory analyses is provided in the ‘Manifold Eccentricity’ methodology sub-section”. 

We added further justification to the manifold eccentricity Methods subsection (Page 26, line 1283):

“Gradient-based measures hold value in developmental contexts, above and beyond traditional graph theory metrics: within a sample of over 600 cognitively-healthy adults aged between 18 and 88 years old, sensitivity of gradient-based within-network functional dispersion to age were stronger and more consistent across networks compared to segregation (Bethlehem et al., 2020). In the context of microstructural profile covariance, modules resolved by Louvain community detection occupied distinct positions across the principal two gradients, suggesting that gradients offer a way to meaningfully order discrete graph theory analyses (Paquola et al., 2019)”. 

We added the following to the Introduction section outlining the application of gradients as cortex-wide coordinate systems (Page 3, Line 121):

“Using the gradient-based approach as a compression tool, thus forgoing the need to specify singular graph theory metrics a priori, we operationalised individual variability in low-dimensional manifolds as eccentricity (Gale et al., 2022; Park et al., 2021). Crucially, such gradients appear to be useful predictors of phenotypic variation, exceeding edge-level connectomics. For example, in the case of functional connectivity gradients, their predictive ability for externalizing symptoms and general cognition in neurotypical adults surpassed that of edge-level connectome-based predictive modelling (Hong et al., 2020), suggesting that capturing lowdimensional manifolds may be particularly powerful biomarkers of psychopathology and cognition”. 

We also added the following to the Discussion section (Page 18, Line 839):

“By capitalising on manifold eccentricity as a composite measure of segregation across development, we build upon an emerging literature pioneering gradients as a method to establish underlying principles of structural (Paquola et al., 2020; Park et al., 2021) and functional (Dong et al., 2021; Margulies et al., 2016; Xia et al., 2022) brain development without a priori specification of specific graph theory metrics of interest”. 

It is unclear whether the statistical tests finding significant dataset effects are capturing effects of neurotypical vs. Neurodivergent, or simply different scanners/sites. Could the neurotypical portion of CALM also be added to distinguish between these two sources of variability affecting dataset effects (i.e. ideally separating this to the effect of site vs. neurotypicality would better distinguish the effect of neurodivergence).

At a group-level, differences in the gradients between the two cohorts are very minor. Indeed, in the manuscript we describe these gradients as being seemingly ‘universal’. But we agree that we should test whether we can directly attribute any simple main effects of ‘dataset’ are resulting from the different site or the phenotype of the participants. The neurotypical portion of CALM (collected at the same site on the same scanner) helped us show that any minor differences in the gradient alignments is likely due to the site/scanner differences rather than the phenotype of the participants. We took the same approach for testing the simple main effects of dataset on manifold eccentricity. To better parse neurotypicality and site effects at an individual-level, we conducted a series of sensitivity analyses. First, in response to the reviewer’s earlier comment, we conducted a series of nodal generalized linear models for communicability and FC gradients derived from neurotypical and neurodivergent portions of CALM, alongside NKI, and tested for an effect of neurotypicality above and beyond scanner. As at the group level, having those additional scans on a ‘comparison’ sample for CALM is very helpful in teasing apart these effects. We find that neurotypicality affects communicability gradient expression to a greater degree than functional connectivity. We visualised these results and added them to Figure 1. Second, we used the same approach but for manifold eccentricity. Again, we demonstrate greater sensitivity of neurotypicality to communicability at a global-level, but we cannot pin these effects down to specific networks because the effects do not survive the necessary multiple comparison correction. We have added these analyses to the manuscript (Page 13, Line 583): 

“Much as with the gradients themselves, we suspected that much of the simple main effect of dataset could reflect the scanner / site, rather than the difference in phenotype. Again, we drew upon the CALM comparison children to help us disentangle these two explanations. As a sensitivity analysis to parse effects of neurotypicality and dataset on manifold eccentricity, we conducted a series of generalized linear models predicting mean global and network-level manifold eccentricity, for each modality. We did this across all the baseline data (i.e. including the neurotypical comparison sample for CALM) using neurotypicality (2 levels: neurodivergent or neurotypical), site (2 levels: CALM or NKI), sex, head motion, and age at scan (Figure 3X). We restricted our analysis to baseline scans to create more equally-balanced groups. In terms of structural manifold eccentricity (N = 313 neurotypical, N = 311 neurodivergent), we observed higher manifold eccentricity in the neurodivergent participants at a global level (β = 0.090, p = 0.019, Cohen’s d = 0.188) but the individual network level effects did not survive the multiple comparison correction necessary for looking across all seven networks, with the default-mode network being the strongest (β = 0.135, p = 0.027, p_FDR = 0.109, Cohen’s d = 0.177). There was no significant effect of neurodiversity on functional manifold eccentricity (N = 292 neurotypical and N = 177 neurodivergent). This suggests that neurodiversity is significantly associated with structural manifold eccentricity, over and above differences in site, but we cannot distinguish these effects reliably in the functional manifold data”. 

Third, we removed the Scheirer-Ray-Hare test from the results for two reasons. First, its initial implementation did not account for repeated measures, and therefore non-independence between observations, as the same participants may have contributed both structural and functional data. Second, if we wanted to repeat this analysis in CALM using the referred and control portions, a significant difference in group size existed, which may affect the measures of variability. Specifically, for baseline CALM, 311 referred and 91 control participants contributed SC data, whilst 177 referred and 79 control participants contributed FC data. We believe that the ‘cleanest’ parsing of dataset and site for effects of eccentricity is achieved using the GLMs in Figure 3. 

We observed no significant effect of neurodivergence on the magnitude of structure-function coupling across development, and have added the following text (Page 14, Line 632):

“To parse effects of neurotypicality and dataset on structure-function coupling, we conducted a series of generalized linear models predicting mean global and network-level coupling using neurotypicality, site, sex, head motion, and age at scan, at baseline (N = 77 CALM neurotypical, N = 173 CALM neurodivergent, and N = 170 NKI). However, we found no significant effects of neurotypicality on structure-function coupling across development”. 

Since we demonstrated no significant effects of neurotypicality on structure-function coupling magnitude across development, but found differential dataset-specific effects of age on coupling development, we added the following sentence at the end of the coupling trajectory results sub-section (Page 14, line 664):

“Together, these effects demonstrate that whilst the magnitude of structure-function coupling appears not to be sensitive to neurodevelopmental phenotype, its development with age is, particularly in higher-order association networks, with developmental change being reduced in the neurodivergent sample”.  

Figure 1.c: A non-parametric permutation test (e.g. Mann-Whitney U test) could quantitatively identify regions with significant group differences in nodal gradient values, providing additional support for the qualitative findings.

This is a great idea. To examine the effect of referral status on nodal gradient values, whilst controlling for covariates (head motion and sex), we conducted a series of generalised linear models. We opted for this instead of a Mann-Whitney U test, as the former tests for differences in distributions, whilst the direction of the t-statistic for referral status from the GLM would allow us to specify the magnitude and direction of differences in nodal gradient values between the two groups. Again, we conducted this in CALM (referred vs control), at an individual-level, as downstream analyses suggested a main effect of dataset (which is reflected in the highly-similar group-level referred and control CALM gradients). We have updated the Results section with the following text (Page 6, Line 283):

“To examine the effect of referral status on participant-level nodal gradient values in CALM, we conducted a series of generalized linear models controlling for head motion, sex and age at scan (Figure 1d). We restricted our analyses to baseline scans to reduce the difference in sample size for the referred (311 communicability and 177 functional gradients, respectively) and control participants (91 communicability and 79 functional gradients, respectively), and to the principal gradients. For communicability, 42 regions showed a significant effect (p < 0.05) of neurodivergence before FDR correction, with 9 post FDR correction. 8 of these 9 regions had negative t-statistics, suggesting a reduced nodal gradient value and representation in the neurodivergent children, encompassing both lower-order somatosensory cortices alongside higher-order fronto-parietal and default-mode networks. The largest reductions were observed within the prefrontal cortices of the defaultmode network (t = -3.992, p = 6.600 x 10^-5, p_FDR = 0.013, Cohen’s d = -0.476), the left orbitofrontal cortex of the limbic network (t = -3.710, p = 2.070 x 10^-4, p_FDR = 0.020, Cohen’s d = -0.442) and right somato-motor cortex (t = -3.612, p = 3.040 x 10^-4, p_FDR = 0.020, Cohen’s d = -0.431). The right visual cortex was the only exception, with stronger gradient representation within the neurotypical cohort (t = 3.071, p = 0.002, p_FDR = 0.048, Cohen’s d = 0.366). For functional connectivity, comparatively fewer regions exhibited a significant effect (p < 0.05) of neurotypicality, with 34 regions prior to FDR correction and 1 post. Significantly stronger gradient representation was observed in neurotypical children within the right precentral ventral division of the defaultmode network (t = 3.930, p = 8.500 x 10^-5, p_FDR = 0.017, Cohen’s d = 0.532). Together, this suggests that the strongest and most robust effects of neurodivergence are observed within gradients of communicability, rather than functional connectivity, where alterations in both affect higher-order associative regions”. 

In the harmonization methodology, it is mentioned that “if harmonisation was successful, we’d expect any significant effects of scanner type before harmonisation to be non-significant after harmonisation”. However, given that there were no significant effects before harmonization, the results reported do not help in evaluating the quality of harmonization.

We agree with the Reviewer, and have removed the post-harmonisation GLMs, and instead stating that there were no significant effects of scanner type before harmonization. 

Figure 3: It would be helpful to include a plot showing the GAMM predictions versus real observations of eccentricity (x-axis: predictions, y-axis: actual values). 

To plot the GAMM-predicted smooth effects of age, which we used for visualisation purposes only, we used the get_predictions function from the itsadug R package. This creates model predictions using the median value of nuisance covariates. Thus, whilst we specified the entire age range, the function automatically chooses the median of head motion, alongside controlling for sex (default level: male) and, for each dataset-specific trajectory. Since the gamm4 package separates the fitted model into a gam and linear mixed effects model (which accounts for participant ID as a random effect), and the get_predictions function only uses gam, random effects are not modelled in the predicted smooths. Therefore, any discrepancy between the observed and predicted manifold eccentricity values is likely due to sensitivity to default choices of covariates other than age, or random effects. To prevent Figure 3 being too over-crowded, we opted to not include the predictions: these were strongly correlated with real structural manifold data, but less for functional manifold data especially where significant developmental change was absent.

The 30mm threshold for filtering short streamlines in tractography is uncommon. What is the rationale for using such a large threshold, given the potential exclusion of many short-range association fibres?

A minimum length of 30mm was the default for the MRtrix3 reconstruction workflow, and something we have previously used. In a previous project, we systematically varied the minimum fibre length and found that this had minimal impact on network organisation (e.g. Mousley et al. 2025). However, we accept that short-range association fibres may have been excluded and have included this in the Discussion as a methodological limitation, alongside our predictions for how the gradients and structure-function coupling may’ve been altered had we included such fibres (Page 20, Line 955):

“A potential methodological limitation in the construction of structural connectomes was the 30mm tract length threshold which, despite being the QSIprep reconstruction default (Cieslak et al., 2021), may have potentially excluded short-range association fibres. This is pertinent as tracts of different lengths exhibit unique distributions across the cortex and functional roles (Bajada et al., 2019) : short-range connections occur throughout the cortex but peak within primary areas, including the primary visual, somato-motor, auditory, and para-hippocampal cortices, and are thought to dominate lower-order sensorimotor functional resting-state networks, whilst long-range connections are most abundant in tertiary association areas and are recruited alongside tracts of varying lengths within higher-order functional resting-state networks. Therefore, inclusion of short-range association fibres may have resulted in a relative increase in representation of lower-order primary areas and functional networks. On the other hand, we also note the potential misinterpretation of short-range fibres: they may be unreliably distinguished from null models in which tractography is restricted by cortical gyri only (Bajada et al., 2019). Further, prior (neonatal) work has demonstrated that the order of connectivity of regions and topological fingerprints are consistent across varying streamline thresholds (Mousley et al., 2025), suggesting minimal impact”. 

Given the spatial smoothing of fMRI data (6mm FWHM), it would be beneficial to apply connectome spatial smoothing to structural connectivity measures for consistent spatial smoothness.

This is an interesting suggestion but given we are looking at structural communicability within a parcellated network, we are not sure that it would make any difference. The data structural data are already very smooth. Nonetheless we have added the following text to the Discussion (Page 20, Line 968): 

“Given the spatial smoothing applied to the functional connectivity data, and examining its correspondence to streamline-count connectomes through structure-function coupling, applying the equivalent smoothing to structural connectomes may improve the reliability of inference, and subsequent sensitivity to cognition and psychopathology. Connectome spatial smoothing involves applying a smoothing kernel to the two streamline endpoints, whereby variations in smoothing kernels are selected to optimise the trade-off between subjectlevel reliability and identifiability, thus increasing the signal-to-noise ratio and the reliability of statistical inferences of brain-behaviour relationships (Mansour et al., 2022). However, we note that such smoothing is more effective for high-resolution connectomes, rather than parcel-level, and so have only made a modest improvement (Mansour et al., 2022)”.

Why was harmonization performed only within the CALM dataset and not across both CALM and NKI datasets? What was the rationale for this decision?

We thought about this very carefully. Harmonization aims to remove scanner or site effects, whilst retaining the crucial characteristics of interest. Our capacity to retain those characteristics is entirely dependent on them being *fully* captured by covariates, which are then incorporated into the harmonization process. Even with the best set of measures, the idea that we can fully capture ‘neurodivergence’ and thus preserve it in the harmonisation process is dubious. Indeed, across CALM and NKI there are limited number of common measures (i.e. not the best set of common measures), and thus we are limited in our ability to fully capture the neurodivergence with covariates. So, we worried that if we put these two very different datasets into the harmonisation process we would essentially eliminate the interesting differences between the datasets. We have added this text to the harmonization section of the Methods (Page 24, Line 1225):

“Harmonization aims to retain key characteristics of interest whilst removing scanner or site effects. However, the site effects in the current study are confounded with neurodivergence, and it is unlikely that neurodivergence may be captured fully using common covariates across CALM and NKI. Therefore, to preserve variation in neurodivergence, whilst reducing scanner effects, we harmonized within the CALM dataset only”. 

The exclusion of subcortical areas from connectivity analyses is not justified. 

This is a good point. We used the Schaefer atlas because we had previously used this to derive both functional and structural connectomes, but we agree that it would have been good to include subcortical areas (Page 20, Line 977). 

“A potential limitation of our study was the exclusion of subcortical regions. However, prior work has shed light on the role of subcortical connectivity in structural and functional gradients, respectively, of neurotypical populations of children and adolescents (Park et al., 2021; Xia et al., 2022). For example, in the context of the primary-to-transmodal and sensorimotor-to-visual functional connectivity gradients, the mean gradient scores within subcortical networks were demonstrated to be relatively stable across childhood and adolescence (Xia et al., 2022). In the context of structural connectivity gradients derived from streamline counts, which we demonstrated were highly consistent with those derived from communicability, subcortical structural manifolds weighted by their cortical connectivity were anchored by the caudate and thalamus at one pole, and by the hippocampus and nucleus accumbens at the opposite pole, with significant age-related manifold expansion within the caudate and thalamus (Park et al., 2021)”. 

In the KNN imputation method, were uniform weights used, or was an inverse distance weighting applied?

Uniform weights were used, and we have updated the manuscript appropriately.

The manuscript should clarify from the outset that the reported sample size (N) includes multiple longitudinal observations from the same individuals and does not reflect the number of unique participants.

We have rectified the Abstract (Page 2, Line 64) and Introduction (Page 3, Line 138):

“We charted the organisational variability of structural (610 participants, N = 390 with one observation, N = 163 with two observations, and N = 57 with three) and functional (512 participants, N = 340 with one observation, N = 128 with two observations, and N = 44 with three)”.

The term “structural gradients” is ambiguous in the introduction. Clarify that these gradients were computed from structural and functional connectivity matrices, not from other structural features (e.g. cortical thickness).

We have clarified this in the Introduction (Page 3, Line 134):

“Applying diffusion-map embedding as an unsupervised machine-learning technique onto matrices of communicability (from streamline SIFT2-weighted fibre bundle capacity) and functional connectivity, we derived gradients of structural and functional brain organisation in children and adolescents…”

Page 5: The sentence, “we calculated the normalized angle of each structural and functional connectome to derive symmetric affinity matrices” is unclear and needs clarification.

We have clarified this within the second paragraph of the Results section (Page 4, Line 185):

“To capture inter-nodal similarity in connectivity, using a normalised angle kernel, we derived individual symmetric affinity matrices from the left and right hemispheres of each communicability and functional connectivity matrix. Varying kernels capture different but highly-related aspects of inter-nodal similarity, such as correlation coefficients, Gaussian kernels, and cosine similarity. Diffusion-map embedding is then applied on the affinity matrices to derive gradients of cortical organisation”. 

Figure 1.a: “Affine A” likely refers to the affinity matrix. The term “affine” may be confusing; consider using a clearer label. It would also help to add descriptive labels for rows and columns (e.g. region x region).

Thank you for this suggestion! We have replaced each of the labels with “pairwise similarity”. We also labelled the rows and columns as regions.

Figure 1.d: Are the cross-group differences statistically significant? If so, please indicate this in the figure.

We have added the results of a series of linear mixed effects models to the legend of Figure 1 (Page 6, line 252):

“indicates a significant effect of dataset (p < 0.05) on variance explained within a linear mixed effects model controlling for head motion, sex, and age at scan”.

The sentence “whose connectomes were successfully thresholded” in the methods is unclear. What does “successfully thresholded” mean? Additionally, this seems to be the first mention of the Schaefer 100 and Brainnetome atlas; clarify where these parcellations are used. 

We have amended the Methodology section (Page 23, Line 1138):

“For each participant, we retained the strongest 10% of connections per row, thus creating fully connected networks required for building affinity matrices. We excluded any connectomes in which such thresholding was not possible due to insufficient non-zero row values. To further ensure accuracy in connectome reconstruction, we excluded any participants whose connectomes failed thresholding in two alternative parcellations: the 100node Schaefer 7-network (Schaefer et al., 2018) and Brainnetome 246-node (Fan et al., 2016) parcellations, respectively”. 

We have also specified the use of the Schaefer 200-node parcellation in the first sentence on the second Results paragraph.

The use of “streamline counts” is misleading, as the method uses SIFT2-weighted fibre bundle capacity rather than raw streamline counts. It would be better to refer to this measure as “SIFT2-weighted fibre bundle capacity” or “FBC”.

We replaced all instances of “streamline counts” with “SIFT2-weighted fibre bundle capacity” as appropriate.

Figure 2.c: Consider adding plots showing changes in eccentricity against (1) degree centrality, and (2) weighted local clustering coefficient. Additionally, a plot showing the relationship between age and mean eccentricity (averaged across nodes) at the individual level would be informative.

We added the correlation between eccentricity and both degree centrality and the weighted local clustering coefficient and included them in our dominance analysis in Figure 2. In terms of the relationship between age and mean (global) eccentricity, these are plotted in Figure 3. 

Figure 2.b: Considering the results of the following sections, it would be interesting to include additional KDE/violin plots to show group differences in the distribution of eccentricity within 7 different functional networks.

As part of our analysis to parse neurotypicality and dataset effects, we tested for group differences in the distribution of structural and functional manifold eccentricity within each of the 7 functional networks in the referred and control portions of CALM and have included instances of significant differences with a coloured arrow to represent the direction of the difference within Figure 3. 

Figure 3: Several panels lack axis labels for x and y axes. Adding these would improve clarity.

To minimise the amount of text in Figure 3, we opted to include labels only for the global-level structural and functional results. However, to aid interpretation, we added a small schematic at the bottom of Figure 3 to represent all axis labels. 

The statement that “differences between datasets only emerged when taking development into account” seems inaccurate. Differences in eccentricity are evident across datasets even before accounting for development (see Fig 2.b and the significance in the Scheirer-Ray-Hare test).

We agree – differences in eccentricity across development and datasets are evident in structural and functional manifold eccentricity, as well as within structure-function coupling. However, effects of neurotypicality were particularly strong for the maturation of structure-function coupling, rather than magnitude. Therefore, we have rephrased this sentence in the Discussion (page 18, line 832):

“Furthermore, group-level structural and functional gradients were highly consistent across datasets, whilst differences between datasets were emphasised when taking development into account, through differing rates of structural and functional manifold expansion, respectively, alongside maturation of structure-function coupling”.

The handling of longitudinal data by adding a random effect for individuals is not clear in the main text. Mentioning this earlier could be helpful. 

We have included this detail in the second sentence of the “developmental trajectories of structural manifold contraction and functional manifold expansion” results sub-section (page 11, line 503):

“We included a random effect for each participant to account for longitudinal data”. 

Figure 4.b: Why were ranks shown instead of actual coefficient of variation values? Consider including a cortical map visualization of the coefficients in the supplementary material.

We visualised the ranks, instead of the actual coefficient of variation (CV) values, due to considerable variability and skew in the magnitude of the CV, ranging from 28.54 (in the right visual network) to 12865.68 (in the parietal portion of the left default-mode network), with a mean of 306.15. If we had visualised the raw CV values, these larger values would’ve been over-represented. We’ve also noticed and rectified an error in the labelling of the colour bar for Figure 4b: the minimum should be most variable (i.e. a rank of 1). To aid contextualisation of the ranks, we have added the following to the Results (page 14, line 626):

“The distribution of cortical coefficients of variation (CV) varied considerably, with the largest CV (in the parietal division of the left default-mode network) being over 400 times that of the smallest (in the right visual network). The distribution of absolute CVs was positively skewed, with a Fisher skewness coefficient g₁ of 7.172, meaning relatively few regions had particularly high inter-individual variability, and highly peaked, with a kurtosis of 54.883, where a normal distribution has a skewness coefficient of 0 and a kurtosis of 3”. 

Reviewer #2 (Public review):

Some differences in developmental trajectories between CALM and NKI (e.g. Figure 4d) are not explained. Are these differences expected, or do they suggest underlying factors that require further investigation?

This is a great point, and we appreciate the push to give a fuller explanation. It is very hard to know whether these effects are expected or not. We certainly don’t know of any other papers that have taken this approach. In response to the reviewer’s point, we decided to run some more analyses to better understand the differences. Having observed stronger age effects on structure-function coupling within the neurotypical NKI dataset, compared to the absent effects in the neurodivergent portion of CALM, we wanted to follow up and test that it really is that coupling is more sensitive to the neurodivergent versus neurotypical difference between CALM and NKI (rather than say, scanner or site effects). In short, we find stronger developmental effects of coupling within the neurotypical portion of CALM, rather than neurodivergent, and have added this to the Results (page 15, line 701):

“To further examine whether a closer correspondence of structure-function coupling with age is associated with neurotypicality, we conducted a follow-up analysis using the additional age-matched neurotypical portion of CALM (N = 77). Given the widespread developmental effects on coupling within the neurotypical NKI sample, compared to the absent effects in the neurodivergent portion of CALM, we would expect strong relationships between age and structure-function coupling with the neurotypical portion of CALM. This is indeed what we found: structure-function coupling showed a linear negative relationship with age globally (F = 16.76, p_FDR < 0.001, adjusted R² = 26.44%), alongside fronto-parietal (F = 9.24, p_FDR = 0.004, adjusted R² = 19.24%), dorsalattention (F = 13.162, p_FDR = 0.001, adjusted R²= 18.14%), ventral attention (F = 11.47, p_FDR  = 0.002, adjusted R²= 22.78), somato-motor (F = 17.37, p_FDR  < 0.001, adjusted R²= 21.92%) and visual (F = 11.79, p_FDR  = 0.002, adjusted R²= 20.81%) networks. Together, this supports our hypothesis that within neurotypical children and adolescents, structure-function coupling decreases with age, showing a stronger effect compared to their neurodivergent counterparts, in tandem with the emergence of higher-order cognition. Thus, whilst the magnitude of structure-function coupling across development appeared insensitive to neurotypicality, its maturation is sensitive. Tentatively, this suggests that neurotypicality is linked to stronger and more consistent maturational development of structure-function coupling, whereby the tethering of functional connectivity to structure across development is adaptive”. 

In conjunction with the Reviewer’s later request to deepen the Discussion, we have included an additional paragraph attempting to explain the differences in neurodevelopmental trajectories of structure-function coupling (Page 19, Line 924):

“Whilst the spatial patterning of structure-function coupling across the cortex has been extensively documented, as explained above, less is known about developmental trajectories of structure-function coupling, or how such trajectories may be altered in those with neurodevelopmental conditions. To our knowledge, only one prior study has examined differences in developmental trajectories of (non-manifold) structure-function coupling in typically-developing children and those with attention-deficit hyperactivity disorder (Soman et al., 2023), one of the most common conditions in the neurodivergent portion of CALM. Namely, using cross-sectional and longitudinal data from children aged between 9 and 14 years old, they demonstrated increased coupling across development in higher-order regions overlapping with the defaultmode, salience, and dorsal attention networks, in children with ADHD, with no significant developmental change in controls, thus encompassing an ectopic developmental trajectory (Di Martino et al., 2014; Soman et al., 2023). Whilst the current work does not focus on any condition, rather the broad mixed population of young people with neurodevelopmental symptoms (including those with and without diagnoses), there are meaningful individual and developmental differences in structure-coupling. Crucially, it is not the case that simply having stronger coupling is desirable. The current work reveals that there are important developmental trajectories in structure-function coupling, suggesting that it undergoes considerable refinement with age. Note that whilst the magnitude of structure-function coupling across development did not differ significantly as a function of neurodivergence, its relationship to age did. Our working hypothesis is that structural connections allow for the ordered integration of functional areas, and the gradual functional modularisation of the developing brain. For instance, those with higher cognitive ability show a stronger refinement of structurefunction coupling across development. Future work in this space needs to better understand not just how structural or functional organisation change with time, but rather how one supports the other”. 

The use of COMBAT may have excluded extreme participants from both datasets, which could explain the lack of correlations found with psychopathology.

COMBAT does not exclude participants from datasets but simply adjusts connectivity estimates. So, the use of COMBAT will not be impacting the links with psychopathology by removing participants. But this did get us thinking. Excluding participants based on high motion may have systematically removed those with high psychopathology scores, meaning incomplete coverage. In other words, we may be under-representing those at the more extreme end of the range, simply because their head-motion levels are higher and thus are more likely to be excluded. We found that despite certain high-motion participants being removed, we still had good coverage of those with high scores and were therefore sensitive within this range. We have added the following to the revised Methods section (Page 26, Line 1338):

“As we removed participants with high motion, this may have overlapped with those with higher psychopathology scores, and thus incomplete coverage. To examine coverage and sensitivity to broad-range psychopathology following quality control, we calculated the Fisher-Pearson skewness statistic g₁ for each of the 6 Conners t-statistic measures and the proportion of youth with a t-statistic equal to or greater than 65, indicating an elevated or very elevated score. Measures of inattention (g₁ = 0.11, 44.20% elevated), hyperactivity/impulsivity (g₁ = 0.48, 36.41% elevated), learning problems (g₁ = 0.45, 37.36% elevated), executive functioning (g₁ = 0.27, 38.16% elevated), aggression (g₁ = 1.65, 15.58% elevated), and peer relations (g₁ = 0.49, 38% elevated) were positively skewed and comprised of at least 15% of children with elevated or very elevated scores, suggesting sufficient coverage of those with extreme scores”. 

There is no discussion of whether the stable patterns of brain organization could result from preprocessing choices or summarizing data to the mean. This should be addressed to rule out methodological artifacts. 

This is a brilliant point. We are necessarily using a very lengthy pipeline, with many design choices to explore structural and functional gradients and their intersection. In conjunction with the Reviewer’s later suggestion to deepen the Discussion, we have added the following paragraph which details the sensitivity analyses we carried out to confirm the observed stable patterns of brain organization (Page 18, Line 863):

“That is, whilst we observed developmental refinement of gradients, in terms of manifold eccentricity, standard deviation, and variance explained, we did not observe replacement. Note, as opposed to calculating gradients based on group data, such as a sliding window approach, which may artificially smooth developmental trends and summarise them to the mean, we used participant-level data throughout. Given the growing application of gradient-based analyses in modelling structural (He et al., 2025; Li et al., 2024) and functional (Dong et al., 2021; Xia et al., 2022) brain development, we hope to provide a blueprint of factors which may affect developmental conclusions drawn from gradient-based frameworks”.

Although imputing missing data was necessary, it would be useful to compare results without imputed data to assess the impact of imputation on findings. 

It is very hard to know the impact of imputation without simply removing those participants with some imputed data. Using a simulation experiment, we expressed the imputation accuracy as the root mean squared error normalized by the range of observable data in each scale. This produced a percentage error margin. We demonstrate that imputation accuracy across all measures is at worst within approximately 11% of the observed data, and at best within approximately 4% of the observed data, and have included the following in the revised Methods section (Page 27, Line 1348):

“Missing data

To avoid a loss of statistical power, we imputed missing data. 27.50% of the sample had one or more missing psychopathology or cognitive measures (equal to 7% of all values), and the data was not missing at random: using a Welch’s t-test, we observed a significant effect of missingness on age [t (264.479) = 3.029, p = 0.003, Cohen’s d = 0.296], whereby children with missing data (M = 12.055 years, SD = 3.272) were younger than those with complete data (M = 12.902 years, SD = 2.685). Using a subset with complete data (N = 456), we randomly sampled 10% of the values in each column with replacement and assigned those as missing, thereby mimicking the proportion of missingness in the entire dataset. We conducted KNN imputation (uniform weights) on the subset with complete data and calculated the imputation accuracy as the root mean squared error normalized by the observed range of each measure. Thus, each measure was assigned a percentage which described the imputation margin of error. Across cognitive measures, imputation was within a 5.40% mean margin of error, with the lowest imputation error in the Trail motor speed task (4.43%) and highest in the Trails number-letter switching task (7.19%). Across psychopathology measures, imputation exhibited a mean 7.81% error margin, with the lowest imputation error in the Conners executive function scale (5.75%) and the highest in the Conners peer relations scale (11.04%). Together, this suggests that imputation was accurate”.

The results section is extensive, with many reports, while the discussion is relatively short and lacks indepth analysis of the findings. Moving some results into the discussion could help balance the sections and provide a deeper interpretation. 

We agree with the Reviewer and appreciate the nudge to expand the Discussion section. We have added 4 sections to the Discussion. The first explores the importance of the default-mode network as a region whose coupling is most consistently predicted by working memory across development and phenotypes, in terms of its underlying anatomy (Paquola et al., 2025) (Page 20, Line 977):

“An emerging theme from our work is the importance of the default-mode network as a region in which structure-function coupling is reliably predicted by working memory across neurodevelopmental phenotypes and datasets during childhood and adolescence. Recent neurotypical adult investigations combining highresolution post-mortem histology, in vivo neuroimaging, and graph-theory analyses have revealed how the underlying neuroanatomy of the default-mode network may support diverse functions (Paquola et al., 2025), and thus exhibit lower structure-function coupling compared to unimodal regions. The default-mode network has distinct neuroanatomy compared to the remaining 6 intrinsic resting-state functional networks (Yeo et al., 2011), containing a distinctive combination of 5 of the 6 von Economo and Koskinas cell types (von Economo & Koskinas, 1925), with an over-representation of heteromodal cortex, and uniquely balancing output across all cortical types. A primary cytoarchitectural axis emerges, beyond which are mosaic-like spatial topographies. The duality of the default-mode network, in terms of its ability to both integrate and be insulated from sensory information, is facilitated by two microarchitecturally distinct subunits anchored at either end of the cytoarchitectural axis (Paquola et al., 2025). Whilst beyond the scope of the current work, structure-function coupling and their predictive value for cognition may also differ across divisions within the default-mode network, particularly given variability in the smoothness and compressibility of cytoarchitectural landscapes across subregions (Paquola et al., 2025)”. 

