I was unable to re-run this file because of this assumption.

In practice, your file size is not so large that re-running the import + data preparation protocols would be time-prohibitive. For the sake of file management, if you wish to create two separate files (one for data importing/cleaning and one for analysis) then that is workable. But iteratively saving and relying upon new data sets complicates reproducibility.

A key ethical insight—hope is not escapism, but moral resistance, akin to Socratic self-knowledge in adversity.

Personally, Social media hasn't negatively affected my mental health; rather, it's time-consuming. I often find myself doom-scrolling down a rabbit hole of posts, but I must admit that I do learn a lot of information. So there are positives and negatives.

This feels parallel to a common criticism I see applied to social media and other digital platforms. The criticism is that its made for white and/or rich and/or male people. In most cases, I don't think its intentional, but it is true that the least oppressed groups get catered to the most. This is relevant here because many things passively cater toward those who are not disabled the most.

Another good example of this I like are curb buts, those dips on sidewalks that go down to the street. It's said that they were originally designed just to help those with wheelchairs navigate off and on the street and sidewalk. But, as it turns out, it helped not only people in wheelchairs, but most people in general, like parents rolling their kids in strollers, people with wheeled carts trying to transport stuff, skateboarders and roller-skates. Whether this story is true or not, it has inspired the term the curb-cut effect, where something designed to aid a disabled person also aids everyone.

Annotation (Stronger Alternative): The author says marketing is too complex for humans and that automation is the only answer. That point makes sense, but it feels a little one sided. A stronger version of this argument would mention that while automation helps with speed and data, human judgment still matters for creativity and ethics. Mixing both human and machine input would make the point more balanced and believable.

Annotation (Soundness): Most of the explanation here is accurate and well grounded in established reinforcement learning concepts. However, saying the “greedy algorithm produces reasonable results” is a bit weak and vague. It’s true only in limited situations where rewards don’t change much or exploration isn’t needed, but in most real world cases, a purely greedy approach performs poorly. The author should clarify the conditions under which the greedy algorithm is actually effective to make the statement sounder and more precise.

on work cited page ONLY add sources you cited from

every in-text-citation should have a corresponding work citied entry.

I find this very interesting because a criticism that is often levied at fairy tales is their enforcing of patriarchal values. This lesson thought by the fairy tales still in a way assumes patriarchal society but it doesn't treat finding a husband as the end goal but as something that can have it's own concerns. This isn't princess marries prince charming because he showed up. It is more like princess thinks about if prince charming is gonna murder her instead of naively following him.

This shows that fairy tales are not an a made up story but rather a reflection of reality. The term happy ending refers to the hope that people have in overcoming hardships. This shows growth from suffering rather than growth from avoiding it. Story telling makes the truth easier to except by adding imagery and magic.

Transition is hard to follow from one idea to the next. The flow of content and expressions needs to be more methodical and progressive with throughlines that bind together content, expression, or the argumentative progression of the chapter.

Consider revising the structure of this sentence to make it more economical and clearly constructed.

good question. they overlap a bit but they serve different purposes.

command = intent

event = outcome

command pattern is about explicit control of an action. you create a Command object, pass it to an executor, and call execute() when you want. you know who asked for it, when it ran, and what the outcome was. it’s about invoking behavior in a controlled and traceable way.

event-driven architecture is about reactions to things that already happened. an event is a statement of fact: “user.created”. it doesn’t command anyone to do something; it just signals that something occurred. listeners may respond or ignore it, you don’t control that directly.

so:

• use commands when you want deterministic, transactional actions with well-defined ownership and lifecycle (e.g. workflows, CQRS “write” side, retryable jobs).
• use events when you want decoupled, asynchronous fan-out or notifications (e.g. “send welcome email” after user created).

many systems use both. commands cause events. example: CreateUserCommand → executed → emits UserCreatedEvent.

Though the evolution of technologies today have obviously been heavily influenced by its origins, there is always something that needs to be new and exciting, never before seen. Could be a reach, but this could be a great example of how things that are constantly evolving were not created for certain human practices, and that our generations are now greedy, always seeking to be better and to invent more technologically advanced things (an example of this in the automobile context would be self-driving cars; just get a chauffeur at that point. Another example in the context of internet is AI - shows how lazy we are when it comes to research. Google wasn't enough, nor was ChatGPT in its original simplicity of assisting with research, AI has evolved to be so efficient, it has started to bleed into robotics.) Essentially, some things are better left simple.

This shows how different ecological interactions occur together and are influenced by climate change. It creates the idea that multiple stressors can act at the same time, demonstrating the complex effects of environmental change on species.

Summary: recent critics of capatalism argue abt the economic inequality of it and "violating basic precepts of rational justification." This is connected to surplus extraction under capitalism. It's marketed as a system of freedom and equality, but remains neither of those things though the following points:

1.) Unjust Abuse of power. 2.)Exploitation is a dividend of servitude, specifically "having to respond to the extractive ends and dispositions of the powerful." Money for example 3.) Structural Domination is a useful and coherent notion. 4.) The Capitalist has global variety. Like Colonial Imperialism, and liberal imperialism (what's happening nowadays.

I agree that implicit inputs such as location tracking raise ethical concerns, especially for people in vulnerable situations. I think this section does a great job of denoting how invisible data collection can have real life consequences. This made me acknowledge how "user input" is not always a voluntary thing... and that the design decisions regarding data collection are also decisions about safety and justice.

I really agree with the idea in this passage about affordances — it makes so much sense when thinking about how we interact with interfaces every day. The point that affordances are not just about what something can do, but whether the user recognizes what can be done, feels super relevant. It’s one thing for a button to be clickable, but it’s another for users to know it’s clickable. I also like how the passage connects affordances to signifiers, like visual or sensory cues that guide users. It reminds me of how modern apps use animations, color changes, or shadows to make buttons feel “touchable.” It’s a small detail, but it really changes how intuitive something feels.

I honestly don't even really understand why its a question of whether or not states should be banning companies from creating these apps. I understand how it could be difficult to monitor companies that are overseas. From my understanding at least I thought the US government could still ban people in the US from using these websites .

I was not expecting this at all when first reading and choosing this article. I think the worries about parents posting pictures of their children is one things but this is a whole different level of crazy. My initial reaction to hearing there are apps that can do this is who the heck is making these apps and what's wrong with them. This just adds a whole new level to the debate about posting children.

I like how this section frames prototyping as a process of decision-making rather than just building for the sake of it. I agree that choosing what to prototype depends a lot on the context of it. Time, resources, and risk are all things that need to be accounted for. This made me realize that smart prototyping is rarely just about creativity, but strategy too.

I used to think prototyping was something you had to do in every design process, but this made me realize it’s more about thinking strategically than just building for the sake of it. The idea that prototyping helps you decide what to learn instead of just testing something random really stood out to me. I also find it super useful that it points out how sometimes it’s better to just go ahead and build the final version if it saves time or effort. Not every project needs multiple rounds of prototypes — it really depends on your goals, skills, and the level of uncertainty. Overall, I think this perspective helps designers (especially students like us) use their time more wisely and make smarter decisions about when and why to prototype.

This really changed my perspective on what prototyping actually means. I have never created a prototype for something before and I honestly just thought of it as a crude version of the final product. This use of prototypes makes much more sense for the design process and the idea of prototypes teaching you about the effectiveness of your solution seems incredibly useful.

Telemedicine has the potential to improve access for populations historically excluded from high-quality healthcare, but attention must be paid to the context in which it is implemented such that it does not worsen health disparities by exacerbating inequities in access or by introducing inequities in quality.

Innovations such as telemedicine greatly improved healthcare delivery during the COVID-19 pandemic and beyond. It enabled individuals in quarantine, those living in remote areas, or those unable to physically visit their doctors to connect with healthcare providers, exchange health information, and receive treatment remotely. However, in other contexts, health inequities deepened for populations lacking the financial resources to access electronic devices or the digital literacy needed to navigate new technologies.

It really made me stop and think about what “normal vision” even means. If some women can see more colours than most people, then the typical human colour range is just one version of reality but our “normal” might actually be a limitation.

This link shows us the concepts of disabled vary across eras and cultures. For example, in the middle ages, the physical differences could be considered religious punishment. But later on, the disability turn into a more biological differences definition way. However, here is a detail, that disability is not simply a physical or cognitive difference, but more about the society defines and responds to those difference. I think it is some how correct since people are social animals, we need to be recognized by society and the collective to a great extent. Disability may initially mean that one is physically unable to participate in social activities, but when a person is completely excluded from social activities, the consequences are similar to those of disability to some extent.

I really like how this chapter explains that disability isn’t just about what someone can’t do, but about what society expects people should be able to do. It made me realize that so many “disabilities” come from poor design choices, not personal limits. For example, being short or colorblind only becomes a problem when things are built without those people in mind.

After reading this, I am curious about how the writer views these situations as a disability, while I slightly disagree. Instead of a disability, I see it as a disadvantage. Of course it's through genetics in which you may be short, or you may have long legs, but in my opinion, its a disadvantage. I mostly think of a disability as a mental or physical impairment that limits a person, yet being short isn't necessarily an impairment, but an unfortunate circumstance.

Hi, I learned EDSPE last winter quarter, and that course talked about disability people and education. Let me realized the real world problem of disability people faced, for example, their works, social identity and so on. Also disability not just refer to physical disabilities, but also includes learning disabilities, cognitive disabilities, emotional disorders, etc. We also discussed appearance anxiety. Therefore, there may be many cases of disability around us, which require us to observe carefully and then be tolerant and understanding.

We need to think critically about how that shapes our understanding of the past and other cultures.

Is Coyote is just a name or a different meaning for something. In this work, Coyote is not referred to as, "the" Coyote but instead just Coyote like it is a name. It is interesting because of the context of the story.

Why was the Bald Eagle the chief of animals? The Bald Eagle is now our countries most treasured bird. It is significant and interesting that in the Salinan Indian creation story the Bald Eagle is the chief of animals and now it is our countries bird. The Bald Eagle was chosen as our national bird in 1782 because of its symbolism of strength and freedom. It sounds like the Salinan peoples associated the Bald Eagle with the same feelings of strength and freedom that we do now.

During the Columbian Exchange in the 1490's, many new ideas and ideology were brought about by both the Native Americans and the Europeans. From both sides, some new information was integrated into old ways of thinking but some information was also disregarded because both peoples believed they were right and set in their ways. Not only new ideas were spread during the Columbian Exchange but resources as well as deadly diseases were spread.

The Cherokee tribe also thought the world was flat just like people long ago. The Cherokee people thought the earth was floating in the ocean being held up but it is interesting how they say that the sun goes down and then returns on its upper side to the starting place to start again. The Cherokee tribe had no idea that the moon and sun were two different things. Aristotle proved the earths roundness long before the Cherokee tribe but they did not have knowledge of this and believed in something else entirely.

Oh. I'll have to look into that more.

Even though life was hard, Clough signed up again. This shows he was proud to serve his country, but also maybe loyal to Britain.

Traditional theories predict that better L2 pronunciation causes L1 attrition, but this study found the opposite: bilinguals who produced nativelike L2 vowels also maintained nativelike L1 vowels.

On average, bilinguals’ English vowels were more nativelike than their Arabic ones, possibly because of English’s global status and frequent exposure through media, education, and communication.

The study also discusses how perception and production might relate, but concludes that more research, especially on vowel perception, is needed to clarify this connection.

Results showed cross-language interactions affected vowels differently: ・For /ɪ/ and /u-ʊ/, bilinguals showed deviations from monolingual norms, but the direction of change differed by group. ・The vowel /a-æ/ was produced natively in both languages, suggesting that clear perceptual distance between L1 and L2 sounds helps bilinguals maintain separate categories.

These results align with the Speech Learning Model (SLM), which states that more distinct L1-L2 sounds are easier to separate and learn accurately.

・Bilinguals differed somewhat from monolinguals, especially for /u–ʊ/, suggesting slight L1 influence but not full attrition. ・English /ʊ/ generally produced more natively than Arabic /u/. ・No effect of sound discrimination aptitude on these vowels.

F2-Bark model: ・Main effect of speaker group and significant interactions:　 　１．Speaker group × speaking condition: 　　　E–A bilinguals had higher F2-Bark than monolinguals in isolation. 　　　Monolinguals showed higher F2-Bark in sentences, but E–A bilinguals showed the opposite (lower F2-Bark).

２．Speaker group × language: ・E–A bilinguals had higher F2-Bark for Arabic /u/ than monolinguals. ・Within E–A bilinguals, Arabic /u/ had higher F2-Bark than English /ʊ/.

If I agree with this frustration it is probably because we don't have great ways of showing private-public on a spectrum. Something that is publicly available but not indexed is different from something that may be indexed, linked to, but does not appear on a recsys platform. Both are more public than a group chat, less "public" than an Instagram post.

I find it sad that it sounds like from Christophers point of view that this specific group of Native Americans were looking out for them and that they were willing to share all their findings but Christopher came looking for things that only benefit him.

This passage shows that Columbus had strict rules for trading with the Natives without permission to do so, but also that the Europeans were interested in the spices that the Natives had access too.

I think this is important to remember when using new "shiny" technologies. One that comes to mind for me is Kahoot. I have found that Kahoot is a great way to engage students in for example a review of a topic for a quiz. I use it in Astronomy, 9th grade science and other classes. I almost always use it in "classic" mode, where I have quiz questions and students compete for points. However there are other game modes where students earn more time to keep playing or possibly added features to a game by answering questions correctly. At one point there was a snowball fight version where you answered questions correctly to get more snowballs. Those other game formats seemed to capture students' interest, but not really engaging them in the actual review questions. Those were just there to help them keep playing the game. The technology needs to engage students in content to be effective.

This is another "will, not way" example. The TA says it's too hard to measure noise. But the author points out that they measure other things like passenger numbers all the time using the same method. They have the way, they just don't have the will.

This is the author's most important recommendation. The TA says fixing noise is too expensive. The author argues that this is wrong. She says that fixing noise like welding the rails is just good maintenance, and good maintenance saves the city money in the long run.

I think Sarah Knight’s diary was originally created for a private setting. However, I think her descriptive storytelling suggests she may have expected a small audience, such as close friends or family, to read it eventually. She includes a small but vivid interaction and details that turn a normal travel log into engaging storytelling, which makes me think she was aware of writing for an audience.

Sarah Knight's comment shows slavery's presence in the northern colonies. Although slavery is often associated with the South, enslaved labor was common in New England, Massachusetts, and Connecticut households and farms during the early 1700s. Sarah Knight criticizes how farmers and their slaves would eat at the same table and eat the same food. Her disapproval of farmers being "too indulgent" with the enslaved people reflects her beliefs in racial hierarchies. It also shows how normalized slavery was in everyday colonial life.

This sentence shows the British failed to stop the protest. It could mean they underestimated the colonists or feared escalating violence. Their silence allowed the Tea Party to succeed. This inaction might have boosted colonial confidence. If any British soldiers had fought back, I personally think that they would be met with a large group of colonists to fight back. Even if British Soldiers had weapons ready, it would have become another major massacre in history between the colonists and the Brits.

This proves they had a clear goal, destroy the tea only. They respected the ships and tried not to cause unnecessary harm. That detail shows they wanted their protest to stay controlled. It implies they hoped to maintain credibility. Tea was significant because it is very popular in Britain, and also one of the higher taxed items. By destroying the tea, it implied that Britain was no longer seen as a rule or threat among the colonists, and that they did not want to be bound by authorization from across the ocean.

This tells us that the situation in Boston was heavily controlled by the British military. The colonists were not acting in a calm and peaceful setting but under watch and intimidation. It shows the larger conflict growing between Britain and the colonies. There were many significant parts to the American revolutions but the Boston Tea Party specifically shows the loyalty and bravery the colonists had to protect their new country, this is significant because it also shows that they were willing to go to war over the new found country and sets up for more events to come.

This shows they used disguises to hide identities. It also reflects the symbolism of breaking away from British rules by taking on a different identity. The disguise protected them from punishment. It emphasizes how dangerous the protest was. This not only created confusion for British soldiers, but also shielded them from public punishment and exiling. Thsi ensured that the same people were involved in over throwing British rule.

This sentence shows how the crowd saw resistance as patriotic. They weren’t acting for personal gain, but for what they believed was right. That sense of duty helped drive the protest. It shows how unity and passion were growing among colonists. Many people back then especially those of the American working class (sewing, fresh produce, black smith, any jobs back then) were highly upset by the taxation, and because of this, unified them together to fight back against the British army

why were neither systems practiced.

The story ends with a traditional oral formula affirming truth while allowing mythic interpretation. It suggests that the story’s purpose is not literal fact, but to teach lessons about respect for nature, balance, and community.

This is another etiological moment, explaining how fog was created. The act of blowing smoke connects spiritual practice (smoking the pipe) with the shaping of the environment, showing the interdependence of nature and spirit in Native belief systems.

The storyteller speaks directly to the audience, reflecting the interactive nature of oral storytelling. The reference to the island resting on the Great Tortoise ties this legend to the Turtle Island creation story, shared among many Native peoples. This places the Wampanoag within a broader Indigenous worldview.

Moshup’s physical traits combine human and natural elements, showing harmony with the environment. His enormous size represents strength and power, while his dark skin and gray hair connect him to both land and sea, major parts of Wampanoag life.

Purpose of this text: One of the purposes of this text is to advertise the Polar X Pro.

Accuracy of this text: This text shows a point of accuracy because it mentions where this training approach was scientifically confirmed to be true in Texas.