The second provides a deeper interpretation and contextualisation of greater sensitivity of communicability, rather than functional connectivity, to neurodivergence (Page 19, Lines 907):

“We consider two possible factors to explain the greater sensitivity of neurodivergence to gradients of communicability, rather than functional connectivity. First, functional connectivity is likely more sensitive to head motion than structural-based communicability and suffers from reduced statistical power due to stricter head motion thresholds, alongside greater inter-individual variability. Second, whilst prior work contrasting functional connectivity gradients from neurotypical adults with those with confirmed ASD diagnoses demonstrated vertex-level reductions in the default-mode network in ASD and marginal increases in sensorymotor communities (Hong et al., 2019), indicating a sensitivity of functional connectivity to neurodivergence, important differences remain. Specifically, whilst the vertex-level group-level differences were modest, in line with our work, greater differences emerged when considering step-wise functional connectivity (SFC); in other words, when considering the dynamic transitions of or information flow through the functional hierarchy underlying the static functional connectomes, such that ASD was characterised by initial faster SFC within the unimodal cortices followed by a lack of convergence within the default-mode network (Hong et al., 2019). This emphasis on information flow and dynamic underlying states may point towards greater sensitivity of neurodivergence to structural communicability – a measure directly capturing information flow – than static functional connectivity”. 

The third paragraph situates our work within a broader landscape of reliable brain-behaviour relationships, focusing on the strengths of combining clinical and normative samples to refine our interpretation of the relationship between gradients and cognition, as well as the importance of equifinality in developmental predictive work (Page 20, line 994):

“In an effort to establish more reliable brain-behaviour relationships despite not having the statistical power afforded by large-scale, typically normative, consortia (Rosenberg & Finn, 2022), we demonstrated the development-dependent link between default-mode structure-function coupling and working memory generalised across clinical (CALM) and normative (NKI) samples, across varying MRI acquisition parameters, and harnessing within- and across-participant variation. Such multivariate associations are likely more reliable than their univariate counterparts (Marek et al., 2022), but can be further optimised using task-related fMRI (Rosenberg & Finn, 2022). The consistency, or lack of, of developmental effects across datasets emphasises the importance of validating brain-behaviour relationships in highly diverse samples. Particularly evident in the case of structure-function coupling development, through our use of contrasting samples, is equifinality (Cicchetti & Rogosch, 1996), a key concept in developmental neuroscience: namely, similar ‘endpoints’ of structure-function coupling may be achieved through different initialisations dependent on working memory. 

The fourth paragraph details methodological limitations in response to Reviewer 1’s suggestions to justify the exclusion of subcortical regions and consider the role of spatial smoothing in structural connectome construction as well as the threshold for filtering short streamlines”. 

While the methods are thorough, it is not always clear whether the optimal approaches were chosen for each step, considering the available data. 

In response to Reviewer 1’s concerns, we conducted several sensitivity analyses to evaluate the robustness of our results in terms of procedure. Specifically, we evaluated the impact of thresholding (full or sparse), level of analysis (individual or group gradients), construction of the structural connectome (communicability or fibre bundle capacity), Procrustes rotation (alignment to group-level gradients before Procrustes), tracking the variance explained in individual connectomes by group-level gradients, impact of head motion, and distinguishing between site and neurotypicality effects. All these analyses converged on the same conclusion: whilst we observe some developmental refinement in gradients, we do not observe replacement. We refer the reviewer to their third point, about whether stable patterns of brain organization were artefactual. 

The introduction is overly long and includes numerous examples that can distract readers unfamiliar with the topic from the main research questions. 

We have removed the following from the Introduction, reducing it to just under 900 words:

“At a molecular level, early developmental patterning of the cortex arises through interacting gradients of morphogens and transcription factors (see Cadwell et al., 2019). The resultant areal and progenitor specialisation produces a diverse pool of neurones, glia, and astrocytes (Hawrylycz et al., 2015). Across childhood, an initial burst in neuronal proliferation is met with later protracted synaptic pruning (Bethlehem et al., 2022), the dynamics of which are governed by an interplay between experience-dependent synaptic plasticity and genomic control (Gottlieb, 2007)”.

“The trends described above reflect group-level developmental trends, but how do we capture these broad anatomical and functional organisational principles at the level of an individual?”

We’ve also trimmed the second Introduction paragraph so that it includes fewer examples, such as removal of the wiring-cost optimisation that underlies structural brain development, as well as removing specific instances of network segregation and integration that occur throughout childhood.

An unproductive waste, because there were no public monuments. Convenient definition, for the invaders!

Ignores slavery of course, but does seem impressed with the idea of religious freedom. He wrote these words, I think, while teaching at Round Hill in Northampton. So he would probably have been familiar with Knowlton in Ashfield. He DID refuse to go to Boston when elected as a representative by the Workingmen's Party, so his politics were probably a bit conservatiove.

Reviewer #2 (Public Review):

Verma et al. provide a short technical report showing that endogenously tagged dynein and dynactin molecules localize to growing microtubule plus-ends and also move processively along microtubules in cells. The data are convincing, and the imaging and movies very nicely demonstrate their claims. I don't have any large technical concerns about the work. It is perhaps not surprising that dynein-dynactin complexes behave this way in cells due to other reports on the topic, but the current data are among some of the nicest direct demonstrations of this phenomenon. It may be somewhat controversial since a separate group has reported that dynein does not move processively in mammalian cells

(https://www.biorxiv.org/content/10.1101/2021.04.05.438428v3).

Author response:

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

Reviewer #1 (Public Review): 

Strengths: 

The work uses a simple and straightforward approach to address the question at hand: is dynein a processive motor in cells? Using a combination of TIRF and spinning disc confocal microscopy, the authors provide a clear and unambiguous answer to this question. 

Thank you for the recognition of the strength of our work

Weaknesses: 

My only significant concern (which is quite minor) is that the authors focus their analysis on dynein movement in cells treated with docetaxol, which could potentially affect the observed behavior. However, this is likely necessary, as without it, motility would not have been observed due to the 'messiness' of dynein localization in a typical cell (e.g., plus end-tracking in addition to cargo transport).

You are exactly correct that this treatment was required to provided us a clear view of motile dynein and p50 puncta. One concern about the treatment that we had noted in our original submission was that the docetaxel derivative SiR tubulin could increase microtubule detyrosination, which has been implicated in affecting the initiation of dynein-dynactin motility but not motility rates (doi: 10.15252/embj.201593071). In response to a comment from reviewer 2 we investigated whether there was a significant increase in alpha-tubulin detyrosination in our treatment conditions and found that there was not. We have removed the discussion of this possibility from the revised version. Please also see response to comments raised by reviewer 2. 

Reviewer 1 (Recommendations for the authors):

Major points: 

(1) The authors measured kinesin-1-GFP intensities in a different cell line (drosophila S2 cells) than what was used for the DHC and p50 measurements (HeLa cells). It is unclear if this provides a fair comparison given the cells provide different environments for the GFP. Although the differences may in fact be trivial, without somehow showing this is indeed a fair comparison, it should at least be noted as a caveat when interpreting relative intensity differences. Alternatively, the authors could compare DHC and p50 intensities to those measured from HeLa cells treated with taxol. 

Thank you for this suggestion. We conducted new rounds of imaging with the DHCEGFP and p50-EGFP clones in conjunction with HeLa cells transiently expressing the human kinesin-1-EGFP and now present the datasets from the new experiments. Importantly, our new data was entirely consistent with the prior analyses as there was not a significant difference between the kinesin-1-EGFP dimer intensities and the DHC-EGFP puncta intensities and there was a statistically significant difference in the intensity of p50 puncta, which were approximately half the intensity of the kinesin-1 and DHC. We have moved the old data comparing the intensities in S2 cells expressing kinesin-1-EGFP to Figure 3 - figure supplement 2 A-D and the new HeLa cell data is now shown in Figure 3 D-G.

(2) Given the low number of observations (41-100 puncta), I think a scatter plot showing all data points would offer readers a more transparent means of viewing the single-molecule data presented in Figures 3A, B, C, and G. I also didn't see 'n' values for plots shown in Figure 3. 

The box and whisker plots have now been replaced with scatter plots showing all data points. The accompanying ‘n’ values have been included in the figure 3 legend as well as the histograms in figures 1 and 2 that are represented in the comparative scatter plots.  

(3) Given the authors have produced a body of work that challenges conclusions from another pre-print (Tirumala et al., 2022 bioRxiv) - specifically, that dynein is not processive in cells - I think it would be useful to include a short discussion about how their work challenges theirs. For example, one significant difference between the two experimental systems that may account for the different observations could simply be that the authors of the Tirumala study used a mouse DHC (in HeLa cells), which may not have the ability to assemble into active and processive dynein-dynactin-adaptor complexes. 

Thank you for pointing this out! At the time we submitted our manuscript we were conflicted about citing a pre-print that had not been peer reviewed simply to point out the discrepancy. If we had done so at that time we would have proposed the exact potential technical issue that you have proposed here. However, at the time we felt it would be better for these issues to be addressed through the review process. Needless to say, we agree with your interpretation and now that the work is published (Tirumala et al. JCB, 2024) it is entirely appropriate to add a discussion on Tirumala et al. where contradictory observations were reported. 

The following statement has been added to the manuscript: 

“In contrast, a separate study (Tirumala et al., 2024) reported that dynein is not highly processive, typically exhibiting runs of very short duration (~0.6 s) in HeLa cells. A notable technical difference that may account for this discrepancy is that our study visualizes endogenously tagged human DHC, whereas Tirumala et al. characterized over-expressed mouse DHC in HeLa cells. Over-expression of the DHC may result in an imbalance of the subunits that comprise the active motor complex, leading to inactive, or less active complexes. Similarly, mouse DHC may not have the ability to efficiently assemble into active and processive dynein-dynactin-adaptor complexes to the same extent as human DHC.”

Minor points: 

(1) "Specifically, the adaptor BICD2 recruited a single dynein to dynactin while BICDR1 and HOOK3 supported assembly of a "double dynein" complex." It would be more accurate to say that dynein-dynactin complexes assembled with Bicd2 "tend to favor single dynein, and the Bicdr1 and Hook3 tend to favor two dyneins" since even Bicd2 can support assembly of 2 dynein-1 dynactin complexes (see Urnavicius et al, Nature 2018). 

Thank you, the manuscript has been edited to reflect this point. 

(2) "Human HeLa cells were engineered using CRISPR/Cas9 to insert a cassette encoding FKBP and EGFP tags in the frame at the 3' end of the dynein heavy chain (DYNC1H1) gene (SF1)." It is unclear to what "SF1" is referring. 

SF1 is supplementary figure 1, which we have now clarified as being Figure 1 – figure supplement 1A.

(3) "The SiR-Tubulin-treated cells were subjected to two-color TIRFM to determine if the DHC puncta exhibited motility and; indeed, puncta were observed streaming along MTs..." This sentence is strangely punctuated (the ";" is likely a typo?). 

Thank you for pointing this out, the typo has been corrected and the sentence now reads:

“The SiR-Tubulin-treated cells were subjected to two-color TIRFM and DHC-EGFP puncta were clearly observed streaming on Sir-Tubulin labeled MTs, which was especially evident on MTs that were pinned between the nucleus and the plasma membrane (Video 3)”

(4) I am unfamiliar with the "MK" acronym shown above the molecular weight ladders in Figure 3H and I. Did the authors mean to use "MW" for molecular weight? 

We intended this to mean MW and the typo has been corrected.

(5) "This suggests that the cargos, which we presume motile dynein-dynactin puncta are bound to, any kinesins..." This sentence is confusing as written. Did the authors mean "and kinesins"? 

Agreed. We have changed this sentence to now read: 

“The velocity and low switching frequency of motile puncta suggest that any kinesin motors associated with cargos being transported by the dynein-dynactin visualized here are inactive and/or cannot effectively bind the MT lattice during dynein-dynactin-mediated transport in interphase HeLa cells.”

Reviewer 2 (Recommendations for the authors):

(1) I am confused as to why the authors introduced an FKBP tag to the DHC and no explanation is given. Is it possible this tag induces artificial dimerization of the DHC? 

FKBP was tagged to DHC for potential knock sideways experiments. Since the current cell line does not express the FKBP counterpart FRB, having FKBP alone in the cell line would not lead to artificial dimerization of DHC.

(2) The authors use a high concentration of SiR-tubulin (1uM) before washing it out. However, they observe strong effects on MT dynamics. The manufacturer states that concentrations below 100nM don't affect MT dynamics, so I am wondering why the authors are using such a high amount that leads to cellular phenotypes. 

We would like to note that in our hands even 100 nM SiR-tubulin impacted MT dynamics if it was incubated for enough time to get a bright signal for imaging, which makes sense since drugs like docetaxel and taxol become enriched in cells over time. Thus, it was a trade-off between the extent/brightness of labeling and the effects on MT dynamics. We opted for shorter incubation with a higher concentration of Sir-Tubulin to achieve rapid MT labeling and efficient suppression of plus-end MT polymerization. This approach proved useful for our needs since the loss of the tip-tacking pool of DHC provided a clearer view of the motile population of MT-associated DHC.

(3) The individual channels should be labeled in the supplemental movies. 

They have now been labelled.

(4) I would like to see example images and kymographs of the GFP-Kinesin-1 control used for fluorescent intensity analysis. Further, the authors use the mean of the intensity distribution, but I wonder why they don't fit the distribution to a Gaussian instead, as that seems more common in the field to me. Do the data fit well to a Gaussian distribution? 

Example images and kymographs of the kinesin-1-EGFP control HeLa cells used for the updated fluorescent intensity analysis have been now added to the manuscript in Figure 3 - figure supplement 1. The kinesin-1-EGFP transiently expressed in HeLa cells exhibited a slower mean velocity and run length than the endogenously tagged HeLa dynein-dynactin. Regarding the distribution, we applied 6 normality tests to the new datasets acquired with DHC and p50 in comparison to human kinesin-EGFP in HeLa cells. While we are confident concluding that the data for p50 was normally distributed (p > 0.05 in 6/6), it was more difficult to reach conclusions about the normality of the datasets for kinesin-1 (p > 0.05 in 4/6) and DHC (p > 0.5 in 1/6). We have decided to report the data as scatter plots (per the suggestion in major point 1 by reviewer 1) in the new Figure 3G since it could be misleading to fit a non-normal distribution with a single Gaussian. We note that the likely non-normal distribution of the DHC data (since it “passed” only 1/6 normality tests) could reflect the presence of other populations (e.g. 1 DHC-EGFP in a motile puncta), but we could also not confidently conclude this since attempting to fit the data with a double Gaussian did not pass statistical muster. Indeed, as stated in the text, on lines 197-198 we do not exclude that the range of DHC intensities measured here may include sub-populations of complexes containing a single dynein dimer with one DHC-EGFP molecule.   

Ultimately, we feel the safest conclusion is that there was not a statically significant difference between the DHC and kinesin-1 dimers (p = 0.32) but there was a statistically significant difference between both the DHC and kinesin-1 dimers compared to the p50 (p values < 0.001), which was ~50% the intensity of DHC and kinesin-1. Altogether this leads us to the fairly conservative conclusion that DHC puncta contain at least one dimer while the p50 puncta likely contain a single p50-EGFP molecule. 

(5) The authors suggest the microtubules in the cells treated with SiR-tubulin may be more detyrosinated due to the treatment. Why don't they measure this using well-characterized antibodies that distinguish tyrosinated/detyrosinated microtubules in cells treated or not with SiR-tubulin? 

At your suggestion, we carried out the experiment and found that under our labeling conditions there was not a notable difference in microtubule detyrosination between DMSO- and SiR-Tubulin-treated cells. Thus, we have removed this caveat from the revised manuscript.

(6) "While we were unable to assess the relative expression levels of tagged versus untagged DHC for technical reasons." Please describe the technical reasons for the inability to measure DHC expression levels for the reader.

We made several attempts to quantify the relative amounts of untagged and tagged protein by Western blotting. The high molecular weight of DHC (~500kDa) makes it difficult to resolve it on a conventional mini gel. We attempted running a gradient mini gel (4%-15%), and doing a western blot; however, we were still unable to detect DHC. To troubleshoot, the experiments were repeated with different dilutions of a commercially available antibody and varying concentrations of cell lysate; however, we were unable to obtain a satisfactory result. 

We hold the view that even if it had it worked it would have been difficult to detect a relatively small difference between the untagged (MW = 500kDa) and tagged DHC (MW = 527kDa) by western blot. We have added language to this effect in the revised manuscript. 

Reviewer #3 (Public Review):

(1). CRISPR-edited HeLa clones: 

(i) The authors indicate that both the DHC-EGFP and p50-EGFP lines are heterozygous and that the level of DHC-EGFP was not measured due to technical difficulties. However, quantification of the relative amounts of untagged and tagged DHC needs to be performed - either using Western blot, immunofluorescence or qPCR comparing the parent cell line and the cell lines used in this work. 

See response to reviewer 2 above. 

(ii) The localization of DHC predominantly at the plus tips (Fig. 1A) is at odds with other work where endogenous or close-to-endogenous levels of DHC were visualized in HeLa cells and other non-polarized cells like HEK293, A-431 and U-251MG (e.g.: OpenCell (https://opencell.czbiohub.org/target/CID001880), Human Protein Atlas  ), https://www.biorxiv.org/content/10.1101/2021.04.05.438428v3). The authors should perform immunofluorescence of DHC in the parental cells and DHC-EGFP cells to confirm there are no expression artifacts in the latter. Additionally, a comparison of the colocalization of DHC with EB1 in the parental and DHC-EGFP and p50-EGFP lines would be good to confirm MT plus-tip localisation of DHC in both lines. 

The microtubule (MT) plus-tip localization of DHC was already observed in the 1990s, as evidenced by publications such as (PMID:10212138) and (PMID:12119357), which were further confirmed by Kobayashi and Murayama  in 2009 (PMID:19915671). We hold the view that further investigation into this localization is not worthwhile since the tip-tracking behavior of DHC-dynactin has been long-established in the field.

(iii) It would also be useful to see entire fields of view of cells expressing DHC-EGFP and p50EGFP (e.g. in Spinning Disk microscopy) to understand if there is heterogeneity in expression. Similarly, it would be useful to report the relative levels of expression of EGFP (by measuring the total intensity of EGFP fluorescence per cell) in those cells employed for the analysis in the manuscript. 

Representative images of fields have been added as Figure 1 - figure supplement 1B and Figure 2 – figure supplement 1 in the revised manuscript. We did not see drastic cell-tocell variation of expression within the clonal cell lines.

(iv) Given that the authors suspect there is differential gene regulation in their CRISPR-edited lines, it cannot be concluded that the DHC-EGFP and p50-EGFP punctae tracked are functional and not piggybacking on untagged proteins. The authors could use the FKBP part of the FKBPEGFP tag to perform knock-sideways of the DHC and p50 to the plasma membrane and confirm abrogation of dynein activity by visualizing known dynein targets such as the Golgi (Golgi should disperse following recruitment of EGFP-tagged DHC-EGFP or p50-EGFP to the PM), or EGF (movement towards the cell center should cease). 

Despite trying different concentrations and extensive troubleshooting, we were not able to replicate the reported observations of Ciliobrevin D or Dynarrestin during mitosis. We would like to emphasize that the velocity (1.2 μm/s) of dynein-dynactin complexes that we measured in HeLa cells was comparable to those measured in iNeurons by Fellows et al. (PMID: 38407313) and for unopposed dynein under in vitro conditions. 

(2) TIFRM and analysis: 

(i) What was the rationale for using TIRFM given its limitation of visualization at/near the plasma membrane? Are the authors confident they are in TIRF mode and not HILO, which would fit with the representative images shown in the manuscript? 

To avoid overcrowding, it was important to image the MT tracks that that were pinned between the nucleus and the plasma membrane. It is unclear to us why the reviewer feels that true TIRFM could not be used to visualize the movement of dynein-dynactin on this population of MTs since the plasma membrane is ~ 3-5 nm and a MT is ~25-27 nm all of which would fall well within the 100-200 nm excitable range of the evanescent wave produced by TIRF. While we feel TIRF can effectively visualize dynein-dynactin motility in cells, we have mentioned the possibility that some imaging may be HILO microscopy in the materials and methods.

(ii) At what depth are the authors imaging DHC-EGFP and p50-EGFP? 

The imaging depth of traditional TIRFM is limited to around 100-200 nm. In adherent interphase HeLa cells the nucleus is in very close proximity (nanometer not micron scale) to the plasma membrane with some cytoskeletal filaments (actin) and microtubules positioned between the plasma membrane and the nuclear membrane. The fact that we were often visualizing MTs positioned between the nucleus and the membrane makes us confident that we were imaging at a depth (100 - 200nm) consistent with TIRFM. 

(iii) The authors rely on manual inspection of tracks before analyzing them in kymographs - this is not rigorous and is prone to bias. They should instead track the molecules using single particle tracking tools (eg. TrackMate/uTrack), and use these traces to then quantify the displacement, velocity, and run-time. 

Although automated single particle tracking tools offer several benefits, including reduced human effort, and scalability for large datasets, they often rely on specialized training datasets and do not generalize well to every dataset. The authors contend that under complex cellular environments human intervention is often necessary to achieve a reliable dataset. Considering the nature of our data we felt it was necessary to manually process the time-lapses. 

(iv) It is unclear how the tracks that were eventually used in the quantification were chosen. Are they representative of the kind of movements seen? Kymographs of dynein movement along an entire MT/cell needs to be shown and all punctae that appear on MTs need to be tracked, and their movement quantified. 

Considering the densely populated environment of a cell, it will be nearly impossible to quantity all the datasets. We selected tracks for quantification, focusing on areas where MTs were pinned between the nucleus and plasma membrane where we could track the movement of a single dynein molecule and where the surroundings were relatively less crowded. 

(v) What is the directionality of the moving punctae? 

In our experience, cells rarely organized their MTs in the textbook radial MT array meaning that one could not confidently conclude that “inward” movements were minus-end directed. Microtubule polarity was also not able to be determined for the MTs positioned between the plasma membrane and the nucleus on which many of the puncta we quantified were moving. It was clear that motile puncta moving on the same MT moved in the same direction with the exception of rare and brief directional switching events. What was more common than directional switching on the same MT were motile puncta exhibiting changes in direction at sharp (sometimes perpendicular) angles indicative of MT track switching, which is a well-characterized behavior of dynein-dynactin (See DOI: 10.1529/biophysj.107.120014).

(vi) Since all the quantification was performed on SiR tubulin-treated cells, it is unclear if the behavior of dynein observed here reflects the behavior of dynein in untreated cells. Analysis of untreated cells is required. 

It was important to quantify SiR tubulin-treated cells because SiR-Tubulin is a docetaxel derivative, and its addition suppressed plus-end MT polymerization resulting in a significant reduction in the DHC tip-tracking population and a clearer view of the motile population of MT-associated DHC puncta. Otherwise, it was challenging to reliably identify motile puncta given the abundance of DHC tip-tracking populations in untreated cells.  

(3) Estimation of stoichiometry of DHC and p50 

Given that the punctae of DHC-EGFP and p50 seemingly bleach on MT before the end of the movie, the authors should use photobleaching to estimate the number of molecules in their punctae, either by simple counting the number of bleaching steps or by measuring single-step sizes and estimating the number of molecules from the intensity of punctae in the first frame. 

Comparing the fluorescence intensity of a known molecule (in our case a kinesin-1EGFP dimer) to calculate the numbers of an unknown protein molecule (in our case Dynein or p50) is a widely accepted technique in the field. For example, refer to PMID: 29899040. To accurately estimate the stoichiometry of DHC and p50 and address the concerns raised by other reviewers, we expressed the human kinesin-EGFP in HeLa cells and analyzed the datasets from new experiments. We did not observe any significant differences between our old and new datasets.

(4) Discussion of prior literature 

Recent work visualizing the behavior of dyneins in HeLa cells (DOI:  10.1101/2021.04.05.438428), which shows results that do not align with observations in this manuscript, has not been discussed. These contradictory findings need to be discussed, and a more objective assessment of the literature in general needs to be undertaken.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public Review):

Overall, it's a well-performed study, however, causality between Plscr1 and Ifnlr1 expression needs to be more firmly established. This is because two recent studies of PLSCR1 KO cells infected with different viruses found no major differences in gene expression levels compared with their WT controls (Xu et al. Nature, 2023; LePen et al. PLoS Biol, 2024). There were also defects in the expression of other cytokines (type I and II IFNs plus TNF-alpha) so a clear explanation of why Ifnlr1 was chosen should also be given.

We appreciate the reviewer’s reference to the two recently published research on PLSCR1’s role in SARS-CoV-2 infections. We have also discussed those studies in the Introduction and Discussion sections of this manuscript. Here, we would like to clarify ourselves for the rationale of investigating Ifn-λr1 signaling.

The reviewer mentioned “defects in the expression of other cytokines (type I and II IFNs plus TNF-alpha)” and requested a clearer explanation of why Ifnlr1 was chosen for study. In our investigation of IAV infection, we observed no defects in the expression of type I and II IFNs or TNF-α in Plscr1^-/- mice; rather, these cytokines were expressed at even higher levels compared to WT controls (Figures 2D and 3A). This indicates that the type I and II IFN and TNF-α signaling pathways remain intact and are not negatively affected by the loss of Plscr1. Notably, Ifn-λr1 expression is the only one among all IFNs and their receptors that is significantly impaired in Plscr1^-/- mice (Figure 3A), justifying our focused investigation of this receptor. To further clarify this point, we have expanded the explanation under the section titled “Plscr1 Binds to Ifn-λr1 Promoter and Activates Ifn-λr1 Transcription in IAV Infection” within the Results. The reviewer noted that previously published studies “found no major differences in gene expression levels compared with their WT controls”, but neither study examined Ifn-λr1 expression.

(1) The authors propose that Plscr1 restricts IAV infection by regulating the type III IFN signaling pathway. While the data show a positive correlation between Ifnlr1 and Plscr1 levels in both mouse and cell culture models, additional evidence is needed to establish causality between the impaired type III IFN pathway, and the increased susceptibility observed in Plscr1-KO mice. To strengthen this conclusion, the following experiments could be undertaken: (i) Measure IAV titers in WT, Plscr1-KO, Ifnlr1-KO, and Plscr1/ Ifnlr1-double KO cells. If the antiviral activity of Plscr1 is highly dependent on Ifnlr1, there should be no further increase in IAV titers in double KO cells compared to single KO cells; (ii) over-express Plscr1 in Ifnlr1-KO cells to determine if it still inhibits IAV infection. If Plscr1's main action is to upregulate Ifnlr1, then it should not be able to rescue susceptibility since Ifnlr1 cannot be expressed in the KO background. If Plscr1 over-expression rescues viral susceptibility, then there are Ifnlr1-independent mechanisms involved. These experiments should help clarify the relative contribution of the type III IFN pathway to Plscr1-mediated antiviral immunity.

We agree with the reviewer that additional evidence is necessary to establish causality between the impaired type III IFN pathway and the increased susceptibility observed in Plscr1-KO mice. As requested by the reviewer, and one step further, we have measured IAV titers in Wt, Plscr1^-/-, Ifn-λr1^-/-, and Plscr1^-/-Ifn-λr1^-/- mouse lungs, which provided us with more comprehensive information at the tissue and organismal level compared to cell culture models. Our results are detailed under “The Anti-Influenza Activity of Plscr1 Is Highly Dependent on Ifn-λr1” within “Results” section and in Supplemental Figure 5. Importantly, there was no further increase in weight loss (Supplemental Figure 5B), total BAL cell counts (Supplemental Figure 5C), neutrophil percentages (Supplemental Figure 5D), and IAV titers (Supplemental Figure 5E) in Plscr1^-/-Ifn-λr1^-/- mouse lungs compared to Ifn-λr1^-/- mouse lungs. These findings indicate that the antiviral activity of Plscr1 is largely dependent on Ifn-λr1.

We agree that overexpression of Plscr1 on an Ifn-λr1^-/- background would provide additional evidence to support our conclusion from the Plscr1^-/-Ifn-λr1^-/- mice. In future studies, we plan to specifically overexpress Plscr1 in ciliated epithelial cells on the Ifn-λr1^-/- background by breeding Plscr1^floxStopFoxj1-Cre⁺Ifn-λr1^-/- mice. In addition, ciliated epithelial cells isolated from Ifn-λr1^-/- murine airways could be transduced with a Plscr1 construct for overexpression. We hypothesize that overexpression of Plscr1 in ciliated epithelial cells will not rescue susceptibility in Ifn-λr1^-/- mice or cells, since our Plscr1^-/-Ifn-λr1^-/- mouse model suggest that Ifn-λr1-independent anti-influenza functions of Plscr1 are likely minor compared to its role in upregulating Ifn-λr1. These future plans have been added to the “Discussion” section, and we look forward to presenting our results in a forthcoming publication.

(3) In Figure 4, the authors demonstrate the interaction between Plscr1 and Ifnlr1. They suggest that this interaction modulates IFN-λ signaling. However, Figures 5C-E show that the 5CA mutant, which lacks surface localization and the ability to bind Ifnlr1, exhibits similar anti-flu activity to WT Plscr1. Does this mean the interaction between Plscr1 and Ifnlr1 is dispensable for Plscr1-mediated antiviral function? Can the authors compare the activation of IFN-λ signaling pathway in Plscr1-KO cells expressing empty vector, WT Plscr1, and 5CA mutant? This could be done by measuring downstream ISG expression or using an ISRE-luciferase reporter assay upon IFN-λ treatment.

We agree with the reviewer that downstream activation of the IFN-λ signaling pathway is a critical component of the proposed regulatory role of PLSCR1. As suggested, we attempted to perform an ISRE-luciferase reporter assay following IFN-λ treatment in PLSCR1 rescue cell lines by transfecting the cells with hGAPDH-rLuc (Addgene #82479) and pGL4.45 [luc2P/ISRE/Hygro] (Promega #E4041).

Despite extensive efforts over several months, we were unable to achieve expression of pGL4.45 [luc2P/ISRE/Hygro] in PLSCR1 rescue cells using either Lipofectamine 3000 or electroporation, as no firefly luciferase activity was detected at baseline or following IFN-λ treatment. In contrast, hGAPDH-rLuc was robustly expressed in these cells.

The pGL4.45 [luc2P/ISRE/Hygro] plasmid was obtained directly from Promega as a purified product, and its sequence was confirmed via whole plasmid sequencing. Additionally, both hGAPDH-rLuc and pGL4.45 [luc2P/ISRE/Hygro] were successfully expressed in 293T cells, indicating that neither the plasmids nor the transfection protocols are inherently faulty.

We suspect that prior modifications to the PLSCR1 rescue cells—such as CRISPR-mediated knockout and lentiviral transduction—may interfere with successful transfection of pGL4.45 [luc2P/ISRE/Hygro] through an as-yet-unknown mechanism. Although these results are disappointing, we will continue troubleshooting and plan to communicate in a separate manuscript once the luciferase assay is successfully established.

Reviewer #1 (Recommendations):

(1) In the introduction, the linkage between the paragraph discussing type III IFN and PLSCR1 needs to be better established. The mention of PLSCR1 being an ISG at the outset may help connect these two paragraphs and make the text appear more logical.

We apologize for the lack of linkage and logic between type 3 IFN and PLSCR1. We have introduced PLSCR1 as an ISG at the beginning of its paragraph as recommended. 

(2) The statement that, “Intriguingly, PLSCR1 is also an antiviral ISG, as its expression can be highly induced by type 1 and 2 interferons in various viral infections[15, 16]. However, whether its expression can be similarly induced by type 3 interferon has not been studied yet.” is incorrect. Xu et al. tested the role of PLSCR1 in type III IFN-induced control of SARS-CoV-2 (ref. 24). This needs to be revised.

We apologize for the incorrect information in the introduction and have revised the paragraph with the proper citation.

(3) In Figure 3B, can the authors provide a comprehensive heatmap that includes all ISGs above the threshold, rather than only a subset? This would offer a more complete overview of the changes in type I, II, and III IFN pathways in Plscr1-KO mice.

As suggested by the reviewer, we have provided a comprehensive heatmap that includes all ISGs above the threshold in Figure 3C (previously Figure 3B). We identified a total of 1,113 ISGs in our dataset with a fold change ≥2. Enlarged heatmaps with gene names are provided in Supplemental Figure 1. Among those ISGs, 584 are regulated exclusively by type 1 IFNs, and 488 are regulated by both type 1 and type 2 interferons. Unfortunately, the Interferome database does not include information on type 3 IFN-inducible genes in mice[1]. Although many ISGs were robustly upregulated in Plscr1^-/- infected lungs, consistent with inflammation data, a large subset of ISGs failed to be transcribed when Ifn-λr1 function was impaired, especially at 7 dpi. We suspect that those non-transcribed ISGs in Plscr1^-/- mice may be specifically regulated by type 3 IFN and represent interesting targets for future research. These results have been added to “Plscr1 Binds to Ifn-λr1 Promoter and Activates Ifn-λr1 Transcription in IAV Infection” within “Results” section.

(4) In Figure 3C, 5B and 7H, immunoblots should also be included to measure changes of Ifnlr1/IFNLR1 protein level.

As requested by the reviewer, we have provided western blots measuring Ifn-λr1/IFN-λR1 protein level in Figure 5B and 7I. The protein expressions were consistent with the PCR results.

(5) In Figure 3H, the amount of RPL30 is also low in the anti-PLSCR1-treated and IgG samples, making it difficult to estimate if ChIP binding is genuinely impacted.

RPL30 Exon 3 serves as a negative control in the ChIP experiment and is not expected to bind either the anti-PLSCR1-treated or the IgG control samples. Anti-Histone H3 treatment is a positive control, with the treated sample expected to show binding to RPL30 Exon 3. We hope this clarification has addressed any further potential confusion from the reviewer.

(6) In Figure 4A, can the authors show a larger slice of the gel with molecular weight markers for both Plscr1 and Ifnlr1. In the coIP, the binding may be indirect through intermediate partners. Proximity ligation assay is a more direct assay for interaction and can be stated as such.

As suggested by the reviewer, we have included whole gel images of Figure 4A with molecular weight markers for both Plscr1 and Ifnlr1 in Supplemental Figure 3. We appreciate the reviewer’s affirmation of proximity ligation assay and have stated it as a more direct assay for interaction under “Plscr1 Interacts with Ifn-λr1 on Pulmonary Epithelial Cell Membrane in IAV Infection” in “Results” section.

(7) In Figure 5A, how is the expression of PLSCR1 WT and mutants driven by an EF-1α promoter can be further upregulated by IAV infection? Can the authors also use immunoblots to examine the protein level of PLSCR1?

We apologize for the confusion and appreciate the reviewer’s careful observation. We were initially surprised by this finding as well, but upon further investigation, we found out that the human PLSCR1 primers used in our qRT-PCR assay can still detect the transcription from the undisturbed portion of the endogenous PLSCR1 mRNA, even in PLSCR1^-/- cells. In the original Figure 5A, data for vector-transduced PLSCR1^-/- were not included because PCR was not performed on those samples at the time. After conducting PCR for vector-transduced PLSCR1^-/- cells, we detected transcription of PLSCR1, which confirms that the signaling originates from endogenous DNA, but not from the EF-1α promoter-driven PLSCR1 plasmid. Please see Author response image 1 below.

Author response image 1.

The forward human PLSCR1 primer we used matches 15-34 nt of Wt PLSCR1, and the reverse primer matches 224-244 nt of Wt PLSCR1. CRISPR-Cas9 KO of PLSCR1 was mediated by sgRNAs in A549 cells and was performed by Xu et al[2]. sgRNA #1 matches 227-246 nt, sgRNA #2 matches 209-228 nt, and sgRNA #3 matches 689-708 nt of Wt PLSCR1. The sgRNAs likely introduced a short deletion or insertion that does not affect transcription. However, those endogenous mRNA transcripts cannot be translated to functional and detectable PLSCR1 proteins, as validated by our western blot (below), as well as western blots performed by Xu et al[2]. Therefore, our primers could amplify endogenous PLSCR1 transcripts upregulated by IAV infection, if 15-244 nt was not disturbed by CRISPR-Cas9 KO. By western blot, we confirmed that only endogenous PLSCR1 expression is upregulated by IAV infection, and exogenous protein expression of PLSCR1 plasmids driven by an EF-1α promoter are not upregulated by IAV infection.

Author response image 2.

To avoid confusion, we have removed the original Figure 5A from the manuscript.

(8) In Figure 5C, the loss of anti-flu activity with the H262Y mutant is modest, suggesting the loss of ifnlr1 transcription is only partly responsible for the susceptibility of Plscr1 KO cells. The anti-flu activity being independent of scramblase activity resembles the earlier discovery of SARS-CoV-2 (Xu et al., 2024). This could be stated in the results since it is an important point that scramblase activity is dispensable for several major human viruses and shifts the emphasis regarding mechanism. It has been appropriately noted in the discussion.

We appreciated the comments and have acknowledged the consistency of our results with those of Xu et al. under “Both Cell Surface and Nuclear PLSCR1 Regulates IFN-λ Signaling and Limits IAV Infection Independent of Its Enzymatic Activity” in the “Results” section.

Reviewer #2 (Recommendations):

(1) The statement that type I interferons are expressed by “almost all cells” is inaccurate (line 61). Type I IFN production is also context-dependent and often restricted to specific cell types upon infection or stimulation.

We apologize for the inaccurate description of the expression pattern of type 1 IFNs and have corrected the restricted cellular sources of type 1 IFNs in the “Introduction”.

(2) The antiviral response is assessed solely through flu M gene expression. Incorporating infectious virus titers (e.g., TCID50 or plaque assay) would provide a more robust and direct measure of antiviral activity.

As requested by the reviewer, we have performed plaque assays on all experiments where flu M gene expression levels were measured (Figure 1G, 5E and 7F, and Supplemental Figure 6E). The plaque assay results are consistent with the flu M gene expressions.

(3) While mRNA expression of interferons is measured, protein levels (e.g., through ELISA) should also be quantified to establish the functional relevance of IFN expression changes.

As requested by the reviewer, we have quantified the protein level of IFN-λ in mouse BAL with ELISA (Figure 2E). The ELISA results are consistent with the mRNA expressions of IFN-λ.

(4) It is unclear whether reduced IFNLR1 expression translates to defective downstream signaling or antiviral responses after IFN-λ treatment in PLSCR1-deficient cells. This is particularly pertinent given the increase in IFN-λ ligand in vivo, which might compensate for receptor downregulation.

We agree with the reviewer that downstream activation of the IFN-λ signaling pathway is a critical aspect of PLSCR1’s proposed regulatory role. To investigate this, we attempted an ISRE-luciferase reporter assay to assess downstream signaling following IFN-λ treatment in PLSCR1 rescue cells. Unfortunately, the experiment encountered unforeseen technical issues. For additional context, please refer to our response to Reviewer #1’s public review #3.

(5) Detailed gating strategies for immune cell subsets are absent and should be included for clarity and reproducibility.

We would like to clarify that the immune cell subsets in BAL fluids were counted manually following cytospin preparation and Diff-Quik staining (Figure 2B and 7H, and Supplemental Figures 2C, 5D, and 8D), rather than by flow cytometry. We hope this resolves the reviewer’s confusion.

(6) The study does not definitively establish that reduced IFN-λ signaling causes the observed in vivo phenotype. Increased morbidity and mortality in PLSCR1-deficient mice could also stem from elevated TNF-α levels and lung damage, as proinflammatory cytokines and/or enhanced lung damage are known contributors to influenza morbidity and mortality. This point warrants detailed discussions.

We agreed with the reviewer that this study does not guarantee a definitive causality between reduced IFN-λ signaling and increased morbidity of Plscr1^-/- mice and more experiments are needed to reach the conclusion. We have acknowledged this limitation of our study in the “Discussion”, as requested by the reviewer. We hope to fully eliminate the confounding elements and definitively establish the proposed causality in future studies.

Reviewer #3 (Public review):

Summary:

Yang et al. have investigated the role of PLSCR1, an antiviral interferon-stimulated gene (ISG), in host protection against IAV infection. Although some antiviral effects of PLSCR1 have been described, its full activity remains incompletely understood.

This study now shows that Plscr1 expression is induced by IAV infection in the respiratory epithelium, and Plscr1 acts to increase Ifn-λr1 expression and enhance IFN-λ signaling possibly through protein-protein interactions on the cell membrane.

Strengths:

The study sheds light on the way Ifnlr1 expression is regulated, an area of research where little is known. The study is extensive and well-performed with relevant genetically modified mouse models and tools.

Weaknesses:

There are some issues that need to be clarified/corrected in the results and figures as presented.

Also, the study does not provide much information about the role of PLSCR1 in the regulation of Ifn-λr1 expression and function in immune cells. This would have been a plus.

We would like to thank the reviewer for the positive feedback and insightful comment regarding the roles of PLSCR1 and IFN-λR1 in immune cells. It is important to note that IFN-λR1 expression is highly restricted in immune cells and is primarily limited to neutrophils and dendritic cells[3]. While dendritic cells were not the focus of this study, we did examine all immune cell subsets in our single cell RNA seq data and performed infection experiments in Plscr1^floxStop/LysM-Cre⁺ mice. We have not observed any significant findings in these populations. On the other hand, we do have some interesting preliminary data suggesting a role for PLSCR1 in regulating Ifn-λr1 expression and function in neutrophils. These findings are discussed in detail in our response to reviewer #3’s recommendation #12.

Reviewer #3 (Recommendations):

(1) In Figure 1B, the Plscr1 label should be moved to the y-axis so that readers don't confuse it with the Plscr1-/- mice used in the other figure panels. The fact that WT mice were used should be added in the figure legend.

We apologize for the confusion in the figures. We have moved Plscr1 label to the y-axis in Figure 1B and have mentioned Wt mice were used in the figure legend.

(2) In Figure 1C and D, the type of dose leading to the presented data should be added to help the reader. Also, shouldn't statistics be added?

We appreciate the suggestion and have added doses to Figure 1C and 1D. We are confused about the request of adding statistics by the reviewer, as two-way ANOVA tests were used to compare weight losses, and the significance was labeled on the figures.

(3) In Figures 1, F, and G, it is not indicated whether sublethal or lethal dose was used for the IAV infection. This should be very clear in the figure and figure legend.

We apologize for the confusion of infection doses used in the figures. We have added doses to Figure 1F, 1G and 1H.

(4) In Figure 1, the CTCF abbreviation should be explained in the Figure legend.

We have explained CTCF in the figure legend as requested.

(5) In Figure 2B, this is percentages of what?

Figure 2B shows the percentages of each immune cell type within total BAL cells.

(6) In Figures 3A and B, transcriptomes for each condition are from how many mice? Also, what do heatmaps show? Fold induction, differences, etc, and from what? What is compared with what? In addition, is there a discordance between the RNAseq data of Figure 3A and the qPCR data of Fig. 3C in terms of Ifnlr1 expression?

In Figure 3A and 3C (previously 3B), RNA from the whole lungs of 9 mice per PBS-treated group and 4 mice per IAV-infected group were pooled for transcriptomic analysis. Figure 3A represents a heatmap of differential gene expression, while Figure 3C (previously 3B) represents fold changes in gene expression relative to uninfected controls. In both heatmaps, gene expression values are color-coded from row minimum (blue) to row maximum (red), enabling comparison across groups within each gene (row). The major comparison of interest in these heatmaps is between Wt infected mice versus Plscr1^-/- infected mice. We have added this information to the figure legend.

We also acknowledge the reviewer’s observation regarding the discordance between the RNA seq data of Figure 3A and the qPCR data of Figure 3B (previously 3C) for Ifnlr1 expression. To address this, we have repeated the qRT-PCR experiment with additional samples at 7 dpi. In the updated results, Wt mice consistently show significantly higher Ifn-λr1 expression than Plscr1^-/- infected mice at both 3 dpi and 7 dpi, consistent with the RNA seq data. However, a time-dependent discrepancy between the RNA-seq and qRT-PCR datasets remains: Ifn-λr1 expression continues to increase at 7 dpi in the RNA-seq data (Figure 3A), whereas it declines in the qRT-PCR results (Figure 3B). The reason for this discrepancy remains unclear and has been addressed in the Discussion section.

(7) In Figure 3D, have the authors checked whether the Ifnlr1 antibody they use is indeed specific for Ifnlr1? Have they used any blocking peptide for the anti-mouse Ifn-λr1 polyclonal antibody they are using? Also, in Figure 3E, the marker used for staining should be indicated in the pictures of the lung section.

Unfortunately, a blocking peptide is not available for the anti-mouse Ifn-λr1 polyclonal antibody used in our study. To assess antibody specificity, we have performed immunofluorescence staining of Ifn-λr1 on lung tissues from Ifn-λr1^-/- mice using the same antibody. No signal was detected (Supplemental Figure 5A), supporting the specificity of the antibody for Ifn-λr1.

As requested by the reviewer, we have added the marker (Ifn-λr1) to the pictures of the lung section in Figure 3E.

(8) In Figure 5, it's better to move each graph's label that stands to the top (e.g. PLSCR1, IFN-λR1 etc) to the y-axis label so that it doesn't get confused with the mouse -/- label.

We apologize for the confusion and have moved the top label to the y-axis in Figure 5.

(9) In Figure 6A, it is claimed that the 'two-dimensional UMAP demonstrated that these main lung cell populations (epithelial, endothelial, mesenchymal, and immune) were dynamic over the course of infection.'. This is not clear by the data. The percentage of cells per cluster should be calculated.

As requested by the reviewer, the proportion (Supplemental Figure 6A) and cell count (Supplemental Figure 6B) of each cluster have been calculated and included in “PLSCR1 Expression Is Upregulated in the Ciliated Airway Epithelial Compartment of Mice following Flu Infection” under “Results” section. Together with the two-dimensional UMAP (Figure 6A), these data demonstrate that the main lung cell populations (epithelial, endothelial, mesenchymal, and immune) were dynamic over the course of infection. Following infection, many populations emerged, particularly within the immune cell clusters. At the same time, some clusters were initially depleted and later restored, such as microvascular endothelial cells (cluster 2). Other populations, such as interferon-responsive fibroblasts (cluster 20), showed a dramatic yet transient expansion during acute infection and disappeared after infection resolved.

(10) In Figure 6 B and C, the legend should indicate that these are Violin plots. Also, if AT2 cells don't express Plscr1, does that indicate that in these cells Plscr1 is not needed for IFN-λR1 expression?

As requested, we have indicated in the legend of Figure 6B and 6C that these are violin plots. Plscr1 is expressed at low levels in AT2 cells. However, it is unclear whether Plscr1 is needed for Ifn-λr1 expression in AT2 cells, and it would be interesting to investigate further.

(11) In lines 302-304, it is stated that 'Among the various epithelial populations, ciliated epithelial cells not only had 303 the highest aggregated expression of Plscr1, but also were the only epithelial cell 304 population in which significantly more Plscr1 was induced in response to IAV infection.'. Which data/ figure support this statement?

Figure 6B shows that among the various epithelial populations, ciliated epithelial cells had the highest aggregated expression of Plscr1. To better illustrate this statement, we have rearranged the order of cell clusters from highest to lowest Plscr1 expression, and added red dots to indicate the mean expression levels for each cluster in Figure 6B.

Ciliated epithelial cells also had the most significant increase in Plscr1 expression (p < 2.22e-16 and p = 6.7e-05) in early IAV infection at 3 dpi (Figure 6C and Supplemental Figure 7A-7K). In comparison, AT1 cells were the only other epithelial cluster to show Plscr1 upregulation at 3dpi, but to a much less extent (p = 0.033, Supplemental Figure 7J). Supplemental Figure 7 was added to better support the statement and the explanation was added to “PLSCR1 Expression Is Upregulated in the Ciliated Airway Epithelial Compartment of Mice following Flu Infection” under “Results” section.

(12) As earlier, if Plscr1 is not expressed in neutrophils (Figure 6F), does that mean IFN-λR1 expression does not require Plscr1 in these cells?

Although Plscr1 is expressed at lower levels in neutrophils compared to epithelial cells, it is still detectable. In fact, our preliminary data suggest that IFN-λR1 expression in neutrophils is dependent on Plscr1. We have isolated neutrophils from peripheral blood and BAL of IAV-infected Wt and Plscr1^-/- mice using a mouse neutrophil enrichment kit. Quantitative PCR results showed that Plscr1^-/- neutrophils exhibit significantly lower expression of Ifn-λr1, alongside elevated levels of Il-1β, Il-6 and Tnf-α in IAV infection (see figures below). These findings suggest that Plscr1 may play an anti-inflammatory role in neutrophils by upregulating Ifn-λr1. These data were not included in the current manuscript because they are beyond the scope of current study, but we hope to address the role of PLSCR1 in regulating IFN-λR1 expression and function in neutrophils in a future study.

Author response image 3.

(13) The Figure 7A legend is not well stated. Something like ' Schematic representation of the experimental design of...' should be included. Also, Figure 7J is not referenced in the text.

We apologize for the unclear Figure 7A legend and have changed it to “Schematic representation of the experimental design of ciliated epithelial cell conditional Plscr1 KI mice.” Figure 8 (previously Figure 7J) has now been referenced in the text.

(14) In the Methods, more specific information in some parts should be provided. For example, the clones of the antibodies used should be included.

Apart from the 10x technology, the kits used and the type of the Illumina sequencing should be provided. Information on how the QC was performed (threshold for reads/cell, detected genes/per cells, and % of mitochondrial genes etc) should be added.

We apologize for the missing information in the “Methods”. We have now provided the clones of the antibodies used, the kit used to generate single-cell transcriptomic libraries, the type of the Illumina sequencing, and the QC performance data.

References

(1) Rusinova, I., et al., Interferome v2.0: an updated database of annotated interferon-regulated genes. Nucleic Acids Res, 2013. 41(Database issue): p. D1040-6.

(2) Xu, D., et al., PLSCR1 is a cell-autonomous defence factor against SARS-CoV-2 infection. Nature, 2023. 619(7971): p. 819-827.

(3) Donnelly, R.P., et al., The expanded family of class II cytokines that share the IL-10 receptor-2 (IL-10R2) chain. J Leukoc Biol, 2004. 76(2): p. 314-21.

Reviewer #1 (Public review):

Here the authors discuss mechanisms of ligand binding and conformational changes in GlnBP (a small E Coli periplasmic binding protein, which binds and carries L-glutamine to the inner membrane ATP-binding cassette (ABC) transporter). The authors have distinguished records in this area and have published seminal works. They include experimentalists and computational scientists. Accordingly, they provide a comprehensive, high quality, experimental and computational work.

They observe that apo- and holo- GlnBP do not generate detectable exchange between open and (semi-) closed conformations on timescales between 100 ns and 10 ms. Especially, the ligand binding and conformational changes in GlnBP that they observe are highly correlated. Their analysis of the results indicates a dominant induced-fit mechanism, where the ligand binds GlnBP prior to conformational rearrangements. They then suggest that an approach resembling the one they undertook can be applied to other protein systems where the coupling mechanism of conformational changes and ligand binding.

They argue that the intuitive model where ligand binding triggers a functionally relevant conformational change was challenged by structural experiments and MD simulations revealing the existence of unliganded closed or semi-closed states and their dynamic exchange with open unbound conformations, discuss alternative mechanisms that were proposed, their merits and difficulties, concluding that the findings were controversial, which, they suggest is due to insufficient availability of experimental evidence to distinguish them. As to further specific conclusions they draw from their results, they determine that a conformational selection mechanism is incompatible with their results, but induced fit is. They thus propose induced fit as the dominant pathway for GlnBP, further supported by the notion that the open conformation is much more likely to bind substrate than the closed one based on steric arguments.

The paper here, which clearly embodies massive careful and high-quality work, is extensive, making use of a range of experimental approaches, including isothermal titration calorimetry, single-molecule Förster resonance energy transfer, and surface-plasmon resonance spectroscopy. The problem the authors undertake is of fundamental importance.

Author response:

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

Reviewer #1 (Public Review):

Here the authors discuss mechanisms of ligand binding and conformational changes in GlnBP (a small E Coli periplasmic binding protein, which binds and carries L-glutamine to the inner membrane ATP-binding cassette (ABC) transporter). The authors have distinguished records in this area and have published seminal works. They include experimentalists and computational scientists. Accordingly, they provide comprehensive, high-quality, experimental and computational work. They observe that apo- and holo- GlnBP does not generate detectable exchange between open and (semi-) closed conformations on timescales between 100 ns and 10 ms. Especially, the ligand binding and conformational changes in GlnBP that they observe are highly correlated. Their analysis of the results indicates a dominant induced-fit mechanism, where the ligand binds GlnBP prior to conformational rearrangements. They then suggest that an approach resembling the one they undertook can be applied to other protein systems where the coupling mechanism of conformational changes and ligand binding. They argue that the intuitive model where ligand binding triggers a functionally relevant conformational change was challenged by structural experiments and MD simulations revealing the existence of unliganded closed or semi-closed states and their dynamic exchange with open unbound conformations, discuss alternative mechanisms that were proposed, their merits and difficulties, concluding that the findings were controversial, which, they suggest is due to insufficient availability of experimental evidence to distinguish them. As to further specific conclusions they draw from their results, they determine that a conformational selection mechanism is incompatible with their results, but induced fit is. They thus propose induced fit as the dominant pathway for GlnBP, further supported by the notion that the open conformation is much more likely to bind substrate than the closed one based on steric arguments. Considering the landscape of substrate-free states, in my view, the closed state is likely to be the most stable and, thus most highly populated. As the authors note and I agree that state can be sterically infeasible for a deep-pocketed substrate. As indeed they also underscore, there is likely to be a range of open states. If the populations of certain states are extremely low, they may not be detected by the experimental (or computational) methods. The free energy landscape of the protein can populate all possible states, with the populations determined by their relative energies. In principle, the protein can visit all states. Whether a particular state is observed depends on the time the protein spends in that state. The frequencies, or propensities, of the visits can determine the protein function. As to a specific order of events, in my view, there isn't any. It is a matter of probabilities which depend on the populations (energies) of the states. The open conformation that is likely to bind is the most favorable, permitting substrate access, followed by minor, induced fit conformational changes. However, a key factor is the ligand concentration. Ligand binding requires overcoming barriers to sustain the equilibrium of the unliganded ensemble, thus time. If the population of the state is low, and ligand concentration is high (often the case in in vitro experiments, and high drug dosage scenarios) binding is likely to take place across a range of available states. This is however a personal interpretation of the data. The paper here, which clearly embodies massive careful, and high-quality work, is extensive, making use of a range of experimental approaches, including isothermal titration calorimetry, single-molecule Förster resonance energy transfer, and surface-plasmon resonance spectroscopy. The problem the authors undertake is of fundamental importance.

Reviewer #2 (Public Review):

The manuscript by Han et al and Cordes is a tour-de-force effort to distinguish between induced fit and conformational selection in glutamine binding protein (GlnBP). 

We thank the referee for the recognition of the work and effort that has gone into this manuscript. 

It is important to say that I don't agree that a decision needs to be made between these two limiting possibilities in the sense that whether a minor population can be observed depends on the experiment and the energy difference between the states. That said, the authors make an important distinction which is that it is not sufficient to observe both states in the ligand-free solution because it is likely that the ligand will not bind to the already closed state. The ligand binds to the open state and the question then is whether the ligand sufficiently changes the energy of the open state to effectively cause it to close. The authors point out that this question requires both a kinetic and a thermodynamic answer. Their "method" combines isothermal titration calorimetry, single-molecule FRET including key results from multi-parameter photon-by-photon hidden Markov modelling (mpH2MM), and SPR. The authors present this "method" of combination of experiments as an approach to definitively differentiate between induced fit and conformational selection. I applaud the rigor with which they perform all of the experiments and agree that others who want to understand the exact mechanism of protein conformational changes connected to ligand binding need to do such a multitude of different experiments to fully characterize the process. However, the situation of GlnBP is somewhat unique in the high affinity of the Gln (slow offrate) as compared to many small molecule binding situations such as enzyme-substrate complexes. It is therefore not surprising that the kinetics result in an induced fit situation. 

For us these comments are an essential part of the conceptual aspects of our work and the resulting research. From a descriptive viewpoint, it is essential for us (and we tried to further highlight and stress this in the updated version of our paper) that IF and CS are two kinetic mechanisms of ligand binding. They imply – if active in a biomolecular system – a temporal order and timescale separation of ligand binding and conformational changes. Since we found many conflicting results for the binding mechanism of GlnBP, but also other SPBs, we decided to assess the situation in GlnBP. 

In the case of the E-S complexes I am familiar with, the dissociation is much more rapid because the substrate binding affinity is in the micromolar range and therefore the re-equilibration of the apo state is much faster. In this case, the rate of closing and opening doesn't change much whether ligand is present or not. Here, of course, once the ligand is bound the re-equilibration is slow. Therefore, I am not sure if the conclusions based on this single protein are transferrable to most other protein-small molecule systems. 

We do not argue that our results and interpretations are valid for most other protein-ligand systems may those be enzymes or simple ligand binders. Yet, based on the conservation of ABC-related SBPs and the fact that quite a few of them show sub-µM Kds, we render it likely to find many analogous situations as for GlnBP also based on our previous results e.g., from de Boer et al., eLife (2019).

I am also not sure if they are transferrable to protein-protein systems where both molecules the ligand and the receptor are expected to have multiscale dynamics that change upon binding.

As we argue above the two mechanisms IF/CS imply a clear temporal order and separation of timescales for ligand binding and conformational changes. These mechanisms are simple and extreme cases that we tested before more complex kinetic schemes are inferred for the description of ligand binding and conformational changes (which might not be necessary). 

Strengths:

The authors provide beautiful ITC data and smFRET data to explore the conformational changes that occur upon Gln binding. Figure 3D and Figure 4 (mpH2MM data) provide the really critical data. The multi-parameter photon-by-photon hidden Markov modelling (mpH2MM) data. In the presence of glutamine concentrations near the Kd, two FRET-active sub-populations are identified that appear to interconvert on timescales slower than 10 ms. They then do a whole bunch of control experiments to look for faster dynamics (Figure 5). They also do TIRF smFRET to try to compare their results to those of previous publications. Here, they find several artifacts are occurring including inactivation of ~50% of the proteins. They also perform SPR experiments to measure the association rate of Gln and obtain expectedly rapid association rates on the order of 10^{^}8 M-1s-1.

Thank you.  

Weaknesses:

Looking at the traces presented in the supplementary figures, one can see that several of the traces have more than one molecule present. The authors should make sure that they use only traces with a single photobleaching event for each fluorophore. One can see steps in some of the green traces that indicate two green fluorophors (likely from 2 different molecules) in the traces. This is one of the frequent problems with TIRF smFRET with proteins, that only some of the spots represent single molecules and the rest need to be filtered out of the analysis.

We have inspected all TIRF data provided with the manuscript and assume that the referee refers to data shown in current Appendix Figure 4/5. We agree that those traces in which no photo bleaching occurs could potentially be questioned, yet they would not change our interpretations and thus decided to leave the figure as is.

The NMR experiments that the authors cite are not in disagreement with the work presented here. NMR is capable of detecting "invisible states" that occur in 1-5% of the population. SmFRET is not capable of detecting these very minor states. I am quite sure that if NMR spectroscopists could add very high concentrations of Gln they would also see a conversion to the closed population.

We agree with the referee that NMR is capable of detecting invisible states that occur in 1-5% of the population (see e.g., the paper cited in our manuscript by Tang, C et al., Open-to-closed transition in apo maltose-binding protein observed by paramagnetic NMR. Nature 2007, 449, 1078). Yet, we see a strong disagreement between our work and papers on GlnBP, where a combination of NMR, FRET and MD was used (Feng, Y. et al., Conformational Dynamics of apo‐GlnBP Revealed by Experimental and Computational Analysis. Angewandte Chemie 2016, 55, 13990; Zhang, L. et al., Ligand-bound glutamine binding protein assumes multiple metastable binding sites with different binding affinities. Communications biology 2020, 3, 1). These inconsistencies were also noted by others in the field (Kooshapur, H. et al., NMR Analysis of Apo Glutamine‐Binding Protein Exposes Challenges in the Study of Interdomain Dynamics. Angewandte Chemie 2019, 58, 16899) and we reemphasize that this latest NMR publication comes to similar conclusions as we present in our manuscript.   

Reviewer #1 (Recommendations For The Authors):

The paper embodies massive careful and high-quality work, and is extensive, making use of a range of experimental approaches, including isothermal titration calorimetry, single-molecule Förster resonance energy transfer, and surface-plasmon resonance spectroscopy. Considering this extensiveness, I do not see what more the authors can do.

We very much appreciate the assessment and positive comments of the referee, but still tried to incorporate simulation data to support our interpretations.

Reviewer #2 (Recommendations For The Authors):

(1) Looking at the traces presented in the supplementary figures, one can see that several of the traces have more than one molecule present. The authors should make sure that they use only traces with a single photobleaching event for each fluorophore. One can see steps in some of the green traces that indicate two green fluorophors (likely from 2 different molecules) in the traces. This is one of the frequent problems with TIRF smFRET with proteins, that only some of the spots represent single molecules and the rest need to be filtered out of the analysis.

See response above for iteration of TIRF data selection and analysis.

(2) The NMR experiments that the authors cite are not in disagreement with the work presented here. NMR is capable of detecting "invisible states" that occur in 1-5% of the population. SmFRET is not capable of detecting these very minor states. I am quite sure that if NMR spectroscopists could add very high concentrations of Gln they would also see a conversion to the closed population.

See response above.

Minor point:

(1) It is difficult to see what is going on between apo and holo in Figure 1B. Could the authors make Figure 1a, 1b apo, and 1b holo in the same orientation (by aligning D2 or D1 to each other in all figures) so one can see which helices are in the same place and which have moved?

We respectfully disagree and decided to keep this figure as it is

Author response:

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

Reviewer #1 (Public review):

Summary:

This study focuses on the bacterial metabolite TMA, generated from dietary choline. These authors and others have previously generated foundational knowledge about the TMA metabolite TMAO, and its role in metabolic disease. This study extends those findings to test whether TMAO's precursor, TMA, and its receptor TAAR5 are also involved and necessary for some of these metabolic phenotypes. They find that mice lacking the host TMA receptor (Taar5-/-) have altered circadian rhythms in gene expression, metabolic hormones, gut microbiome composition, and olfactory and innate behavior. In parallel, mice lacking bacterial TMA production or host TMA oxidation have altered circadian rhythms.

Strengths:

These authors use state-of-the-art bacterial and murine genetics to dissect the roles of TMA, TMAO, and their receptor in various metabolic outcomes (primarily measuring plasma and tissue cytokine/gene expression). They also follow a unique and unexpected behavioral/olfactory phenotype. Statistics are impeccable.

Weaknesses:

Enthusiasm for the manuscript is dampened by some ambiguous writing and the presentation of ideas in the introduction, both of which could easily be improved upon revision.

We apologize for the abbreviated and ambiguous writing style in our original submission. Given Reviewer 2 also suggested reorganizing and rewriting certain parts, we have spent time to remove ambiguity by adding additional points of clarification and adding more historical context to justify studying TMA-TAAR5 signaling in regulating host circadian rhythms. We have also reorganized the presentation of data aligned with this.