I had heard the term west indies before but never realized that it was used to refer to the Caribbean. This was interesting to learn.

It is surprising that Fortunato suddenly regains his awareness, but it is already too late for him to escape. Montresor’s calm reaction to his desperate struggle is unexpected and chilling.

This isn't really an ideal way to begin a paragraph, as it has vague language all throughout, and doesn't really transition well within the established line of reasoning. The use of "Anyway" implies a greater contrast between the perceived and actual conception of the authors' thesis than actually exists. Based on the readings up to this point, the reader would assume that the authors advocate for a hybrid model of moral agency owing to the unique moral agency of AI. The statement here is not exactly a contrary to that, but rather a further development and clarification if anything. This should be directly stated in the sentence here, or, alternatively, the beginning of the sentence could simply be removed outright. The rest of the sentence is still problematic. The terms of "discover" and "clarify the agency" do not offer too much insight into what the author is actually trying to convey. It echoes previous ideas, making it in some ways feel redundant, but it also doesn't exactly correlate with what the paragraph discusses later.

The introduction of Moor's model of moral agency feels fairly random; it isn't really set up prior. The topic is very much important to the section and the article as a whole, but a more smoother transition, along with more exposition, would have been preferred. The authors appear to assume that the reader already has some familiarity with the model, which, depending on their intended audience, might be warranted.

I do not fully get the purpose of this example here. It does provide an instance of a "good" XAI program which satisfies the criteria discussed, comprehensive scope and understandability. Right afterwards, however, the authors point out how this is insufficient. By itself, the example feels a bit bare. It could have been utilized to illustrate the authors' latter point, but it needs to be better transitioned. A statement emphasizing such insufficiency, or drawing attention to greater concerns in the public, would be necessary in order to properly connect this example with the rest of the paragraph.

I am unclear on which debate exactly the authors are referring to. The only debate or controversy mentioned thus far within this section was that which concerned with which model of XAI to use to best fulfill ethical goals, but it doesn't really align with the content of the statement, which is confusing in of itself. In a later paragraph, the conflict between the "correct" and "excellent" explanations is introduced, which could be what the term is referring to. If so, this section has a somewhat confused line of reasoning.

This line of reasoning is somewhat vague, as the premises do not feel as if they have been properly established prior. The statement here is effectively a summary of the authors' position on AI autonomy, so it follows that the ideas on which this statement is based upon would be found and expounded upon in preceding paragraphs. This is indeed the case, but the relationship is not as direct as I would have liked. The premises outlined here are not per se the quintessential topics of the paragraphs in this section, but they are rather scattered here and there throughout them. There isn't really a paragraph dedicated to explaining the distinction between human actions and algorithmic behavior, or on the origins of moral judgement. These ideas are definitely touched upon, but indirectly. As a result, this section and the authors' reasoning in it could be a little difficult to follow.

I find this segment to be interesting. It is a brief interlude which almost interrupts the ongoing narrative about the intelligence of AI to touch upon the possibility of strong AI. It is debatable whether there is much purpose to this segment. It is somewhat related to the preceding topics, which covered issues and controversies brought up in AI discourse, but it is not exactly pertinent. It might have been better placed near the beginning of a later paragraph which deals more specifically with strong AI. Still, it does not pose too much issue in its present state, and could be reasonably left as it is.

The diction used in this segment is somewhat vague. There is an express line of reasoning present: as AI can make decisions on its own, it possesses a unique moral agency, and for that reason moral agency for AI should be thoroughly reconsidered, especially since it is so prevalent in our lives. But the hypophora here is structured oddly. "To answer this question" is an odd beginning, especially as the following statement doesn't answer the question at all. A more fitting introduction would be something along the lines of "This invites further thought." The following transition of "that said" is similarly odd, as there isn't much direct relation between the two statements. This segment should have flowed more directly between the first and last statements, clearly the most pertinent ones here, while the middle should have been an auxiliary support to the final.

It’s interesting how he begins so calmly, just describing a painting — but there’s already something unsettling underneath. It makes me curious about what really happened to the Duchess.

I was shocked by how easily he admits giving “commands”, as if ordering his wife’s death was just another act of pride. He sounds more offended by his wife’s kindness.

The author's words appear calm, but I feel something terrible happened, like he ended his wife’s life without remorse.

Pas sûr que réexpliquer la mécanique historique de l'expansion des pêcheries du Nord global soit une super intro pour un papier.

It's almost impossible to believe how we generate those writings, but metacommentary will be long enough to describe.

im crashing out. this detail, ugh. you are just so good! so good. it's that balance of reading and imagining but also reading and remembering. like this shit actually happened. you're so good.

all of life is this big contradiction but yunho you love him you Love him!!!!!!!!!!!!!

everything hurts

a beat late but perfect anyway A BEAT LATE BUT PERFCT ANYWAY

mingudding i think i feel something in my heart

But you don't have to be. You don't have to be him anymore. It's never too late to change. It's aways the perfect time to change.

what is life but a death sentence?

"The Sound of Settling" by Death Cab for Cutie

I've got a hunger twisting my stomach into knots that my tongue has tied off, my brain's repeating if you've got an impulse let it out, but they never make it past my mouth.

he's waiting for mingi to give up on him because he sees everytime he lets himself love mingi be a giving up on himself. but yunho it's okay to let go of these rigid standards you set yourself to, to have empty hands again, because then you can hold onto him

The performance. But Yunho, every you is still you, even the one you hate being, even the one you can pretend to be. The fact you can play this role is a testament to who you are, and you are someone who would sacrifice yourself to love the boy you love

"religion as a crutch for his crippling anxiety" oh my god. you've nailed it. the yunho characterization. the complex role of religion. oversharing, but when i first started learning more about yunho i was absolutely shocked and stumped by his faith. this is the parasocialism taking over but i genuinely, genuinely would think about it, turning over the idea of god and good and faith and why in the world ateez jeong yunho held onto it so strongly. i'd say even up to two years ago i never "got" religion. i remember in high school reading a book called "the god delusion" because i was raised absolutely devoid of faith and had so much trouble Believing in myself better yet something greater than me. but, things started to make sense. i think maybe that just takes time. but i remember being in agony wondering why the hell jeong yunho, who is good in every way i understand the word, needs religion. what's so wrong with him? i would ask myself. it's one thing to be born with faith, it's another to choose to hold onto, to come back to it. i had been taking that evil and sin class as well as that diary class and was deeply contemplating the role of confession in truth and why is it worth it to even say any of this out loud. and, well, it's because you get to be yourself after. after so much repression, so much secrecy, so much hating yourself for being who you are, in the end you're going to die so you might as die Yourself. thank you for this. it's like these past few years of my life have been articulated

Yes, Mingi isn't the type to give up on you. He's Mingi after all. What does time mean in the face of... love? Well, too much. But also: nothing at all

an angel! but he's not an angel! he's just mingi....

He believes so much in him, I'm crying. Because to Yunho, that's all real.What he feels is so real to him... What he believes dictates everything about his life. He believes Mingi will go far and he believes he won't and so he think, he knows, it'll never work out. But he's wrong.

He wants to be Mingi's equal in every way, be the man he deserves, but he's Too Much. Too hungry. Too... Yunho.

You know, Yunho dehumanizes himself, seeing himself so lowly, but at the same time he dehumanizes Mingi, seeing him so highly, putting him up on that pedestal. Let him be hurt, wounded, loved by you, Yunho. He's just human, too. Doesn't he deserve to be human too?

So he can Be an asshole because he sees himself that way already, he believes. I see. But also because being an asshole requires nothing of him, no true expectation, more, it's a lacking. A void of where something else should be (obedience? kindness? consideration?) What do we call that failure? And why is it we are always trying to rise above it? Why are we born way down here, so far away

What is the world without judgment? What would we do? And does he perform in fear of judgment? Is that what it is? But from who? Mingi? Or himself. Because he hate himself for not being able to control this one thing... his want. It's proof of his undoing, his animal nature, his straying from God. God and religion being related to obedience, and Yunho not being able to tame his emotions.... making him just like the rest, meaning just like every other person. Human.

The no choice here, the fate of it all, he's doomed because he wants, he's saved because he wants I'd go as far as to say that his want is what makes him a human, it's what sets him off the path of fate. Because yes there is fate, it's that we're all going to die, but some of us still Want anyway. And I'm beginning to think that's the whole point.

But he does say them. They're engraved on the roof of his mouth

He wants so badly for that to be enough, to be able to take from Mingi what he wants and have that be what he wants, but it isn't. It isn't enough because it's all mental and not physical. Sex is so in your head, such a mental experience, while also being so purely physical. The mind makes up for what the body can't comprehend and in that gap... it's almost as if Yunho feels so much that he cannot process it as anything but something too much for him to deserve. He feels so much his mind has to call it something else entirely. Well, baby, it's love.

so interesting to see hm fluctuate between being the thing to burn and damage mingi but then mingi to be the one to melt him... these two fire signs... an aries and a leo :,)

But to Yunho, good is scaring Mingi off and sparing Yunho of ever having to face himself. Is that really good, Yunho? How could it be?

In a panel I went to once, someone said "in the pursuit of happiness, there is no justice" in regards to love and relationships. because you may Want and Want, but simply wanting isn't enough for someone to want you back or to want you in the way you want to be wanted and that isn't anyone's fault... and so there is no "fair" and there is no "justice" (i need to go dig through my notes and read more about that)

I really love how you play around with language and use words that denote something more, something filthier here. Usually it's "churning in his stomach" but the word gut here is so... animal. Like an animal that's already dead, guts out on the floor. Churning in his gut, oh it makes me shiver. Churning where he's most animal, the messy intestines that are of no use anymore...

it is not con-sensus but

con - fluence - vergence

towards a fixed point, where no further improvements are needed

rejection of comform(ance)

seeking novelty not for its own sake

bur for expanding potential

I think she is optimistic that she would find happiness as her father had in the colonies!!

I am completely new to education and these concepts. This is a great explanation of a term that I have heard before, but have not necessarily had an adequate breakdown of. After reading the description I have come to realize that this is one thing my family practiced when teaching new life skills. I like having this segment to refer back to.

The Assembly-Line Instruction has been horrible for students and teachers alike. I have always learned more in the "non-traditional" ways of learning and encourage “non-traditional” learning in my classrooms. As a special education teacher and foods teacher I want my students to be successful in life not just school so I teach mostly by using activity based learning and I always remind kids it is ok for our project or food not to turn out ok because we will learn from it as long as we are putting forth an earnest effort.

in a gradual, subtle way, but with harmful effects.

For this explanation would there be core skills that every person in childhood possesses and any specific skill learned would be a branch off of this main skill? For example, motor skill is a core skill and a specific skill learned later in life if dribbling for soccer. In order to be able to dribble you need to first develop your motor skills, meaning dribbling is a more advanced motor skill.

I used to think that the job of college advisors was only to help with class schedules, but now I see that they also give emotional support and guidance when students face problems. It’s interesting to know that building a relationship with an advisor can really make a big difference in college life.

When we take care of ourselves, we have more energy and positivity to share with others. It made me realize that loving yourself is the first step to loving others. I used to think taking care of myself was less important than caring for others, but now I see how closely they are connected.

In this page, it shows us in the facebook's privacy setting, it allows users to find their facebook accounts by using their phone number, but even if user want to close that feature other people can still use their phone number to find their facebook accounts. One detail is facebook said they did not find evidence of abuse for the find feature. So I think for the large platform of such bid companies, they have to protect user's privacy, since their consumer base is really large. They have the responsibility to do that.

This creates a problem worth investigating.

because the collision is assumed to be perfectly "Elastic", which is not real but only assumed for the Ideal Gases In Real life the molecules loses very small amount of energy.

lol what if they think they know sm ab finance that they can take on these decisions. but borrowing money from friends is not an outcome that should come out of this. also if goal is to introduce saving and budgeting practice then outcome shouldnt bhi ki ye nai cheez ke bare me pata chala so chalo ab kartein hein

but that means ur study failed if its main goal was savings and budgeting

but these results are a smaller section of the sample anyway. plus recheck if 1/2 of treatment (finance) is compared to whole control (health)

good so that teachers can discuss what the others said/discussed, but again teachers may be lying

I wonder how this contrasts, historically, with vegetarians in India…

I feel like this is a situational friend, like if you go to class with someone and you go to study group for that class, but after the class ends we part ways.

creating a boundary is good, but not always, it can mean that someone has recognized something they are uncomfortable with about their situation, and want to create space but aren't sure how, which could also relate to avoiding.

A lot of the time, or maybe just with me, I can see myself rushing into this stage to get to the integrating stage, but usually it's because i'm so excited to be around the person and to have a 'someone.' which reminds me of how a happy dog is so excited for you to be homme they run up to you and jump on you at the door, and you're so overwhelmed you push them away.

I just learned about The Ba'ba. It is called "The Holiest of Holies." It was built during the Old Testament times when God told them exactly how to build it. They have had to rebuild it, but it has real gold, and the doors (covered in the cloth) are pure gold.

Random thought but I feel like there are many emperors in China that rule for very long periods of time.

On the Similarities Between the SGI Doctrinal Text and Professor Miyata’s Paper

Issue 1.

Lately, on social media, there have been discussions suggesting that The Book on the Doctrinal Foundation of the SGI, published immediately after President Daisaku Ikeda’s passing, closely resembles several papers written by Professor Koichi Miyata. I also share this impression.

Mr. Suda, former Vice Leader of the SGI Study Department, makes the following claim in his Letter to President Harada regarding the “Teaching Outline”: “I have heard that the main individuals behind the creation of the Teaching Outline were Mr. Miyata and Mr. Kanno, both professors emeritus at Soka University. From their standpoint as researchers, however, they have shown a marked tendency to defer to the Minobu sect of Nichiren Buddhism, which represents the mainstream of academic Nichiren studies, seemingly out of fear of criticism from that sect. As a result, the entire Teaching Outline can be seen as having been assimilated to the doctrines of the Minobu sect.” On the other hand, the SGI Men’s Division Doctrinal Office officially denied any involvement of Professors Miyata and Kanno, stating on the Seikyo Shimbun website that “this claim is factually incorrect, and neither Professor Miyata nor Professor Kanno were members of the publication committee.” (Reference: Seikyo Online) In response, I conducted a careful comparative analysis of The Book on the Doctrinal Foundation of the SGI and Professor Miyata’s papers, employing not only a close textual reading but also the analytical functions of a natural language processing AI (ChatGPT) to ensure objectivity. The results revealed a level of similarity far beyond my expectations—one that can hardly be overlooked.

SGI is a large religious organization with approximately twelve million members in Japan and around the world, and The Book on the Doctrinal Foundation of the SGI appears to have become the organization’s core doctrinal text following President Ikeda’s passing. In this regard, Suda, in his Letter to President Harada regarding the “Teaching Outline”, points out that “Even now, it seems that the ‘Teaching Outline’ is being followed in articles in the Soka Shimpo and Seikyo Shimbun newspapers, as well as in the commentary on The Object of Devotion for Observing the Mind, and I think that this is a dangerous situation.” Therefore, this issue is of considerable importance for the future of the SGI’s doctrinal study.

At the same time, it should be emphasized that the purpose of this paper is not to criticize any individual personally, but rather to ensure the accuracy and scholarly transparency of doctrinal materials.To maintain the credibility of SGI’s doctrinal studies, it is increasingly necessary to clarify bibliographical sources and secure philosophical consistency in future publications.

Professor Koichi Miyata, “The Structure and Issues of Udana Nichiko’s Honzon Ryakuben” (2017–2018, pp. 38–39)

“The passage ‘The doctrine of three thousand realms in a single moment of life is found in only one place, hidden in the depths of the “Life Span” chapter of the essential teaching of the Lotus Sutra’ (WND I: 30) can be interpreted, from the overall context, to mean that the doctrine of the true “three thousand realms in a single moment of life” is hidden in the text of the “Life Span” chapter—that is, in the passage revealing enlightenment countless kalpas ago.” The Book on the Doctrinal Foundation of the SGI (Kyōgaku Yōkō, 2023, p. 70) “The great sage Nichiren states in The Opening of the Eyes, ‘The doctrine of three thousand realms in a single moment of life is found in only one place, hidden in the depths of the “Life Span” chapter of the essential teaching of the Lotus Sutra’ (WND I: 30). He perceived that, at the very depths of the chapter The Life Span of the Thus Come One, which expounds enlightenment countless kalpas ago, the essential doctrine of three thousand realms in a single moment of life in the Lotus Sutra is revealed.” Commentary The Book on the Doctrinal Foundation of the SGI makes no reference to Miyata’s paper. Yet both the book and Miyata’s interpretation share a distinctive view: that the passage describing “enlightenment countless kalpas ago” conceals the doctrine of three thousand realms in a single moment of life. In the Book on the Doctrinal Foundation of the SGI, this interpretation is presented as if it were Nichiren’s own insight, raising serious concerns regarding the proper attribution of scholarly authority. In this respect, the book may be seen as raising a significant issue of academic integrity. Incidentally, the traditional SGI interpretation—found in the third President Daisaku Ikeda’s works such as The Lecture on the Orally Transmitted Teachings II (pp. 32–33)—is that this doctrine is concealed in the passage “Originally I practiced the bodhisattva way” (Burton Watson, The Lotus Sutra, p. 268) in the Life Span chapter. From this perspective, The Book on the Doctrinal Foundation represents a problematic departure from that established tradition.