Reviewer #2 (Public review):

Summary:

In the manuscript by Mahen et al., entitled "Gut Microbe-Derived Trimethylamine Shapes Circadian Rhythms Through the Host Receptor TAAR5," the authors investigate the interplay between a host G protein-coupled receptor (TAAR5), the gut microbiota-derived metabolite trimethylamine (TMA), and the host circadian system. Using a combination of genetically engineered mouse and bacterial models, the study demonstrates a link between microbial signaling and circadian regulation, particularly through effects observed in the olfactory system. Overall, this manuscript presents a novel and valuable contribution to our understanding of hostmicrobe interactions and circadian biology. However, several sections would benefit from improved clarity, organization, and mechanistic depth to fully support the authors' conclusions.

Strengths:

(1) The manuscript addresses an important and timely topic in host-microbe communication and circadian biology.

(2) The studies employ multiple complementary models, e.g., Taar5 knockout mice, microbial mutants, which enhance the depth of the investigation.

(3) The integration of behavioral, hormonal, microbial, and transcript-level data provides a multifaceted view of the observed phenotype.

(4) The identification of olfactory-linked circadian changes in the context of gut microbes adds a novel perspective to the field.

Weaknesses:

While the manuscript presents compelling data, several weaknesses limit the clarity and strength of the conclusions.

(1) The presentation of hormonal, cytokine, behavioral, and microbiome data would benefit from clearer organization, more detailed descriptions, and functional grouping to aid interpretation.

We appreciate this comment and have reorganized the data to improve functional grouping and readability. We have also added additional detail to descriptions of the data in the revised figure legends and results.

(2) Some transitions-particularly from behavioral to microbiome data-are abrupt and would benefit from better contextual framing.

We agree with this comment, and have added additional language to provide smoother transitions. This in many cases brings in historical context of why we focused on both behavioral and microbiome alterations in this body of work.

(3) The microbial rhythmicity analyses lack detail on methods and visualization, and the sequencing metadata (e.g., sample type, sex, method) are not clearly stated.

We apologize for this, and have now added more detail in our methods, figures, and figure legends to ensure the reader can easily understand sample type, sex, and the methods used. 

(4) Several figures are difficult to interpret due to dense layouts or vague legends, and key metabolites and gene expression comparisons are either underexplained or not consistently assessed across models.

Aligned with the last comment we now added more detail in our methods, figures, and figure legends to provide clear information. We have now provided additional data showing the same key metabolites, hormones, and gene expression alterations in each model if the same endpoints were measured.

(5) Finally, while the authors suggest a causal role for TAAR5 and its ligand in circadian regulation, the current data remain correlative; mechanistic experiments or stronger disclaimers are needed to support these claims.

We agree with this comment, and as a result have removed any language causally linking TMA and TAAR5 together in circadian regulation. Instead, we only state finding in each model and refrain from overinterpreting.

Reviewer #3 (Public review):

Summary:

Deletion of the TMA-sensor TAAR5 results in circadian alterations in gene expression, particularly in the olfactory bulb, plasma hormones, and neurobehaviors.

Strengths:

Genetic background was rigorously controlled.

Comprehensive characterization.

Weaknesses:

The weaknesses identified by this reviewer are minor.

Overall, the studies are very nicely done. However, despite careful experimentation, I note that even the controls vary considerably in their gene expression, etc, across time (eg, compare control graphs for Cry 1 in IB, 4B). It makes me wonder how inherently noisy these measurements are. While I think that the overall point that the Taar5 KO shows circadian changes is robust, future studies to dissect which changes are reproducible over the noise would be helpful.

We thank the reviewer for this insightful comment. We completely agree that there are clear differences in the circadian data in experiments from Taar5^-/- mice and those from gnotobiotic mice where we have genetically deleted CutC. Although the data from Taar5^-/- mice show nice robust circadian rhythms, the data from mice where microbial CutC is altered have inherently more “noise”. We attribute some of this to the fact that the Taar5^-/- mouse experiment have a fully intact and diverse gut microbiome . Whereas, the gnotobiotic study with CutC manipulation includes only a 6 member microbiome community that does not represent the normal microbiome diversity in the gut. This defined synthetic community was used as a rigorous reductionist approach, but likely affected the normal interactions between a complex intact gut microbiome and host circadian rhythms. We have added some additional discussion to indicate this in the limitations section of the manuscript.

Impact:

These data add to the growing literature pointing to a role for the TMA/TMAO pathway in olfaction and neurobehavioral.

Reviewer #1 (Recommendations for the authors):

I suggest a revision of the writing and organization. The potential impact of the study after reading the introduction is unclear. One example, in the intro, " TMAO levels are associated with many human diseases including diverse forms of CVD5-12, obesity13,14, type 2 diabetes15,16, chronic kidney disease (CKD)17,18, neurodegenerative conditions including Parkinson's and Alzheimer's disease19,20, and several cancers21,22" It would be helpful to explain how the previous literature has distinguished that the driver of these phenotypes is TMA/TMAO and not increased choline intake. Basically, for a TMA/O novice reader, a more detailed intro would be helpful.

We appreciate this insightful comment and have now provided a more expansive historical context for the reader regarding the effects of choline consumption (which impacts many things, including choline, acetylcholine, phosphatidylcholine, TMA, TMAO, etc) versus the primary effects of TMA and TMAO.

There were also many uses of vague language (regulation/impact/etc). Directionality would be super helpful.

We thank the reviewer for this recommendation and have improved language as suggested to show directionality of our findings. The terms regulation, impact, shape etc. are used only when we describe multiple variable changing at the same time over the time course of a 24-hour circadian period (some increased and some decreased).

Reviewer #2 (Recommendations for the authors):

In the manuscript by Mahen et al., entitled "Gut Microbe-Derived Trimethylamine Shapes Circadian Rhythms Through the Host Receptor TAAR5," the authors investigate the interplay between a host G protein-coupled receptor (TAAR5), the gut microbiota-derived metabolite trimethylamine (TMA), and the host circadian system. Using a combination of genetically engineered mouse and bacterial models, the study demonstrates a link between microbial signaling and circadian regulation, particularly through effects observed in the olfactory system. Overall, this manuscript presents a novel and valuable contribution to our understanding of hostmicrobe interactions and circadian biology. However, several sections would benefit from improved clarity, organization, and mechanistic depth to fully support the authors' conclusions. Below are specific major and minor suggestions intended to enhance the presentation and interpretation of the data.

Major suggestions:

(1) Consider adding a schematic/model figure as Panel A early in the manuscript to help readers understand the experimental conditions and major comparisons being made.

We thank the reviewer for this recommendation and have added a graphical abstract figure to help the reader understand the major comparisons being made. 

(2) Could the authors present body weight and food intake characteristics in Taar5 KO vs. WT animals?

We have added body weight data as requested in Figure 1, Figure supplement 1. Although we have not stressed these mice with a high fat diet for these behavioral studies, under chow-fed conditions studied here we did not find any significant differences in body weight. Given no difference in body weight, we did not collect data on food consumption and have mentioned this as a limitation in the discussion.  

(3) Several figures, especially Figures 3 and 4, and Supplemental Figures, would benefit from more structured organization and expanded legends. Grouping related data into thematic panels (e.g., satiety vs. appetite hormones, behavioral domains) may help improve readability.

We appreciate the reviewer’s thoughtful comments and agree that reorganization would improve clarity. We have reorganized figures to improve clarity and have expanded the figure legends to provide more detail on experimental methods. 

(4) Clarify and expand the description of hormonal and cytokine changes. For instance, the phrase "altered rhythmic levels" is vague - do the authors mean dampened, phase-shifted, enhanced, etc., relative to WT controls?

Given a similar suggestion was made by Reviewer 1, we have provided more precise language focused on directionality and which specific endpoints we are referring to. For anything looking at circadian rhythms, the revised manuscript includes specific indications when we are discussing mesor, amplitude, and acrophase alterations. The terms regulation, impact, shape etc. are used only when we describe multiple complex variables changing at the same time over the time course of a 24-hour circadian period (some increased and some decreased).

(5) Consider grouping hormones and cytokines functionally (e.g., satiety vs. appetite-stimulating, pro- vs. antiinflammatory) to better interpret how these changes relate to the KO phenotype.

We thank the reviewer for this recommendation, and have re-organized figure panels to reflect this.

(6) Please provide a more detailed description of the behavioral results, particularly those in Supplemental Figure 2.

We have both expanded the methods description in the revised figure legends, but have also added a more detailed description of the behavioral results.

(7) As with hormonal data, behavioral outcomes would be easier to follow if organized thematically (e.g., locomotor activity, anxiety-like behavior, circadian-related behavior), especially for readers less familiar with behavioral assays.

We appreciate this reviewer’s comment and agree that we can better group our data to show how each test is associated with the type of behavior it assesses. As a result we have reorganized the behavioral data into broad categories such as olfactory-related, innate, cognitive, depressive/anxiety-like, or social behaviors. We have also new data in each of these behavioral categories to provide a more comprehensive understanding of behavioral alterations seen in Taar5^-/- mice.

(8) The following statement needs clarification: "Also, it is important to note that many behavioral phenotypes examined, including tests not shown, were unaltered in Taar5-/- mice (Figures S2G, S2H, and S2I)." Consider rephrasing to explicitly state the intended message: are the authors emphasizing a lack of behavioral phenotype, or highlighting specific unaltered aspects?

We apologize for this confusing statement, and have changed the verbiage to improve readability. To expand the comprehensive nature of this study, we also now include the tests that were “not shown” in the original submission to provide a more comprehensive understanding of behavioral alterations seen in Taar5^-/- mice. These new data are included as 6 different figure supplements to main Figure 2.

(9) The transition from behavior to microbiome data feels abrupt. Can the authors better explain whether the behavioral changes are thought to result from gut microbial function, independent of TMA-Taar5 signaling?

We apologize for the poor transitions in our writing style. We have spent time to explain the previous findings linking the TMA pathway to circadian reorganization of the gut microbiome (mostly coming from our original paper Schugar R, et al. 2022, eLife) and how this correlates with behavioral phenotypes. Although at this point it is difficult to know whether the microbiome changes are driving behavioral changes, or vice versa it could be central TAAR5 signaling is altering oscillations in gut microbiome, we present our findings here as a framework for follow up studies to more precisely get at these questions. It is important to note that our experiment using defined community gnotobiotic mice with or without the capacity to produce TMA (i.e. CutC-null community) shows that clearly microbial TMA production can impact host circadian rhythms in the olfactory bulb. Additional experiments beyond the scope of this work will be required to test which phenotypes originate from TMA-TAAR5 signaling versus more broad effects of the restructured gut microbiome.

(10) For Figure 3A, please expand the microbiome results with more granularity:

(a) Indicate in the Results section whether the sequencing method was 16S amplicon or metagenomic.

Sequencing was done using 16S rRNA amplicon sequencing using methods published by our group (PMID: 36417437, PMID: 35448550).

(b) State whether samples were from males, females, or a mix. 

We have indicated that all mice from Figure 1 were male mice in the revised figure legend.

(c) Clarify whether beta diversity is based on phylogenetic or non-phylogenetic metrics. Consider using both  types if not already done.

Beta diversity was analyzed using the Bray-Curtis dissimilarity index as the metric. Details have been included in the methods section.

(d) Make lines partially transparent in the Beta-diversity plot so that individual points are visible.

We have now updated the Beta-diversity plot with individual points visualized.

(e) Clarify what percentage of variation in the Beta-diversity plot is explained by CCA1, and whether this low percentage suggests minimal community-level differences.

We have updated the Beta-diversity plot to include the R² and p-values associated with these data.

(f) Confirm if the y-axis on the Beta-diversity plot should be labeled CCA2 rather than "CCAA 1".

We appreciate this comments, given it identified a typographical error in the plot. The revised figure now include the proper label of CCA2 instead of CCAA 1.

(11) For Figure 3B:

(a) Provide a description of the taxonomy plot in the results.

We have added a description of the taxonomy plot in the revised results section.

(b) Add phylum-level labels and enlarge the legend to improve the readability of genus-level data.

We agree this is a good suggestion so have enlarged the legend for the genus-level data and have also added phylum-level plots as well in the revised manuscript in Figure 3, figure supplement 1.

(12) Rhythmicity of the microbiome is central to the manuscript. The current approach of comparing relative abundance at discrete time points is limiting.

We thank the reviewer for this comment. We agree with this statement that discrete timepoint are not enough to describe circadian rhythmicity. In addition to comparing genotypes at discrete time points, we also used a rigorous cosinor analysis to plot the data over a 24-hour time period, and those differences are shown in the figure itself as well as Table 1. 

(a) Please describe how rhythmicity was determined, e.g., what data or statistical method supports the statement: "Taar5-/- mice showed loss of the normal rhythmicity for Dubosiella and Odoribacter genera yet gained in amplitude of rhythmicity for Bacteroides genera (Figure 3 and S3)."

We appreciate this reviewer comment. Rhythmicity was determined using a cosinor analysis by use of an R program. Cosinor analysis is a statistical method used to model and analyze rhythmic patterns in time-series data, typically assuming a sinusoidal (cosine) shape. It estimates key parameters like mesor (mean level), amplitude (height of oscillation), and acrophase (timing of the peak), making it especially useful in fields like chronobiology and circadian rhythm research. We have used this in previous research to describe circadian rhythms. We do plan to improve language considering directionality of these circadian changes. 

(b) Supplemental Figure S3 needs reorganization to highlight key findings. It's not currently clear how taxa are arranged or what trends are being shown.

The data in Figure S3 show the entire 24-hour time course of the cecal taxa that were significantly altered for at least one time point between Taar5^+/+ and Taar5^-/- mice. Given we showed time pointspecific alterations in the Main Figure 3, we thought these more expansive plots would be important to show to depict how the circadian rhythms were altered.

(c) Supplemental Table 1, which includes 16S features, should be referenced and discussed in the microbiome section.

We have now referenced and discussed Supplemental Table 1 which includes all cosinor statistics for microbiome and other data presented in circadian time point studies.

(13) Did the authors quantify the 16S rRNA gene via RT-PCR to determine if this was similar between KO and WT over the 24-hour period?

We did not quantify 16S rRNA gene via RT-PCR, but do not think adding this will change our overall interpretations.

(14) Reorganize Figure 4 to align with the order of results discussed-starting with TMA and TMAO, followed by related metabolites like choline, L-carnitine, and gamma-butyrobetaine.

We thank the reviewer for this comment. We have chosen this organization because it is ordered from substrates (choline, L-carnitine, and betaine) to the microbe-associated products (TMA then TMAO). We will improve the writing associated with this figure to clearly explain this organization.

(a) Although the changes in the latter metabolites are more modest, they may still have physiological relevance. Could the authors comment on their significance?

We appreciate this reviewer comment and agree. We have expanded the results and discussion to address this.

(15) The authors note similarities in circadian gene expression between Taar5 KO mice and Clostridium sporogenes WT vs. ΔcutC mice, but the gene patterns are not consistent.

(a) Can the authors clarify what conclusions can reasonably be drawn from this comparison?

We hesitate to make definitive conclusions in the manuscript on why the gene patterns are not consistent, because it would be speculation. However, one major factor likely driving differences is the status of the diversity of the gut microbiome in the different studies. For instance, in the studies using Taar5^+/+ and Taar5^-/- mice there is a very diverse microbiome in these conventionally housed mice. In contrast, by design the experiment using Clostridium sporogenes WT vs. ΔcutC communities is a reductionist approach that allows us to genetically define TMA production. In these gnotobiotic mice, the simplified community has very limited diversity and this likely alters the host circadian rhythms in gene expression quite dramatically. Although it is impossible to directly compare the results between these experiments given the difference microbiome diversity, there are clearly alterations in host gene expression when we manipulate TMA production (i.e. ΔcutC community) or TMA sensing (i.e. Taar5^-/-). 

(16) Were circadian and metabolic genes (e.g., Arntl, Cry1, Per2, Pemt, Pdk4) also analyzed in brown adipose tissue of Taar5 KO mice, and how do these results compare to the Clostridium models?

We thank the reviewer for this comment. Unfortunately, we did not collect brown adipose tissue in our original Taar5 study. We plan on doing this in future follow up studies studying cold-induced thermogenesis that are beyond the scope of this manuscript. However, we have decided to include data from our two timepoint Taar5 study which looks at ZT2 (9am) and ZT14 (9pm). There are clear differences in circadian genes between these timepoints. 

(17) To allow a more direct comparison, please ensure the same cytokines (e.g., IL-1β, IL-2, TNF-α, IFN-γ, IL6, IL-33) are reported for both the Taar5 KO and microbial models.

We thank the reviewer for this comment and now include data from the same cytokines for each study.

(18) What was the defined microbial community used to colonize germ-free mice with C. sporogenes strains? Did this community exhibit oscillatory behavior?

To define TMA levels using a genetically-tractable model of a defined microbial community, we leveraged access to the community originally described by our collaborator Dr. Federico Rey (University of Wisconsin – Madison) (PMID: 25784704). We chose this community because it provide some functional metabolic diversity and is well known to allow for sufficient versus deficient TMA production. We are thankful for the reviewer comments about oscillatory behavior of this defined community, and to be responsive have performed sequencing to detect the species over time. These data are now included in the revised manuscript and show that there are clear differences in the oscillatory behavior of the defined community members. These data provide additional support that bacterial TMA production not only alters host circadian rhythms, but also the rhythmic behavior of gut bacteria themselves which has never been described before.

(19) Can the authors explain the rationale for measuring additional metabolites such as tryptophan, indole acetic acid, phenylacetic acid, and phenylacetylglycine? How are these linked to CutC gene function or Taar5 signaling?

We appreciate that this could be confusing, but have included other gut microbial metabolites to be as comprehensive as possible. This is important to include because we have found in other gnotobiotic studies where we have genetically altered metabolite production, if we alter one gut microbe-derived metabolite there can be unexpected alterations in other distinct classes of microbe-derived metabolites (PMID: 37352836). This is likely due to the fact that complex microbe-microbe and microbehost interactions work together to define systemic levels of circulating metabolites, influencing both the production and turnover of distinct and unrelated metabolites.

(20) The authors make several strong claims suggesting that loss of Taar5 or disruption of its ligand directly alters the circadian gene network. However, the current data are correlative. The authors should clarify that these findings demonstrate associations rather than direct causal effects, unless additional mechanistic evidence is provided. Approaches such as studies conducted in constant darkness, measurements of wheelrunning behavior, or analyses that control for potential confounding factors, e.g., inflammation or metabolic disruption, would help establish whether the observed changes in clock gene expression are primary or secondary effects. The authors are encouraged to either soften these causal claims or acknowledge this limitation explicitly in the discussion.

We thank the reviewer for this comment. We agree and have softened our language about direct effects of TMA via TAAR5 because we agree the data presented here are correlative only. 

Minor suggestions:

(1) Avoid repetitive phrases such as "it is important to note..." for improved flow. Rephrasing these instances will enhance readability.

We thank the reviewer for this suggestion and have deleted such repetitive phrases.  

(2) For Figure 2, remove interpretations above he graphs and use simple, descriptive panel labels, similar to those in Supplemental Figure 2.

We have removed these interpretations as suggested, but have retained descriptive panel labels to help the reader understand what type of data are being presented.

Reviewer #3 (Recommendations for the authors):

Minor:

In Figure 1D, UCP1 does not appear to be significantly changed.

We thank the reviewer for this comment and agree that UCP1 gene expression is not significantly altered . However, given the key role that UCP1 plays in white adipose tissue beiging, which is suppressed by the TMAO pathway, we think it is critical to show that this effect appears unaffected by perturbed TMA-TAAR5 signaling.

It would be helpful, in the discussion, to summarize any consistent changes across Taar5 KO, CutC deletion, and FMO3 deletion.

We have added this to the discussion, but as discussed above we hesitate to make strong interpretations about consistency between the models because the microbiome diversity is so different between the studies, and we did not measure all endpoints in both models.

For the Cosinor analysis, it may be helpful to remove the p-values that are >0.05 from the figures.

We have now removed any non-significant p-values that are associated with our figures. 

For Figure 2, Supplement 1E, what are the two bars for each genotype?

We appreciate the reviewer pointing this out and will further explain this test in the figure with labels and in the legend.

Author response:

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

Editors comments:

I would encourage you to submit a revised version that addresses the following two points:

[a] The point from Reviewer #1 about a possible major confounding factor. The following article might be germane here: Baas and Fennell, 2019: https://papers.ssrn.com/sol3/papers.cfm?abstract_id=3339568

I don’t believe that the point raised by reviewer 1 is a confounder, see my response below.

This article highlighted was in my reading list, but I did not cite it because I was confused by its methods.

The point from Reviewer #4 about the abstract. It is important that the abstract says something about how reviewers reacted to the original versions of articles in which they were cited (ie, the odds ratio = 0.84, etc result), before going on to discuss how they reacted to revised articles (ie, the odds ratio = 1.61, etc result). I would suggest doing this along the following lines - but please feel free to reword the passage "but this effect was not strong/conclusive":

When reviewers were cited in the original version of the article under review, they were less likely to approve the article compared with reviewers who were not cited, but this effect was not strong/conclusive (odds ratio = 0.84; adjusted 99.4% CI: 0.69-1.03). However, when reviewers were cited in the revised version of the article, they were more likely to approve compared with reviewers who were not cited (odds ratio = 1.61; adjusted 99.4% CI: 1.16-2.23).

I have changed the abstract to include the odds ratios for version 1 and have used the same wording as from the main text.

Reviewer #1 (Public review):

Summary:

The work used open peer reviews and followed them through a succession of reviews and author revisions. It assessed whether a reviewer had requested the author include additional citations and references to the reviewers' work. It then assessed whether the author had followed these suggestions and what the probability of acceptance was based on the authors decision. Reviewers who were cited were more likely to recommend the article for publication when compared with reviewers that were not cited. Reviewers who requested and received a citation were much likely to accept than reviewers that requested and did not receive a citation.

Strengths and weaknesses:

The work's strengths are the in-depth and thorough statistical analysis it contains and the very large dataset it uses. The methods are robust and reported in detail.

I am still concerned that there is a major confounding factor: if you ignore the reviewers requests for citations are you more likely to have ignored all their other suggestions too? This has now been mentioned briefly and slightly circuitously in the limitations section. I would still like this (I think) major limitation to be given more consideration and discussion, although I am happy that it cannot be addressed directly in the analysis.

This is likely to happen, but I do not think it’s a confounder. A confounder needs to be associated with both the outcome and the exposure of interest. If we consider forthright authors who are more likely to rebuff all suggestions, then they would receive just as many citation and self-citation requests as authors who were more compliant. The behaviour of forthright authors would likely only reduce the association seen in most authors which would be reflected in the odds ratios.

Reviewer #2 (Public review):

Summary:

This article examines reviewer coercion in the form of requesting citations to the reviewer's own work as a possible trade for acceptance and shows that, under certain conditions, this happens.

Strengths:

The methods are well done and the results support the conclusions that some reviewers "request" self-citations and may be making acceptance decisions based on whether an author fulfills that request.

Weakness:

I thank the author for addressing my comments about the original version.

Reviewer #3 (Public review):

Summary:

In this article, Barnett examines a pressing question regarding citing behavior of authors during the peer review process. In particular, the author studies the interaction between reviewers and authors, focusing on the odds of acceptance, and how this may be affected by whether or not the authors cited the reviewers' prior work, whether the reviewer requested such citations be added, and whether the authors complied/how that affected the reviewer decision-making.

Strengths:

The author uses a clever analytical design, examining four journals that use the same open peer review system, in which the identities of the authors and reviewers are both available and linkable to structured data. Categorical information about the approval is also available as structured data. This design allows a large scale investigation of this question.

Weaknesses:

My original concerns have been largely addressed. Much more detail is provided about the number of documents under consideration for each analysis, which clarifies a great deal.

Much of the observed reviewer behavior disappears or has much lower effect sizes depending on whether "Accept with Reservations" is considered an Accept or a Reject. This is acknowledged in the results text. Language has been toned down in the revised version.

The conditional analysis on the 441 reviews (lines 224-228) does support the revised interpretation as presented.

No additional concerns are noted.

Reviewer #4 (Public review):

Summary:

This work investigates whether a citation to a referee made by a paper is associated with a more positive evaluation by that referee for that paper. It provides evidence supporting this hypothesis. The work also investigates the role of self-citations by referees where the referee would ask authors to cite the referee's paper.

Strengths:

This is an important problem: referees for scientific papers must provide their impartial opinions rooted in core scientific principles. Any undue influence due to the role of citations breaks this requirement. This work studies the possible presence and extent of this.

The methods are solid and well done. The work uses a matched pair design which controls for article-level confounding and further investigates robustness to other potential confounds.

Weaknesses:

The authors have addressed most concerns in the initial review. The only remaining concern is the asymmetric reporting and highlighting of version 1 (null result) versus version 2 (rejecting null). For example the abstract says "We find that reviewers who were cited in the article under review were more likely to recommend approval, but only after the first version (odds ratio = 1.61; adjusted 99.4% CI: 1.16 to 2.23)" instead of a symmetric sentence "We find ... in version 1 and ... in version 2".

The latest version now includes the results for both versions.

Reviewer #1 (Public review):

Summary:

Overexpression of the mRNA binding protein Ssd1 was shown before to expand the replicative lifespan of yeast cells, whereas ssd1 deletion had the opposite effect. Here, the authors provide initial evidence that overproduced Ssd1 might act via sequestration of mRNAs of the Aft1/2-dependent iron regulon. Ssd1 overexpression restricts activation of the iron regulon and limits accumulation of Fe2+ inside cells, thereby likely lowering oxidative damage. The effects of Ssd1 overexpression and calorie restriction on lifespan are epistatic, suggesting that they might act through the same pathway.

Strengths:

The study is well-designed and involves analysis of single yeast cells during replicative aging. The findings are well displayed and largely support the derived model, which also has implications on lifespan of other organisms including humans.

Weaknesses:

The model is largely supported by the findings, however they remain correlative at the same time. Whether the knockout of ssd1 shortens lifespan by increased intracellular Fe2+ levels is unknown and the shortened lifespan might be caused by different Ssd1 functions. The finding that increased Ssd1 levels form condensates in a cell-cycle dependent is interesting, yet the role of the condensates in lifespan expansion remains untested and unlinked.

Comments on revisions:

In their revised version and response letter the authors have largely addressed my previous concerns. I would have liked to see an experimental response to some of the points of criticism, but I accept that they have been addressed purely in writing. There are some aspects that should be further elaborated by the authors. I agree that determining the mRNAs that co-sequester with Ssd1 foci will be part of an independent study, yet whether Ssd1 foci are relevant for lifespan expansion remains unclear and I would have hoped for some more detailed consideration on this point in the discussion section. Similarly, it should be clearly stated that the impact of Ssd1 overexpression is unlinked from the cellular function of Ssd1 produced at authentic levels and that the short-lived phenotype of a ssd1 knockout is likely not caused by overactivation of the iron regulon (based on the author´s reply). I will appreciate it if the authors include these aspects more clearly in the discussion.

Reviewer #2 (Public review):

This manuscript describes the use of a powerful technique called microfluidics to elucidate the mechanisms explaining how overexpression (OE) of Ssd1 and caloric restriction (CR) in yeast extend replicative lifespan (RLS). Microfluidics measures RLS by trapping cells in chambers mounted to a slide. The chambers hold the mother cell but allow daughters to escape. The slide, with many chambers, is recorded during the entire process, roughly 72 hours, with the video monitored afterwards to count how many daughters each of the trapped mothers produces. The power of the method is what can be done with it. For example, the entire process can be viewed by fluorescence so that GFP and mCherry-tagged proteins can be followed as cells age. The budding yeast is the only model where bona fide replicative aging can be measured, and microfluidics is the only system that allows protein localization and levels to be measured in a single cell while aging. The authors do a wonderful job of showing what this combination of tools can do.

The authors had previously shown that Ssd1, an mRNA-binding protein, extends RLS when overexpressed. This was attributed to Ssd1 sequestering away specific mRNAs under stress, likely leading to reduced ribosomal function. It remained completely unknown how Ssd1 OE extended RLS. The authors observed that overexpressed, but not normally expressed, Ssd1 formed cytoplasmic condensates during mitosis that are resolved by cytokinesis. When the condensates fail to be resolved at the end of mitosis, this signals death.

It has become clear in the literature that iron accumulation increases with age within the cell. The transcriptional programs that activate the iron regulon also become elevated in aging cells. This is thought to be due to impaired mitochondrial function in aging cells, with increased iron accumulation as an attempt at restoring mitochondrial activity. The authors show that Ssd1 OE and CR both reduce the expression of the iron regulon. The data presented indicate that iron accumulation shortens RLS: deletion of iron regulon components extends RLS, and adding iron to WT cells decreases RLS, but not when Ssd1 is overexpressed or when cells are calorically restricted. Interestingly, iron chelation using BPS has no impact on WT RLS, but decreases the elevated RLS in CR cells and cells overexpressing Ssd1. It was not initially clear why iron chelation would inhibit the extended lifespan seen with CR and Ssd1 OE. This was addressed by an experiment where it was shown that the iron regulon is induced (FIT2 induction) when iron is chelated. Thus, the detrimental effects of induction of the iron regulon by BPS and iron accumulation on RLS cannot be tempered by Ssd1 OE and CR once turned on.

Comments on Revised Version:

I am content with the authors' responses to my prior comments.

Author response:

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

Reviewer #2 (Public review):

(1) Why would BPS not reduce RLS in WT cells? The authors could test whether OE of FIT2 reduces RLS in WT cells.  

Our data indicate that the iron regulon gets turned on naturally in old cells, presumably due to reduced iron sensing, limiting their lifespan. Although we haven’t tested it experimentally, BPS would also turn on the iron regulon presumably in wild type cells and therefore would have a redundant effect with the activation of the iron regulon that occurs naturally during normal aging. It may be interesting in the future to see if higher levels of BPS can shorten the lifespan of wildtype cells. Similarly, we would predict that overexpression of FIT2 may reduce the lifespan, as its deletion has been shown to extend RLS.  

(2) The authors should add a brief explanation for why the GDP1 promoter was chosen for Ssd1 OE.

We used the same promoter that was used to overexpress Ssd1 in all previous studies. This is now stated in the text along with the relevant citations. 

(3) On page 12, growth to saturation was described as glucose starvation. This is more accurately described as nutrient deprivation. Referring to it as glucose starvation is akin to CR, which growing to saturation is not. Ssd1 OE formed condensates upon saturation but not in CR. Why do the authors think Ssd1 OE did not form condensates upon CR?

Too mild a stress?

This is a fair comment, and we have now changed glucose starvation to nutrient deprivation, as it is more accurate. The effects of nutrient starvation are profound: the cell cycle stops, autophagy is induced, cells undergo the diauxic shift, metabolism changes. None of these changes occur during calorie restriction (0.05% glucose) such that it is not too surprising that Ssd1 does not form condensates during CR. We speculate that the stress is just too mild.   

(4) The authors conclude that the main mechanism for RLS extension in CR and Ssd1 OE is the inhibition of the iron regulon in aging cells. The data certainly supports this. However, this may be an overstatement as other mutations block CR, such as mutations that impair respiration. The authors do note that induction of the iron regulon in aging cells could be a response to impaired mitochondrial function. Thus, it seems that the main goal of CR and Ssd1 OE may be to restore mitochondrial function in aging cells, one way being inactivation of the iron regulon. A discussion of how other mutations impact CR would be of benefit.

While some labs have shown that respiration impacts CR, this is not the case in other studies. For example, an impactful paper by Kaeberlein et al., PLOS Genetics 2005 showed that CR does extend lifespan in respiratory deficient strains using many different strain backgrounds.

(5) The cell cycle regulation of Ssd1 OE condensates is very interesting. There does not appear to be literature linking Ssd1 with proteasome-dependent protein turnover. Many proteins involved in cell cycle regulation and genome stability are regulated through ubiquitination. It is not necessary to do anything here about it, but it would be interesting to address how Ssd1 condensates may be regulated with such precision.

we see no evidence of changes in Ssd1 protein intensity during the cell cycle. The difference therefore we speculate is at the post translational level rather than Ssd1 degradation and there are known cell cycle regulated phosphatase and kinase that regulates Ssd1 phosphorylation and condensation state whose timing of function match when the Ssd1 condensates appear and dissolve in the cell cycle. We have now discussed this and elude to it in the model. 

(6) While reading the draft, I kept asking myself what the relevance to human biology was. I was very impressed with the extensive literature review at the end of the discussion, going over how well conserved this strategy is in yeast with humans. I suggest referring to this earlier, perhaps even in the abstract. This would nail down how relevant this model is for understanding human longevity regulation.

Thank you, we have now mentioned in the abstract the relevance to human work. 

In conclusion, I enjoyed reading this manuscript, describing how Ssd1 OE and CR lead to RLS increases, using different mechanisms. However, since the 2 strategies appear to be using redundant mechanisms, I was surprised that synergism was not observed.

We thank the reviewer for their kind comment. We propose that Ssd1 overexpression impacts the levels of the iron regulon transcripts, which would be downstream of the point in the pathway that is affected by CR, i.e., nuclear localization of Aft1. The lack of synergy fits with this model, as Ssd1 overexpression cannot impact the iron regulon transcripts if they are not induced due to CR. We have now improved the model to make the impact of these different anti-aging interventions on activation of the iron regulon more clear.

Reviewer #3 (Public review):

My main concern is that the central reasoning of the paper-that Ssd1 overexpression and CR prevent the activation of the iron regulon-appears to be contradicted by previous findings, and the authors may actually be misrepresenting these studies, unless I am mistaken. In the manuscript, the authors state on two occasions:

"Intriguingly, transcripts that had altered abundance in CR vs control media and in SSD1 vs ssd1∆ yeast included the FIT1, FIT2, FIT3, and ARN1 genes of the iron regulon (8)"

"Ssd1 and CR both reduce the levels of mRNAs of genes within the iron regulon: FIT1, FIT2, FIT3 and ARN1 (8)"

However, reference (8) by Kaeberlein et al. actually says the opposite:

"Using RNA derived from three independent experiments, a total of 97 genes were observed to undergo a change in expression >1.5-fold in SSD1-V cells relative to ssd1d cells (supplemental Table 1 at http://www.genetics.org/supplemental/). Of these 97 genes, only 6 underwent similar transcriptional changes in calorically restricted cells (Table 2). This is only slightly greater than the number of genes expected to overlap between the SSD1-V and CR datasets by chance and is in contrast to the highly significant overlap in transcriptional changes observed between CR and HAP4 overexpression (Lin et al. 2002) or between CR and high external osmolarity (Kaeberlein et al. 2002). Intriguingly, of the 6 genes that show similar transcriptional changes in calorically restricted cells and SSD1-V cells, 4 are involved in ironsiderochrome transport: FIT1, FIT2, FIT3, and ARN1 (supplemental Table 1 at http://www.genetics.org/supplemental/)."

Although the phrasing might be ambiguous at first reading, this interpretation is confirmed upon reviewing Matt Kaeberlein's PhD thesis: https://dspace.mit.edu/handle/1721.1/8318 (page 264 and so on).

Moreover, consistent with this, activation of the iron regulon during calorie restriction (or the diauxic shift) has also been observed in two other articles:

https://doi.org/10.1016/S1016-8478(23)13999-9

https://doi.org/10.1074/jbc.M307447200

Taken together, these contradictory data might blur the proposed model and make it unclear how to reconcile the results.

We thank the reviewer for pointing this out. Upon further consideration, we have now removed all mention of this paper from our manuscript as it is irrelevant to our situation, because the mRNA abundance studies during CR or with and without Ssd1 were not performed in situations in which the iron regulon is even activated such as aging, so there would not be any opportunity to detect reduced transcript levels due to CR or Ssd1 presence. Also, none of these studies were performed with Ssd1 overexpression which is the situation we are examining.  Our data clearly show that Ssd1 overexpression and CR reduced / prevented, respectively, production of proteins from the iron regulon during aging.

We do not feel that the iron regulon being activated by nutrient depletion at the diauxic shift is a fair comparison to the situation in cells happily dividing during CR. The levels of nutrient deprivation used in those studies have profound effects including arresting cell growth, activating autophagy, altering metabolism. The levels of CR that we use (0.05% glucose) does not activate any of these changes nor the iron regulon in young cells or old cells (Fig. 4).  

Reviewer #1 (Recommendations for the authors):

(1) The role of Ssd1 condensate formation in mRNA sequestration and lifespan expansion remains unclear. Thus, the study involves two parts (Ssd1 condensate formation and lifespan expansion via limiting Fe2+ accumulation), which are poorly linked. The study will therefore benefit from further data linking the two aspects.

Future experiments are planned to determine what mRNAs reside in the age-induced Ssd1 overexpression condensates, to determine if they include the iron regulon transcripts. This will require us to optimize isolation of old cells and isolation of the Ssd1 condensates from them, and is beyond the scope of the present study.

(2) The beneficial effects of Ssd1 overexpression and calorie restriction (CR) on lifespan are epistatic, yet the claim that both experimental conditions act via the same pathway should be further documented. It is recommended to combine Ssd1 overexpression with a well-defined condition that expands lifespan through a mechanism not involving changes in Fe2+ levels. A further increase in lifespan upon combining such conditions would at least indirectly support the authors' claim.

We have more than epistatic evidence to indicate that Ssd1 overexpression and CR are in the same pathway. Ssd1 overexpression and CR result in failure to properly induce the iron regulon during aging and subsequent reduced levels of iron, resulting in lifespan extension, supporting that they act via the same pathway. We do appreciate the point though and epistasis analyses are on our list for future studies.

(3) It is highly recommended to analyze ssd1 knockout cells: Is the shortened lifespan caused by intracellular Fe2+ accumulation, as predicted by the model? Does the knockout lead to an overactivation of the iron regulon? Such analysis will also document the physiological relevance of authentic Ssd1 levels in controlling yeast lifespan. The authors could test this possibility by determining intracellular Fe2+ levels (as done in Figure 5) and testing whether the mutant cells are partially rescued by the presence of an iron chelator (as done in Figure 5C).

We don’t think the normal role of Ssd1 is to sequester the iron regulon mRNAs to prevent its activation, given that wild type yeast with endogenous Ssd1 activates the iron regulon during aging. Rather, the failure to activate the iron regulon during aging is unique to when Ssd1 is overexpressed not at endogenous Ssd1 levels. As such, it may not be the case that the short lifespan of ssd1 yeast is due to iron accumulation (if that happens); yeast lacking SSD1 also have cell wall biogenesis problems and the defects in cell wall biogenesis shorten the replicative lifespan (Molon et al., Biogerentology 2018  PMID 29189912). 

(4) Figure 4: The authors could not analyze the impact of Ssd1 overexpression on the localization of GFP-Aft1 due to synthetic sickness. This was not observed under calorie restriction (CR) conditions and is therefore unexpected. Why should Ssd1 overexpression and CR have such diverse impacts on cellular physiology when combined with GFP-Aft1? Isn`t that observation arguing against CR and increased Ssd1 levels acting through the same pathway? A further clarification of this point is necessary.

Without further experimentation, we can only speculate that cellular changes that are unique to overexpression of Ssd1 and not shared with CR cause a negative interaction with GFP-Aft1. Of note, Aft1 has functions in addition to its role in activating the iron regulon (aft1∆ strains have a growth defect independent from its role in iron regulon activation [27]) and we have shown previously that overexpressed Ssd1 has a reduction in global protein translation. Future experiments would be necessary to delineate the basis for this synthetic sickness.

(5) Lowering Fe2+ levels upon Ssd1 overexpression is predicted to reduce oxidative stress. It is suggested to determine ROS levels upon Ssd1 overexpression to bolster that point.

This is a great suggestion. The lowering of Fe2+ in the Ssd1 mutants is something that happens at the end of the lifespan and therefore we would need to do experiments to detect reduced ROS using a live dye on our microfluidics platform. We are not aware of any live fluorescent reporters of ROS.  

Reviewer #2 (Recommendations for the authors):

(1) Page 6, 7th line of Replicative lifespan analyses, there is a double bracket.

This has been corrected. Thank you

(2) Page 18, line 6 of "failure to activate..." section, "revered" should be replaced with "reversed".

This has been corrected. Thank you

(3) Page 23, fix writing on line 2 of "Effects of CR..." section.

This has been corrected. Thank you

(4) Page 24, Author contributions section, replace "performed devised" with "designed".

This has been corrected. Thank you

Reviewer #3 (Recommendations for the authors):

(1) Figure 3C: The panel legend is somewhat confusing due to the color scheme and the scattering of labels across panels. A more consistent labeling strategy would help readability.

We agree, and the labelling has now been improved. Thank you. 

(2) Figure 3D vs Figure 3B: it appears that Fit2 activation occurs substantially earlier than Aft1 translocation, which reduces the predictive value of Fit2 compared to Aft1. This is puzzling given that Fit2 is expected to be a direct target of Aft1. Could this discrepancy be related to the thresholding used for Fit2-mCherry display? The color scale in Figure 3D is also somewhat misleading, as most of the segments appear greenish. A continuous color gradient, perhaps restricted to the [10-120] interval, might give a clearer picture of iron regulon activation.

For the Aft1-mcherry experiment, we are only able to accurately annotate nuclear localization when Aft1 has been fully (or mostly) translocated into the nucleus from the cytoplasm such that this data is likely to be on the conservative side. However, activation of the iron regulon likely occurs as Aft1 is translocated into the nucleolus, so a minimal initial amount of Aft1 (for which we don’t have enough resolution in this system to detect) could be enough for FIT2 and ARN1 induction.  By contrast, the Fit2 and Arn1 signal is measuring increase over a background of nothing, so is very easy to detect even at low level induction. To allow the readers to see all our data without over thresholding, we prefer to present the induction of Fit2 and Arn1 at all intensity levels even the very low level induction (green).

(3) "In control strains, expression of Fit2 and Arn1 varied across the population, but generally increased with age": for the right panel, normalization might be more appropriate. What is the fold change in fluorescence during lifespan? Reporting ΔmCherry intensity alone does not provide a quantitative measure of induction.

We have changed the figure to show quantitation as fold change, as suggested.

(4) Figure 6 (model): The model figure is conceptually useful but not easy to follow in its current form; a revised schematic with a clearer depiction of the pathway activations at different replicative ages would be helpful.

We have changed the figure to make the model more clear, as suggested.

yasss slayyy!!!

Reviewer #2 (Public review):

Summary:

This study examines the dynamic interplay between infant attention and hierarchical maternal behaviors from a social information processing perspective. By employing a comprehensive naturalistic framework, the author quantified interactions across both low-level (sensory) and high-level (semantic) features. With correlation analysis with these features, they found that within social contexts, behaviors such as joint attention - shaped by mutual interaction - exhibit patterns distinct from unilateral responding or mimicry. In contrast to traditional semi-structured behavioral observation and coding, the methods employed in this study were designed to consciously and sensitively capture these dynamic features and relate them temporally. This approach contributes to a more integrated understanding of the developmental principles underlying capacities like joint action and communication.

Strengths:

The manuscript's core strength lies in its innovative, dynamic, and hierarchical framework for investigating early social attention. The findings reveal complex adaptive scaffolding strategies: for instance, when infants focus on objects, mothers reduce low-level sensory input, minimising distractions. Furthermore, the results indicate that, even from early development, maternal behaviors are both driven by and predictive of infant attention, confirming that attention involves complex interactive processes that unfold across multiple levels, from salience to semantics.

From a methodological standpoint, the use of unstructured play situations, combined with multi-channel, high-precision time-series analyses, undoubtedly required substantial effort in both data collection and coding. Compared to the relatively two-dimensional analytical approaches common in prior research, this study's introduction of lower-level and higher-level features to explore the hierarchical organization of processing across development is highly plausible. The psychological processes reflected by these quantified physical features span multiple domains - including emotion, motion, and phonetics - and the high temporal sampling rate ensures fine-grained resolution.

Critically, these features are extracted through a suite of advanced machine learning and computational methods, which automate the extraction of objective metrics from audiovisual data. Consequently, the methodological flow significantly enhances data utilization and offers valuable inspiration for future behavioral coding research aiming for high ecological validity.

Weaknesses:

The conclusion of this paper is generally supported by the data and analysis, but some aspects of data analysis need to be clarified and extended.

(1) A more explicit justification for the selection and theoretical categorization of the eight interaction features may be needed. The paper introduces a distinction between "lower-level" and "higher-level" features but does not clearly articulate the criteria underpinning this classification. While a continuum is acknowledged, the practical division requires a principled rationale. For instance, is the classification based on the temporal scale of the features, the degree of cognitive processing required for their integration, or their proximity to sensory input versus semantic meaning?

(2) The claims regarding age-related differences in Predictions 2 are not fully substantiated by the current analyses. The findings primarily rely on observing that an effect is significant in one age group but not the other (e.g., the association between object naming and attention is significant at 15 months but not at 5 months). However, this pattern alone does not constitute evidence about whether the two age groups differ significantly from each other. The absence of a direct statistical comparison (e.g., an interaction test in a model that includes age as a factor) creates an inferential gap. To robustly support developmental change, formal tests of the Age × Feature interaction on infant attention are required.

(3) Another potential methodological issue concerns the potential confounding effect of parents' use of the infant's name. The analysis of "object naming" does not clarify whether utterances containing object words (e.g., "panda") were distinct from those that also incorporated the infant's name (e.g., "Look, Sarah, the panda!"). Given that a child's own name is a highly salient social cue known to robustly capture infant attention, its co-occurrence with object labels could potentially inflate or confound the measured effect of object naming itself. It would be important to know whether and how frequently infants' names were called, whether this variable was analyzed separately, and if its effect was statistically disentangled from that of pure object labeling.

(4) Interpretation of results requires clarification regarding the extended temporal lags reported, specifically the negative correlation between maternal vocal spectral flux and infant attention at 6.54 to 9.52 seconds (Figure 4C). The authors interpret this as a forward-prediction, suggesting that a decrease in acoustic variability leads to increased infant attention several seconds later. However, a lag of such duration seems unusually long for a direct, contingent infant response to a specific vocal feature. Is there existing empirical evidence from infant research to support such a prolonged response latency? Alternatively, could this signal suggest a slower, cyclical pattern of the interaction rather than a direct causal link?

Reviewer #3 (Public review):

Summary:

This manuscript presents an ambitious integration of multiple artificial intelligence technologies to examine social learning in naturalistic mother-infant interactions. The authors aimed to quantify how information flows between mothers and infants across different communicative modalities and timescales, using speech analysis (Whisper), pose detection (MMPose), facial expression recognition, and semantic modeling (GPT-2) in a unified analytical framework. Their goal was to provide unprecedented quantitative precision in measuring behavioral coordination and information transfer patterns during social learning, moving beyond traditional observational coding approaches to examine cross-modal coordination patterns and semantic contingencies in real-time across multiple temporal scales.

Strengths:

The integration of multiple AI tools into a coherent analytical framework represents a genuine methodological breakthrough that advances our capabilities for studying complex social phenomena. The authors successfully analyzed naturalistic interactions at a scale and level of detail that was not previously possible, examining 33 5-month-old and 34 15-month-old dyads across multiple modalities simultaneously. This sophisticated analytical pipeline, combining speech analysis, semantic modeling, pose detection, and facial expression recognition, provides new capabilities for studying social interactions that extend far beyond what traditional observational coding could achieve.

The specific findings about hierarchical information flow patterns across different timescales are particularly valuable and would not have been possible without this sophisticated analytical approach. The discovery that mothers reduce low-level sensory input when infants focus on objects, while increases in object naming and information rate associate with sustained attention, provides new empirical insights into how social learning unfolds in naturalistic settings. The temporal dynamics analyses reveal interesting patterns of behavioral coordination that extend our understanding of how caregivers adaptively modify their responses to support infant attention across multiple communicative channels simultaneously.

The scale of data collection and the comprehensive multi-modal approach are impressive, opening up new possibilities for understanding social learning processes. The methodological innovations demonstrate how modern computational tools can be systematically integrated to reveal new quantitative aspects of well-established developmental phenomena. The computational features developed for this study represent innovative applications of information theory and computer vision to developmental research.

Weaknesses:

Several major limitations affect the reliability and interpretability of the findings. The sample sizes of 33-34 dyads per age group are relatively modest for the complexity of analyses performed, which include eight different features examined across various time lags with extensive statistical comparisons. The study lacks adequate power analysis to demonstrate whether these sample sizes are sufficient to detect meaningful effect sizes, which is particularly concerning given the multiple comparison burden inherent in this type of multi-modal, multi-timescale analysis.

The statistical framework presents several concerns that limit confidence in the findings. Inter-rater reliability for gaze coding shows substantial but not excellent agreement (κ = 0.628), with only 22% of the data undergoing double coding. Given that gaze coding forms the foundation for all subsequent analyses of joint attention and information flow, this reliability level may systematically influence findings. The multiple comparison correction strategies vary inconsistently across different analyses, with some using FDR correction and others treating lower-level and higher-level features separately. Additionally, object naming analyses employed one-sided tests (p<0.05) while others used two-sided tests (p<0.025) without clear theoretical or methodological justification for these differences.

The validation of AI tools in the specific context of mother-infant interactions is insufficient and represents a critical limitation. The performance characteristics of Whisper with infant-directed speech, the precision of MMPose for detecting facial landmarks in young children, and the accuracy of facial expression recognition tools in infant contexts are not adequately validated for this population. These sophisticated tools may not perform optimally in the specific context of mother-infant interactions, where speech patterns, facial expressions, and body movements may differ substantially from their training data.

The theoretical positioning requires substantial refinement to better acknowledge the extensive existing literature. The authors are working within a well-established theoretical framework that has long recognized social learning as an active, bidirectional process. The joint attention literature, beginning with foundational work by Bruner (1983) and continuing through contemporary theories of social cognition by researchers like Tomasello (1995), has emphasized the communicative and adaptive nature of attentional processes. The scaffolding literature, including seminal work by Wood, Bruner, and Ross (1976), has demonstrated how parents adjust their support based on children's developing competencies. Moreover, there is a substantial body of micro-analytic research that has employed sophisticated quantitative methods to study social interactions, including work by Stern (1985) on microsecond-level interactions and research using time-series methods to examine dyadic coordination patterns.

The cross-correlation analyses have inherent limitations for causal inference that are not adequately acknowledged. The interpretation of temporal correlation patterns in terms of directional influence requires more cautious consideration, as observational data have fundamental constraints for establishing causality. The ecological validity is also questionable due to the laboratory tabletop interaction paradigm and the sample's demographic homogeneity, consisting primarily of white, highly educated, high-income mothers.

Reviewer #1 (Public review):

Summary:

Lumen formation is a fundamental morphogenetic event essential for the function of all tubular organs, notably the vertebrate vascular network, where continuous and patent conduits ensure blood flow and tissue perfusion. The mechanisms by which endothelial cells organize to create and maintain luminal space have historically been categorized into two broad strategies: cell shape changes, which involve alterations in apical-basal polarity and cytoskeletal architecture, and cell rearrangements, wherein intercellular junctions and positional relationships are remodeled to form uninterrupted conduits. The study presented here focuses on the latter process, highlighting a unique morphogenetic module, junction-based lamellipodia (JBL), as the driver for endothelial rearrangements.

Strengths:

The key mechanistic insight from this work is the requirement of the Arp2/3 complex, the classical nucleator of branched actin filament networks, for JBL protrusion. This implicates Arp2/3-mediated actin polymerization in pushing force generation, enabling plasma membrane advancement at junctional sites. The dependence on Arp2/3 positions JBL within the family of lamellipodia-like structures, but the junctional origin and function distinguish them from canonical, leading-edge lamellipodia seen in cell migration.

Weaknesses:

The study primarily presents descriptive observations and includes limited quantitative analyses or genetic modifications. Molecular mechanisms are typically interrogated through the use of pharmacological inhibitors rather than genetic approaches. Furthermore, the precise semantic distinction between JAIL and JBL requires additional clarification, as current evidence suggests their biological relevance may substantially overlap.

Author response:

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

Reviewer #1 (Public Review):

Summary:

Ravichandran et al investigate the regulatory panels that determine the polarization state of macrophages. They identify regulatory factors involved in M1 and M2 polarization states by using their network analysis pipeline. They demonstrate that a set of three regulatory factors (RFs) i.e., CEBPB, NFE2L2, and BCL3 can change macrophage polarization from the M1 state to the M2 state. They also show that siRNA-mediated knockdown of those 3-RF in THP1-derived M0 cells, in the presence of M1 stimulant increases the expression of M2 markers and showed decreased bactericidal effect. This study provides an elegant computational framework to explore the macrophage heterogeneity upon different external stimuli and adds an interesting approach to understanding the dynamics of macrophage phenotypes after pathogen challenge.

Strengths:

This study identified new regulatory factors involved in M1 to M2 macrophage polarization. The authors used their own network analysis pipeline to analyze the available datasets. The authors showed 13 different clusters of macrophages that encounter different external stimuli, which is interesting and could be translationally relevant as in physiological conditions after pathogen challenge, the body shows dynamic changes in different cytokines/chemokines that could lead to different polarization states of macrophages. The authors validated their primary computational findings with in vitro assays by knocking down the three regulatory factors-NCB.

We thank the reviewer for reading our manuscript and for the encouraging comments.

Weaknesses:

One weakness of the paper is the insufficient analysis performed on all the clusters. They used macrophages treated with 28 distinct stimuli, which included a very interesting combination of pro- and anti-inflammatory cytokines/factors that can be very important in the context of in vivo pathogen challenge, but they did not characterize the full spectrum of clusters. 

We have performed a functional enrichment analysis of all the clusters and added a section describing the results (Fig 1B). We believe this work will provide a basis for future experiments to characterize other clusters.

We have also performed a Principal Component Analysis (PCA) using hall mark genes of inflammation and the NCB panel alone to show the relative position of all clusters with respect to each other

Although they mentioned that their identified regulatory panels could determine the precise polarization state, they restricted their analysis to only the two well-established macrophage polarization states, M1 and M2. Analyzing the other states beyond M1 and M2 could substantially advance the field. They mentioned the regulatory factors involved in individual clusters but did not study the potential pathway involving the target genes of these regulatory factors, which can show the importance of different macrophage polarization states. Importantly, these findings were not validated in primary cells or using in vivo models.

We agree it would be useful to demonstrate the polarization switch in other systems as well. However, it is currently infeasible for us to perform these experiments. 

Reviewer #2 (Public Review):

Summary:

The authors of this manuscript address an important question regarding how macrophages respond to external stimuli to create different functional phenotypes, also known as macrophage polarization. Although this has been studied extensively, the authors argue that the transcription factors that mediate the change in state in response to a specific trigger remain unknown. They create a "master" human gene regulatory network and then analyze existing gene expression data consisting of PBMC-derived macrophage response to 28 stimuli, which they sort into thirteen different states defined by perturbed gene expression networks. They then identify the top transcription factors involved in each response that have the strongest predicted association with the perturbation patterns they identify. Finally, using S. aureus infection as one example of a stimulus that macrophages respond to, they infect THP-1 cells while perturbing regulatory factors that they have identified and show that these factors have a functional effect on the macrophage response.

Strengths:

The computational work done to create a "master" hGRN, response networks for each of the 28 stimuli studied, and the clustering of stimuli into 13 macrophage states is useful. The data generated will be a helpful resource for researchers who want to determine the regulatory factors involved in response to a particular stimulus and could serve as a hypothesis generator for future studies.

The streamlined system used here - macrophages in culture responding to a single stimulus - is useful for removing confounding factors and studying the elements involved in response to each stimulus.

The use of a functional study with S. aureus infection is helpful to provide proof of principle that the authors' computational analysis generates data that is testable and valid for in vitro analysis.

We thank the reviewer for reading our manuscript and for the encouraging comments

Weaknesses:

Although a streamlined system is helpful for interrogating responses to a stimulus without the confounding effects of other factors, the reality is that macrophages respond to these stimuli within a niche and while interacting with other cell types. The functional analysis shown is just the first step in testing a hypothesis generated from this data and should be followed with analysis in primary human cells or in an in vivo model system if possible.

It would be helpful for the authors to determine whether the effects they see in the THP-1 immortalized cell line are reproduced in another macrophage cell line, or ideally in PBMC-derived macrophages.

We agree; It would be useful in the future to demonstrate the polarization switch in other systems as well. We believe the results we provide here will inform future studies on other systems. 

The paper would benefit from an expanded explanation of the network mining approach used, as well as the cluster stability analysis and the Epitracer analysis. Although these approaches may be published elsewhere, readers with a non-computational background would benefit from additional descriptions.

We have elaborated on the network mining approach and added a schematic diagram (Fig S13) to describe the EpiTracer algorithm.

Although the authors identify 13 different polarization states, they return to the iM0/M1/M2 paradigm for their validation and functional assays. It would be useful to comment on the broader applications of a 13-state model.

We have included a new figure panel describing the functional enrichment analysis of all the clusters (Fig 1B) and added a section describing the results. We have also performed a Principal Component Analysis (PCA) using hallmark gene of inflammation and the NCB panel alone to show the relative position of all clusters with respect to each other. The PCA plot shows that C11(M1) and C3(M2) are roughly at two extreme ends, with other clusters between them, forming something resembling a punctuated continuum of states.

The relative contributions of each "switching factor" to the phenotype remain unclear, especially as knocking out each individual factor changes different aspects of the model (Fig. S5).

Fig S5 shows the effect on phenotype upon individual knockdown of the switching factors, from which we deduce that CEBPB has the largest contribution in determining the phenotype. However, we maintain that all three genes are necessary as a panel for M1/M2 switching. 

Reviewer #1 (Recommendations For The Authors):

The manuscript by Ravichandran et al describes the networks of genes that they named j"RF" associated with M1 to M2 polarization of macrophages by using their computational pipelines. They have shown 13 clusters of human macrophage polarization state by using an available database of different combinatorial treatments with cytokines, endotoxin, or growth factors, which is interesting and could be useful in the research field. However, there are a few comments which will help to understand the subject more precisely.

(1,2) The authors claimed to identify key regulatory factors involved in the human macrophage polarization from M1 to M2. However, recent advances suggest that macrophage polarization cannot be restricted to M1 and M2 only, which is also supported by the authors' data that shows 13 clusters of macrophages. However, they only focused on the difference between clusters 11 and 3 considering conventional M1 and M2. It will be more interesting to analyze the other clusters and how they relate to the established and simplistic M1 and M2 paradigms.

It will be interesting to know if they found any difference in the enriched pathways among these different clusters considering the exclusive regulatory factors and their targets.

We appreciate the point and have addressed it as follows. In the revised manuscript, we have discussed the clusters in detail and have provided the key regulatory factors (RF) combinations and target genes that define distinct macrophage population states (Please refer: Data file S2, S3). We have also discussed the associated immunological processes with each cluster, particularly in relation to the C11 and C3 clusters. We have added a new panel in Fig 1 to illustrate a heatmap indicating the enrichment of pathways relevant to inflammation in each of the clusters (Fig 1B).   Indeed, there is a substantial difference in the enrichment terms between the extreme ends (M1, M2) and significant differences in some of the pathways between clusters.   

(3) The authors have shown the involvement of NCB at 72h post LPS treatment. Are these RF involved in late response genes or act at the earlier time point of LPS treatment? Understanding the RF involvement in the dynamic response of macrophages to any stimulant will be important.

Using the data available for different time points (30 mins to 72 hours), we plotted the fold change (with respect to unstimulated cells) in M1 and M2 clusters for each of the NCB genes and observe clear divergence in the trend at 24 hours and have provided them as newly added (Supplementary Figure 9  A, B, C).

(4) The authors showed that the knockdown of RF- NCB can switch the M1 to M2. However, they showed a few conventional markers known to be M2 markers. What happens if NCB is overexpressed or knocked down in other treatment conditions/other clusters? Is the RF-NCB only involved in these two specific stimulations or their overexpression can promote M2 polarization in any given stimuli?

It is an interesting question but for practical reasons, experimental work was limited to M1 and M2 clusters as the aim was to establish proof of concept and could not be scaled up for all clusters, which would require a large amount of work and possibly a separate study.  We believe the description of the clusters that we have provided will enable the design of future experiments that will throw light on the significance of the intermediate clusters.  

(5) The authors have shown that knockdown of RF- NCB decreases pathogen clearance, but what are their altered functions? Are they more efficient in cellular debris clearance or resolution of inflammation? The authors can check the mRNA expression of markers/cytokines involved in those processes, in the NCB knockdown condition.

Indeed. Expression levels were measured for the following genes: CXCL2, IL1B, iNOS, SOCS3 (which are pro-inflammatory markers), as well as MRC1, ARG1, TGFB, IL10 (anti-inflammatory markers), as shown in Fig 4B.  

Minor comments:

(1, 2). How the authors evaluate the performance of their knowledge-based gene network. The authors should write the methods in detail, how they generated the simulated network, and evaluated the simulated dataset.

Gene network construction and module detection have many tools available. The authors need to mention which one they used. The authors should show whether their findings are consistent with at least another two module-detection methods (eg; "RedeR") to strengthen their claim.

We have added a schematic figure (Supplementary Fig S11) and detailed description of network construction and mining in the Methods section, as follows: We have reconstructed a comprehensive knowledge-based human Gene Regulatory Network (hGRN), which consists of Regulatory Factors (RF) to Target Gene (TG) and RF to RF interactions. To achieve this, we curated experimentally determined regulatory interactions (RF-TG, RF-RF) associated with human regulatory factors (Wingender et al., 2013). These interactions were sourced from several resources, including: (a) literature-curated resources like the Human Transcriptional Regulation Interactions database (HTRIdb) (Bovolenta et al., 2012), Regulatory Network Repository (RegNetwork) (Liu et al., 2015), Transcriptional Regulatory Relationships Unraveled by Sentence-based Text-mining (TRRUST) (Han et al., 2015), and the TRANSFAC resource from Harmonizome (Rouillard et al., 2016);  (b) ChEA3, which contains ChIP-seq determined interactions (Keenan et al., 2019); and (c) high-confidence protein-protein binding interactions (RF-RF) from the human protein-protein interaction network-2 (hPPiN2) (Ravichandran et al., 2021). As a result, our hGRN comprises 27,702 nodes and 890,991 interactions.  It is important to note that none of the edges/interactions in the hGRN are data-driven. We utilized this extensive hGRN, which encompasses the experimentally determined interactions/edges, to infer stimulant-specific hGRNs and top paths using our in-house network mining algorithm, ResponseNet. We have previously demonstrated that ResponseNet, which utilizes a knowledge-based network and a sensitive interrogation algorithm, outperformed data-driven network inference methods in capturing biologically relevant processes and genes, whose validation is reported earlier (Ravichandran and Chandra, 2019; Sambaturu et al., 2021).