In this respect, Suda, former Vice Leader of the SGI Study Department (2024, p. 53), criticizes this book, stating that “Although The Book on the Doctrinal Foundation was published immediately after Ikeda’s passing and claims to have been supervised by him, its content significantly deviates from Ikeda’s ideological framework during his lifetime. Thus, the assertion that the book was under Ikeda’s supervision can be seen as an attempt to misuse his name rather than a genuine reflection of his doctrinal stance.”

Furthermore, in his paper, Professor Miyata rejects the traditional interpretation that locates the doctrine in the passage “Originally I practiced the bodhisattva way” (Burton Watson, The Lotus Sutra, p. 268) and offers his own alternative view. The following section examines the possibility that this reinterpretation found its way into The Book on the Doctrinal Foundation of the SGI.

Reference

Ikeda, D. (1968) Gogikuden Kōgi [Lecture on the Oral Transmission of the Teachings, vol. 2]. Tokyo: Soka Gakkai.

Miyata, K. (2017–2018). The Structure and Issues of Udana Nichiko’s Honzon Ryakuben. Available at: http://hw001.spaaqs.ne.jp/miya33x/honzonryakuben.pdf [Accessed 24 October 2025].

Nakamura, M. (2025) Kyôgaku Yōkō to Moto Sōka Daigaku Kyōju no Ronbun no Hikaku Kensō [A Comparative Examination of the Book on the Doctrinal Foundation of SGI and Papers by Former Soka University Professors]. Available at: https://jikatsu.net/wp-content/uploads/2025/10/4f92b9e0e1e7f83a456ee2c6d262748b.pdf [Accessed 24 October 2025].

Soka Gakkai. (1999). The Writing of Nichiren Daishonin. Tokyo: Soka Gakkai.

Soka Gakkai (2023) Kyōgaku Yōkō [The Book on the Doctrinal Foundation of SGI]. Tokyo: Soka Gakkai. Available at: https://www.amazon.co.jp/dp/4412017028 (Accessed: 24 October 2025).

SGI Study Department (2024). “The Teaching Outline” is the Culmination of the Soka Renaissance. Available at: https://www.seikyoonline.com/article/603E8EF7E9B96D20AF2920005F5C1C6B [Accessed 10 October 2025].

Suda, H. (2024). Letter to President Harada regarding the “Teaching Outline”, 12 September 2024. file_20240930-185744.pdf [Accessed 24 October 2025].

Suda, H. (2024). A Critique of the Book on Doctrinal Foundation of Soka Gakkai from the Perspective of Buddhist History: In Light of Nichiren Buddhism as the Global Religion Taught by SGI President Daisaku Ikeda. Available at: https://jikatsu.net/download/1st-english-edition-a-critique-of-the-book-on-doctrinal-foundation-of-soka-gakkai-from-the-perspective-of-buddhist-history/

Watson, B. (1993). The Lotus Sutra. New York: Columbia University Press.

• Running can counteract some negative effects of an unhealthy, Western-style diet, according to researchers from University College Cork.
• The study found that exercise restores key metabolites linked to mental well-being and balances crucial hormones disrupted by a diet high in sugar, fat, and processed foods.
• Rats fed high-calorie “cafeteria diet” foods showed major disturbances in gut metabolism, with 100 out of 175 metabolites significantly altered; running partially restored balance, especially for anserine, indole-3-carboxylate, and deoxyinosine.
• Physically active rats on the same poor diet had normalized levels of insulin and leptin compared to sedentary ones, showing exercise helps regulate hormonal balance.
• The body activated compensatory hormonal mechanisms, such as changes in GLP-1 and PYY levels, to stabilize metabolism under poor dietary conditions.
• The study also linked exercise to improved neurogenesis (formation of new neurons) in the hippocampus, but only when paired with a healthy diet—junk food appeared to suppress this regenerative effect.
• Despite running’s benefits, researchers emphasized that good nutrition remains essential for full brain health and mental performance.
• The findings offer insight into how exercise may protect mental well-being even amid widespread consumption of processed foods.

What kinds of sources, from which perspective, you need.

These AI tools are difficult to learn with a steep learning curve, but the efficiency boost outweighs this.

This chapter does not mention energy use or environmental impact at all.

How do we identify the folks who are just faking it until the make it with synthetic knowledge.

Pre-emptive note: it seems logical that the very next paragraph references Paul Graham directly; my very next move was going to be to connect the writer's self-reported experiences here with Graham on writing, had it not been the case that that job was already done.

As I've said before: I'm not in the same boat with Graham on the writing-is-thinking stance. The difficulty with seeing my own thoughts fixed in words after an initial pass is not in their inadequacy or their being a source of illusory and fleeting comfort with said illusion now made stark for everyone to see, but a mixture of (a) a lack of "punch", and/or (b) the places where a dishonest broker could exploit the yet-to-be shored up wording to suggest/assert the presence of some weakness in thought regarding the thing being argued for, where such purported weakness would be the real illusion.

The lack of satisfaction I feel when trying to capture my thoughts in English (my first language) isn't too far off from the lack of satisfaction at being able to comprehensively express a simple declarative in another language only because of the fact that don't know, say, the right word for the noun in that language. It doesn't lead me to agonize about how well-supported my observations about a backhoe are just because I've never been introduced to the word for backhoe in that language.

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

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Manuscript number: RC-2025-03130

Corresponding author(s): Ellie S. Heckscher

[The "revision plan" should delineate the revisions that authors intend to carry out in response to the points raised by the referees. It also provides the authors with the opportunity to explain their view of the paper and of the referee reports.

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1. General Statements [optional]

We thank all three reviewers for their feedback on the paper. Reviewers stated that the paper was of broad interest to developmental biologists and neurobiologists. However, we want to ensure that our two key conceptual contributions are clear. We clarify in the following paragraph and include a revised abstract. We will update the introduction and paper to better reflect these advances. We also attach a supplemental table 1, which was inadvertently omitted from the previous submission due to our error.

The first advance is that serially homologous neuroblasts follow a multimodal production model: In principle, stem cells can divide any number of times, from once to throughout the entire lifetime of the animal. And, on each division, a stem cell can generate either a proliferative daughter cell or a post-mitotic neuron. Together, therefore, there is a vast potential number of neurons any given stem cell could produce. From the literature on the vertebrate neocortex, we had the following models: (1) "random production" model, in which any number of neurons could be made by a stem cell; or (2) "unitary production" model, in which the same number of neurons (~eight) is produced by a stem cell regardless of context. Our data revealed an entirely new "multi-modal production" model, which could not have been predicted by prior literature. In the context of serially homologous neuroblasts arrayed along the Drosophila larval body axis, sets of five to seven neurons are produced in increments of one, two, or four. These increments correspond to units called temporal cohorts. Temporal cohorts are lineage fragments, or small set of neurons that share synaptic partners, making them lineage-based units of circuit assembly. Thus, in a multimodal production model, serially homologous stem cells produce different numbers of temporal cohorts depending on location. Our data advance the field by showing that stem cells produce circuit-relevant sets of neurons by adding or omitting temporal cohorts from a region, to meet regional needs.

Key to understanding the second advance is that there are multiple types of temporal cohorts: early-born Notch OFF, early-born Notch ON, late-born Notch OFF, and late-born Notch ON. One temporal cohort type, the early-born Notch OFF, is found in every segment, which we term the "ubiquitous" temporal cohort. The other temporal cohort types can be produced in various combinations depending on the stem cell division pattern and segmental location. In a result that could not have been predicted, we found that the ubiquitous temporal cohorts are refined both in terms of the number of neurons and their connectivity, depending on body region. In contrast, when other temporal cohort types are produced, they are not refined to the same degree.

The impact of this work is to advance how we think about stem cell-based circuit assembly.

2. Description of the planned revisions

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

*Summary: The study by Vasudevan et al intends to address how serially homologous neural progenitors generate different numbers and types of neurons depending on their location along the body axis. *

Investigation of full repertoire of neurogenesis for these progenitors necessitates a precise ability to track the fates of both progenitors and their neuronal progeny making it extremely difficult in vertebrate paradigm. The authors used NB3-3 in the developing fly embryo as a model to investigate the full extent of the flexibility in neurogenesis from a single type of serially homologous stem cell. Previous work showed NB3-3 generates neurons including lateral interneurons that can be positively labeled by Even-skipped, but detailed characterization of the NB3-3 lineage mainly focused on 3 segments during embryogenesis. The authors defined the number of EL neurons in all segments of the central nervous system in early larvae after the completion of circuit formation and carried out clonal analyses to determine the proliferation pattern of NB3-3. They described the failure to express Eve in Notch OFF/B neurons as a new mechanism for controlling the number of EL neurons and PCD limits EL neurons in terminal segments.

• *Thank you! In addition to the contributions highlighted by the reviewer, we also showed that all segments have ELs with early-born molecular identities, but only a subset have ELs with late-born identities (Figure 5). And we showed that early-born temporal cohorts can be mapped into different circuits depending on the axial region (Figure 6).

*Major comments: The authors performed careful analyses of the NB3-3 lineage using EL neurons. My main concerns are limited applicability of their findings and lack of mechanisms as how NB3-3 generate various numbers of EL neurons. Their findings are exclusively relevant to the NB3-3 lineage despite their effort in highlighting that other NB lineages also generate temporal cohorts of EL neurons. *

  Thank you for raising these points. First, to clarify, as Reviewer 4 also mentioned, NB3-3 is the only lineage to produce EL neurons. We will ensure that this is clearly stated in the revised text.

We agree that our findings might not apply beyond the NB3-3 lineage. However, as this is the first study of its kind, it is impossible to know a priori to what extent the concepts surfaced here are generalizable. In our opinion, this speaks to the novelty and impact of the study. A contribution is to motivate a need for future studies. We will make this explicit in our updated manuscript in the Discussion section.

  Our manuscript provides cell biological mechanisms that explain how stem cells give rise to different numbers of EL neurons in different regions, including stem cell division duration and type, neural cell death, identity gene expression, and differentiation state. If the reviewer is interested in genetic or molecular mechanisms, this is an interesting point. Several prior studies using NB3-3 as a model (e.g., Tsuji et al., 2008, Birkholz et al., 2013, Baumgardt et al., 2014) have elucidated the genetic regulation of specific cell biological processes. However, these studies provided fragmentary insight with regard to serially homologous stem cell development along the body axis. A comprehensive understanding of how the NB3-3 lineage, or any other serially homologous lineage, develops was missing. This is what makes our study both novel and needed. Without an analysis that both examines every segment and assays multiple cell biological processes, we would have missed key insights: that there is a ubiquitous type of temporal cohort, and that neurons within the ubiquitous temporal cohort are selectively refined post-mitotically (See General Statements for more details).

*I disagreed with their conclusion that failure to express Eve as a mechanism for controlling EL neuron numbers when Eve serves as the marker for these neurons. Are there any other strategy to assess the fates and functions of these cells beside relying solely on Eve expression? I am not familiar with the significance of Eve expression on the functions of these neurons. Is it possible to perform clonal analyses of NB3-3 mutant for Eve and see if these neurons adopt different functionalities/identities? *

• We agree that if Eve were only a marker, our logic would be circular. The Eve homolog, Evx1/2 is crucial for vertebrate interneuron cell fate (Moran-Rivard et al., 2001). Eve is essential for motor neuron morphology in Drosophila *(Fujioka et al., 2003). Eve is critical in Even-skipped for both the morphology and function of Even-skipped interneurons (Marshall et al., 2022). Hence, ELs cannot fully differentiate or incorporate into circuits without Eve. Thus, we use the failure to express Eve as a mechanism for controlling EL number. Furthermore, our prior study (Wang et al., 2022) showed that NB3-3 Notch OFF neurons in A1 that fail to express Eve have small soma and "stick-like" neurite projections that are typical of undifferentiated neurons. We will be sure to add this context to the revised manuscript.

*If NB3-3 in the SEZ continually generate GMCs based on the interpretation of clonal analyses and depicted in Fig. 2A, why is the percent of clones that are 1:0 virtually at or near 100% from division 6-11 shown in 2G? *

Admittedly, the ts-MARCM heat-shock-based lineage tracing experiments are inherently messy. This is part of the reason why we included the G-TRACE lineage tracing experiments in Figure 3. In Figure 3E, one can see that the number of Notch ON/A neurons in SEZ3 is equal to the number of ELs in that segment (Figure 1E). This is a second independent method that supports the assertion that in SEZ, NB3-3 stem cells continually generate GMCs. Given this independent observation, it leads us to believe that this question is most likely explained by technical issues inherent in ts-MARCM. These issues include but are not limited to: cell-type specific accessibility/success of heat-shock induced recombination; variably effective RNAi; and idiosyncrasies of the EL-GAL4 line used to detect recombination events. If the question is why the data is only reported for division 6-11, the answer is that the ts-MARCM dataset, which included SEZ clones only used later heat-shock time points (line from the paper "for the SEZ-containing dataset, inductions started at NB3-3's 5th division"). Along with this revision plan, we will include Supplemental Table 1, which was inadvertently omitted from the previous submission due to our error. This table shows all of the clonal data. We will include a section in the discussion to describe limitations in ts-MARCM.

The authors also indicate that NB3-3 in the abdomen directly generate Notch OFF/B cells that assume EL neuronal identity. In this scenario, shouldn't the percent of 1:0 clones be 100% in later divisions in Fig. 2G? Based on the number of clones in abdomen shown in Fig. 2E, I cannot seem to understand how the authors come to the percent of 1:0 clones shown in Fig. 2G

  We agree that one might expect the 12th division to be 100% 1:0 clones in the abdomen. Unfortunately, we didn't sample that late in our dataset, and even when we sampled the inferred 11th division, we had a small sample size (Figure 2E). Other studies suggest that NB3-3 in the abdomen directly generates Notch OFF/B neurons (Baumgardt et al., 2014), which served as our starting point. We will revise the text to make this clearer. As you can see from Figure 3E, there is only one NB3-3 Notch ON/ A neuron produced in each abdominal segment in comparison to the number of NB3-3 Notch OFF/B/EL neurons (Figure 1E). According to two independent assessments, Figure 3 and Baumgardt et al., 2014, the data support the conclusion that NB3-3 in the abdomen directly generates Notch OFF/B cells that assume EL identity for all but one of their divisions. Again, we believe technical issues make the ts-MARCM dataset messy. We will include a section in the discussion to describe limitations in ts-MARCM.

*There are many potentially interesting questions related to this study that can significantly broaden the impact of this study. For example, are other NB lineages that also generate distinct temporal cohorts of EL neurons display similar proliferation patterns (type 1 division in SEZ, early termination of cell division in thoracic segments and type 0 division in abdomen)? *

• *NB3-3 is the only lineage that makes ELs; Many lineages switch proliferation fates along the body axis. Previous studies have described how this switch in division patterns produces the wedge-shaped CNS: Cobeta et al., 2017. In the revision, we will be sure to clarify both points.

*Why does NB3-3 in the thoracic segment become quiescence so much sooner than SEZ and abdominal segments? *

• *NB3-3 in the thorax enters quiescence due to Hox genes and temporal transcription factors (Tsuji et al., 2008). In the revision, we will be sure to clarify this point.

The authors' observations suggest that NB3-3 in SEZ and abdomen generate a similar number of EL neurons despite the difference in their division patterns (type 1 vs type 0). Are the mechanisms that promote EL neuron generate in NB3-3 in SEZ and abdomen the same? Anything else is known beside Notch OFF?

• We agree this is an interesting point. Previous work has detailed NB3-3 division patterns, showing Type 1 divisions in the thorax, and Type 1 to Type 0 switch in the abdomen (Baumgardt et al., 2014). However, the proliferation pattern of NB3-3 in the SEZ had not been addressed until our study. Figures 2 and 3 suggest the following (1) SEZ proliferates for the duration of embryonic neurogenesis; (2) It produces a GMC on each division; (3) the GMC divides to produce one EL Notch OFF neuron and one Notch ON neuron. In our revision, we will manipulate the Notch pathway using two mutants, sanpodo, which produces two Notch OFF cells, and numb*, which produces two Notch ON cells (Skeath et al., 1998), to specifically test how ELs in the SEZ are regulated by Notch signaling. The other difference we know of between the SEZ, and abdomen is Hox gene expression. In Figure S2, we show that a subset of ELs in the SEZ express the anterior Hox genes, Sex combs reduced (Scr). The role of Hox genes in this lineage is an interesting question, as addressed in the discussion. This is an important future direction that merits in-depth study and is beyond the scope of what of this study is trying to accomplish.

Minor commentsThe authors' writing style is highly unusual especially in the result section. There is an overwhelming large amount of background information in the result section but very thin description on their observations. The background information portion also includes previously published observations. Since the nature of this study is not hypothesis-driven, it is very confusing to read in many places and difficult to distinguish their original observations from previously published results and making. One easily achievable improvement is to insert relevant figure numbers into the text more often.

Thank you for this comment. It is invaluable. In the revision, we will expand the background into a more comprehensive introduction and present the results more clearly. We will certainly insert relevant figure numbers. In responding to the reviewer's comments above, we can see where our writing lacked clarity and will improve these areas. Thank you again.