We utilized our in-house response network approach to identify the stimulant-specific top active and repressed perturbations (Ravichandran and Chandra, 2019; Sambaturu et al., 2021). This is clearly described in the revised manuscript. To summarize, we generated stimulant-specific Gene Regulatory Networks (GRNs) by applying weights to the master human Gene Regulatory Network (hGRN) based on differential transcriptomic responses to stimulants (i.e., comparing stimulant-treated conditions to baseline). We then produced individually weighted networks for each stimulant and implemented a refined network mining technique to extract the most significant pathways. Furthermore, we have previously conducted a systematic comparison of our network mining strategy with other data-driven module detection methods, including jActiveModules (Ideker et al, 2002), WGCNA (Langfelder et al, 2008), and ARACNE (Margolin et al, 2006). Our findings demonstrated that our approach outperformed conventional data-driven network inference methods in capturing the biologically pertinent processes and genes (Ravichandran and Chandra, 2019). Since we have experimentally validated what we predicted from the network analysis, we do not see a need for performing the computational analysis with another algorithm. Moreover, different network analyses are based on different aspects of identifying functionally relevant genes or subnetworks. While each of them output useful information, given the scale of the network and the number of different biologically significant subnetworks and genes that could be present in an unbiased network such as what we have used, the output from different methods need not agree with each other as they may capture different aspects all together and hence is not guaranteed to be informative.  

(3) Representation of Fig 2B is difficult to understand the authors' interpretation of 'the 3-RF combination has 1293 targets, 359 covering about 53% of the top-perturbed network' for general readers. If the authors can simplify the interpretation will be helpful for the readers.

This is replaced with clearer figures in the revised manuscript (Figure 2A, 2B), and the associated text is also rephrased for clarity.

Reviewer #2 (Recommendations For The Authors):

Major comments:

(1) It would be helpful for the authors to determine whether the effects they see in the THP-1 immortalized cell line are reproduced in another macrophage cell line, or ideally in PBMC-derived macrophages if this is feasible. If using PBMC- or bone marrow-derived macrophages is beyond the scope of what the authors can reasonably perform, they could consider using another macrophage cell line such as RAW 264.7 cells, which would also provide orthogonal validation from a mouse model.

At this point of time, it is unfortunately infeasible for us to perform these experiments, due to resource limitation.  Moreover, it would require a lot of time. We hope that our work provides pointers for anyone working on mouse models or other model systems to design their studies on regulatory controls and the aspect of generalizability of our findings in Thp-1 cell lines to other systems will eventually emerge.

(2) It would be helpful for the authors to provide an expanded explanation of the network mining approach used, as well as the cluster stability analysis and the Epitracer analysis. Although these approaches may be published elsewhere, readers with a non-computational background would benefit from additional descriptions. A schematic figure would also be helpful to clarify their approach.

We have added a new schematic diagram in Supplementary figures (S13) and a detailed text in the Methods section describing the network mining analysis and epitracer identification in the revised manuscript. 

(3) It would be helpful for the authors to comment on whether the thirteen polarization states that they identify align with other analyses that have been performed using data collected from stimulated macrophages, or whether this is a novel finding, especially as the original paper from which the primary data are derived identified 9 clusters. More broadly, since the authors eventually return to the M1-M2 paradigm, it is unclear whether there is any functional support for a 13-state model - it is also possible that macrophages exist along a continuum of stimulation states rather than in discrete clusters. This at least merits further discussion, which could focus on different axes of polarization as discussed and shown in the original paper.

As described in the manuscript, Clustering based on the differential transcriptome profile of RF-set1, which contains 265 transcription factors (TFs), in response to 28 stimulants, resulted in 13 distinct clusters. The cluster member associations inferred from RF-set1 were similar in number and pattern to those inferred from the entire differential transcriptome (n=12,164; Fig. S2, cophenetic coefficient = 0.68; p-value = 1.25e−51). Furthermore, the inferred cluster pattern largely matched the clustering pattern previously described for the same dataset  (Xue et al., 2014).  Our contribution: The pattern we observed from the top-ranked epicenters in each cluster suggests that a subset of differentially expressed genes (DEGs) present in our top networks is sufficient for achieving differentiation. Our gene-regulatory models suggest that saturated (SA and PA) and unsaturated (LA, LiA, and OA) fatty acids, which were previously grouped together, mediate distinct modes of resolution and are now separated into two sub-branches. Similarly, the effects of IFNγ and sLPS, previously combined, are now distinctly resolved, aligning with known regulatory differences (Hoeksema et al., 2015; Kang et al., 2019). 

The principal takeaway from this analysis is not the exact number of clusters but rather the molecular basis it provides for the differentiation of functional states, with M1 and M2 representing two ends of the spectrum. Several other states are dispersed within the polarization spectrum, which we describe as a punctuated continuum. For our switching studies, we focused on clusters C11 (M1-like) and C2 (M2-like) due to their established functional relevance. However, future studies are required to explore the functional relevance of other clusters. We have added a discussion on this aspect as suggested.

(4) It would be helpful to define the contribution of each component of the NCB group to M1 polarization.

We assessed the impact of CEBPB, NFE2L2, and BCL3 on C2 (M1-like) polarization states by quantifying the expression levels of M1 and M2 markers. Our findings indicate that knocking down CEBPB led to a significant downregulation in the expression of M1 markers and an increase in M2 marker expression. In contrast, NFE2L2 and BCL3 knockdown resulted in decreased expression of M1 markers without a corresponding significant increase in M2 markers. These results suggest that CEBPB is crucial for M1 to the M2 transition. We have added a note on pg 22 to emphasize this better.

(5) NRF2, CEBPb, and BCL3 all have well-described roles in macrophage polarization. To add clarity to their discussion, the authors should cite relevant literature (eg PMIDs 15465827, 27211851, and others) and discuss how their findings extend what is currently known about the contribution of these individual proteins to macrophage responses.

The role of NFE2L2, CEBPB and BCL3 in macrophage polarization and state transition are described in the discussion section. The PMIDs mentioned by the reviewer are added as well. 

(6) The effect size of NCB knockdown in the in vitro Staph aureus model shown in 4C is fairly small - bacterial killing assays typically require at least a log of difference to demonstrate a convincing effect. It would be helpful for the authors to include a positive control for this experiment (for example, STAT4) to frame the magnitude of their effect.

We thank the reviewer for the comment, however, we would like to point out that the difference in CFU plotted in log₁₀ scale, as per common practice. The CFUs are therefore almost halved due to the knockdown in absolute scale and reproduced multiple times with statistically significant results (p-value <0.01). We feel it is sufficient to demonstrate that the NCB geneset by themselves bring out a change in polarization and hence the killing effect. We have used STAT4 as a control for marker measurements as shown in Fig 3C. While carrying out CFU with siSTAT4 may add additional information, we have proceeded to perform the infection experiments with and without the NCB knockdown as that remains the main focus of the study. 

Minor recommendations:

(1) Is there a difference between the data represented in Figure 1A-B and Figure S1? If this is the same data, there is no need to repeat it, and Figure 1 could be composed only of the current panels C and D.

We have removed Figure1 A and B as it illustrates the same point as Figure S1. We have retained Figures C and D and renamed them as new Figure 1A and C. In addition, we have added a new panel Fig 1B (in response to earlier points). 

(2) Could Figure 2B be represented in a different way? The circles do not contain any readable information about the genes, and it may be less visually overwhelming to represent this with just the large and small triangles. Perhaps the individual genes represented by the circles could be listed in a supplemental table or Excel file.

We have provided a new Figure 2 A and B panels for the M1 and M2 clusters respectively, which has only the barcode genes along with a functional annotation. The full network is already provided in supplementary data. 

(3) When indicating the N for all experiments performed in the figure legends, the authors should indicate whether these were technical or biological replicates.

We appreciate the reviewers for the suggestion. We have indicated what N is for all figure legends.

(4) Fig 3B: the y-axis is confusing - it appears that normalization is actually to the untreated cells.

Yes indeed. The normalization is with respect to the untreated cells as per standard practice. We have indicated this clearly in the legend.

(5) The 72-hour time point in Fig S8 shows unexpected results. Could the authors explain or propose a hypothesis for why CXCL2 and IL1b abruptly decrease while iNOS and MRC1 abruptly increase?

The purpose of the mentioned experiment was to standardize the time point of M1 polarization post S. aureus  infection. In this regard,  we profiled the expression levels of markers at various time points. We chose to study the 24 hour time point for all the future experiments based on the significant upregulation of NCB seen in the macrophages.  We believe that the 72 hour time point may show effects that are different since the initial immune response would have waned leading to differences in cytokine dynamics. However, as this is not the focus of our study, we are not discussing this aspect further.

Reviewer #2 (Public review):

Summary:

Through this study the authors combine a number of innovative technologies including scRNAseq to provide insight into Crohn's disease. Importantly, samples from pediatric patients are included. The authors develop a principled and unbiased tiered clustering approach, termed ARBOL. Through high-resolution scRNAseq analysis the authors identify differences in cell subsets and states during pediCD relative to FGID. The authors provide histology data demonstrating T cell localisation within the epithelium. Importantly, the authors find anti-TNF treatment pushes the pediatric cellular ecosystem towards an adult state.

Strengths:

This study is well presented. The introduction clearly explains the important knowledge gaps in the field, the importance of this research, the samples that are used and study design.<br /> The results clearly explain the data, without overstating any findings. The data is well presented. The discussion expands on key findings and any limitations to the study are clearly explained.

I think the biological findings from and bioinformatic approach used in, this study, will be of interest to many and significantly add to the field.

Weaknesses:

(1) The ARBOL approach for iterative tiered clustering on a specific disease condition was demonstrated to work very well on the datasets generated in this study where there were no obvious batch effects across patients. What if strong batch effects are present across donors where PCA fails to mitigate such effects? Are there any batch correction tools implemented in ARBOL for such cases?

The authors have addressed this comment during review

(2) The authors mentioned that the clustering tree from the recursive sub-clustering contained too much noise, and they therefore used another approach to build a hierarchical clustering tree for the bottom-level clusters based on unified gene space. But in general, how consistent are these two trees?

The authors have addressed this comment during review

Comments on revisions:

I have no additional comments. The authors addressed my previous comments well.

Author response:

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

Reviewer #1 (Public Review):

Summary:

Crohn's disease is a prevalent inflammatory bowel disease that often results in patient relapse post anti-TNF blockades. This study employs a multifaceted approach utilizing single-cell RNA sequencing, flow cytometry, and histological analyses to elucidate the cellular alterations in pediatric Crohn's disease patients pre and post-anti-TNF treatment and comparing them with non-inflamed pediatric controls. Utilizing an innovative clustering approach, the research distinguishes distinct cellular states that signify the disease's progression and response to treatment. Notably, the study suggests that the anti-TNF treatment pushes pediatric patients towards a cellular state resembling adult patients with persistent relapses. This study's depth offers a nuanced understanding of cell states in CD progression that might forecast the disease trajectory and therapy response.

Robust Data Integration: The authors adeptly integrate diverse data types: scRNA-seq, histological images, flow cytometry, and clinical metadata, providing a holistic view of the disease mechanism and response to treatment.

Novel Clustering Approach: The introduction and utilization of ARBOL, a tiered clustering approach, enhances the granularity and reliability of cell type identification from scRNA-seq data.

Clinical Relevance: By associating scRNA-seq findings with clinical metadata, the study offers potentially significant insights into the trajectory of disease severity and anti-TNF response; which might help with the personalized treatment regimens.

Treatment Dynamics: The transition of the pediatric cellular ecosystem towards an adult, more treatment-refractory state upon anti-TNF treatment is a significant finding. It would be beneficial to probe deeper into the temporal dynamics and the mechanisms underlying this transition.

Comparative Analysis with Adult CD: The positioning of on-treatment biopsies between treatment-naïve pediCD and on-treatment adult CD is intriguing. A more in-depth exploration comparing pediatric and adult cellular ecosystems could provide valuable insights into disease evolution.

Areas of improvement:

(1) The legends accompanying the figures are quite concise. It would be beneficial to provide a more detailed description within the legends, incorporating specifics about the experiments conducted and a clearer representation of the data points. 

We agree that it is beneficial to have descriptive figure legends that balance elements of experimental design, methodology, and statistical analyses employed in order to have a clear understanding throughout the manuscript. We have gone through and clarified areas throughout.  

(2) Statistical significance is missing from Fig. 1c WBC count plot, Fig. 2 b-e panels. Please provide it even if it's not significant. Also, the legend should have the details of stat test used.

We have now added details of statistical significance data in the Figure 1 legends. Please note that Mann-Whitney U-test was used for clinical categorical data.

(3) In the study, the NOA group is characterized by patients who, after thorough clinical evaluations, were deemed to exhibit milder symptoms, negating the need for anti-TNF prescriptions. This mild nature could potentially align the NOA group closer to FGID-a condition intrinsically defined by its low to non-inflammatory characteristics. Such an alignment sparks curiosity: is there a marked correlation between these two groups? A preliminary observation suggesting such a relationship can be spotted in Figure 6, particularly panels A and B. Given the prevalence of FGID among the pediatric population, it might be prudent for the authors to delve deeper into this potential overlap, as insights gained from mild-CD cases could provide valuable information for managing FGID.

Thank you for this insightful point. On histopathology and endoscopy, the NOA exhibited microscopic and macroscopic inflammation which landed these patients with the CD diagnosis, albeit mild on both micro and macro accounts. By contrast, the FGID group by definition will not have inflammation of microscopic and macroscopic evaluation. There is great interest in the field of adult and pediatric gastroenterology to understand why patients develop symptoms without evidence of inflammation. However, in 2023 the diagnostic tools of endoscopy with biopsy and histopathology is not sensitive enough to detect transcript level inflammation, positioning single-cell technology to be able to reveal further information in both disease processes.

Based on the reviewer’s suggestions, we have calculated a heatmap of overlapping NOA and FGID cell states along the Figure 6a joint-PC1, showing where NOA CD patients and FGID patients overlap in terms of cell states. This is displayed in Supplemental Figure 15d. This revealed a set of T, Myeloid, and Epithelial cell states that were most important in describing variance along the FGID-CD axis, allowing us to hone in on similarities at the boundary between FGID and CD. By comparing the joint cell states with CD atlas curated cluster names, we identified CCR7-expressing T cell states and GSTA2-expressing epithelial states associated with this overlap. 

(4) Furthermore, Figure 7 employs multi-dimensional immunofluorescence to compare CD, encompassing all its subtypes, with FGID. If the data permits, subdividing CD into PR, FR, and NOA for this comparison could offer a more nuanced understanding of the disease spectrum. Such a granular perspective is invaluable for clinical assessments. The key question then remains: do the sample categorizations for the immunofluorescence study accommodate this proposed stratification?

Thank you for the thoughtful discussion. We agree that stratifying Crohn’s disease by PR, FR, and NOA would provide valuable clinical insight. Unfortunately our multiplex IF cohort was designed to maximize overall CD versus FGID comparisons and does not contain enough samples in patient subgroups to power such an analysis. We have highlighted this limitation in the text.  

(5)The study's most captivating revelation is the proximity of anti-TNF-treated pediatric CD (pediCD) biopsies to adult treatment-refractory CD. Such an observation naturally raises the question: How does this alignment compare to a standard adult colon, and what proportion of this similarity is genuinely disease-specific versus reflective of an adult state? To what degree does the similarity highlight disease-specific traits?

Delving deeper, it will be of interest to see whether anti-TNF treatment is nudging the transcriptional state of the cells towards a more mature adult stage or veering them into a treatment-resistant trajectory. If anti-TNF therapy is indeed steering cells toward a more adult-like state, it might signify a natural maturation process; however, if it's directing them toward a treatment-refractory state, the long-term therapeutic strategies for pediatric patients might need reconsideration.

Thank you to the reviewer for another insightful point. We agree that age-matched samples are critical to evaluate disease cell states and hence we have age-matched controls in our pediatric cohort. Our timeline of follow-up only spans 3 years and patients remain in the pediatric age range at times of follow-up endoscopy and biopsy and would not be reflective of an adult GI state. We believe that the cellular behavior from naïve to treatment biopsy to on treatment biopsy is reflective of disease state rather than movement towards and adult-like state. We would also like to point out that pediatric onset IBD (Crohn’s and ulcerative colitis) traditionally has been harder to treat and presents with more extensive disease state (PMID: 22643596) and the ability to detect need for therapy escalation/change would be an invaluable tool for clinicians.  

We share the reviewer’s interest in disentangling a natural maturation process from disease and treatment-specific changes. Because the patients who were not given treatment did not move towards the adult-like phenotype, it could point to a push towards a treatment-resistant trajectory. To further support these findings, we generated a new disease-pseudotime figure Supplemental Figure 17, using cross-validation methods and the TradeSeq package. This figure was designed to track how each pediatric sample shifts from the treatment-naïve state through antiTNF therapy and to test the robustness of these shifts across samples. The new visualizations show patterns that do not recapitulate natural aging processes but rather shifts across all cell types associated with antiTNF treatment.

Reviewer #2 (Public Review):

Summary:

Through this study, the authors combine a number of innovative technologies including scRNAseq to provide insight into Crohn's disease. Importantly samples from pediatric patients are included. The authors develop a principled and unbiased tiered clustering approach, termed ARBOL. Through high-resolution scRNAseq analysis the authors identify differences in cell subsets and states during pediCD relative to FGID. The authors provide histology data demonstrating T cell localisation within the epithelium. Importantly, the authors find anti-TNF treatment pushes the pediatric cellular ecosystem toward an adult state.

Strengths:

This study is well presented. The introduction clearly explains the important knowledge gaps in the field, the importance of this research, the samples that are used, and study design.

The results clearly explain the data, without overstating any findings. The data is well presented. The discussion expands on key findings and any limitations to the study are clearly explained.

I think the biological findings from, and bioinformatic approach used in this study, will be of interest to many and significantly add to the field.

Weaknesses:

(1) The ARBOL approach for iterative tiered clustering on a specific disease condition was demonstrated to work very well on the datasets generated in this study where there were no obvious batch effects across patients. What if strong batch effects are present across donors where PCA fails to mitigate such effects? Are there any batch correction tools implemented in ARBOL for such cases?

We thank the reviewer for their insightful point, the full extent to which ARBOL can address batch effects requires further study. To this end we integrated Harmony into the ARBOL architecture and used it in the paper to integrate a previous study with the data presented (Figure 8). We have added to ARBOL’s github README how to use Harmony with the automated clustering method. With ARBOL, as well as traditional clustering methods, batch effects can cause artifactual clustering at any tier of clustering. Due to iteration, this can cause batch effects to present themselves in a single round of clustering, followed by further rounds of clustering that appear highly similar within each batch subset. Harmony addresses this issue, removing these batch-related clustering rounds. The later arrangement of fine-grained clusters using the bottom-up approach can use the batch-corrected latent space to calculate relationships between cell states, removing the effects from both sides of the algorithm. As stated, the extent to which ARBOL can be used to systematically address these batch effects requires further research, but the algorithmic architecture of ARBOL is well suited to address these effects.

(2) The authors mentioned that the clustering tree from the recursive sub-clustering contained too much noise, and they therefore used another approach to build a hierarchical clustering tree for the bottom-level clusters based on unified gene space. But in general, how consistent are these two trees?

Thank you for this thoughtful question. The two tree methodologies are not consistent due to their algorithmic differences, but both are important for several reasons: 

(1) The clustering tree is top-down, meaning low resolution lineage-related clusters are calculated first. Doublets and quality differences can cause very small clusters of different lineages (endothelial vs fibroblast) to fall under the incorrect lineage at first in the sub clustering tree, but these are recaptured during further sub clustering rounds, and then disentangled by the cluster-centroid tree.

(2) The hierarchical tree is a rose tree, meaning each branching point can contain several daughter branches, while taxonomies based on distances between species (or cell types in this case) are binary trees with only 2 branches per branching point, because distances between each cluster are unique. Because this taxonomy, or bottom-up, is different from the top-down approach, it is useful to then look at how these bottom-level clusters are similar. To that end, we performed pair-wise differential expression between all end clusters and clustered based on those genes. 

(3) Calculation of a binary tree represents a quantitative basis for comparing the transcriptomic distance between clusters as opposed to relying on distances calculated within a heuristic manifold such as UMAP or algorithmic similarity space such as cluster definitions based on KNN graphs.

In practice, this dual view rescues small clusters that may have been mis-grouped by technical artifacts and gives a quantitative distance based hierarchy that can be compared across metadata covariates.

Reviewer #1 (Public review):

Summary:

In their previous publication (Dong et al. Cell Reports 2024), the authors showed that citalopram treatment resulted in reduced tumor size by binding to the E380 site of GLUT1 and inhibiting the glycolytic metabolism of HCC cells, instead of the classical citalopram receptor. Given that C5aR1 was also identified as the potential receptors of citalopram in the previous report, the authors focused on exploring the potential of immune-dependent anti-tumor effect of citalopram via C5aR1. C5aR1 was found to be expressed on tumor-associated macrophages (TAMs) and citalopram administration showed potential to improve the stability of C5aR1 in vitro. Through macrophage depletion and adoptive transfer approaches in HCC mouse models, the data demonstrated the potential importance of C5aR1-expressing macrophage in the anti-tumor effect of citalopram in vivo. Mechanistically, their in vitro data suggested that citalopram may regulate the phagocytosis potential and polarization of macrophages through C5aR1. Next, they tried to investigate the direct link between citalopram and CD8+T cells by including an additional MASH-associated HCC mouse model. Their data suggest that citalopram may upregulate the glycolytic metabolism of CD8+T cells, probability via GLUT3 but not GLUT1-mediated glucose uptake. Lastly, as the systemic 5-HT level is down-regulated by citalopram, the authors analyzed the association between a low 5-HT and a superior CD8+T cell function against tumor. Although the data is informative, the rationale for working on additional mechanisms and logical link among different parts are not clear. In addition, some of the conclusion is also not fully supported by the current data.

Strengths:

The idea of repurposing clinical-in-used drugs showed great potential for immediate clinical translation. The data here suggested that the anti-depression drug, citalopram displayed immune regulatory role on TAM via a new target C5aR1 in HCC.

Comments on revised version:

The authors have addressed most of my concerns about the paper.

Author response:

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

Reviewer #1 (Public review): 

Summary:

In their previous publication (Dong et al. Cell Reports 2024), the authors showed that citalopram treatment resulted in reduced tumor size by binding to the E380 site of GLUT1 and inhibiting the glycolytic metabolism of HCC cells, instead of the classical citalopram receptor. Given that C5aR1 was also identified as the potential receptor of citalopram in the previous report, the authors focused on exploring the potential of the immune-dependent anti-tumor effect of citalopram via C5aR1. C5aR1 was found to be expressed on tumor-associated macrophages (TAMs) and citalopram administration showed potential to improve the stability of C5aR1 in vitro. Through macrophage depletion and adoptive transfer approaches in HCC mouse models, the data demonstrated the potential importance of C5aR1-expressing macrophage in the anti-tumor effect of citalopram in vivo. Mechanistically, their in vitro data suggested that citalopram may regulate the phagocytosis potential and polarization of macrophages through C5aR1. Next, they tried to investigate the direct link between citalopram and CD8+T cells by including an additional MASH-associated HCC mouse model. Their data suggest that citalopram may upregulate the glycolytic metabolism of CD8+T cells, probability via GLUT3 but not GLUT1-mediated glucose uptake. Lastly, as the systemic 5-HT level is down-regulated by citalopram, the authors analyzed the association between a low 5-HT and a superior CD8+T cell function against a tumor. Although the data is informative, the rationale for working on additional mechanisms and logical links among different parts is not clear. In addition, some of the conclusion is also not fully supported by the current data. 

We thank the reviewer for their comprehensive summary of our study and appreciate the valuable feedback. We have made improvements based on these comments, and a detailed response addressing each point is presented below.

Strengths: 

The idea of repurposing clinical-in-used drugs showed great potential for immediate clinical translation. The data here suggested that the anti-depression drug, citalopram displayed an immune regulatory role on TAM via a new target C5aR1 in HCC.

We thank the reviewer for recognizing the strengths of our study.

Weaknesses: 

(1) The authors concluded that citalopram had a 'potential immune-dependent effect' based on the tumor weight difference between Rag-/- and C57 mice in Figure 1. However, tumor weight differences may also be attributed to a non-immune regulatory pathway. In addition, how do the authors calculate relative tumor weight? What is the rationale for using relative one but not absolute tumor weight to reflect the anti-tumor effect? 

We appreciate your insights into the potential contributions of non-immune regulatory pathways to the observed tumor weight differences between Rag1^-/-and wild type C57BL/6 mice. Indeed, the anti-tumor effects of citalopram involve non-immune mechanisms. Previously, we have demonstrated the direct effects of citalopram on cancer cell proliferation, apoptosis, and metabolic processes (PMID: 39388353). In this study, we focused on immune-dependent mechanisms, utilizing Rag1^-/- mice to investigate a potential immune-mediated effect. The relative tumor weight was calculated by assigning an arbitrary value of 1 to the Rag1^-/- mice in the DMSO treatment group, with all other tumor weights expressed relative to this baseline. As suggested, we have included absolute tumor weight data in the revised Figure 1B, 1E, 1F, and 3B.

(2) The authors used shSlc6a4 tumor cell lines to demonstrate that citalopram's effects are independent of the conventional SERT receptor (Figure 1C-F). However, this does not entirely exclude the possibility that SERT may still play a role in this context, as it can be expressed in other cells within the tumor microenvironment. What is the expression profiling of Slc6a4 in the HCC tumor microenvironment? In addition, in Figure 1F, the tumor growth of shSlc6a4 in C57 mice displayed a decreased trend, suggesting a possible role of Slc6a4. 

As suggested, we probed the expression pattern of SERT in HCC and its tumor microenvironment. Using a single cell sequencing dataset of HCC (GSE125449), we revealed that SERT is also expressed by T cells, tumor-associated endothelial cells, and cancer-associated fibroblasts (see revised Figure S2G). Therefore, we cannot fully rule out the possibility that citalopram may influence these cellular components within the TME and contribute to its therapeutic effects. In the revised manuscript, we have included and discussed this result. In Figure 1F, SERT knockdown led to a 9% reduction in tumor growth, however, this difference was not statistically significant (0.619 ± 0.099 g vs. 0.594 ± 0.129 g; p = 0.75).

(3) Why did the authors choose to study phagocytosis in Figures 3G-H? As an important player, TAM regulates tumor growth via various mechanisms. 

We choose to investigate phagocytosis because citalopram targets C5aR1-expressing TAM. C5aR1 is a receptor for the complement component C5a, which plays a crucial role in mediating the phagocytosis process in macrophages. In the revised manuscript, we have highlighted this rationale.

(4) The information on unchanged deposition of C5a has been mentioned in this manuscript (Figures 3D and 3F), the authors should explain further in the manuscript, for example, C5a could bind to receptors other than C5aR1 and/or C5a bind to C5aR1 by different docking anchors compared with citalopram.

Thank you for your insightful comment. In Figure 3D, tumor growth was attenuated in C5ar1^-/- recipients compared with C5ar1^-/- recipients, whereas C5a deposition remained unchanged. This suggests that while C5a is still present, its interaction with C5aR1 is critical for influencing tumor growth dynamics. In Figure 3F, C5a deposition was not affected by citalopram treatment. Indeed, docking analysis and DARTS assay revealed that citalopram binds to the D282 site of C5aR1. Previous report has shown that mutations on E199 and D282 reduce C5a binding affinity to C5aR1 (PMID: 37169960). Therefore, the impact of citalopram is primarily on C5a/C5aR1 interactions and downstream signaling pathways, rather than on altering C5a levels. In the revised manuscript, we have included this interpretation.

(5) Figure 3I-M - the flow cytometry data suggested that citalopram treatment altered the proportions of total TAM, M1 and M2 subsets, CD4⁺ and CD8⁺T cells, DCs, and B cells. Why does the author conclude that the enhanced phagocytosis of TAM was one of the major mechanisms of citalopram? As the overall TAM number was regulated, the contribution of phagocytosis to tumor growth may be limited. 

We thank the reviewer’s valuable input. Indeed, recent studies have demonstrated that targeting C5aR1⁺ TAMs can induce many anti-tumor effects, such as macrophage polarization and CD8⁺ T cell infiltration (PMID: 30300579, PMID: 38331868, and PMID: 38098230). In the revised manuscript, we have clarified our conclusion to better articulate the relationship between citalopram treatment, TAM populations, and their phagocytic activity, with particular emphasis on the role of CD8⁺ T cells. For macrophage phagocytosis, one possible explanation is that citalopram targets C5aR1 to enhance macrophage phagocytosis and subsequent antigen presentation and/or cytokine production, which promotes T cell recruitment and activity as well as modulate other aspects of tumor immunity. Given that the anti-tumor effects of citalopram are largely dependent on CD8⁺ T cells, we conclude that CD8⁺ T cells are essential for the effector mechanisms of citalopram.

(6) Figure 4 - what is the rationale for using the MASH-associated HCC mouse model to study metabolic regulation in CD8⁺ T cells? The tumor microenvironment and tumor growth would be quite different. In addition, how does this part link up with the mechanisms related to C5aR1 and TAM? The authors also brought GLUT1 back in the last part and focused on CD8⁺ T cell metabolism, which was totally separated from previous data. 

We chose the MASH-associated HCC mouse model because it closely mimics the etiology of metabolic-associated fatty liver disease (MAFLD), which is a significant contributor to the development of cirrhosis and HCC. In addition to the MASH-associated HCC mouse model, the study also incorporated the orthotopic Hepa1-6 tumor model. In our previous publication (Dong et al., Cell Reports 2024), we employed both of these HCC models. Therefore, we utilized the same two mouse models in this study. The inclusion of CD8⁺ T cells in our study is based on the understanding that citalopram targets GLUT1, which plays a crucial role in glucose uptake (PMID: 39388353). CD8⁺T cell function is heavily reliant on glycolytic metabolism, making it essential to investigate how citalopram’s effects on GLUT1 influence the metabolic pathways and functionality of these immune cells. In this study, we identified that the primary glucose transporter in CD8⁺ T cells is GLUT3, rather than GLUT1. The data presented in Figure 4 aim to illustrate the additional effect of citalopram on peripheral 5-HT levels, which, in turn, influences CD8⁺ T cell functionality. By linking these findings, we clarify how citalopram impacts both TAMs and CD8⁺ T cells. CD8⁺ T cells can be influenced by citalopram through various mechanisms, including TAM-dependent mechanisms, reduced systemic serum 5-HT concentrations, and unidentified direct effects. In the revised manuscript, we have enhanced the background information to avoid any gaps.

(7) Figure 5, the authors illustrated their mechanism that citalopram regulates CD8⁺ T cell anti-tumor immunity through proinflammatory TAM with no experimental evidence. Using only CD206 and MHCII to represent TAM subsets obviously is not sufficient. 

Thank you for your valuable comments. As noted by the reviewer, TAMs can influence CD8⁺ T cell anti-tumor immunity through various mechanisms. In this study, we focused on elucidating the impact of citalopram on pro-inflammatory TAMs, which in turn affect CD8⁺ T cell anti-tumor immunity and ultimately influence tumor outcomes. Therefore, in the mechanistic diagram, we highlighted the effect of citalopram on pro-inflammatory TAMs, while the causal relationship between TAMs and CD8⁺ T cell anti-tumor immunity was indicated with a dotted line due to the limited evidence presented in this study. Additionally, we have expanded our discussion on how citalopram regulates CD8⁺ T cell anti-tumor immunity through pro-inflammatory TAMs.

For the analysis of TAMs, we initially sorted CD45⁺F4/80⁺CD11b⁺ cells and assessed M1/M2 polarization by measuring CD206 and MHCII expression. As an added strength, we isolated TAMs from the orthotopic GLUT1^KD Hepa1-6 model using CD11b microbeads and conducted real-time qPCR analysis of M1-oriented (Il6, Ifnb1, and Nos2) and M2-oriented (Mrc1, Il10, and Arg1) markers. Consistent with our flow cytometry data, the qPCR results confirmed that citalopram induces a pro-inflammatory TAM phenotype (revised Figure S9A).

Reviewer #2 (Public review): Summary: 

Dong et al. present a thorough investigation into the potential of repurposing citalopram, an SSRI, for hepatocellular carcinoma (HCC) therapy. The study highlights the dual mechanisms by which citalopram exerts anti-tumor effects: reprogramming tumor-associated macrophages (TAMs) toward an anti-tumor phenotype via C5aR1 modulation and suppressing cancer cell metabolism through GLUT1 inhibition while enhancing CD8+ T cell activation. The findings emphasize the potential of drug repurposing strategies and position C5aR1 as a promising immunotherapeutic target. However, certain aspects of experimental design and clinical relevance could be further developed to strengthen the study's impact. 

We thank the reviewer’s thoughtful review and constructive feedback. As suggested, we have made improvements based on the feedback provided.

Strength: 

It provides detailed evidence of citalopram's non-canonical action on C5aR1, demonstrating its ability to modulate macrophage behavior and enhance CD8+ T cell cytotoxicity. The use of DARTS assays, in silico docking, and gene signature network analyses offers robust validation of drug-target interactions. Additionally, the dual focus on immune cell reprogramming and metabolic suppression presents a thorough strategy for HCC therapy. By emphasizing the potential for existing drugs like citalopram to be repurposed, the study also underscores the feasibility of translational applications. 

We sincerely appreciate the reviewer’s recognition of the detailed evidence supporting citalopram’s non-canonical action on C5aR1, along with the innovative methodologies employed and the promising potential for repurposing existing drugs in HCC therapy.

Major weaknesses/suggestions: 

The dataset and signature database used for GSEA analyses are not clearly specified, limiting reproducibility. The manuscript does not fully explore the potential promiscuity of citalopram's interactions across GLUT1, C5aR1, and SERT1, which could provide a deeper understanding of binding selectivity. The absence of GLUT1 knockdown or knockout experiments in macrophages prevents a complete assessment of GLUT1's role in macrophage versus tumor cell metabolism. Furthermore, there is minimal discussion of clinical data on SSRI use in HCC patients. Incorporating survival outcomes based on SSRI treatment could strengthen the study's translational relevance. 

By addressing these limitations, the manuscript could make an even stronger contribution to the fields of cancer immunotherapy and drug repurposing. 

We appreciate the reviewer’s valuable suggestions. As suggested, we have included the following revisions:

(a) GSEA analyses: For GSEA analyses, we conducted RNA sequencing (RNA-seq) analysis on HCC-LM3 cells treated with citalopram or fluvoxamine, which led to the identification of 114 differentially expressed genes (DEGs; 80 co-upregulated and 34 co-downregulated), as reported previously (PMID: 39388353). These DEGs were then utilized to create an SSRI-related gene signature. Subsequently, we analyzed RNA-seq data from liver HCC (LIHC) samples in The Cancer Genome Atlas (TCGA) cohort, comprising 371 samples, categorizing them into high and low expression groups based on the median expression levels of each candidate target gene (such as C5AR1). Finally, we performed GSEA on the grouped samples (C5AR1-high versus C5AR1-low) using the SSRI-related gene signature. In the revised manuscript, we have included this information in the “Materials and Methods” section.

(b) Exploration of binding selectivity: We acknowledge the importance of exploring the potential promiscuity of citalopram’s interactions across GLUT1, C5aR1, and SERT1. While we cannot provide further experimental data to support this aspect, we have included the following points in the revised manuscript: 1) We emphasize the significance of exploring the relative binding affinities of citalopram to GLUT1, C5aR1, and SERT, as varying affinities could influence the drug’s overall efficacy. As highlighted in the current manuscript and our previous publication (PMID: 39388353), citalopram interacts with C5aR1 and GLUT1 through distinct binding sites and mechanisms, whereas its interaction with SERT is characterized by a more direct inhibition of serotonin binding (PMID: 27049939). To gain deeper insights into these interactions, employing techniques such as surface plasmon resonance or biolayer interferometry could provide valuable quantitative data on binding kinetics and affinities for each target. 2) We discuss how citalopram’s interactions with multiple targets may contribute to its therapeutic effects, particularly in the context of immune modulation and tumor progression. The potential for citalopram to exhibit diverse mechanisms of action through its interactions with these proteins warrants further investigation. A comprehensive understanding of these pathways could lead to the development of improved therapeutic strategies.

(c) GLUT1 knockdown in macrophages: In the revised manuscript, we revealed that TAMs predominantly express GLUT3 but not GLUT1 (Figures S8B and S8C). GLUT1 knockdown in THP-1 cells did not significantly impact their glycolytic metabolism (Figure S8D), whereas GLUT3 knockdown led to a marked reduction in glycolysis in THP-1 cells.

(d) Clinical data on SSRI use in HCC patients: Previously, we have reported that SSRIs use is associated with reduced disease progression in HCC patients (PMID: 39388353) (Cell Rep. 2024 Oct 22;43(10):114818.). As detailed below:

“We determined whether SSRIs for alleviating HCC are supported by real-world data. A total of 3061 patients with liver cancer were extracted from the Swedish Cancer Register. Among them, 695 patients had been administrated with post-diagnostic SSRIs. The Kaplan-Meier survival analysis suggested that patients who utilized SSRIs exhibited a significantly improved metastasis-free survival compared to those who did not use SSRIs, with a P value of log-rank test at 0.0002. Cox regression analysis showed that SSRI use was associated with a lower risk of metastasis (HR = 0.78; 95% CI, 0.62-0.99)”.

Reviewer #1 (Recommendations for the authors):

(1) Add experiments to address the questions listed in the weaknesses.

As suggested, related experiments are performed to strengthen the conclusions.

(2) It would be appreciated to show the expression profile of SERT or employ KO mouse models to eliminate the effect of SERT.

As suggested, analysis of a single-cell sequencing dataset of HCC (GSE125449) revealed that SERT is expressed not only in HCC cells but also in T cells, tumor-associated endothelial cells, and cancer-associated fibroblasts (Figure S2G). Consistently, SERT has been reported as an immune checkpoint restricting CD8 T cell antitumor immunity (PMID: 40403728). Furthermore, SERT KO mice (Cyagen Biosciences, S-KO-02549) was employed to investigate the effects of citalopram. However, the Slc6a4 gene knockout in mice resulted in a significant decrease in 5-HT levels in the brain and a lack of cortical columnar structures. Importantly, the mice exhibited an intolerance to citalopram treatment. Therefore, we did not pursue further investigation into the effects of citalopram in SERT KO mice.

(3) Due to the concern of specificity and animal health, it would be more direct if the authors could use, for example, C5ar1-fl/fl x Adgre1-Cre mouse models.

Thank you for your valuable suggestion. We fully agree with your comment regarding the value of introducing C5ar1-fl/fl and Adgre1-Cre mouse models, along with the necessary experimental setups, to substantiate this point. However, in our study, the C5ar1 KO mice exhibited normal overall appearance and viability, indicating that the model is generally healthy. Furthermore, we have validated the specific role of C5aR1 in macrophages through bone marrow reconstitution experiments, reinforcing the importance of C5aR1 in these cells. Therefore, we chose the current model to balance experimental effectiveness with considerations for animal health.

(4) For example, a GSEA or GO analysis of comparison of macrophages from C5ar1-/- or C5ar1+/- mice may point to the enriched pathway of phagocytosis in macrophages derived from C5ar1-/- rather than C5ar1+/- mice, and this information is helpful for the integrity of this work. Besides, it would be more reliable if a nucleus staining is included in Figures 3G and 3H.

As suggested, macrophages were isolated from tumor-bearing C5ar1^-/- and C5ar1^+/- mice and subsequently analyzed using RNA sequencing. The Gene Set Enrichment Analysis (GSEA) revealed a significant enrichment of the phagocytosis pathway in macrophages derived from C5ar1^-/- mice compared to those from C5ar1^+/- mice (see revised Figure S6A). While we acknowledge that the addition of a nucleus staining would enhance reliability, we would like to point out that this style of presentation is also commonly found in articles related to phagocytosis. Furthermore, this experiment involved a significant number of experimental mice, and in accordance with the 3Rs principle for animal experiments, we did not obtain additional sorted TAMs to perform the phagocytosis assay. Thank you for your understanding.

(5) In line 122, there is a typo, and it should be 'analysis'.

Thank you for pointing out the typo. It has been corrected to "analysis" in the revised manuscript.

(6) In line 217, there is no causal relationship between the contexts, and using 'as a result' may lead to misunderstanding.

As suggested, ‘as a result’ has been removed to avoid any misunderstanding.

(7) In line 322, please make sure if it should be HBS or PBS.

It is PBS, and revisions have been made.

(8) Figure S7, the calculation of cell proportions needs to use a consistent denominator.

As suggested, we calculated cell proportions using a consistent denominator (CD45⁺ cells).

(9) Figure 4C, label error.

Thanks for your careful review. It has been corrected to "MASH".

Reviewer #2 (Recommendations for the authors):

Dong et al. present compelling evidence for repurposing citalopram, a selective serotonin reuptake inhibitor (SSRI), as a potential therapeutic for hepatocellular carcinoma (HCC). While the concept of SSRI repurposing is not novel, this manuscript provides valuable insights into the drug's dual mechanisms: targeting tumor-associated macrophages (TAMs) via C5aR1 modulation and enhancing CD8+ T cell activity, alongside inhibiting cancer cell metabolism through GLUT1 suppression. The findings underscore the promise of drug repurposing strategies and identify C5aR1 as a noteworthy immunotherapeutic target. Addressing the following points will enhance the manuscript's impact and relevance to cancer immunotherapy.

Specific Comments:

(1) The authors identify C5aR1 on TAMs as a direct target of citalopram, independent of its classical SERT target, using drug-induced gene signature network analysis and co-immunofluorescence of CD163+ macrophages with C5aR1. The DARTS assay further supports the binding of C5aR1 to citalopram, complemented by in silico docking analysis adapted from their previous GLUT1 study. Since GLUT1 and SERT1 are transporter proteins while C5aR1 is a GPCR, these heterogeneous binding interactions suggest potential promiscuity in SSRI-target engagement.

(a) Figure 2A: The authors identify C5aR1 as a target using GSEA but do not specify the dataset used (e.g., cancer or immune cells) or the signature database consulted. Providing this context would enhance reproducibility.

For GSEA, we performed RNA sequencing (RNA-seq) on HCC-LM3 cells treated with citalopram or fluvoxamine and identified 114 differentially expressed genes (DEGs), which included 80 genes that were co-upregulated and 34 that were co-downregulated, as previously documented (PMID: 39388353). These DEGs were subsequently used to develop an SSRI-related gene signature. We then employed the RNA-seq data from liver hepatocellular carcinoma (LIHC) samples within The Cancer Genome Atlas (TCGA) cohort, which included 371 samples. HCC samples in the TCGA cohort were categorized into high and low expression groups based on the median expression levels of each candidate target gene, such as C5AR1. Finally, we conducted GSEA on the grouped samples (such as C5AR1-high versus C5AR1-low) using the SSRI-related gene signature. For reproducibility, detailed information has been added to the “Materials and Methods” section of the revised manuscript.

(b) Figure 2F: Given citalopram's reported role in inhibiting GLUT1, a comparative discussion on the relative contributions of GLUT1 inhibition versus C5aR1 modulation in tumor suppression is warranted. Performing a DARTS assay for GLUT1 in THP-1 cells, which express high GLUT1 levels and exhibit upregulation in M1 macrophages (https://doi.org/10.1038/s41467-022-33526-z), would clarify SSRI interactions with macrophage metabolism.

As suggested, we first investigated citalopram treatment in THP-1 cells. The result showed the glycolytic metabolism of THP-1 cells remained largely unaffected following citalopram treatment, as evidenced by glucose uptake, lactate release, and extracellular acidification rate (ECAR) (Figure S8A). Next, we mined a single cell sequencing datasets of HCC and revealed that TAMs predominantly express GLUT3 but not GLUT1 (Figure S8B). Consistently, Western blotting analysis showed a higher expression of GLUT3 and minimal levels of GLUT1 in THP-1 cells (Figure S8C). Consistently, it has been well documented that GLUT1 expression increased after M1 polarization stimuli an GLUT3 expression increased after M2 stimulation in macrophages (PMID: 37721853, PMID: 36216803). GLUT1 knockdown in THP-1 cells did not significantly impact their glycolytic metabolism (Figure S8D), whereas GLUT3 knockdown led to a marked reduction in glycolysis in THP-1 cells. Based on these findings, we conclude that the effects of citalopram on macrophages are primarily mediated through targeting C5aR1 rather than GLUT1.

(c) Figures 2H-I: A comparison of drug-protein interactions across GLUT1, C5aR1, and SERT1 would be valuable to identify potential shared or distinct binding features.

Citalopram exhibits distinct binding characteristics across its various targets, including GLUT1, C5aR1, and its classical target, SERT. In the case of C5aR1, our in silico docking analysis identified two key binding conformations at the orthosteric site. The interactions involved significant electrostatic contacts between citalopram’s amino group and negatively charged residues like E199 and D282. Notably, D282’s accessibility and orientation towards the binding cavity suggest it plays a crucial role in citalopram binding, highlighting the importance of specific amino acid interactions at this site. For GLUT1 (PMID: 39388353), citalopram’s interaction also demonstrated notable hydrophobic contacts, particularly through the fluorophenyl group with residues V328, P385, and L325. The cyanophtalane group penetrated the substrate-binding cavity, indicating that citalopram could occupy a similar binding site as glucose, which is distinct from the binding mechanism observed in C5aR1. The involvement of E380 in both poses for GLUT1 further emphasizes the role of electrostatic interactions in mediating citalopram’s binding to this transporter. In contrast, for SERT (PMID: 27049939), citalopram locks the transporter in an outward-open conformation by occupying the central binding site, which is located between transmembrane helices 1, 3, 6, 8 and 10. This binding directly obstructs serotonin from accessing its binding site, illustrating a more definitive blockade mechanism. Additionally, the allosteric site at SERT, positioned between extracellular loops 4 and 6 and transmembrane helices 1, 6, 10, and 11, enhances this blockade by sterically hindering ligand unbinding, thus providing a clear explanation for the allosteric modulation of serotonin transport. In summary, while citalopram interacts with C5aR1 and GLUT1 through distinct binding sites and mechanisms, its interaction with SERT is characterized by a more straightforward blockade of serotonin binding. The unique structural and functional attributes of each target highlight the versatility of citalopram and suggest that its pharmacological effects may vary significantly depending on the specific protein being targeted. In the revised manuscript, we have included detailed information in the revised manuscript.

(2) The manuscript presents evidence that citalopram reprograms TAMs to an anti-tumor phenotype, enhancing their phagocytic capacity.

(a) Bone Marrow Reconstitution Experiments (Figure 3): The use of donor (dC5aR1) and recipient (rC5aR1) mice is significant but requires clarification. Explicitly defining donor and recipient terminology and including a schematic of the experimental design would improve reader comprehension.

We appreciate your valuable feedback. As suggested, the terminology for donor (dC5aR1) and recipient (rC5aR1) mice was defined: “we injected GLUT1^KD Hepa1-6 cells into syngeneic recipient C5ar1^-/- (rC5ar1^-/- ) mice that had been reconstituted with donor C5ar1^+/- (dC5ar1^+/-) or C5ar1^-/- (dC5ar1^-/-) bone marrow (BM) cells to analyze the therapeutic effect of citalopram”. Additionally, we have included a schematic of the experimental design to enhance reader comprehension (see revised Figure 3E).

(b) GLUT1 Knockdown (KD) Tumor Cells: While GLUT1 KD tumor cells are utilized, the authors do not assess GLUT1 KD or knockout (KO) in macrophages. Testing the effect of citalopram on macrophages with GLUT1 KO/KD would help determine the relative importance of C5aR1 versus GLUT1 in mediating SSRI effects.

As responded above, GLUT1 knockdown in THP-1 cells did not significantly alter their glycolytic metabolism (Figure S8D). This observation can be explained by the predominant expression of GLUT3 in TAMs rather than GLUT1 (Figures S8B and S8C). Indeed, knockdown of GLUT3 led to a significant reduction in glycolysis in THP-1 cells (Figure S8C).

(c) C5aR1's Pro-Tumoral Role: The authors state that C5aR1 fosters an immunosuppressive microenvironment but omit a discussion of current literature on C5aR1's pro-tumoral role (e.g., https://doi.org/10.1038/s41467-024-48637-y, https://www.nature.com/articles/s41419-024-06500-4, https://doi.org/10.1016/j.ymthe.2023.12.010). Including this background in both the introduction and discussion would contextualize their findings.

Thanks for your valuable feedback. As suggested, we have revised the manuscript to include discussions on C5aR1’s pro-tumoral role, referencing the suggested studies in both the introduction and discussion sections for better context. As detailed below:

(1) Targeting C5aR1⁺ TAMs effectively reverses tumor progression and enhances anti-tumor response;

(2) Targeting C5aR1 reprograms TAMs from a protumor state to an antitumor state, promoting the secretion of CXCL9 and CXCL10 while facilitating the recruitment of cytotoxic CD8⁺ T cells;

(3) Moreover, citalopram induces TAM phenotypic polarization towards to a M1 proinflammatory state, which supports anti-tumor immune response within the TME.

(d) C5aR1 Expression in TAMs: Is C5aR1 expression constitutive in TAMs? Further details on C5aR1 expression dynamics in TAMs under different conditions could strengthen the discussion. Public datasets on TAMs in various states (e.g., https://www.nature.com/articles/s41586-023-06682-5, https://www.cell.com/cell/abstract/S0092-8674(19)31119-5, https://pubmed.ncbi.nlm.nih.gov/36657444/) may offer useful insights.

Thank you for your valuable suggestions. As suggested, we investigated the expression patterns of C5aR1 in TAMs using a HCC cohort (http://cancer-pku.cn:3838/HCC/). In the study conducted by Qiming Zhang et al. (PMID: 31675496), six distinct macrophage subclusters were identified, with M4-c1-THBS1 and M4-c2-C1QA showing significant enrichment in tumor tissues. M4-c1-THBS1 was enriched with signatures indicative of myeloid-derived suppressor cells (MDSCs), while M4-c2-C1QA exhibited characteristics that resembled those of TAMs as well as M1 and M2 macrophages. Our subsequent analysis revealed that C5aR1 is highly expressed in these two clusters, while expression levels in the other macrophage clusters were notably lower (see revised Figure S3).

(3) The manuscript shows that citalopram-induced reductions in systemic serotonin levels enhance CD8+ T cell activation and cytotoxicity, as evidenced by increased glycolytic metabolism and elevated IFN-γ, TNF-α, and GZMB expression.

(a) How CD8+ T cell activation is done in serotonin-deficient environments?

As reported (PMID: 34524861), one possible explanation is that serotonin may enhance PD-L1 expression on cancer cells, thereby impairing CD8⁺ T cell function. A deficiency of serotonin in the tumor microenvironment can delay tumor growth by promoting the accumulation and effector functions of CD8⁺ T cells while reducing PD-L1 expression. In addition to the SERT-mediated transport and 5-HT receptor signaling, CD8⁺ T cells can express TPH1 (PMID: 38215751, PMID: 40403728), enabling them to synthesize endogenous 5-HT, which activates their activity through serotonylation-dependent mechanisms (PMID: 38215751). In the revised manuscript, we have incorporated these interpretations.

(4) Suggestions for the model figure revision-C5aR1 in TAMs without Citalopram (Figure 5).

(a) Including a control scenario depicting receptor status and function in TAMs without citalopram treatment would provide a clearer baseline for understanding citalopram's effects.

Thank you for your valuable input regarding the model figure revision. We have included a revised mechanism model that depicts the receptor status and function of C5aR1 in TAMs without citalopram treatment, as you suggested.

(5) Suggestions for addressing clinical relevance.

The study predominantly uses preclinical mouse models, although some human HCC data is analyzed (Figures 2B and 3O). However, there is no discussion of clinical data on SSRI use in HCC patients.

Incorporating an analysis of patient survival outcomes based on SSRI treatment (e.g., https://pmc.ncbi.nlm.nih.gov/articles/PMC5444756/, https://pmc.ncbi.nlm.nih.gov/articles/PMC10483320/) would enhance the translational relevance of the findings.

Previously, we reported that the use of SSRIs is associated with reduced disease progression in HCC patients, based on real-world data from the Swedish Cancer Register (PMID: 39388353). As suggested, we have further discussed the clinical relevance of SSRIs in the revised manuscript. As detailed below:

“In a study involving 308,938 participants with HCC, findings indicated that the use of antidepressants following an HCC diagnosis was linked to a decreased risk of both overall mortality and cancer-specific mortality (PMID: 37672269). These associations were consistently observed across various subgroups, including different classes of antidepressants and patients with comorbidities such as hepatitis B or C infections, liver cirrhosis, and alcohol use disorders. Similarly, our analysis of real-world data from the Swedish Cancer Register demonstrated that SSRIs are correlated with slower disease progression in HCC patients (PMID: 39388353). Given these insights, antidepressants, especially SSRIs, show significant potential as anticancer therapies for individuals diagnosed with HCC”.

This also implicitly means that killing "others" is allowed. They might be playing the war game, yes, but maybe their country unlisted them unwillingly, how are they different from civilians?

Then these go unoticed, invisibilised. Much like prostitution is. Much like porn... yet his author seems to frame it as positive?

Reviewer #1 (Public review):

Summary:

The authors examine the neural correlates of face recognition deficits in individuals with Developmental Prosopagnosia (DP; 'face blindness'). Contrary to theories that poor face recognition is driven by reduced spatial integration (via smaller receptive fields), here the authors find that the properties of receptive fields in face-selective brain regions are the same in typical individuals vs. those with DP. The main analysis technique is population Receptive Field (pRF) mapping, with a wide range of measures considered. The authors report that there are no differences in goodness-of-fit (R2), the properties of the pRFs (neither size, location, nor the gain and exponent of the Compressive Spatial Summation model), nor their coverage of the visual field. The relationship of these properties to the visual field (notably the increase in pRF size with eccentricity) is also similar between the groups. Eye movements do not differ between the groups.

Strengths:

Although this is a null result, the large number of null results gives confidence that there are unlikely to be differences between the two groups. Together, this makes a compelling case that DP is not driven by differences in the spatial selectivity of face-selective brain regions, an important finding that directly informs theories of face recognition. The paper is well written and enjoyable to read, the studies have clearly been carefully conducted with clear justification for design decisions, and the analyses are thorough.

Weaknesses:

One potential issue relates to the localisation of face-selective regions in the two groups. As in most studies of the neural basis of face recognition, localisers are used to find the face-selective Regions of Interest (ROIs) - OFA, mFus, and pFus, with comparison to the scene-selective PPA. To do so, faces are contrasted against other objects to find these regions (or scenes vs. others for the PPA). The one consistent difference that does emerge between groups in the paper is in the selectivity of these regions, which are less selective for faces in DP than in typical individuals (e.g., Figure 1B), as one might expect. 6/20 prosopagnosic individuals are also missing mFus, relative to only 2/20 typical individuals. This, to me, raises the question of whether the two groups are being compared fairly. If the localised regions were smaller and/or displaced in the DPs, this might select only a subset of the neural populations typically involved in face recognition. Perhaps the difference between groups lies outside this region. In other words, it could be that the differences in prosopagnosic face recognition lie in the neurons that are not able to be localised by this approach. The authors consider in the discussion whether their DPs may not have been 'true DPs', which is convincing (p. 12). The question here is whether the regions selected are truly the 'prosopagnosic brain areas' or whether there is a kind of survivor bias (i.e., the regions selected are normal, but perhaps the difference lies in the nature/extent of the regions. At present, the only consideration given to explain the differences in prosopagnosia is that there may be 'qualitative' differences between the two (which may be true), but I would give more thought to this.

The discussion considers the differences between the current study and an unpublished preprint (Witthoft et al, 2016), where DPs were found to have smaller pRFs than typical individuals. The discussion presents the argument that the current results are likely more robust, given the use of images within the pRF mapping stimuli here (faces, objects, etc) as opposed to checkerboards in the prior work, and the use of the CSS model here as opposed to a linear Gaussian model previously. This is convincing, but fails to address why there is a lack of difference in the control vs. DP group here. If anything, I would have imagined that the use of faces in mapping stimuli would have promoted differences between the groups (given the apparent difference in selectivity in DPs vs. controls seen here), which adds to the reliability of the present result. Greater consideration of why this should have led to a lack of difference would be ideal. The latter point about pRF models (Gaussian vs. CSS) does seem pertinent, for instance - could the 'qualitative' difference lead to changes in the shape of these pRFs in prosopagnosia that are better characterised by the CSS model, perhaps? Perhaps more straightforwardly, and related to the above, could differences in the localisation of face-selective regions have driven the difference in prior work compared to here?

Finally, the lack of variations in the spatial properties of these brain regions is interesting in light of the theories that spatial integration is a key aspect of effective face recognition. In this context, it is interesting to note the marked drop in R2 values in face-selective regions like mFus relative to earlier cortex. The authors note in some sense that this is related to the larger receptive field size, but is there a broader point here that perhaps the receptive field model (even with Compressive Spatial Summation) is simply a poor fit for the function of these areas? Could it be that these areas are simply not spatial at all? A broader link between the null results presented here and their implications for theories of face recognition would be ideal.

Reviewer #2 (Public review):

Summary:

This is a well-conducted and clearly written manuscript addressing the link between population receptive fields (pRFs) and visual behavior. The authors test whether developmental prosopagnosia (DP) involves atypical pRFs in face-selective regions, a hypothesis suggested by prior work with a small DP sample. Using a larger cohort of DPs and controls, robust pRF mapping with appropriate stimuli and CSS modeling, and careful in-scanner eye tracking, the authors report no group differences in pRF properties across the visual processing hierarchy. These results suggest that reduced spatial integration is unlikely to account for holistic face processing deficits in DP.

Strengths:

The dataset quality, sample size, and methodological rigor are notable strengths.

Weaknesses:

The primary concern is the interpretation of the results.

(1) Relationship between pRFs and spatial integration

While atypical pRF properties could contribute to deficits in spatial integration, impairments in holistic processing in DPs are not necessarily caused by pRF abnormalities. The discussion could be strengthened by considering alternative explanations for reduced spatial integration, such as altered structural or functional connectivity in the face network, which has been reported to underlie DP's difficulties in integrating facial features.

(2) Beyond the null hypothesis testing framework

The title claims "normal spatial integration," yet this conclusion is based on a failure to reject the null hypothesis, which does not justify accepting the alternative hypothesis. To substantiate a claim of "normal," the authors would need to provide analyses quantifying evidence for the absence of effects, e.g., using a Bayesian framework.

(3) Face-specific or broader visual processing

Prior work from the senior author's lab (Jiahui et al., 2018) reported pronounced reductions in scene selectivity and marginal reductions in body selectivity in DPs, suggesting that visual processing deficits in DPs may extend beyond faces. While the manuscript includes PPA as a high-level control region for scene perception, scene selectivity was not directly reported. The authors could also consider individual differences and potential data-quality confounds (tSNR difference between and within groups, several obvious outliers in the figures, etc). For instance, examining whether reduced tSNR in DPs contributed to lower face selectivity in the DP group in this dataset.

(4) Linking pRF properties to behavior

The manuscript aims to examine the relationship between pRF properties and behavior, but currently reports only one aspect of pRF (size) in relation to a single behavioral measure (CFMT), without full statistical reporting:

"We found no significant association between participants' CFMT scores and mean pRF size in OFA, pFUS, or mFUS."

For comprehensive reporting, the authors could examine additional pRF properties (e.g., center, eccentricity, scaling between eccentricity and pRF size, shape of visual field coverage, etc), additional ROIs (early, intermediate, and category-selective areas), and relate them to multiple behavioral measures (e.g., HEVA, PI20, FFT). This would provide a full picture of how pRF characteristics relate to behavioral performance in DP.

Author response:

Reviewer #1 (Public review):

Summary:

The authors examine the neural correlates of face recognition deficits in individuals with Developmental Prosopagnosia (DP; 'face blindness'). Contrary to theories that poor face recognition is driven by reduced spatial integration (via smaller receptive fields), here the authors find that the properties of receptive fields in face-selective brain regions are the same in typical individuals vs. those with DP. The main analysis technique is population Receptive Field (pRF) mapping, with a wide range of measures considered. The authors report that there are no differences in goodness-of-fit (R2), the properties of the pRFs (neither size, location, nor the gain and exponent of the Compressive Spatial Summation model), nor their coverage of the visual field. The relationship of these properties to the visual field (notably the increase in pRF size with eccentricity) is also similar between the groups. Eye movements do not differ between the groups.

Strengths:

Although this is a null result, the large number of null results gives confidence that there are unlikely to be differences between the two groups. Together, this makes a compelling case that DP is not driven by differences in the spatial selectivity of face-selective brain regions, an important finding that directly informs theories of face recognition. The paper is well written and enjoyable to read, the studies have clearly been carefully conducted with clear justification for design decisions, and the analyses are thorough.

Weaknesses:

One potential issue relates to the localisation of face-selective regions in the two groups. As in most studies of the neural basis of face recognition, localisers are used to find the face-selective Regions of Interest (ROIs) - OFA, mFus, and pFus, with comparison to the scene-selective PPA. To do so, faces are contrasted against other objects to find these regions (or scenes vs. others for the PPA). The one consistent difference that does emerge between groups in the paper is in the selectivity of these regions, which are less selective for faces in DP than in typical individuals (e.g., Figure 1B), as one might expect. 6/20 prosopagnosic individuals are also missing mFus, relative to only 2/20 typical individuals. This, to me, raises the question of whether the two groups are being compared fairly. If the localised regions were smaller and/or displaced in the DPs, this might select only a subset of the neural populations typically involved in face recognition. Perhaps the difference between groups lies outside this region. In other words, it could be that the differences in prosopagnosic face recognition lie in the neurons that are not able to be localised by this approach. The authors consider in the discussion whether their DPs may not have been 'true DPs', which is convincing (p. 12). The question here is whether the regions selected are truly the 'prosopagnosic brain areas' or whether there is a kind of survivor bias (i.e., the regions selected are normal, but perhaps the difference lies in the nature/extent of the regions. At present, the only consideration given to explain the differences in prosopagnosia is that there may be 'qualitative' differences between the two (which may be true), but I would give more thought to this.

We acknowledge that face-selective ROIs in DPs, relative to controls, may be smaller, less selective, or altogether missing when traditional methods of localization with fixed thresholds are used (Furl et al, 2011). For this reason - to circumvent potential survivor bias and ensure ROI voxel counts across participants are equated - we used a method of ROI definition whereby each subject’s individual statistical map from the localizer was intersected with a generously-sized group mask for each ROI and the top 20% most category-selective voxels were retained for the pRF analysis (Norman-Haignere et al., 2013; Jiahui et al., 2018). This means that the raw number of voxels per ROI was equal across all participants with respect to the common group space, thereby ensuring a fair comparison even in cases where one group shows diminished category-selectivity. The details of the ROI definition are provided in the Methods at the end of the manuscript. To ensure readers understand our approach, we will also make more explicit mention of this in the main body of the manuscript. 

With regard to the question of whether face-selective ROIs may be displaced in DPs compared to controls, previous work from the senior author’s lab (Jiahui et al., 2018) shows that, despite exhibiting weaker activations, the peak coordinates of significant clusters in DPs occupy very similar locations to those of controls. And, even if there were indeed slight displacements of face-selective ROIs for some subjects, the group-defined masks used in the present analysis were large enough to capture the majority of the top voxels. In the supplemental materials section, we will include a diagram of the group masks used in our study.