Reviewer #1 (Significance (Required)):

The study by Vasudevan et al intends to address how serially homologous neural progenitors generate different numbers and types of neurons depending on their location along the body axis. Investigation of full repertoire of neurogenesis for these progenitors necessitates a precise ability to track the fates of both progenitors and their neuronal progeny making it extremely difficult in vertebrate paradigm. The authors used NB3-3 in the developing fly embryo as a model to investigate the full extent of the flexibility in neurogenesis from a single type of serially homologous stem cell. Previous work showed NB3-3 generates neurons including lateral interneurons that can be positively labeled by Even-skipped, but detailed characterization of the NB3-3 lineage mainly focused on 3 segments during embryogenesis. The authors defined the number of EL neurons in all segments of the central nervous system in early larvae after the completion of circuit formation and carried out clonal analyses to determine the proliferation pattern of NB3-3. They described the failure to express Eve in Notch OFF/B neurons as a new mechanism for controlling the number of EL neurons and PCD limits EL neurons in terminal segments.

Because this text is the same as the summary, please see our response to that section.

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

In this manuscript, Vasudevan et al provide a detailed characterisation of the different numbers and temporal birthdates of Even-skipped Lateral (EL) neurons produced at in different segments from the same neuroblast, NB3-3. The work highlights the differences in EL neuronal generation across segments is achieved through a combination of different division patterns, failure to upregulate EL marker Eve and segment-specific program cell death. For neurons born within the same window and segment, the authors describe additional heterogeneity in their circuit formation. The work underscores the large diversity that the same neuroblast can generate across segments.

Thank you!

Major comments:

- Based on the ts-MARCM 1:0 clones representing 100% of the SEZ clones at any given inferred cell division, the authors conclude "NB3-3 neuroblasts generate proliferative daughter GMCs in the SEZ and thorax on most divisions". Figure 2G does not have any data for SEZ before inferred division 5, whereas there is data in other regions. The authors also state "In the SEZ and abdomen, ELs were labelled regardless of induction time." In reference to Fig 2F, which seems inaccurate given there are no SEZ clones before inferred division 5. There is no comment on this fact, which is surprising give their focus on temporal cohorts. The authors should explain this discrepancy, if known, or modify their statements to reflect the data.

• *Thank you for raising this point. The reason is because we produced two ts-MARCM datasets. One had SEZ clones, the other did not. The dataset with SEZ clones used heat shock protocols only for later time points, because those were most informative. The text from the paper is "We combined a published ts-MARCM (Wang et al., 2022) dataset with a new one (Table S1). The differences between the datasets are (1) CNSs were imaged either at low resolution for all regions (SEZ to terminus) or higher resolution for nerve cords (thorax to terminus); (2) for the SEZ-containing dataset, inductions started at NB3-3's 5th division. The combined data includes ~12 different heat shock protocols, 80 CNS, and 234 clones (Table S2)". In response to this comment, however, we will further clarify this point. In addition, we are submitting Supplemental table 1, which contains all the clonal data, as you can see experiments a-h lack SEZ data and experiments i-k contain SEZ data.

- The temporal cohort (early-born vs late-born) identity is exclusively examined based on markers. Given the absence of SEZ clones from early NB3-3 divisions, a time course showing that the SEZ generate early-born Els or some other complementary method would be desirable.

Thank you for raising this point. We show early-born versus late-born identity using markers in Figure 5. We conducted the time-course experiment as suggested and can confirm that there are early-born ELs in the SEZ at stage 13. We will include a new Supplemental Figure that includes a time course of EL number at stages 11, 13, 15, and 17 for segments SEZ3 to Te2 in the revision. See figure below.

- The authors repeatedly refer to their work as showing how a stem cell type can have "flexibility". Flexibility would imply that NB3-3 from one segment could adopt a different behaviour (different division pattern, or cell death or connectivity) if it were placed in a different segment. This is not what is being shown. In my opinion, "heterogeneity" of the same neuroblast across different segments would be more appropriate.

• *Thank you for this comment. We will change the wording to heterogeneity in the revision.

Minor comments:

- Figure 2A depicts a combination of known data and conclusions from their own (mainly SEZ). The authors might consider editing the figure to highlight what is new. A possibility would be for figure A to be a diagram of the experimental design and their summary division pattern to be shown after the new data instead of being panel A.

Thank you for this suggestion. We will make the suggested change.

- The authors state that they combined published ts-MARCM with their new one, which differed in a number ways that they list, but they don't specify which limitations are associated with the published vs new dataset. Could the authors please clarify?

  We now include Supplemental Table 1, which shows the complete combined datasets. In the first dataset, experiments a-h, the CNS was imaged at high resolution, but in a smaller region. The limitation is that the SEZ is missing. In the second dataset, i-k, inductions started at NB3-3's 5th division. The limitation is that we fail to sample early time points. This was a strategic decision. There were two possible scenarios: (1) in the SEZ, NB3-3 divided early, made GMCs, but both daughters expressed Eve. (2) in the SEZ, NB3-3 divided for the entirety of the embryonic neurogenesis, making GMCs, with only the Notch OFF daughters expressing Eve-our data support (2). Only late heat shocks were needed to distinguish between these possibilities. As these experiments are labor-intensive, we focused our efforts on the later time points. We will make this clearer in our revised text.

- The title refers exclusively to "temporal cohorts", which in the manuscript are defined quite narrowly and do not seem to apply to all segments.

• *Thank you! This, in our opinion, is a central, not a minor point to raise, because the impact of this study involves temporal cohort biology. We outlined the essential concepts in Part 1 "general statements" section of this revision plan. We did not mean to use "temporal cohort" in a limited sense, and we can see how the writing of our results section led to this comment. We will revise to make this clear.

- Several cited references are missing from the Reference list at the end. Could the authors please double check this? (e.g. Matsushita, 1997; Sweeney et al., 2018)

• *Thank you, we will remedy this!

- Legend for figure 2 is a bit confusing, there is a "(A)" within the legend for (D), which indicates that segments A1-A7 are shown (this seems inaccurate, as it only goes to A6).

Thank you, we will remedy this!

Reviewer #3 (Significance (Required)):

This study provides a comprehensive analysis of different cell biological scenarios for a neuroblast to generate distinct progeny across repeating axial units. The strength is the detailed and systematic approach across segments and possible scenarios: different division patterns, cell death, molecular marker expression. While it focuses on one specific neuroblast of the ventral nerve cord of Drosophila, the authors have done extensive work to place their findings and interpretation in the context of other cell types and across model organisms both in the introduction and discussion. This makes the work of interest for developmental biologists in general, neurodevelopment research in particular and those interested in circuit assembly, beyond their specialised community. This point of view comes from someone working in vertebrate CNS development.

Thank you!

Reviewer #4 (Evidence, reproducibility and clarity (Required)):

Summary

This manuscript addresses the question of how the number of neurons produced by each progenitor in the nervous system is determined. To address this question the authors use the Drosophila embryo model. They focus on a single type of neural stem cell (neuroblast), with homologues in each hemisegment along the anterior-posterior axis.

Using a combination of clonal labelling, antibody stainings, and blockade of programmed cell death, they provide a detailed description of segment-specific differences in the proliferation patterns of these neuroblasts, as well as in the fate and survival of their neuronal progeny.

Furthermore, by employing trans-synaptic labelling, they demonstrate that neurons derived from the same progenitor type receive distinct patterns of synaptic input depending on their segmental origin, in part due to their temporal window origin.

Overall this work shows that different mechanisms contribute to the final number and identity of the neuronal progeny arising from a single progenitor, even within homologous progenitors along the anterior posterior body axis.

Thank you!

Major Comments

I would suggest adding line numbers to the text for future submissions, this massively helps providing comments.

  Thank you for this comment. We will definitely add line numbers to the revised manuscript. We also thank you for providing comments despite this oversight on our part. We appreciate your time, and did not mean to make extra work.

*The authors propose that all neuroblasts produce the same type of temporal cohort (early born) and that, by changing the pattern of cell division, different temporal cohorts can be added. The way this this presented in the abstract sounds like an obvious thing, what would be the alternative scenario/s? *

  Thank you for raising the point that the abstract should be updated. We have included a revised abstract. The things that are obvious are: (1) changing a neuroblast's division pattern will change the number of neurons produced, and (2) if you have late-born neurons, the stem cell must at some point, have made early-born neurons. However, within those bounds is an extremely large parameter space. Each stem cell can choose to divide or not, and it can also choose to produce a proliferative daughter or not. The stem cell must navigate these choices at every division. The field had two models for what a stem cell might do - a "random production" model and a "unitary production" model. Our data support a third "multimodal production" model, which could not have been predicted based on prior literature or data.

We had raised these points in the discussion as follows-

"Under a null model, the durations and types of proliferation would vary stochastically across segments, resulting in a continuous and unstructured distribution of neuron numbers (Llorca et al., 2019). In a unitary production model, based on the vertebrate neocortex, there is a fixed neurogenic output of ~8-9 neurons per progenitor (Gao et al., 2014). However, our data support a third model, a multimodal production model. In a multimodal model, serially homologous neuroblasts generate different numbers of neurons depending on the segment."

We will now update the text to address this concern.

Here it's the late born neurons that lack in thoracic segments because of early NB quiescence, but it cannot be excluded that different neuroblast types adopt a different strategy.

• *True. Neural development is complex. Other lineages could easily employ alternative strategies. Our study presents a new conceptual framework that should inspire future research.

I found the ts-MARCM results confusing for 2 reasons:

1- It's not clear to me why there are so many single cell clones in div 3 and 4 in abdominal segments. This is not compatible with the division model depicted for abdominal segments, unless GMCs are produced in those division window and the MARCM hits the GMC, as also mentioned in the legend for G. This aspect is important because, either the previous model by Baumgardt et al. - please correct cit. currently Gunnar et al. 2026 - is wrong, or something strange happens in this experiment, or the relative temporal order is incorrect.

Thank you for raising this point. Having multiple single-cell (i.e., 1:0) clones in divisions 3 and 4 is not precisely what would be predicted by the model in Figure 2C. In part because heat-shock-based recombination methods in fly are stochastic and inherently "messy", we also conducted a second set of lineage tracing experiments, as shown in Figure 3, using G-TRACE. Figure 3E shows one Notch ON/A neuron in each abdominal segment, suggesting there is only one GMC present during lineage progression. But Figure 3E's result does not localize the GMC to any particular division. One possibility is that the GMC is generated once, but randomly throughout lineage progression. This possibility is consistent with the idea that the relative temporal order is incorrect and suggests that Baumgardt is erroneous. However, the Baumgardt data are strong, so we do not favor this idea. A second possibility, which we favor, is that something strange happened in this experiment. Here is how we envision the strange occurrence: heterogeneity in the EL driver. Ts-MARCM's recombination timing dictates the upper limit for the number of cells within a clone. However, recombination is detected by GAL4. So, if the GAL4 driver for some reason detects fewer cells than one expects, then one would see unusually small clones as is the case in question. To detect Ts-MARCM recombination in Figure 2, we used the EL-GAL4 driver. The EL-GAL4 driver is an enhancer fragment, ~400KB, meaning that it does not capture the full regulatory context of the eve locus. In our experience (e.g., Manning et al., 2012), drivers using small enhancers tend to give highly-specific, but somewhat variable expression, and this is the case for EL-GAL4 in our experience. We will update the discussion to discuss the ts-MARCM dataset and its limitations. And, we will correct the citation to Baumgardt et al., 2014, not Gunnar. Thank you!

2- In segments other than abdomen, it is quite rare to hit proper clones, it appears that only GMCs are hit by recombination, with very few exceptions. Could the author please provide an explanation for this or at least mention this aspect?

• *This is true. We cannot explain it. It could have something to do with the RNAi cassettes that are used in ts-MARCM, because in the original paper they mention that RNAi can be differently regulated in GMCs versus neuroblasts (Yu et al., 2009). We will mention it in the revised discussion about ts-MARCM limitations.

It is also unclear whether in F the graph includes all types of clones (including 1:0 clones). This is important, because the timing of division for NBs and GMCs is different, and inclusion of 1:0 might lead to a wrong estimate of the NB proliferation window (longer than it actually is because GMCs divide for longer). This is particularly important for the SEZ, where most clones in normalised division 10 and 11 are with ratio 1:0, thus compatible with both terminal division as well as GMC division.

• *The graph in F does include all types of clones. We provide Supplemental Table 1, which shows the full dataset. Unfortunately, we do not have enough data to analyze only NB clones. We agree that the estimate of the NB proliferation window is coarse using this analysis method and could overrepresent the division time by one cell division. We will mention this in the discussion and make sure that our results text is free from any overreaching claims about the precision of these measurements.

To obtain an estimate of the timing of division, the authors normalise clone size to the size of the bigger clone in the abdomen. What happened to those samples where no abdominal clones were hit? Were they simply excluded from the analysis?

  From the analysis in Figure 2, we excluded the clones that were SEZ, thorax, or terminus only. They were rare. They are shown in Supplemental Table 1, which will now be added in our revision plan.

It is proposed that in the thorax late temporal cohort neurons are not produced, yet the ts-MARCM experiment detects some 1:0 clones. What is the fate of these cells? Are they all derived from GMC division and therefore decoupled from the temporal identity window? Or is this a re-activation of division?

Figure 2F shows at the inferred 11th NB3-3 division, 100% of thoracic clones are of the 1:0 type. This is an n=1 observation (Supplemental Table 1, row f-Jan20-2). When we look at the morphology of this thoracic EL, we can see that it is a fully differentiated neuron that crosses the midline and ascends to the CNS, which is similar to EL morphologies in A1, so we don't think it's a whole new cell type. We have no way of determining whether this neuron was derived from a GMC division. It is also possible that this is an infrequent event or a technical anomaly. To address the question of reactivation of the thoracic NB3-3 division, we plan to include a Supplemental Figure of EL number over developmental time (stages 11, 13, 15, 17) for segments SEZ3 to Te2. This is the same data that we mentioned to Reviewer 3. This will reveal the extent to which the thorax produces late-born ELs.

*"in A1, a majority of segments had one Notch OFF/B neuron that failed to label with Eve" does "the majority" in this sentence mean that there were cases where all B neurons were labelled with Eve? If yes, where would this stochasticity come from? *

• • Yes, "the majority" in this sentence means that there were cases where all B neurons were labeled by Eve. In Figure 3F, for segment A1, that number is four. In contrast, there are 6 cases where B neurons failed to label with Eve. We can only speculate about the origin of the stochasticity. It could be biological (e.g., low level of Eve expression) or technical (e.g., poor antibody penetration). We plan to mention this in the discussion.

Additionally, there is no evidence that it's the first born NotchOFF neuron in A1 that does not express Eve. The authors should clarify where this speculation comes from.

• *The evidence that the first-born Notch OFF neuron in A1 does not express Eve comes from our ts-MARCM data: "So far, our ts-MARCM analyses grouped segments into regions (Figure 2A-C), however, EL number varies on a segment-by-segment basis (Figure 1). Therefore, we looked for segment-by-segment differences in ts-MARCM data (Table S1). The only detectable difference was between A1 and the other abdominal segments: When both A1 and another abdominal segment were labeled in a single CNS, a majority had smaller A1 clones. These data suggest that the production of ELs by NB3-3 neuroblasts lags in A1 compared to A2-A7." We will add a representation of these data to the ts-MARCM figure. As we stated above, we will add a Supplemental Figure of EL number over developmental time (stages 11, 13, 15, 17) for segments SEZ3 to Te2, which could strengthen this point.

When discussing trends shared with other phyla:

A- "In the mammalian spinal cord, more neurons are present in regions that control limbs (Francius et al., 2013). Analogously, EL numbers do not smoothly taper from anterior to posterior; instead, the largest number of ELs is found in two non-adjacent regions, SEZ and the abdomen." It's unclear what is the link between the figure in the mammalian spinal cord and the Drosophila embryo. The embryo doesn't even have limbs and the number of neurons measured here refer only to a single lineage, while there could be (and in fact there are) lineage-to-lineage differences that could depict a different scenario.

Thank you for this comment. We will rewrite this sentence, "in the mammalian spinal cord, more neurons are present in regions that control limbs (Francius et al., 2013)" to more accurately reflect the data in the Francius paper, and make the parallel more explicit. We will say "the size of columns of V3, V1, V2a, V2b, and V0v neurons differ at brachial compared to lumbar levels in the developing spinal cord." This removes the confusion about limbs and somewhat mitigates the concern about lineage-to-lineage differences, at least from the perspective of the spinal cord.

B- The parallelism between V1 mouse neurons and EL Drosophila neurons is also unclear to me. The similarity in fold change across segments could be a pure coincidence and, from what I understand, the two cell types are not functionally linked.

  Thank you for this comment. We believe this is the sentence in question (sorry about no line numbers). "(3) In the mouse spinal cord, ~10-fold differences in molecular subtypes for V1 neurons (Sweeney et al., 2018). In *Drosophila*, NB3-3 neuroblasts show differences in EL number, depending on region, with similar fold changes, suggesting this trait is shared across phyla."  The emphasis was intended to be on the fold-changes, not cell types. Coincidence or not, it is parallel. We will update the sentence to say "(3) In the mouse spinal cord, ~10-fold differences in molecular subtypes for V1 neurons (Sweeney et al., 2018). Although V1 neurons are not direct homologs of EL neurons, the number also varies ~10-fold depending on the region. One possibility is that this trait is shared across phyla." And, we will remove the final part of the paragraph, which distracts from the point "Thus, for this study and future research, NB3-3 development now offers a uniquely tractable, detailed, and comprehensive model for studying how stem cells flexibly produce neurons."

Minor comments:

I found the manuscript somewhat difficult to follow, even though I am familiar with both the model and the topic. For non-specialist readers, I expect it will be even more challenging. The presentation of the results often feels fragmented, at times resembling a sequence of brief statements rather than a continuous narrative. I would encourage the authors to provide more synthesis and interpretation, for example by summarising key findings, rather than listing in detail the number of neurons labelled in each segment for every experiment. This would make the results more accessible and easier to digest.