The reviewer here also points out that more DPs than controls were missing the mFUS region (6/20 DPs vs 2/20 controls; Figure 1C). However, ‘missing’ in this context was not based on face-selectivity but rather a lack of retinotopic tuning. PRFs were fit to all voxels within each ROI - with all subjects starting out with equal voxel counts - and thereafter, voxels for which the variance explained by the pRF model was below 20% were excluded from subsequent analysis. We decided that any ROI with fewer than 10 voxels remaining after thresholding on the pRF fit should be deemed ‘missing’ since we considered the amount of data insufficient to reliably characterize the region’s retinotopic profile. While it may be somewhat interesting that four more DPs than controls were ‘missing’ left mFUS, using this particular set of decision criteria, it is important to keep in mind that left mFUS was just one of six face-selective regions under study. The other five regions, many of which evinced strong fits by the pRF model, were represented comparably in DPs and controls and showed high similarity in the pRF parameters. Furthermore, across most participants, mFUS exhibited a low proportion of retinotopically modulated voxels (defined as voxels with pRF R squared greater than 20%, see Figure 1D). A follow-up analysis showed that the count of voxels surviving pRF R squared thresholding in left mFUS was not significantly correlated with mean pRF size (r(30)=0.23, t=1.28,  p=0.21) indicating that the greater exclusion of DPs in this region is unlikely to have biased the group’s average pRF size.

The discussion considers the differences between the current study and an unpublished preprint (Witthoft et al, 2016), where DPs were found to have smaller pRFs than typical individuals. The discussion presents the argument that the current results are likely more robust, given the use of images within the pRF mapping stimuli here (faces, objects, etc) as opposed to checkerboards in the prior work, and the use of the CSS model here as opposed to a linear Gaussian model previously. This is convincing, but fails to address why there is a lack of difference in the control vs. DP group here. If anything, I would have imagined that the use of faces in mapping stimuli would have promoted differences between the groups (given the apparent difference in selectivity in DPs vs. controls seen here), which adds to the reliability of the present result. Greater consideration of why this should have led to a lack of difference would be ideal. The latter point about pRF models (Gaussian vs. CSS) does seem pertinent, for instance - could the 'qualitative' difference lead to changes in the shape of these pRFs in prosopagnosia that are better characterised by the CSS model, perhaps? Perhaps more straightforwardly, and related to the above, could differences in the localisation of face-selective regions have driven the difference in prior work compared to here?

We agree that the use of high-level mapping stimuli (including faces) adds to the reliability of the present results for DPs and could have further emphasized differences between the groups if true differences did, in fact, exist. We speculate on the extent to which the type of mapping stimuli and various other methodological factors (e.g. stimulus size, aperture design, pRF model) could have explained the divergent findings in our study versus that of Witthoft et al. (2016) in the section of the Discussion titled, “What factors may have contributed to the different results for the present study and Witthoft et al. (2016)”. In brief, our use of more colorful, naturalistic stimuli targeting higher-level visual areas elicited better model fits than the black and white checkerboard pattern used by Witthoft et al. (2016). The CSS model we used is better suited for higher-level regions and makes fewer assumptions than the linear pRF model. The field of view of our stimulus was smaller but still relevant for real-world perception of faces. Finally, our aperture design and longer run length likely also improved reliability. Overall, these methodological improvements, along with our larger sample size, provide stronger evidence for our findings. These are our best attempts to make sense of the divergent findings, but it is not possible to come to a definitive explanation. Examples abound of exaggerated or spurious effects from small-scale studies that ultimately fail to replicate in the related field of dyslexia research (Jednorog et al., 2015; Ramus et al., 2018) and neuroimaging research more generally (Turner et al., 2018; Poldrack et al., 2017). Sometimes there are clear explanations for a lack of replicability (e.g. software bugs, overly flexible preprocessing methods, etc.), but many times the real reason cannot be determined.

Regarding the type of pRF model deployed, our use of a non-linear exponent (versus a linear model as in the Witthoft et al. (2016) preprint) is unlikely to explain the similarity we observed between the groups in terms of pRF size. Specifically, the groups did not show substantial differences in the exponent by ROI, as seen in Figure 1E, so the use of a linear model should, in theory, produce similar outcomes for the two groups. We will mention this point in the main text.

Finally, the lack of variations in the spatial properties of these brain regions is interesting in light of the theories that spatial integration is a key aspect of effective face recognition. In this context, it is interesting to note the marked drop in R2 values in face-selective regions like mFus relative to earlier cortex. The authors note in some sense that this is related to the larger receptive field size, but is there a broader point here that perhaps the receptive field model (even with Compressive Spatial Summation) is simply a poor fit for the function of these areas? Could it be that these areas are simply not spatial at all? A broader link between the null results presented here and their implications for theories of face recognition would be ideal.

The weaker pRF fits found in mFUS, to us, raise the question of whether there is a more effective pRF stimulus for these more anterior regions. For example, it might be possible to obtain higher and more reliable responses there using single isolated faces (Cf. Kay, Weiner, Grill-Spector, 2015). More broadly, though, we agree that it is important to acknowledge that the receptive field model might ultimately be a coarse and incomplete characterization of neural function in these areas. As the other reviewer suggests, one possibility is that other brain processes (e.g. functional or structural connectivity between ROIs) may give rise to holistic face processing in ways that are not captured by pRF properties.

Reviewer #2 (Public review):

Summary:

This is a well-conducted and clearly written manuscript addressing the link between population receptive fields (pRFs) and visual behavior. The authors test whether developmental prosopagnosia (DP) involves atypical pRFs in face-selective regions, a hypothesis suggested by prior work with a small DP sample. Using a larger cohort of DPs and controls, robust pRF mapping with appropriate stimuli and CSS modeling, and careful in-scanner eye tracking, the authors report no group differences in pRF properties across the visual processing hierarchy. These results suggest that reduced spatial integration is unlikely to account for holistic face processing deficits in DP.

Strengths:

The dataset quality, sample size, and methodological rigor are notable strengths.

Weaknesses:

The primary concern is the interpretation of the results.

(1) Relationship between pRFs and spatial integration

While atypical pRF properties could contribute to deficits in spatial integration, impairments in holistic processing in DPs are not necessarily caused by pRF abnormalities. The discussion could be strengthened by considering alternative explanations for reduced spatial integration, such as altered structural or functional connectivity in the face network, which has been reported to underlie DP's difficulties in integrating facial features.

We agree the Discussion section could benefit from mentioning that alterations to other neural mechanisms, besides pRF organization, could produce deficits in holistic processing. This could take the form of altered functional connectivity (Rosenthal et al., 2017; Lohse et al., 2016; Avidan et al., 2014) or altered structural connectivity (Gomez et al., 2015; Song et al., 2015)

(2) Beyond the null hypothesis testing framework

The title claims "normal spatial integration," yet this conclusion is based on a failure to reject the null hypothesis, which does not justify accepting the alternative hypothesis. To substantiate a claim of "normal," the authors would need to provide analyses quantifying evidence for the absence of effects, e.g., using a Bayesian framework.

We acknowledge that, using frequentist statistical methods, failing to reject the null hypothesis is not sufficient to claim equivalence. For the revision, we will look into additional analyses that could quantify evidence for the null hypothesis. And we will adjust the wording of the title in this regard.

(3) Face-specific or broader visual processing

Prior work from the senior author's lab (Jiahui et al., 2018) reported pronounced reductions in scene selectivity and marginal reductions in body selectivity in DPs, suggesting that visual processing deficits in DPs may extend beyond faces. While the manuscript includes PPA as a high-level control region for scene perception, scene selectivity was not directly reported. The authors could also consider individual differences and potential data-quality confounds (tSNR difference between and within groups, several obvious outliers in the figures, etc). For instance, examining whether reduced tSNR in DPs contributed to lower face selectivity in the DP group in this dataset.

Thank you for this suggestion - we will compare tSNR between the groups as a measure of data quality and we will include these comparisons. A preliminary look indicates that both groups possessed similar distributions of tSNR across many of the face-selective regions investigated here.

(4) Linking pRF properties to behavior

The manuscript aims to examine the relationship between pRF properties and behavior, but currently reports only one aspect of pRF (size) in relation to a single behavioral measure (CFMT), without full statistical reporting:

"We found no significant association between participants' CFMT scores and mean pRF size in OFA, pFUS, or mFUS."

For comprehensive reporting, the authors could examine additional pRF properties (e.g., center, eccentricity, scaling between eccentricity and pRF size, shape of visual field coverage, etc), additional ROIs (early, intermediate, and category-selective areas), and relate them to multiple behavioral measures (e.g., HEVA, PI20, FFT). This would provide a full picture of how pRF characteristics relate to behavioral performance in DP.

We will report the full statistical values (r, p) for the (albeit non-significant) relationship between CFMT score and pRF size - thank you for bringing that to our attention. Additionally, we will add other analyses assessing the relationship between a wider array of pRF measures and the other behavioral tests administered to provide a more comprehensive picture of the relation between pRFs and behavior.

References:

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Furl, N., Garrido, L., Dolan, R. J., Driver, J., & Duchaine, B. (2011). Fusiform gyrus face selectivity relates to individual differences in facial recognition ability. Journal of Cognitive Neuroscience, 23(7), 1723–1740. https://doi.org/10.1162/jocn.2010.21545

Gomez, J., Pestilli, F., Witthoft, N., Golarai, G., Liberman, A., Poltoratski, S., Yoon, J., & Grill-Spector, K. (2015). Functionally Defined White Matter Reveals Segregated Pathways in Human Ventral Temporal Cortex Associated with Category-Specific Processing. Neuron, 85(1), 216–227. https://doi.org/10.1016/j.neuron.2014.12.027

Jednoróg, K., Marchewka, A., Altarelli, I., Monzalvo Lopez, A. K., van Ermingen-Marbach, M., Grande, M., Grabowska, A., Heim, S., & Ramus, F. (2015). How reliable are gray matter disruptions in specific reading disability across multiple countries and languages? Insights from a large-scale voxel-based morphometry study. Human Brain Mapping, 36(5), 1741–1754. https://doi.org/10.1002/hbm.22734

Jiahui, G., Yang, H., & Duchaine, B. (2018). Developmental prosopagnosics have widespread selectivity reductions across category-selective visual cortex. Proceedings of the National Academy of Sciences of the United States of America, 115(28), E6418–E6427. https://doi.org/10.1073/pnas.1802246115

Kay, K. N., Weiner, K. S., Kay, K. N., & Weiner, K. S. (2015). Attention Reduces Spatial Uncertainty in Human Ventral Temporal Cortex Attention Reduces Spatial Uncertainty in Human Ventral Temporal Cortex. Current Biology, 25(5), 595–600. https://doi.org/10.1016/j.cub.2014.12.050

Lohse, M., Garrido, L., Driver, J., Dolan, R. J., Duchaine, B. C., & Furl, N. (2016). Effective connectivity from early visual cortex to posterior occipitotemporal face areas supports face selectivity and predicts developmental prosopagnosia. Journal of Neuroscience, 36(13), 3821–3828. https://doi.org/10.1523/JNEUROSCI.3621-15.2016

Norman-Haignere, S., Kanwisher, N., & McDermott, J. H. (2013). Cortical pitch regions in humans respond primarily to resolved harmonics and are located in specific tonotopic regions of anterior auditory cortex. Journal of Neuroscience, 33(50), 19451–19469. https://doi.org/10.1523/JNEUROSCI.2880-13.2013

Poldrack, R. A., Baker, C. I., Durnez, J., Gorgolewski, K. J., Matthews, P. M., Munafò, M. R., Nichols, T. E., Poline, J. B., Vul, E., & Yarkoni, T. (2017). Scanning the horizon: Towards transparent and reproducible neuroimaging research. Nature Reviews Neuroscience, 18(2), 115–126. https://doi.org/10.1038/nrn.2016.167

Ramus, F., Altarelli, I., Jednoróg, K., Zhao, J., & Scotto di Covella, L. (2018). Neuroanatomy of developmental dyslexia: Pitfalls and promise. Neuroscience and Biobehavioral Reviews, 84(July 2017), 434–452. https://doi.org/10.1016/j.neubiorev.2017.08.001

Rosenthal, G., Tanzer, M., Simony, E., Hasson, U., Behrmann, M., & Avidan, G. (2017). Altered topology of neural circuits in congenital prosopagnosia. ELife, 6, 1–20. https://doi.org/10.7554/eLife.25069

Song, S., Garrido, L., Nagy, Z., Mohammadi, S., Steel, A., Driver, J., Dolan, R. J., Duchaine, B., & Furl, N. (2015). Local but not long-range microstructural differences of the ventral temporal cortex in developmental prosopagnosia. Neuropsychologia, 78, 195–206. https://doi.org/10.1016/j.neuropsychologia.2015.10.010

Turner, B. O., Paul, E. J., Miller, M. B., & Barbey, A. K. (2018). Small sample sizes reduce the replicability of task-based fMRI studies. Communications Biology, 1(1). https://doi.org/10.1038/s42003-018-0073-z

Witthoft, N., Poltoratski, S., Nguyen, M., Golarai, G., Liberman, A., LaRocque, K., Smith, M., & Grill-Spector, K. (2016). Reduced spatial integration in the ventral visual cortex underlies face recognition deficits in developmental prosopagnosia. BioRxiv, 1–26.

eLife Assessment

This manuscript makes a valuable contribution to understanding learning in multidimensional environments with spurious associations, which is critical for understanding learning in the real world. The evidence is based on model simulations and a preregistered human behavioral study, but remains incomplete because of inconclusive empirical results and insufficiencies in the modeling. Moreover, there are open questions about the nature and extent to which the behavioral task induced semantic congruency.

Reviewer #1 (Public review):

Summary:

This paper reports model simulations and a human behavioral experiment studying predictive learning in a multidimensional environment. The authors claim that semantic biases help people resolve ambiguity about predictive relationships due to spurious correlations.

Strengths:

(1) The general question addressed by the paper is important.

(2) The paper is clearly written.

(3) Experiments and analyses are rigorously executed.

Weaknesses:

(1) Showing that people can be misled by spurious correlations, and that they can overcome this to some extent by using semantic structure, is not especially surprising to me. Related literature already exists on illusory correlation, illusory causation, superstitious behavior, and inductive biases in causal structure learning. None of this work features in the paper, which is rather narrowly focused on a particular class of predictive representations, which, in fact, may not be particularly relevant for this experiment. I also feel that the paper is rather long and complex for what is ultimately a simple point based on a single experiment.

(2) Putting myself in the shoes of an experimental subject, I struggled to understand the nature of semantic congruency. I don't understand why the builder and terminal robots should have similar features is considered a natural semantic inductive bias. Humans build things all the time that look different from them, and we build machines that construct artifacts that look different from the machines. I think the fact that the manipulation worked attests to the ability of human subjects to pick up on patterns rather than supporting the idea that this reflects an inductive bias they brought to the experiment.

(3) As the authors note, because the experiment uses only a single transition, it's not clear that it can really test the distinctive aspects of the SR/SF framework, which come into play over longer horizons. So I'm not really sure to what extent this paper is fundamentally about SFs, as it's currently advertised.

(4) One issue with the inductive bias as defined in Equation 15 is that I don't think it will converge to the correct SR matrix. Thus, the bias is not just affecting the learning dynamics, but also the asymptotic value (if there even is one; that's not clear either). As an empirical model, this isn't necessarily wrong, but it does mess with the interpretation of the estimator. We're now talking about a different object from the SR.

(5) Some aspects of the empirical and model-based results only provide weak support for the proposed model. The following null effects don't agree with the predictions of the model:

(a) No effect of condition on reward.

(b) No effect of condition on composition spurious predictiveness.

(c) No effect of condition on the fitted bias parameter. The authors present some additional exploratory analyses that they use to support their claims, but this should be considered weaker support than the results of preregistered analyses.

(6) I appreciate that the authors were transparent about which predictions weren't confirmed. I don't think they're necessarily deal-breakers for the paper's claims. However, these caveats don't show up anywhere in the Discussion.

(7) I also worry that the study might have been underpowered to detect some of these effects. The preregistration doesn't describe any pilot data that could be used to estimate effect sizes, and it doesn't present any power analysis to support the chosen sample sizes, which I think are on the small side for this kind of study.

Reviewer #3 (Public review):

The article's main question is how humans handle spurious transitions between object features when learning a predictive model for decision-making. The authors conjecture that humans use semantic knowledge about plausible causal relations as an inductive bias to distinguish true from spurious links.

The authors simulate a successor feature (SF) model, demonstrating its susceptibility to suboptimal learning in the presence of spurious transitions caused by co-occurring but independent causal factors. This effect worsens with an increasing number of planning steps and higher co-occurrence rates. In a preregistered study (N=100), they show that humans are also affected by spurious transitions, but perform somewhat better when true transitions occur between features within the same semantic category. However, no evidence for the benefits of semantic congruency was found in test trials involving novel configurations, and attempts to model these biases within an SF framework remained inconclusive.

Strengths:

(1) The authors tackle an important question.

(2) Their simulations employ a simple yet powerful SF modeling framework, offering computational insights into the problem.

(3) The empirical study is preregistered, and the authors transparently report both positive and null findings.

(4) The behavioral benefit during learning in the congruent vs incongruent condition is interesting

Weaknesses:

(1) A major issue is that approximately one quarter of participants failed to learn, while another quarter appeared to use conjunctive or configural learning strategies. This raises questions about the appropriateness of the proposed feature-based learning framework for this task. Extensive prior research suggests that learning about multi-attribute objects is unlikely to involve independent feature learners (see, e.g., the classic discussion of configural vs. elemental learning in conditioning: Bush & Mosteller, 1951; Estes, 1950).

(2) A second concern is the lack of explicit acknowledgment and specification of the essential role of the co-occurrence of causal factors. With sufficient training, SF models can develop much stronger representations of reliable vs. spurious transitions, and simple mechanisms like forgetting or decay of weaker transitions would amplify this effect. This should be clarified from the outset, and the occurrence rates used in all tasks and simulations need to be clearly stated.

(3) Another problem is that the modeling approach did not adequately capture participant behavior. While the authors demonstrate that the b parameter influences model behavior in anticipated ways, it remains unclear how a model could account for the observed congruency advantage during learning but not at test.

(4) Finally, the conceptualization of semantic biases is somewhat unclear. As I understand it, participants could rely on knowledge such as "the shape of a building robot's head determines the kind of head it will build," while the type of robot arm would not affect the head shape. However, this assumption seems counterintuitive - isn't it plausible that a versatile arm is needed to build certain types of robot heads?

eLife Assessment

AGC kinases, such as PKN1, are regulated by activation loop phosphorylation. This paper reports that exposing cells to high concentrations of monovalent cations induces rapid activation loop dephosphorylation, with rapid re-phosphorylation when physiological salt is restored. Re-phosphorylation is apparently independent of ATP or candidate kinases, and the paper presents an extraordinary and unconventional mechanism involving phosphate exchange between the activation loop and an unknown acceptor molecule. The findings are intriguing and the approach is logical, but the evidence is incomplete and the significance unclear until the biochemical mechanism is identified.

Reviewer #1 (Public review):

The authors found that high concentrations of a series of monovalent cations, NaCl, KCl, RbCl, and CsCl (although not LiCl), but not equal high osmolarity treatment of cultured cells induced rapid loss of phosphate from pT774 in the activation loop (AL) of the PKN1 Ser/Thr protein kinase, as well the cognate AL phosphoresidue in other related AGC family kinases, including PKCζ, PKCλ, and p70 S6 kinase. Focusing on PKN1, they showed that restoration of the extracellular salt concentration to physiological levels resulted in equally rapid recovery of AL phosphorylation. Using both okadaic acid PP1/PP2A inhibitor, and a selective PP2A inhibitor, PP2A was implicated as the protein phosphatase required for the rapid dephosphorylation of PIN1 pT774 in response to high salt. By making PKN1 T778A knock-in mouse fibroblast cells and re-expressing WT and a kinase-dead mutant PKN1, as well as use of PDK1 KO MEFs, they showed that recovery of T774 phosphorylation did not require PDK1, the protein kinase known to phosphorylate this site in cells, or the kinase activity of PKN1 itself. Surprisingly, they found that dephosphorylation of the PKN1 AL site also occurred when cell lysates were adjusted to high salt, with re-phosphorylation of T774 occurring rapidly when physiological salt level was restored by dilution. Their in vitro lysate experiments also demonstrated that depletion of ATP by apyrase treatment or sequestration of Mg2+ by EDTA did not prevent T744 re-phosphorylation, which would rule out a conventional protein kinase. Various GST-tagged fragments of PKN1, including a 767-780 AL 14-mer peptide,e exhibited the same curious de- and re-phosphorylation effect when mixed with cell lysates and exposed to high KCl followed by dilution. Using 32P γ-ATP and PDK1 to generate 32P-labeled phospho-GST-PKN1 (767-788). They showed the 32P signal was lost from GST-PKN1 (767-788) in lysates exposed to high salt, and restored again upon dilution. Similar results were obtained with unlabeled samples using PhosTag analysis to resolve phosphospecies.

They went on to test three possible models to explain their data:

(1) Model 1. Intramolecular transfer of the pT774 phosphate group, where the pT774 phosphate is reversibly transferred onto another residue in the same PKN1 molecule in response to high and normal salt concentrations. They attempted to rule out this model by mutating possible noncanonical phosphate acceptors in the 776GYGDRTSTFCGTPE788 peptide, making C776, D770A, R771A, and E780A mutant peptides, without observing any effect on the dephosphorylation/re-phosphorylation phenomenon.

(2) Model 2. Re-phosphorylation of T774 involves an unidentified phosphate donor, distinct from ATP or phospho-PKN1. This model was ruled out in several ways, including by demonstrating that added 32P-labeled PKN1 lost its 32P signal in high salt-exposed lysates, with the 32P signal being recovered upon dilution even in the presence of excess unlabeled ATP.

(3) Model 3. Reversible transfer of the pT774 phosphate group onto an intermediary factor (X) in the presence of high salt and re-phosphorylation in cis by phospho-X upon dilution, which is the model they favored. In support of this model, they showed that the pT774 phosphate could not be transferred onto another PKN1 fragment of a different size, nor did GST-PKN1 767-788 pretreated with λ-phosphatase regain phosphate. In the end, however, they were unable to identify the hypothetical factor X, and no 32P-labeled protein was observed in the experiment with 32P-labeled PKN1 upon high salt-induced dephosphorylation.

This is an intriguing and unexpected set of findings that could herald a new protein kinase regulatory mechanism, but ultimately, we are left with an intriguing observation without a clear-cut explanation. The authors have been very methodical in their analysis of this odd phenomenon, and their data and conclusions, for the most part, seem convincing, although some of the blot signals are rather weak. However, despite all their efforts, the identity of the hypothetical factor X, which can transiently accept a phosphate from pT774 in the PKN1 activation loop in response to supraphysiological alkali metal cation concentrations and then donate it back again to T774 in cis, when physiological salt concentrations are restored, remains unclear.

As it stands, there are several unresolved issues that need to be addressed.

(1) The real conundrum, as their data show, is that phospho-X cannot phosphorylate PKN1 in trans, and therefore has to act in cis, meaning that phospho-X must somehow remain associated with the same dephosphorylated PKN1 molecule that the phosphate came from. Because a small molecule would rapidly diffuse away from PKN1, the only reasonable model is that X is a protein and not a small molecule, such as creatine (the authors considered X unlikely to be a small molecule for other reasons). However, if X were a protein, then it should have been labeled and detectable on the gel in the 32P-experiment shown in Figure 6C, but no other 32P-labeled band was observed in lane 5. Even if phospho-X has a labile phosphate linkage that would be lost upon SDS-gel electrophoresis, it is unclear how phospho-X would remain associated with the very short 14-mer PKN1 activation loop peptide, especially under the extremely dilute conditions of a cell lysate.

(2) The evidence that PP2A is required in PKN1 dephosphorylation is reasonable, and in the Discussion, the authors consider various scenarios in which PP2A could be involved in generating the hypothetical phospho-X needed for T774 re-phosphorylation, most of which do not seem very plausible. In the end, it remains unclear how free phosphate released from pT774 in PKN1 by PP2A, which does not employ a phosphoenzyme intermediate, ends up covalently attached to molecule X.

(3) The interpretation of the in vitro data is complicated by the fact that cell lysis results in a massive dilution of both proteins and any small molecules present in the cell (apparently dilution with lysis buffer was at least 10-fold initially, and then a further 2-fold to restore normal salt levels), making it hard to imagine how a large or small molecule would remain tightly associated with a PKN1 molecule, i.e. Model 3 really only works if re-phosphorylation of T774 is a zero order/intramolecular reaction. Moreover, the re-phosphorylation reaction rates would be expected to fall dramatically upon dilution of both the dephosphorylated GST-PKN1 767-788 protein and phospho-X during restoration of normal salt, meaning that the kinetics of T774 re-phosphorylation should be significantly slower in vitro. In this connection, it would be informative if the authors carried out a lysate dilution series to test the extent to which the observed phenomenon is dilution-independent.

(4) Another issue is that most of the results, apart from the 32P-labeling experiment, are dependent on the specificity of the anti-pT774 PKN1 antibodies they used. The fact that the C776A mutant peptide gave a weaker anti-pT774 signal might be because phospho-Ab binding is, in part, dependent on recognition of Cys776. In turn, this suggests the possibility that reversible oxidation of C776 might cause the loss and regain of the pT774 signal at high and low salt concentrations, as a result of the oxidized form of C776 preventing anti-pT774 antibody binding. The Cell Signaling Technology phospho-PRK1 (Thr774)/PRK2 (Thr816) antibody (#2611) that was used here was generated against a synthetic peptide containing pT774, and while the exact antigenic peptide sequence is not given in the CST catalogue, presumably it had 4 or 5 residues on either side of pT774 (GYGDRTSTFCGTPE) (although C776 might have been substituted in the antigenic peptide because of issues with Cys oxidation).

(5) Perhaps the most important deficiency is that the target for the monovalent cation that induces PKN1 activation loop dephosphorylation was not established. Is this somehow a direct effect of cations on PKN1 itself - this seems unlikely, since this effect is observed with a 14-mer PKN1 activation loop peptide - or is this an indirect effect? In terms of possible indirect mechanisms, high salt treatment of cells is known to induce elevated ROS as a result of mitochondrial damage, which could lead to oxidative modification of cysteines, such as C776, in the activation loop and might interfere with anti-pT774 antibody recognition.

In summary, the authors have put a great deal of thought and resources into trying to solve this intriguing puzzle, but despite a lot of effort, have not convincingly elucidated how this dephosphorylation/re-phosphorylation process works. For this, they need to identify phospho-X and define how it remains associated with the original pT774 PKN1 molecule in order to carry out re-phosphorylation.

Reviewer #2 (Public review):

Summary:

This study reports a highly unconventional mechanism by which AGC kinases might undergo reversible activation-loop (T-loop) phosphorylation through an ATP-independent phosphate recycling process that is modulated by alkali metal ions such as Na⁺ and K⁺. The authors propose that these ions trigger phosphate dissociation and subsequent reattachment in the absence of ATP or canonical kinase activity, implying the existence of a novel phosphate-transferring intermediate. If validated, this would represent a radical departure from established models of kinase regulation and signal transduction. I note that this study is personally funded by one of the authors.

Strengths:

The study addresses an important and fundamental question in protein phosphorylation biology. The authors have conducted an impressive number of biochemical experiments spanning cellular and in vitro systems, with multiple orthogonal readouts. The idea of an ATP-independent phosphate recycling mechanism is original and thought-provoking, challenging conventional assumptions and inviting further exploration. The manuscript is well organized and written with considerable technical detail.

Weaknesses:

The central mechanistic claim contradicts extensive existing evidence on AGC kinase regulation derived from decades of biochemical, mechanistic, pharmacological, genetic, and structural studies. The data, while extensive, do not provide sufficiently direct or quantitative evidence to support the existence of ATP-independent phosphate transfer. Alternative explanations, such as low-level residual ATP-dependent re-phosphorylation or assay artifacts, are not fully excluded. They claim that an unidentified factor-x is involved, but do not provide evidence for the existence of this molecule or characterize this. The physiological relevance of the ion concentrations used is unclear, as the conditions far exceed normal intercellular levels. Overall, the findings are not yet convincing enough to support a paradigm shift in our understanding of AGC kinase activation, in my opinion.

Reviewer #3 (Public review):

This is an intriguing paper that reports a potentially novel mechanism of reversible phosphorylation of AGC kinase activation segments by changes in sodium and potassium ion concentrations. The authors show for a variety of AGC kinases that incubating diverse eukaryotic cell types in 450 and 600 mM NaCl results in dephosphorylation of the activation segment. In contrast, phosphorylation of the activation segment for p38 kinases increases. No dephosphorylation of AGC kinases activation segment occurs with sorbitol, thus dephosphorylation is independent of osmotic pressure. This effect is rapidly reversed when cells are returned to normal media and the AGC kinase is re-phosphorylated. This phenomenon is also observed for eukaryotic cell-free extracts, and is induced by other alkali metal ions but not lithium. Importantly, no dephosphorylation is observed in the E. coli cell extract.

The authors also make the following observations:

(1) Dephosphorylation is dependent on PP2A.

(2) Re-phosphorylation is not dependent on PDK1, ATP, and Mg2+.

(3) The K/Na-dependent dephosphorylation/phosphorylation is observed even for relatively short protein segments that incorporate the activation segment.

(4) The phosphorylation observed occurs in cis, i.e., only the activation segment of the protein that is dephosphorylated becomes phosphorylated on reduced KCl. An activation segment from a different length protein is not phosphorylated.

(5) No evidence for auto(de)phosphorylation.

(6) The authors propose three models to explain the dephosphorylation/phosphorylation mechanism. Their experimental data suggest that an acceptor molecule is responsible for accepting the phosphate group and then transferring it back to the activation segment.

Comments on results and experiments:

(1) Are these results an artefact of their assay? The authors mainly use immunoblotting to assess the phosphorylation status of AGC kinase. However, an assay artefact would not show a difference between control and okadaic-acid-treated cells (Figure 3A). Moreover, the authors show dephosphorylation/phosphorylation using radiolabelling (Figure 6C).

(2) Preferably, the authors would have a control to test dephosphorylation/phosphorylation does not occur in the absence of cell extract. The E. coli extract shows that dephosphorylation/phosphorylation is specific to eukaryotic cell extracts.

(3) The authors should show that dephosphorylation/phosphorylation occurs on the same residue of the activation segment (by mass spec).

(4) Since phosphorylation levels are assessed using immunoblots, the levels of dephosphorylation/phosphorylation are not quantified. What proportion of AGC kinase is phosphorylated initially (before Na/K-induced dephosphorylation)?

(5) The experiment to test autophosphorylation (Figure 4, Figure supplement 1B) is not completely convincing because the authors use a cell line with a PKN1 mutant knock-in. Possibly PKN2 or another AGC kinase could phosphorylate the proteins expressed from the transfection vector - although the authors do test with AGC kinase inhibitors.

(6) What are the two bands in Figure 6C (lanes 'Con' and 'diluted)? Only one band disappears with KCl. There is one band in Figure 6 Supplement 2.

In summary, the results presented in this paper are highly unusual. Generally, the manuscript is well written and the figures are clear. The authors have performed numerous experiments to understand this process. These appear robust, and most of their data lend credence to their model in Figure 6Aiii. The idea that a phosphate group can be transferred by an enzyme onto/between molecule(s) is not unprecedented, i.e., phosphoglycerate mutase catalyses 3-phosphoglycerate isomerisation through a phosphorylenzyme intermediate. It will be important to identify this transfer enzyme. One observation that does not fit easily with their model is the role of PP2A. Since protein dephosphorylation by PP2A does not involve a phosphorylenzyme intermediate, if the initial dephosphorylation reaction is catalysed by PP2A, it is very difficult to envision how the free phosphate is then used to phosphorylate the activation segment.