• *Thank you for this comment. We will provide more synthesis and interpretation in results by summarizing key findings.

From the way the MS is written it's not clear from the beginning that the work focuses exclusively on embryonic-born neurons. Since in Drosophila neuronal stem cells undergo two rounds of neurogenesis, one in the embryo and one in the larva, this omission could lead to confusion.

  Thank you for this comment. We will mention this in the abstract, introduction and discussion.

In the abstract, what would be the other temporal cohorts generated in specific regions? (ref to: "In specific regions, NB3-3 neuroblasts produce additional types of temporal cohorts, including but not limited to the late-born EL temporal cohort.")

  In this manuscript, we use lineage tracing to identify four types of temporal cohorts- early-born Notch ON, early-born Notch OFF, late-born Notch ON, and late-born Notch OFF. This is now reflected in the revised abstract. ELs are early-born Notch OFF and/or late-born Notch OFF.

This sentence in the introduction is inaccurate: "The Drosophila CNS is

organized into an anterior hindbrain-like subesophageal zone (SEZ) and a posterior spinal cord-like nerve cord". The anterior hindbrain-like portion of the CNS is in fact the supraesophageal ganglion (or cerebrum), while the SEZ is a posterior-like region.

  Thank you. We will change this sentence to: "The *Drosophila* CNS is

organized into a hindbrain-like subesophageal zone (SEZ) and a spinal cord-like nerve cord".

Fig 1E: the encoding of the significance is not immediately clear. In the legend the 4 stars could also be arranged in the same way for clarity.

• *Thank you. We will change it for clarity.

Fig 2E legend: it is mentioned that B corresponds to a 1:4 clone, however the MARCM example is shown for C and it's a 1:5.

Thank you. We will fix this.

The occurrence of "undifferentiated" neurons in Th segments is in less than 10% of the clones, I wonder if this a stochastic or deterministic event and to what extent small cell bodies could just be the consequence of local differences in tissue architecture.

• Because we are using a stochastic technique, it is difficult for us to determine whether the occurrence of neurons with small somas is a stochastic or deterministic event. Several papers suggest neurons with small axons are found across insect species (Pearson and Fourtner, 1975; Burrows, 1996). Neurons with a small soma and short axons/ axonless are found in the Drosophila embryonic abdominal nerve cord (Lacin et al., 2009). In our unpublished work from the Drosophila* nerve cord at a first instar larval stage, we found small somas with short axons in segment A1 (see Figure 4.6 below). This leads us to believe it is not a consequence of local tissue architecture.

Fig 2I: it's unclear what the purple means (I suppose it might be Eve expression) and why in J there should be one purple cell not labelled by the ts-MARCM when this is not present in H and I.

Purple is Eve. We will add labels for stains used in H and I, and remove the extra purple cell from the illustration in J.

"When synapses do occur, they are numerically similar from segment to segment". It's unclear where the evidence for this statement comes from, please clarify or remove the sentence.

We calibrated our trans-Tango data against available connectomic data using segment A1 as a reference. We learned that the trans-tango method only identifies strongly (>15 synapses) connected neurons.

"First, we calibrated trans-Tango for use in larval Drosophila, focusing on segment A1, where connectome data are available (Wang et al., 2022). In the connectome, of the five early-born ELs in A1, three are strongly connected to CHOs (>15 synapses), two are weakly connected (15 synapses) connected to somatosensory neurons."

  We will modify this sentence to say "when synapses do occur they are of similar strengths from segment to segment"

"In SEZ2, NB3-3 divides 10 times (Figure 2F)". Figure 2F does not support this statement and Figure 7 shows 12 divisions. Possibly SEZ2 and 3 have been inverted in this statement, please clarify.

Thank you for pointing this out. We will correct it!

**Referees cross-commenting**

I agree with most of the comments/suggestions provided by the other two reviewers.

In particular:

I agree with reviewer #1's comment about failure to express Eve being a mechanism for controlling neurons number, as this is a circular argument.

• *We address this earlier and direct you to that text. Briefly, Eve is not just a marker, but a key differentiation gene for ELs.

I agree with reviewer #2's concern about the use of the word "flexibility"; "heterogeneity" would be a more appropriate term, as I would associate the word "flexibility" to the ability of a single neuroblast in a single segment to produce neurons with different fates under, for example, unusual growth conditions. Here no genetic/epigenetic manipulations were performed to address flexibility and the observed (stereotypical) differences result from axial patterning.

• *We will change this, thank you.

*As a note, Reviewer #1 asks about other temporal cohorts of EL neurons produced by other lineages, but these neurons are specifically generated from NB3-3. *

• *Thank you for adding this clarification.

To generalise the observations reported in this study, the authors would need to focus on other molecularly defined temporal cohorts or, more generally, on other lineages, which, however, are likely to adopt different combinations of mecahnisms to tune progeny number across segments.

• *We agree that further studies are needed to assess the generalizability of our findings.

Reviewer #4 (Significance (Required)):

In Drosophila melanogaster, the relationship between neural progenitors and their neuronal progeny has been studied in great detail. This work has provided a comprehensive description of the number of progenitors present in each embryonic segment, their molecular identities, the number of neurons they produce, and the temporal transcriptional cascades that couple progenitor temporal identity to neuronal fate.

This work adds to the existing knowledge a detailed characterisation of intersegmental differences in the pattern of proliferation of a single type of neuronal progenitor as well as in post-divisional fate depending on anterior-posterior position in the body axis (i.e. programmed cell death and Notch signalling activation). This is a first step towards understanding the cellular and molecular mechanisms underlying such differences, but it's not disclosing them.

We have disclosed the cellular mechanisms- stem cell division duration and type, neural cell death, identity gene expression, and differentiation state -unless something else is envisaged by this comment. The molecular mechanisms are beyond the scope of this paper.

That homologous neuroblasts can generate variable numbers of progeny neurons depending on their segmental position has been established previously. What this manuscript adds is the demonstration that these differences arise through a combination of altered division patterns and differential programmed cell death, thereby revealing a more complex and less predictable scenario than could have been anticipated from existing knowledge in other contexts. The advance provided by this study is therefore incremental, refining rather than overturning our understanding of how segmental diversity in neuroblast lineages is achieved.

The key conceptual advances provided by this study are described in the General Statements section above. We don't overturn, but we advance the field.

By touching on the general question of how progenitors generate diversity, this work could be of broad interest to developmental neuroscientists beyond the fly field. However, the way it is currently written does not make it very accessible to non-specialists.

Thank you for this comment. We will endeavor to make it more accessible in the revised manuscript. Reviewer 3, an expert in vertebrate neurobiology, agreed that our work was of broad interest.

My expertise: Drosophila neurodevelopment, nerve cord, cell types specification

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

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

With this Revision Plan, we submit a revised abstract, and a supplemental table 1. We plan to address every point raised by the reviewers.

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

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

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript addresses the question of how the number of neurons produced by each progenitor in the nervous system is determined. To address this question the authors use the Drosophila embryo model. They focus on a single type of neural stem cell (neuroblast), with homologues in each hemisegment along the anterior-posterior axis.

Using a combination of clonal labelling, antibody stainings, and blockade of programmed cell death, they provide a detailed description of segment-specific differences in the proliferation patterns of these neuroblasts, as well as in the fate and survival of their neuronal progeny. Furthermore, by employing trans-synaptic labelling, they demonstrate that neurons derived from the same progenitor type receive distinct patterns of synaptic input depending on their segmental origin, in part due to their temporal window origin. Overall this work shows that different mechanisms contribute to the final number and identity of the neuronal progeny arising from a single progenitor, even within homologous progenitors along the anterior posterior body axis.

Major Comments

I would suggest adding line numbers to the text for future submissions, this massively helps providing comments.

The authors propose that all neuroblasts produce the same type of temporal cohort (early born) and that, by changing the pattern of cell division, different temporal cohorts can be added. The way this this presented in the abstract sounds like an obvious thing, what would be the alternative scenario/s? Here it's the late born neurons that lack in thoracic segments because of early NB quiescence, but it cannot be excluded that different neuroblast types adopt a different strategy.

I found the ts-MARCM results confusing for 2 reasons:

1. It's not clear to me why there are so many single cell clones in div 3 and 4 in abdominal segments. This is not compatible with the division model depicted for abdominal segments, unless GMCs are produced in those division window and the MARCM hits the GMC, as also mentioned in the legend for G. This aspect is important because, either the previous model by Baumgardt et al. - please correct cit. currently Gunnar et al. 2026 - is wrong, or something strange happens in this experiment, or the relative temporal order is incorrect.
2. In segments other than abdomen, it is quite rare to hit proper clones, it appears that only GMCs are hit by recombination, with very few exceptions. Could the author please provide an explanation for this or at least mention this aspect? It is also unclear whether in F the graph includes all types of clones (including 1:0 clones). This is important, because the timing of division for NBs and GMCs is different, and inclusion of 1:0 might lead to a wrong estimate of the NB proliferation window (longer than it actually is because GMCs divide for longer). This is particularly important for the SEZ, where most clones in normalised division 10 and 11 are with ratio 1:0, thus compatible with both terminal division as well as GMC division.

To obtain an estimate of the timing of division, the authors normalise clone size to the size of the bigger clone in the abdomen. What happened to those samples where no abdominal clones were hit? Were they simply excluded from the analysis?

It is proposed that in the thorax late temporal cohort neurons are not produced, yet the ts-MARCM experiment detects some 1:0 clones. What is the fate of these cells? Are they all derived from GMC division and therefore decoupled from the temporal identity window? Or is this a re-activation of division?

"in A1, a majority of segments had one Notch OFF/B neuron that failed to label with Eve" does "the majority" in this sentence mean that there were cases where all B neurons were labelled with Eve? If yes, where would this stochasticity come from? Additionally, there is no evidence that it's the first born NotchOFF neuron in A1 that does not express Eve. The authors should clarify where this speculation comes from. When discussing trends shared with other phyla:

A- "In the mammalian spinal cord, more neurons are present in regions that control limbs (Francius et al., 2013). Analogously, EL numbers do not smoothly taper from anterior to posterior; instead, the largest number of ELs is found in two non-adjacent regions, SEZ and the abdomen." It's unclear what is the link between the figure in the mammalian spinal cord and the Drosophila embryo. The embryo doesn't even have limbs and the number of neurons measured here refer only to a single lineage, while there could be (and in fact there are) lineage-to-lineage differences that could depict a different scenario.

B- The parallelism between V1 mouse neurons and EL Drosophila neurons is also unclear to me. The similarity in fold change across segments could be a pure coincidence and, from what I understand, the two cell types are not functionally linked.

Minor comments:

I found the manuscript somewhat difficult to follow, even though I am familiar with both the model and the topic. For non-specialist readers, I expect it will be even more challenging. The presentation of the results often feels fragmented, at times resembling a sequence of brief statements rather than a continuous narrative. I would encourage the authors to provide more synthesis and interpretation, for example by summarising key findings, rather than listing in detail the number of neurons labelled in each segment for every experiment. This would make the results more accessible and easier to digest.

From the way the MS is written it's not clear from the beginning that the work focuses exclusively on embryonic-born neurons. Since in Drosophila neuronal stem cells undergo two rounds of neurogenesis, one in the embryo and one in the larva, this omission could lead to confusion.

In the abstract, what would be the other temporal cohorts generated in specific regions? (ref to: "In specific regions, NB3-3 neuroblasts produce additional types of temporal cohorts, including but not limited to the late-born EL temporal cohort.")

This sentence in the introduction is inaccurate: "The Drosophila CNS is organized into an anterior hindbrain-like subesophageal zone (SEZ) and a posterior spinal cord-like nerve cord". The anterior hindbrain-like portion of the CNS is in fact the supraesophageal ganglion (or cerebrum), while the SEZ is a posterior-like region.

Fig 1E: the encoding of the significance is not immediately clear. In the legend the 4 stars could also be arranged in the same way for clarity.

Fig 2E legend: it is mentioned that B corresponds to a 1:4 clone, however the MARCM example is shown for C and it's a 1:5.

The occurrence of "undifferentiated" neurons in Th segments is in less than 10% of the clones, I wonder if this a stochastic or deterministic event and to what extent small cell bodies could just be the consequence of local differences in tissue architecture.

Fig 2I: it's unclear what the purple means (I suppose it might be Eve expression) and why in J there should be one purple cell not labelled by the ts-MARCM when this is not present in H and I.

"When synapses do occur, they are numerically similar from segment to segment". It's unclear where the evidence for this statement comes from, please clarify or remove the sentence.

"In SEZ2, NB3-3 divides 10 times (Figure 2F)". Figure 2F does not support this statement and Figure 7 shows 12 divisions. Possibly SEZ2 and 3 have been inverted in this statement, please clarify.

Referees cross-commenting

I agree with most of the comments/suggestions provided by the other two reviewers. In particular: I agree with reviewer #1's comment about failure to express Eve being a mechanism for controlling neurons number, as this is a circular argument. I agree with reviewer #2's concern about the use of the word "flexibility"; "heterogeneity" would be a more appropriate term, as I would associate the word "flexibility" to the ability of a single neuroblast in a single segment to produce neurons with different fates under, for example, unusual growth conditions. Here no genetic/epigenetic manipulations were performed to address flexibility and the observed (stereotypical) differences result from axial patterning. As a note, Reviewer #1 asks about other temporal cohorts of EL neurons produced by other lineages, but these neurons are specifically generated from NB3-3. To generalise the observations reported in this study, the authors would need to focus on other molecularly defined temporal cohorts or, more generally, on other lineages, which, however, are likely to adopt different combinations of mecahnisms to tune progeny number across segments.

Significance

In Drosophila melanogaster, the relationship between neural progenitors and their neuronal progeny has been studied in great detail. This work has provided a comprehensive description of the number of progenitors present in each embryonic segment, their molecular identities, the number of neurons they produce, and the temporal transcriptional cascades that couple progenitor temporal identity to neuronal fate. This work adds to the existing knowledge a detailed characterisation of intersegmental differences in the pattern of proliferation of a single type of neuronal progenitor as well as in post-divisional fate depending on anterior-posterior position in the body axis (i.e. programmed cell death and Notch signalling activation). This is a first step towards understanding the cellular and molecular mechanisms underlying such differences, but it's not disclosing them.

That homologous neuroblasts can generate variable numbers of progeny neurons depending on their segmental position has been established previously. What this manuscript adds is the demonstration that these differences arise through a combination of altered division patterns and differential programmed cell death, thereby revealing a more complex and less predictable scenario than could have been anticipated from existing knowledge in other contexts. The advance provided by this study is therefore incremental, refining rather than overturning our understanding of how segmental diversity in neuroblast lineages is achieved. By touching on the general question of how progenitors generate diversity, this work could be of broad interest to developmental neuroscientists beyond the fly field. However, the way it is currently written does not make it very accessible to non-specialists.

My expertise: Drosophila neurodevelopment, nerve cord, cell types specification

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Referee #2

Evidence, reproducibility and clarity

In this manuscript, Vasudevan et al provide a detailed characterisation of the different numbers and temporal birthdates of Even-skipped Lateral (EL) neurons produced at in different segments from the same neuroblast, NB3-3. The work highlights the differences in EL neuronal generation across segments is achieved through a combination of different division patterns, failure to upregulate EL marker Eve and segment-specific program cell death. For neurons born within the same window and segment, the authors describe additional heterogeneity in their circuit formation. The work underscores the large diversity that the same neuroblast can generate across segments.

Major comments:

• Based on the ts-MARCM 1:0 clones representing 100% of the SEZ clones at any given inferred cell division, the authors conclude "NB3-3 neuroblasts generate proliferative daughter GMCs in the SEZ and thorax on most divisions". Figure 2G does not have any data for SEZ before inferred division 5, whereas there is data in other regions. The authors also state "In the SEZ and abdomen, ELs were labelled regardless of induction time." In reference to Fig 2F, which seems inaccurate given there are no SEZ clones before inferred division 5. There is no comment on this fact, which is surprising give their focus on temporal cohorts. The authors should explain this discrepancy, if known, or modify their statements to reflect the data.
• The temporal cohort (early-born vs late-born) identity is exclusively examined based on markers. Given the absence of SEZ clones from early NB3-3 divisions, a time course showing that the SEZ generate early-born Els or some other complementary method would be desirable.
• The authors repeatedly refer to their work as showing how a stem cell type can have "flexibility". Flexibility would imply that NB3-3 from one segment could adopt a different behaviour (different division pattern, or cell death or connectivity) if it were placed in a different segment. This is not what is being shown. In my opinion, "heterogeneity" of the same neuroblast across different segments would be more appropriate.

Minor comments:

• Figure 2A depicts a combination of known data and conclusions from their own (mainly SEZ). The authors might consider editing the figure to highlight what is new. A possibility would be for figure A to be a diagram of the experimental design and their summary division pattern to be shown after the new data instead of being panel A.
• The authors state that they combined published ts-MARCM with their new one, which differed in a number ways that they list, but they don't specify which limitations are associated with the published vs new dataset. Could the authors please clarify?
• The title refers exclusively to "temporal cohorts", which in the manuscript are defined quite narrowly and do not seem to apply to all segments.
• Several cited references are missing from the Reference list at the end. Could the authors please double check this? (e.g. Matsushita, 1997; Sweeney et al., 2018)
• Legend for figure 2 is a bit confusing, there is a "(A)" within the legend for (D), which indicates that segments A1-A7 are shown (this seems inaccurate, as it only goes to A6).

Significance

This study provides a comprehensive analysis of different cell biological scenarios for a neuroblast to generate distinct progeny across repeating axial units. The strength is the detailed and systematic approach across segments and possible scenarios: different division patterns, cell death, molecular marker expression. While it focuses on one specific neuroblast of the ventral nerve cord of Drosophila, the authors have done extensive work to place their findings and interpretation in the context of other cell types and across model organisms both in the introduction and discussion. This makes the work of interest for developmental biologists in general, neurodevelopment research in particular and those interested in circuit assembly, beyond their specialised community. This point of view comes from someone working in vertebrate CNS development.

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Referee #1

Evidence, reproducibility and clarity

Summary: The study by Vasudevan et al intends to address how serially homologous neural progenitors generate different numbers and types of neurons depending on their location along the body axis. Investigation of full repertoire of neurogenesis for these progenitors necessitates a precise ability to track the fates of both progenitors and their neuronal progeny making it extremely difficult in vertebrate paradigm. The authors used NB3-3 in the developing fly embryo as a model to investigate the full extent of the flexibility in neurogenesis from a single type of serially homologous stem cell. Previous work showed NB3-3 generates neurons including lateral interneurons that can be positively labeled by Even-skipped, but detailed characterization of the NB3-3 lineage mainly focused on 3 segments during embryogenesis. The authors defined the number of EL neurons in all segments of the central nervous system in early larvae after the completion of circuit formation and carried out clonal analyses to determine the proliferation pattern of NB3-3. They described the failure to express Eve in Notch OFF/B neurons as a new mechanism for controlling the number of EL neurons and PCD limits EL neurons in terminal segments.

Major comments: The authors performed careful analyses of the NB3-3 lineage using EL neurons. My main concerns are limited applicability of their findings and lack of mechanisms as how NB3-3 generate various numbers of EL neurons. Their findings are exclusively relevant to the NB3-3 lineage despite their effort in highlighting that other NB lineages also generate temporal cohorts of EL neurons. I disagreed with their conclusion that failure to express Eve as a mechanism for controlling EL neuron numbers when Eve serves as the marker for these neurons. Are there any other strategy to assess the fates and functions of these cells beside relying solely on Eve expression? I am not familiar with the significance of Eve expression on the functions of these neurons. Is it possible to perform clonal analyses of NB3-3 mutant for Eve and see if these neurons adopt different functionalities/identities? If NB3-3 in the SEZ continually generate GMCs based on the interpretation of clonal analyses and depicted in Fig. 2A, why is the percent of clones that are 1:0 virtually at or near 100% from division 6-11 shown in 2G? The authors also indicate that NB3-3 in the abdomen directly generate Notch OFF/B cells that assume EL neuronal identity. In this scenario, shouldn't the percent of 1:0 clones be 100% in later divisions in Fig. 2G? Based on the number of clones in abdomen shown in Fig. 2E, I cannot seem to understand how the authors come to the percent of 1:0 clones shown in Fig. 2G

There are many potentially interesting questions related to this study that can significantly broaden the impact of this study. For example, are other NB lineages that also generate distinct temporal cohorts of EL neurons display similar proliferation patterns (type 1 division in SEZ, early termination of cell division in thoracic segments and type 0 division in abdomen)? Why does NB3-3 in the thoracic segment become quiescence so much sooner than SEZ and abdominal segments? The authors' observations suggest that NB3-3 in SEZ and abdomen generate a similar number of EL neurons despite the difference in their division patterns (type 1 vs type 0). Are the mechanisms that promote EL neuron generate in NB3-3 in SEZ and abdomen the same? Anything else is known beside Notch OFF?

Minor comments:

The authors' writing style is highly unusual especially in the result section. There is an overwhelming large amount of background information in the result section but very thin description on their observations. The background information portion also includes previously published observations. Since the nature of this study is not hypothesis-driven, it is very confusing to read in many places and difficult to distinguish their original observations from previously published results and making. One easily achievable improvement is to insert relevant figure numbers into the text more often.

Significance

The study by Vasudevan et al intends to address how serially homologous neural progenitors generate different numbers and types of neurons depending on their location along the body axis. Investigation of full repertoire of neurogenesis for these progenitors necessitates a precise ability to track the fates of both progenitors and their neuronal progeny making it extremely difficult in vertebrate paradigm. The authors used NB3-3 in the developing fly embryo as a model to investigate the full extent of the flexibility in neurogenesis from a single type of serially homologous stem cell. Previous work showed NB3-3 generates neurons including lateral interneurons that can be positively labeled by Even-skipped, but detailed characterization of the NB3-3 lineage mainly focused on 3 segments during embryogenesis. The authors defined the number of EL neurons in all segments of the central nervous system in early larvae after the completion of circuit formation and carried out clonal analyses to determine the proliferation pattern of NB3-3. They described the failure to express Eve in Notch OFF/B neurons as a new mechanism for controlling the number of EL neurons and PCD limits EL neurons in terminal segments.

Interesting point about paying attention to the "the". Normally we skip over "the". But here, "the" has sigficiant meaning.

I am a bit confused on how to interpret this. From looking at the link, the "Philosopher" he refers to is Plato, and the quote I am guessing, from the citations, is from Plato's ethics. Plato lists several virtues: courage, moderation, piety, and justice (Scavone 2023). I'd like to read the original by Plato before making real conclusions, but I believe the author's argument is appealing to both the virtues of moderation and piety. We've established already that among the differing medieval attitudes around games, one of the conclusions was moderation was key, such as this passage selected from the textbook, which was originally by John Salisbury, "'There are, however, times when, viewed from a certain aspect, games of chance are permissible. For example, if without evil consequences they alleviate the strain of heavy responsibilities and if without harming character they introduce an agreeable period of relaxation. Liberty to do as one pleases is justified if moderation controls the act'" (Milliman, 587), and so it's easy to see how, say, dice games would contradict Plato's virtue of moderation from a more severe perspective, since they can become addictive and make a gambler of a person. There is also a contradiction to the virtue of piety that the author may be appealing to, that since a person should "direct his action to something else" he means, potentially, that games distract a person from both their other responsibilities (both religion and justice if you were to look at it under the lens of Plato's virtues) and from the worship of God, not because a person should be spending every second of their time on these things, but because they have the capacity to steer a person the wrong way and tempt them away from keeping to the virtues.

I've left a link to the article I looked at here, it is by Daniel C. Scavone.

In this article Carnival seems to be a day for boys to bring their roosters to fight each other. Previously, we read this was a celebration before Lent, " a rejoicing period of time" (Milliman, 597). Lent from my understanding is where you give something up in order to develop or strengthen your relationship to God. This seems to be an interesting game especially since this would be a game to relax the students before a time of ceremonial divinity. This game also fits in with ceremonial combat mention by Milliman (591). I wonder why it was deemed morally acceptable to have animals fight but not have tournaments. This seems like it would feed a love of violence. However, this book does not mention details of how far the cock-fight would go, so maybe not. There seems to be a respect for knowing how to fight as a discipline and actually fighting as a sport.

I wonder if Isildore of Seville would have preferred this version of theatre, since he denounces the musical theatre performances he describes on page 370. I think part of his concerns are that the musical performances may "excite" the more indecent parts of the human craving, but in religious dramas like these, the performance is appealing to the religious morality of the audience.

via u/schematical at https://reddit.com/user/schematical/comments/1oe41bx/what_is_a_database_index_as_explained_to_a_1930s/

Perhaps it's a question of the "long search" versus the "short search"? Long searches with proper connecting tissue are more often the thing that produces innovation out of serendipity and this is the thing of greatest value versus "What time does the Superbowl start?". How do you build a database index to improve the "long search"?

See, for example Keith Thomas' problem: https://hyp.is/DFLyZljJEe2dD-t046xWvQ/www.lrb.co.uk/the-paper/v32/n11/keith-thomas/diary

The author's perspective is that Russia seeks to become a global power but has a number of obstacles. At the end of the cold war left Russia with not the same status as a world power like the Soviet Union was. To gain the status as a global superpower once again countries have to rely on their own resources and advantages for hegemony. Being naive with other global powers can bring down the status that they are building up. But the author questions its overall power such as military capabilities and how it can counter threats from the middle east, central and south Asia how they can compete with other great powers to gain influence near its borders.

This part hit hard because it shows how deep-rooted bias in media shapes public perception. By constantly under-representing or stereotyping certain groups, the media reinforces inequality. Discussing this in class would help students recognize bias, not just in obvious hate speech but in everyday portrayals. De Abreu is essentially saying: to think critically, we must see whose stories are missing—not just who is shown.

This line really captures the heart of media literacy—it’s not about memorizing facts about media, but about questioning what we see and hear. De Abreu emphasizes that without critical thinking, media literacy becomes empty. It reminds me that consuming news or social posts passively makes us more likely to be influenced by bias or misinformation. True literacy means asking who made this, why, and how it’s shaping what I believe.

Reviewer #3 (Public review):

Summary:

CTF18-RFC is an alternative eukaryotic PCNA sliding clamp loader which is thought to specialize in loading PCNA on the leading strand. Eukaryotic clamp loaders (RFC complexes) have an interchangeable large subunit which is responsible for their specialized functions. The authors show that the CTF18 large subunit has several features responsible for its weaker PCNA loading activity, and that the resulting weakened stability of the complex is compensated by a novel beta hairpin backside hook. The authors show this hook is required for the optimal stability and activity of the complex.

Relevance:

The structural findings are important for understanding RFC enzymology and novel ways that the widespread class of AAA ATPases can be adapted to specialized functions. A better understanding of CTF18-RFC function will also provide clarity into aspects of DNA replication, cohesion establishment and the DNA damage response.

Strengths:

The cryo-EM structures are of high quality enabling accurate modelling of the complex and providing a strong basis for analyzing differences and similarities with other RFC complexes.

Weaknesses:

The manuscript would have benefited from a more detailed biochemical analysis using mutagenesis and assays to tease apart the differences with the canonical RFC complex. Analysis of the FRET assay could be improved.

Overall appraisal:

Overall, the work presented here is solid and important. The data is mostly sufficient to support the stated conclusions.

Comments on revisions:

While the authors addressed my previous specific concerns, they have now added a new experiment which raises new concerns.

The FRET clamp loading experiments (Fig. 6) appear to be overfitted so that the fitted values are unlikely to be robust and it is difficult to know what they mean, and this is not explained in this manuscript. Specifically, the contribution of two exponentials is floated in each experiment. By eye, CTF18-RFC looks much slower than RFC1-RFC (as also shown previously in the literature) but the kinetic constants and text suggest it is faster. This is because the contribution of the fast exponential is substantially decreased, and the rate constants then compensate for this. There is a similar change in contribution of the slow and fast rates between WT CTF18 and the variant (where the data curves look the same) and this has been balanced out by a change in the rate constants, which is then interpreted as a defect. I doubt the data are strong enough to confidently fit all these co-dependent parameters, especially for CTF18, where a fast initial phase is not visible. I would recommend either removing this figure or doing a more careful and thorough analysis.

Author response:

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

Reviewer #1 (Public review): 

Summary: 

The authors report the structure of the human CTF18-RFC complex bound to PCNA. Similar structures (and more) have been reported by the O'Donnell and Li labs. This study should add to our understanding of CTF18-RFC in DNA replication and clamp loaders in general. However, there are numerous major issues that I recommend the authors fix. 

Strengths: 

The structures reported are strong and useful for comparison with other clamp loader structures that have been reported lately. 

Weaknesses: 

The structures don't show how CTF18-RFC opens or loads PCNA. There are recent structures from other groups that do examine these steps in more detail, although this does not really dampen this reviewer's enthusiasm. It does mean that the authors should spend their time investigating aspects of CTF18-RFC function that were overlooked or not explored in detail in the competing papers. The paper poorly describes the interactions of CTF18-RFC with PCNA and the ATPase active sites, which are the main interest points. The nomenclature choices made by the authors make the manuscript very difficult to read. 

Reviewer #2 (Public review): 

Summary 

Briola and co-authors have performed a structural analysis of the human CTF18 clamp loader bound to PCNA. The authors purified the complexes and formed a complex in solution. They used cryo-EM to determine the structure to high resolution. The complex assumed an auto-inhibited conformation, where DNA binding is blocked, which is of regulatory importance and suggests that additional factors could be required to support PCNA loading on DNA. The authors carefully analysed the structure and compared it to RFC and related structures. 

Strength & Weakness 

Their overall analysis is of high quality, and they identified, among other things, a human-specific beta-hairpin in Ctf18 that flexibly tethers Ctf18 to Rfc2-5. Indeed, deletion of the beta-hairpin resulted in reduced complex stability and a reduction in a primer extension assay with Pol ε. This is potentially very interesting, although some more work is needed on the quantification. Moreover, the authors argue that the Ctf18 ATP-binding domain assumes a more flexible organisation, but their visual representation could be improved. 

The data are discussed accurately and relevantly, which provides an important framework for rationalising the results. 

All in all, this is a high-quality manuscript that identifies a key intermediate in CTF18dependent clamp loading. 

Reviewer #3 (Public review): 

Summary: 

CTF18-RFC is an alternative eukaryotic PCNA sliding clamp loader that is thought to specialize in loading PCNA on the leading strand. Eukaryotic clamp loaders (RFC complexes) have an interchangeable large subunit that is responsible for their specialized functions. The authors show that the CTF18 large subunit has several features responsible for its weaker PCNA loading activity and that the resulting weakened stability of the complex is compensated by a novel beta hairpin backside hook. The authors show this hook is required for the optimal stability and activity of the complex. 

Relevance: 

The structural findings are important for understanding RFC enzymology and novel ways that the widespread class of AAA ATPases can be adapted to specialized functions. A better understanding of CTF18-RFC function will also provide clarity into aspects of DNA replication, cohesion establishment, and the DNA damage response. 

Strengths: 

The cryo-EM structures are of high quality enabling accurate modelling of the complex and providing a strong basis for analyzing differences and similarities with other RFC complexes. 

Weaknesses: 

The manuscript would have benefitted from more detailed biochemical analysis to tease apart the differences with the canonical RFC complex. 

I'm not aware of using Mg depletion to trap active states of AAA ATPases. Perhaps the authors could provide a reference to successful examples of this and explain why they chose not to use the more standard practice in the field of using ATP analogues to increase the lifespan of reaction intermediates. 

Overall appraisal: 

Overall the work presented here is solid and important. The data is sufficient to support the stated conclusions and so I do not suggest any additional experiments. 

Reviewer #1 (Recommendations for the authors): 

We thank the reviewer for their positive comments and for their thorough review. All raised points have been addressed below.

Major points 

(1) The nomenclature used in the paper is very confusing and sometimes incorrect. The authors refer to CTF18 protein as "Ctf18", and the entire CTF18-RFC complex as "CTF18". This results in massive confusion because it is hard to ascertain whether the authors are discussing the individual subunits or the entire complex. Because these are human proteins, each protein name should be fully capitalized (i.e. CTF18, RFC4 etc). The full complex should be referred to more clearly with the designation CTF18-RFC or CTF18-RLC (RFC-like complex). Also, because the yeast and human clamp loader complexes use the same nomenclature for different subunits, it would be best for the authors to use the "A, B, C, D, E subunit" nomenclature that has been standard in the field for the past 20 years. Finally, the authors try to distinguish PCNA subunits by labeling them "PCNA2" or "PCNA1" (see Page 8 lines 180,181 for an example). This is confusing because the names of the RFC subunits have similar formats (RFC2, RFC3, RFC4, etc). In the case of RFC this denotes unique genes, whereas PCNA is a homotrimer. Could the authors think of another way to denote the different subunits, such as super/subscript? PCNA-I, PCNA-II, PCNA-III? 

We thank the reviewer for pointing out the confusing nomenclature. Following the referee suggestion, we now refer to the CTF18 full complex as “CTF18-RFC”. We prefer keeping the nomenclature used for CTFC18 subunits as RFC2, RFC3 etc., as recently used in Yuan et al, Science, 2024. However, we followed the referee’s suggestion for PCNA subunits, now referred to as PCNA-I, PCNA-II and PCNA-III.

(2) I believe that the authors are over-interpreting their data in Figure 1. The claim that "less sharp definition" of the map corresponding to the AAA+ domain of Ctf18 supports a relatively high mobility of this subunit is largely unsubstantiated. There are several reasons why one could get varying resolution in a cryo-EM reconstruction, such as compositional heterogeneity, preferred orientation artifacts, or how the complex interacts with the air-water interface. If other data were presented that showed this subunit is flexible, this evidence would support that data but cannot alone as justification for subunit mobility. Along these lines, how was the buried surface area (2300 vs 1400 A2) calculated? Is this the total surface area or only the buried surface area involving the AAA+ domains? It is surprising that these numbers are so different considering that the subunits and complexes look so similar (Figures 1c and 2b). 

We respectfully disagree with the suggestion that our interpretation of local flexibility in the AAA+ domain of Ctf18 is overreaching. Several lines of evidence support this interpretation. First, compositional heterogeneity is unlikely, as the A′ domain of Ctf18 is well-resolved and forms stable interactions with RFC3, indicating that Ctf18 is consistently incorporated into the complex. Second, preferred orientation artifacts are excluded, as the particle distribution shows excellent angular coverage (Fig. S9a). Third, we now include a 3D variability analysis (3DVA; Supplementary Video 1), which reveals local conformational heterogeneity centered around the AAA+ domain of Ctf18, consistent with intrinsic flexibility.

Regarding the buried surface area values, the reported numbers refer specifically to the interfaces between the AAA+ domain of Ctf18 and RFC2, and are derived from buried surface area calculations performed with PISA. The smaller interface (~1400 Ų) compared to RFC1–RFC2 (~2300 Ų) reflects low sequence identity (~26%) and divergent structural features, including the absence of conserved elements such as the canonical PIP-box in Ctf18. We have clarified and expanded this explanation in the revised manuscript (Page 7).

(3) The authors very briefly discuss interactions with PCNA and how the CTF18-RFC complex differs from the RFC complex. This is amongst the most interesting results from their work, but also not well-developed. Moreover, Figure 3D describing these interactions is extremely unclear. I feel like this observation had potential to be interesting, but is largely ignored by the authors. 

We thank the referee for pointing this out. We have expanded the section describing the interactions of CTF18-RFC and PCNA (Page 9 in the new manuscript), and made a new panel figure with further details (Fig. 3D).  

(4) The authors make the observation that key ATP-binding residues in RFC4 are displaced and incompatible with nucleotide binding in their CTF18-RFC structure compared to the hRFC structure. This should be a main-text figure showing these displacements and how it is incompatible with ATP binding. Again, this is likely an interesting finding that is largely glossed over by the authors. 

We now discuss this feature in detail (Pag 11 in the new manuscript), and added two figure insets (Fig. 4c) describing the incompatibility of RFC4 with nucleotide binding.

(5) The authors claim that the work of another group (citation 50) "validate(s) our predictions regarding the significant similarities between CTF18-RFC and canonical RFC in loading PCNA onto a ss/dsDNA junction." However, as far as this reviewer can tell the work in citation 50 was posted online before the first draft of this manuscript appeared on biorxiv, so it is dubious to claim that these were "predictions." 

We agree with the referee about this claim. We have now revised the text as follows:

“While our work was being finalized, several cryo-EM structures of human CTF18-RFC bound to PCNA and primer/template DNA were reported by another group (He et al, PNAS, 2024). These findings are consistent with the distinct features of CTF18-RFC observed in our structures and independently support the notion of significant mechanistic similarity between CTF18-RFC and canonical RFC in loading PCNA onto a ss/dsDNA junction”.

(6) The authors use a primer extension assay to test the effects of truncating the Nterminal beta hairpin of CTF18. However, this assay is only a proxy for loading efficiency and the observed effects of the mutation are rather subtle. The authors could test their hypothesis more clearly if they performed an ATPase assay or even better a clamp loading assay. 

We thank the referee for this valuable suggestion. In response, we have performed clamp loading assays comparing the activities of human RFC, wild-type CTF18-RFC, and the β-hairpin–truncated CTF18-RFC mutant. The results, now presented in Fig. 6 and Table 1 of the revised manuscript, clearly show that truncation of the N-terminal βhairpin results in a slower rate of PCNA loading. We propose that this reduced loading rate likely contributes to the diminished Pol ε–mediated DNA synthesis observed in the primer extension assays.

Minor points 

(1) Page 3 line 53 the introduction suggests that ATP hydrolysis prompts clamp closure. While this may be the case, to my knowledge all recent structural work shows that closure can occur without ATP hydrolysis. It may be better to rephrase it to highlight that under normal loading conditions, ATP hydrolysis occurs before clamp closure. 

The text now reads (Page 3): 

“DNA binding prompts the closure of the clamp and hydrolysis of ATP induces the concurrent disassembly of the closed clamp loader from the sliding clamp-DNA complex, completing the cycle necessary for the engagement of the replicative polymerases to start DNA synthesis.”

(2) Page 3 line 60, I do not see how the employment of alternative loaders highlights the specificity of the loading mechanism - would it not be possible for multiple loaders to have promiscuous clamp loading? 

We thank the referee for this comment. The text now reads (Page 3):

“However, eukaryotes also employ alternative loaders (20), including CTF18-RFC (6, 21-24), which likely use a conserved loading mechanism but are functionally specialized through specific protein interactions and context-dependent roles in DNA replication.”

(3) Page 4 line 75 could you please cite a study that shows Ctf8 and Dcc1 bind to the Ctf18 C-terminus and that a long linker is predicted to be flexible? 

Two references have been added (Stokes et al, NAR, 2020 and Grabarczyk et al, Structure, 2018)

(4) Figure 2A has the N-terminal region of Ctf18 as bound to RFC3 but should likely be labeled as bound to RFC5. This caused significant confusion while trying to parse this figure. Further, the inclusion of "X" as a sequence - does this refer to a sequence that was not buildable in the cryo-EM map? I would be surprised that density immediately after the conserved DEXX box motif is unbuildable. If this is the case, it should be clearly stated in the figure legend that "X" denotes an unbuildable sequence. For the conserved beta-hairpin in the sequence, could the authors superimpose the AlphaFold prediction onto their structure? It would be more informative than just looking at the sequence. 

We apologize for this confusion. The error in Figure 2A has been corrected. The figure caption now explicitely says that “X” refers to amino acid residues in the sequence which were not modelled. A superposition of the cryo-EM model of the N-terminal Beta hairpin in human Ctf18 and AlphaFold predictions for this feature in drosophila and yeast Ctf18 is now presented in Figure 2A.

(5) Page 8 line 168, the use of the term "RFC5" here feels improper, since the "C" subunit is not RFC5 in all lower eukaryotes (see comment above about nomenclature). For instance, in S cerevisiae, the C subunit is RFC3. I would expect this interaction to be maintained in all C subunits, not all RFC5 subunits. 

The text now reads (Page 8):

“Therefore, lower eukaryotes may use a similar b-hairpin motif to bind the corresponding subunit of the RFC-module complex (RFC5 in human, Rfc3 in S. cerevisiae), emphasizing its importance.”  

(6) Page 10 line 228, the authors claim that hydrolysis is dispensable at the Ctf18/RFC2 interface based on evidence from RFC1/RFC2 interface, by analogy that this is the "A/B" interface in both loaders. However, the wording makes it sound as if the cited data were collected while studying Ctf18 loaders. The authors should clarify this point. 

The text has been modified as follows (Pag 11): 

“Prior research has indicated that hydrolysis at the large subunit/RFC2 interface is not essential for clamp loading by various loaders (48-51), while the others are critical for the clamp-loading activity of eukaryotic RFCs. “

(7) Page 11 line 243/244 the authors introduce the separation pin. Could they clarify whether Ctf18 contains any aromatic residues in this structural motif that would suggest it serves the same functional purpose? Also, the authors highlight this is similar to yeast RFC, which makes it sound like this is not conserved in human RFC, but the structural motif is also conserved in human RFC. 

We thank the reviewer for this helpful comment. We have clarified in the revised text (Page 12) that the separation pin is conserved not only in yeast RFC but also in human RFC, and now note that human Ctf18 also harbors aromatic residues at the corresponding positions. This observation is supported by the new panel in Figure 4e.

Minutia 

(1) Page 2 line 37 please remove the word "and" before PCNA. 

This has been corrected.

(2) Please define AAA+ and update the language to clarify that not all pentameric AAA+ ATPases are clamp loaders. 

AAA+ has been now defined (Page 3).

(3) Page 4 line 86 Given the relatively weak interaction of Pol ε. 

This has been corrected.

(4) Page 8 line 204 the authors likely mean "leucine" and not "lysine". 

We thank the reviewer for catching this. The error has been corrected.

(5) Page 14 line 300, the authors claim that CTF18 utilizes three subunits but then list four. 

We have corrected this.

Reviewer #2 (Recommendations for the authors): 

We thank the reviewer for their positive comments and valuable suggestions. The points raised by the referee have been addressed below.

Major point: 

(1) Please quantify Figure 6 and S9 from 3 independent repeats and determine the standard deviation to show the variability of the Ctf18 beta hairpin deletion.  The authors suggest that a suboptimal Ctf18 complex interaction with PCNA impacts the stability of the complex, but do not test this hypothesis. Could the suboptimal PIP motif in Ctf18 be changed to an improved motif and the impact tested in the primer extension assay? Although not essential, it would be a nice way to explore the mechanism. 

We thank the reviewer for the suggestion. However, we note that Figure 6b (now 7b) already presents the quantification of the primer extension assay from three independent replicates, with error bars showing standard deviations, and includes the calculated rate of product accumulation. These data clearly indicate a 42% reduction in primer synthesis rate upon deletion of the Ctf18 β-hairpin.

We agree that we do not provide direct evidence of impaired complex stability upon deletion of the Ctf18 β-hairpin. However, the 2D classification of the cryo-EM dataset (Figure S9) shows a marked reduction in the number of particles corresponding to intact CTF18-RFC–PCNA complexes in the β-hairpin deletion sample, with the majority of particles corresponding to free PCNA. This contrasts with the wild-type dataset, where complex particles are predominant. These findings indirectly suggest that deletion of the β-hairpin compromises the stability or assembly of the clamp-loader–clamp complex.

We thank the reviewer for the valuable suggestion to mutate the weak PIP-box of Ctf18. While an interesting direction, we instead sought to directly test the mechanism by performing quantitative clamp loading assays. These assays revealed a significant reduction in the rate of PCNA loading by the CTF18^Δ165–194-RFCmutant (Figure 6), supporting the conclusion that the β-hairpin contributes to productive PCNA loading. This loading delay likely underlies the reduced rate of primer extension observed in the Pol ε assay (Figure 7), consistent with impaired formation of processive polymerase– clamp complexes.

(2) I did not see the method describing how the 2D classes were quantified to evaluate the impact of the Ctf18 beta hairpin deletion on complex formation. Please add the relevant information. 

The relevant information has been added to the Method section:

“For quantification of complex stability, the number of particles contributing to each 2D class was extracted from the classification metadata (Datasets 1 and 3). All classes showing isolated PCNA rings were summed and compared to the total number of particles in classes representing intact CTF18-RFC–PCNA complexes. This analysis was performed for both wild-type and β-hairpin deletion mutant datasets. Notably, no 2D classes corresponding to free PCNA were observed in the wild-type dataset, whereas in the mutant dataset, a substantial fraction of particles corresponded to isolated PCNA, suggesting reduced stability of the mutant complex.”

Minor point: 

(1) Page 2, line 25. Detail what type of mobility is referred to. Do you mean flexibility in the EM-map? 

We have clarified this. The text now reads:

“The unique RFC1 (Ctf18) large subunit of CTF18-RFC, which based on the cryo-EM map shows high relative flexibility, is anchored to PCNA through an atypical low-affinity PIP box”

(2) Page 4, line 82. Please introduce CMGE, or at least state what the abbreviation stands for. 

This has been addressed.

(3) Page 4, line 89. Specify that the architecture of the HUMAN CTF18-RFC module is not known, as the yeast one has been published. 

At the time our study was initiated, the architecture of the human CTF18-RFC module was unknown. A structure of the human complex was published by another group during the final stages of our work and is now properly acknowledged in the Discussion.

(4) Page 6. Is it possible to illustrate why the autoinhibited state cannot bind to DNA? A visual representation would be nice. 

We thank the reviewer for this suggestion. Figure 4b in the original manuscript already illustrates why the autoinhibited, overtwisted conformation of the CTF18-RFC pentamer cannot accommodate DNA. In this state, the inner chamber of the loader is sterically occluded, precluding the binding of duplex DNA.

Reviewer #3 (Recommendations for the authors): 

We thank Reviewer #3 for their constructive feedback and positive overall assessment of our work.

We also thank the reviewer for their remarks on the use of Mg depletion to halt hydrolysis. Magnesium is an essential cofactor for ATP hydrolysis, and its depletion is expected to effectively prevent catalysis by destabilizing the transition state, possibly more completely than the use of slowly hydrolysable analogues such as ATPγS. We have recently employed Mg^²+ depletion to successfully trap a pre-hydrolytic intermediate in a replicative AAA+ helicase engaged in DNA unwinding (Shahid et al., Nature, 2025). This precedent supports the rationale for our choice, and the reference has now been included in the revised manuscript.

I think the authors deposited the FSC curve for the +Mg structure in the -Mg structure PDB/EMDB entry according to the validation report. 

We thank the reviewer for their careful inspection of the deposition materials. The discrepancy in the deposited FSC curve has now been corrected, and the appropriate FSC curves have been assigned to the correct PDB/EMDB entries.

Scale back this expanded edit to only one longer paragraph and make sure to recalibrate the section with an awareness of the Section header's organizing principle being temporal, seasonal patterns of activity. Revise the prose to help frame this from the start and move some the discourse analysis work being done here to the linguistic analysis section, effectively coordinate the transition to highlight CUNY discourse conventions as part of the local public sphere of these subreddits

Reviewer #1 (Public review):

This paper by Troyer et al. measures the positioning and diffusivity of RNaseE-mEos3.2 proteins in E. coli as a function of rifampicin treatment, compares RNaseE to other E. coli proteins, and measures the effect of changes in domain composition on this localization and motion. The straightforward study is thoroughly presented, including very good descriptions of the imaging parameters and the image analysis/modeling involved, which is good because the key impact of the work lies in presenting this clear methodology for determining the position and mobility of a series of proteins in living bacteria cells.

Most of my concerns in the original review were addressed in this round of revisions based on new text, experiments, and analysis, including most notably:

-A revision of the abstract to focus on the actual topic of the manuscript.<br /> -New experiments (Fig. S1) to confirm that there is no significant undercounting of the fast-moving cytoplasmic population<br /> -Removing the experiments discussion related to degradosome proteins rather than overstating results.<br /> -Improving the logical flow and writing.

One minor concern still remains:

-Though the discussion of the rifampicin-treated cells is improved, this experiment is motivated (line 196) as "To test the effect of mRNA substrates on RNE diffusion", but the conclusion of the paragraph (based on similarities with the effect on LacY) is that the observed changes are due to factors other than the concentration of mRNA substrates, such that the effect of mRNA has not been tested.

Reviewer #3 (Public review):

Summary:

The manuscript by Troyer et al quantitatively measured the membrane localization and diffusion of RNase E, an essential ribonuclease for mRNA turnover as well as tRNA and rRNA processing in bacteria cells. Using single-molecule tracking in live E. coli cells, the authors investigated the impact of membrane targeting sequence (MTS) and the C-terminal domain (CTD) on the membrane localization and diffusion of RNase E under various perturbations. Finally, the authors tried to correlate the membrane localization of RNase E to its function on co- and post-transcriptional mRNA decay using lacZ mRNA as a model.

The major findings of the manuscripts include:

(1) WT RNase E is mostly membrane localized via MTS, confirming previous results. The diffusion of RNase E is increased upon removal of MTS or CTD, and more significantly increased upon removal of both regions.

(2) By tagging RNase E MTS and different lengths of LacY transmembrane domain (LacY2, LacY6 or LacY12) to mEos3.2, the results demonstrate that short LacY transmembrane sequence (LacY2 and LacY6) can increase the diffusion of mEos3.2 on the membrane compared to MTS, further supported by the molecular dynamics simulation. The similar trend was roughly observed in RNase E mutants with MTS switched to LacY transmembrane domains.

(3) The removal of RNase E MTS significantly increases the co-transcriptional degradation of lacZ mRNA, but has minimal effect on the post-transcriptional degradation of lacZ mRNA. Removal of CTD of RNase E overall decrease the mRNA decay rates, suggesting the synergistic effect of CTD on RNase E activity.

Strengths:

(1) The manuscript is clearly written with very detailed methods description and analysis parameters.

(2) The conclusions are mostly supported by the data and analysis.

(3) Some of the main conclusions are interesting and important for understanding the cellular behavior and function of RNase E.

Weaknesses:

The authors have addressed my previous concerns in the revised manuscript.

Comments on revisions:

I have one additional comment. When interpreting the small increase in the diffusion coefficient of RNase E when treating the cell with rifampicin, the authors rule out the possibility that only a small fraction of RNase E interacts with mRNA and suggest that it is more likely the mRNA-RNase E interaction is transient. However, I am wondering about an alternative possibility that RNase E prefers mRNAs with low ribosome density or even untranslated mRNAs?

Author response:

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

Reviewer #1 (Public review): 

This paper measures the positioning and diffusivity of RNaseE-mEos3.2 proteins in E. coli as a function of rifampicin treatment, compares RNaseE to other E. coli proteins, and measures the effect of changes in domain composition on this localization and motion. The straightforward study is thoroughly presented, including very good descriptions of the imaging parameters and the image analysis/modeling involved, which is good because the key impact of the work lies in presenting this clear methodology for determining the position and mobility of a series of proteins in living bacteria cells. 

Thank you for the nice summary and positive feedback on the descriptions and methodology. 

My key notes and concerns are listed below; the most important concerns are indicated with asterisks. 

(1) The very start of the abstract mentions that the domain composition of RNase E varies among species, which leads the reader to believe that the modifications made to E. coli RNase E would be to swap in the domains from other species, but the experiment is actually to swap in domains from other E. coli proteins. The impact of this work would be increased by examining, for instance, RNase E domains from B. subtilis and C. crescentus as mentioned in the introduction. 

Thank you for the suggestions. We agree that the sentence may convey an unintended expectation. Our original intention was to note the presence and absence of certain domains of RNase E (e.g. membrane-binding motif and CTD) vary across species, rather than the actual sequence variations. To avoid any misinterpretation, we decided to remove the sentence from the abstract. Using the domains of B. subtilis and C. crescentus RNase E in E. coli is a very interesting suggestion, but we will leave that for a future study. 

(2) Furthermore, the introduction ends by suggesting that this work will modulate the localization, diffusion, and activity of RNase E for "various applications", but no applications are discussed in the discussion or conclusion. The impact of this work would be increased by actually indicating potential reasons why one would want to modulate the activity of RNase E. 

Thank you for this suggestion. For example, an E. coli strain expressing membranebound RNase E without CTD can help stabilize mRNAs and enhance protein expression. In fact, this idea was used in a commercial BL21 cell line (Invitrogen’s One Shot BL21 Star), to increase the yield of protein expression. We also think that environmentally modulated MB% of RNase E can be useful for controlling the mRNA half-lives and protein expression levels in different conditions. We discussed these ideas at the end of the Discussion.

(3) Lines 114 - 115: "The xNorm histogram of RNase E shows two peaks corresponding to each side edge of the membrane": "side edge" is not a helpful term. I suggest instead: "...corresponding to the membrane at each side of the cell" 

Thank you. We made the suggested change.

(4) A key concern of this reviewer is that, since membrane-bound proteins diffuse more slowly than cytoplasmic proteins, some significant undercounting of the % of cytoplasmic proteins is expected due to decreased detectability of the faster-moving proteins. This would not be a problem for the LacZ imaging where essentially all proteins are cytoplasmic, but would significantly affect the reported MB% for the intermediate protein constructs. How is this undercounting considered and taken into account? One could, for instance, compare LacZ vs. LacY (or RNase E) copy numbers detected in fixed cells to those detected in living cells to estimate it.  

Thank you for raising this point and suggesting a possible way to address this. We compared the number of tracks for mEos3.2-fused proteins in live vs fixed cells and tested the undercounting effect of cytoplasmic molecules. We compared WT RNase E molecules in live and fixed cells and found that there are about 50% lower molecules detected in the fixed cells, which agrees with the expectation that fluorescent proteins lose their signal upon fixation. Similarly, cytoplasmic RNase E (RNase E ΔMTS) copy number was also ~50% less in the fixed cells compared to live cells. If cytoplasmic molecules were undercounted compared membrane-bound molecules in live cells, fixation would reduce the copy number less than 50%. The comparable ratio of 50% indicates that the undercounting issue is not significant. This control analysis is provided in Figure S1B-C, and we made corresponding textual change in the result section as below:

For this analysis, we first confirmed that proteins localized on the membrane and in the cytoplasm are detected with equal probability, despite differences in their mobilities (Fig. S1B-C). 

(5) The rifampicin treatment study is not presented well. Firstly, it is found that LacY diffuses more rapidly upon rifampicin treatment. This change is attributed to changes in crowding at the membrane due to mRNA. Several other things change in cells after adding rif, including ATP levels, and these factors should be considered. More importantly, since the change in the diffusivity of RNaseE is similar to the change in diffusivity of LacY, then it seems that most of the change in RNaseE diffusion is NOT due to RNaseE-mRNAribosome binding, but rather due to whatever crowding/viscosity effects are experienced by LacY (along these lines: the error reported for D is SEM, but really should be a confidence interval, as in Figure 1, to give the reader a better sense of how different (or similar) 1.47 and 1.25 are). 

We agree with the reviewer that upon rifampicin treatment, RNase E’s D increases to a similar extent as that of LacY. Hence, the increase likely arises from a factor common to both proteins. We have added the reviewer’s suggested interpretation as a possible explanation in the manuscript as below. 

The similar fold change in D_RNE and D_LacY upon rif treatment suggests that the change in RNE diffusion may largely be attributed to physical changes in the intracellular environment (such as reduced viscosity or macromolecular crowding[41,42]), rather than a loss of RNA-RNE interactions.

As requested by the reviewer, we have provided confidence intervals for our D values in Table S8. Because these intervals are very narrow, we chose to present the SEM as the error metric for D and have also reported the corresponding errors for the fold-change values whenever we describe the fold differences between D values. 

(6) Lines 185-189: it is surprising to me that the CTD mutants both have the same change in D (5.5x and 5.3x) relative to their full-length counterparts since D for the membranebound WT protein should be much less sensitive to protein size than D for the cytoplasmic MTS mutant. Can the authors comment? 

Perhaps the reviewer understood that these differences are the ratios between +/-CTD (e.g. WT RNE vs ΔCTD). However, the differences we mentioned were from membrane-bound vs cytoplasmic versions of RNase E with comparable sizes (e.g. WT RNase E vs RNase E ΔMTS). We modified text and added a summary sentence at the end of the paragraph to clarify the point.

We found that D_ΔMTS is ~5.5 times that of D_RNE (Fig. 3B). [...] Together, these results suggest that the membrane binding reduces RNE mobility by a factor of 5.

That being said, we also realized a similar fold difference between +/-CTD. Specifically, WT RNE vs RNE ΔCTD (both membrane-bound) show a ~4.1-fold difference and RNE ΔMTS vs RNE ΔMTS ΔCTD (both cytoplasmic) show ~3.9-fold difference. We do not currently do not have a clear explanation for this pattern. Given that these two pairs have a similar change in mass, we speculate that the relationship between D and molecular mass may be comparable for membrane-bound and free-floating RNE variants. 

(7) Lines 190-194. Again, the confidence intervals and experimental uncertainties should be considered before drawing biological conclusions. It would seem that there is "no significant change" in the rhlB and pnp mutants, and I would avoid saying "especially for ∆pnp" when the same conclusion is true for both (one shouldn't say 1.04 is "very minute" and 1.08 is just kind of small - they are pretty much the same within experiments like this). 

Thank you for raising this point, which we fully agree with. That being said, we decided to remove results related to the degradosome proteins to improve the flow of the paper. We are preparing another paper related to the RNA degradosome complex formation. 

(8) Lines 221-223 " This is remarkable because their molecular masses (and thus size) are expected to be larger than that of MTS" should be reconsidered: diffusion in a membrane does not follow the Einstein law (indeed lines 223-225 agree with me and disagree with lines 221-223). (Also the discussion paragraph starting at line 375). Rather, it is generally limited by the interactions with the transmembrane segments with the membrane. So Figure 3D does not contain the right data for a comparison, and what is surprising to me is that MTS doesn't diffuse considerably faster than LacY2. 

We agree with the reviewer’s point that diffusion in a membrane does not follow the Stokes-Einstein law. That is why we introduced Saffman’s model. However, even in this model, proteins of larger size (or mass) should be slower than smaller size (a reason why we presented Figure 3D, now 4D). In other words, both Einstein and Saffman models predict that larger particles diffuse slower, although the exact scaling relationship differs between two models. Here, we assume that mass is related to the size. Contrary to Saffman’s model for membrane proteins, LacY2 diffuses faster than MTS despite of large size. Using MD simulations, we showed that this discrepancy can be explained by different interaction energies as the reviewer mentioned. This analysis further demonstrates that the size is not the only factor to consider protein diffusion in the membrane. We edited the paragraph to clarify the expectations and our interpretations.

According to the Stokes-Einstein relation for diffusion in simple fluids[49] and the Saffman-Delbruck diffusion model for membrane proteins, D decreases as particle size increases, albeit with different scaling behaviors. […] Thus, if size (or mass) were the primary determinant of diffusion, LacY2 and LacY6 would diffuse more slowly than the smaller MTS. The observed discrepancy instead implies that D may be governed by how each motif interacts with the membrane. For example, the way that TM domains are anchored to the membrane may facilitate faster lateral diffusion with surrounding lipids. 

(9) The logical connection between the membrane-association discussion (which seems to ignore associations with other proteins in the cell) and the preceding +/- rifampicin discussion (which seeks to attribute very small changes to mRNA association) is confusing.

Thank you for raising this point. We re-arranged the second result section to present diffusion due to membrane binding first before rifampicin. Furthermore, we stated our hypothesis and expectations in the beginning of the results section. This addition will legitimate our logic flow.

(10) Separately, the manuscript should be read through again for grammar and usage. For instance, the title should be: "Single-molecule imaging reveals the *roles* of *the* membrane-binding motif and *the* C-terminal domain of RNase E in its localization and diffusion in Escherichia coli". Also, some writing is unwieldy, for instance, "RNase E's D" would be easier to read if written as D_{RNaseE}. (underscore = subscript), and there is a lot of repetition in the sentence structures. 

Thank you for catching grammar mistakes. We went through extensive proofreading to avoid these mistakes and also used simple notation suggested by the reviewer, such as D_RNE, to make it easier to read. Thank you again for your suggestions.

Reviewer #2 (Public review): 

Summary: 

Troyer and colleagues have studied the in vivo localisation and mobility of the E.coli RNaseE (a protein key for mRNA degradation in all bacteria) as well as the impact of two key protein segments (MTS and CTD) on RNase E cellular localisation and mobility. Such sequences are important to study since there is significant sequence diversity within bacteria, as well as a lack of clarity about their functional effects. Using single-molecule tracking in living bacteria, the authors confirmed that >90% of RNaseE localised on the membrane, and measured its diffusion coefficient. Via a series of mutants, they also showed that MTS leads to stronger membrane association and slower diffusion compared to a transmembrane motif (despite the latter being more embedded in the membrane), and that the CTD weakens membrane binding. The study also rationalised how the interplay of MTS and CTD modulate mRNA metabolism (and hence gene expression) in different cellular contexts. 

Strengths: 

The study uses powerful single-molecule tracking in living cells along with solid quantitative analysis, and provides direct measurements for the mobility and localisation of E.coli RNaseE, adding to information from complementary studies and other bacteria. The exploration of different membrane-binding motifs (both MTS and CTD) has novelty and provides insight on how sequence and membrane interactions can control function of protein-associated membranes and complexes. The methods and membrane-protein standards used contribute to the toolbox for molecular analysis in live bacteria. 

Thank you for the nice summary of our work and positive comments about the paper’s strengths.

Weaknesses: 

The Results sections can be structured better to present the main hypotheses to be tested. For example, since it is well known that RNase E is membrane-localised (via its MTS), one expects its mobility to be mainly controlled by the interaction with the membrane (rather than with other molecules, such as polysomes and the degradosome). The results indeed support this expectation - however, the manuscript in its current form does not lay down the dominant hypothesis early on (see second Results chapter), and instead considers the rifampicin-addition results as "surprising"; it will be best to outline the most likely hypotheses, and then discuss the results in that light. 

Thank you for this comment. We addressed this point by stating our main hypothesis from the beginning of the results section. We also agree with the reviewer that the membrane binding effect should be discussed first; hence, we re-arranged the result section. In the revised manuscript, we discuss the effect of membrane binding on diffusion first, followed by rif effects.

Similarly, the authors should first discuss the different modes of interaction for a peripheral anchor vs a transmembrane anchor, outline the state of knowledge and possibilities, and then discuss their result; in its current version, the ms considers the LacY2 and LacY6 faster diffusion compared to MTS "remarkable", but considering the very different mode of interaction, there is no clear expectation prior to the experiment. In the same section, it would be good to see how the MD simulations capture the motion of LacY6 and LacY12, since this will provide a set of results consistent with the experimental set. 

Thank you for pointing this out. In fact, there is little discussion in the literature about the different modes of interaction for a peripheral anchor vs a transmembrane anchor. To our knowledge, our work (experiments and MD simulations) is the first that directly compared the two to reveal that the peripheral anchor has higher interaction energy than the transmembrane anchor. We added a sentence “Despite the prevalence of peripheral membrane proteins, how they interact with the membrane and how this differs from TM proteins remain poorly understood”. Furthermore, we added the MD simulation result of LacY6 and LacY12 in Figure 4E-F.

The work will benefit from further exploration of the membrane-RNase E interactions; e.g., the effect of membrane composition is explored by just using two different growth media (which on its own is not a well-controlled setting), and no attempts to change the MTS itself were made. The manuscript will benefit from considering experiments that explore the diversity of RNaseE interactions in different species; for example, the authors may want to consider the possibility of using the membrane-localisation signals of functional homologs of RNaseE in different bacteria (e.g., B. subtilis). It would be good to look at the effect of CTD deletions in a similar context (i.e., in addition to the MTS substitution by LacY2 and LacY6). 

Thank you very much for this suggestion. During revision, we engineered point mutations in MTS and analyzed critical hydrophobic residues for membrane binding. We characterized MB% in both +/-CTD variants (Fig. 2 and Fig. S6) and their effect on lacZ mRNA degradation (Fig. 6). We will leave the use of membrane motif of B. subtilis RNase E for future study. 

The manuscript will benefit from further discussion of the unstructured nature of the CTD, especially since the RNase CTD is well known to form condensates in Caulobacter crescentus; it is unclear how the authors excluded any roles for RNaseE phase separation in the mobility of RNaseE in E.coli cells. 

Yes, we agree with the reviewer that the intrinsically disordered nature of the CTD might contribute to condensate formation. We explored this possibility using both epifluorescence microscopy (with a YFP fusion) and single-molecule imaging with cluster analysis (using an mEos3.2 fusion). Please see Figure S8. We did observe some weak de-clustering of RNase E upon CTD deletion. In the current study, we are unable to quantify the extent to which clustering contributes to the slow diffusion of RNase E. However, we speculate that the clustering may be linked to the low MB% of certain RNE mutants containing CTD, and we discussed this possibility in the Discussion.

[…] further supporting that the CTD decreases membrane association across RNE variants. We speculate that this effect may be related to the CTD’s role in promoting phase-separated ribonucleoprotein condensates, as observed in Caulobacter crescentus[19]. In E. coli, we also observed a modest increase in the clustering tendency of RNE compared to ΔCTD (Fig. S8). 

Some statements in the Discussion require support with example calculations or toning down substantially. Specifically, it is not clear how the authors conclude that RNaseE interacts with its substrate for a short time (and what this time may actually be); further, the speculation about the MTS "not being an efficient membrane-binding motif for diffusion" lacks adequate support as it stands. 

Thank you for these points. To elaborate our point on transient interaction between RNase E and RNA, we added a sentence “Specifically, if RNE interacts with mRNAs for ~20 ms or less, the slow-diffusing state would last shorter than the frame interval and remain undetected in our experiment.” Also, we added this sentence in the discussion.

One possible explanation is that RNA-bound RNE (and RNase Y) is short-lived compared to our frame interval (~20 ms), unlike other RNA-binding proteins related to transcription and translation, interacting with RNA for ~1 min for elongation [48].

Plus, we clarified the wording used in the second sentence that the reviewer pointed out as follows,

Lastly, the slow diffusion of the MTS in comparison to LacY2 and LacY6 suggests that MTS is less favorable for rapid lateral motion in the membrane. 

Reviewer #3 (Public review): 

Summary: 

The manuscript by Troyer et al quantitatively measured the membrane localization and diffusion of RNase E, an essential ribonuclease for mRNA turnover as well as tRNA and rRNA processing in bacteria cells. Using single-molecule tracking in live E. coli cells, the authors investigated the impact of membrane targeting sequence (MTS) and the Cterminal domain (CTD) on the membrane localization and diffusion of RNase E under various perturbations. Finally, the authors tried to correlate the membrane localization of RNase E to its function on co- and post-transcriptional mRNA decay using lacZ mRNA as a model. 

The major findings of the manuscripts include: 

(1) WT RNase E is mostly membrane localized via MTS, confirming previous results. The diffusion of RNase E is increased upon removal of MTS or CTD, and more significantly increased upon removal of both regions. 

(2) By tagging RNase E MTS and different lengths of LacY transmembrane domain (LacY2, LacY6, or LacY12) to mEos3.2, the results demonstrate that short LacY transmembrane sequence (LacY2 and LacY6) can increase the diffusion of mEos3.2 on the membrane compared to MTS, further supported by the molecular dynamics simulation. A similar trend was roughly observed in RNase E mutants with MTS switched to LacY transmembrane domains. 

(3) The removal of RNase E MTS significantly increases the co-transcriptional degradation of lacZ mRNA, but has minimal effect on the post-transcriptional degradation of lacZ mRNA. Removal of CTD of RNase E overall decreases the mRNA decay rates, suggesting the synergistic effect of CTD on RNase E activity. 

Strengths: 

(1) The manuscript is clearly written with very detailed method descriptions and analysis parameters. 

(2) The conclusions are mostly supported by the data and analysis. 

(3) Some of the main conclusions are interesting and important for understanding the cellular behavior and function of RNase E. 

Thank you for your thorough summary of our work and positive comments.

Weaknesses: 

(1) Some of the observations show inconsistent or context-dependent trends that make it hard to generalize certain conclusions. Those points are worth discussion at least. Examples include: 

(a) The authors conclude that MTS segment exhibits reduced MB% when succinate is used as a carbon source compared to glycerol, whereas LacY2 segment maintains 100% membrane localization, suggesting that MTS can lose membrane affinity in the former growth condition (Ln 341-342). However, the opposite case was observed for the WT RNase E and RNase E-LacY2-CTD, in which RNase E-LacY2-CTD showed reduced MB% in the succinate-containing M9 media compared to the WT RNase E (Ln 264-267). This opposite trend was not discussed. In the absence of CTD, would the media-dependent membrane localization be similar to the membrane localization sequence or to the fulllength RNase E? 

This is a great point. Thank you for pointing out the discrepancy in data. We think the weak membrane interaction of RNaseE-lacY2-CTD likely stems from the structure instability in the presence of the CTD. Our data shows that an RNase E variant with a cytoplasmic population under a normal growth condition exhibits a greater cytoplasmic fraction in a poor growth media. In contrast, RNaseE-MTS and RNaseE-LacY2 lacking the CTD both showed 100% MB% under both normal and poor growth conditions. These results are presented in Figure S6 and further discussed in the Discussion section.

The loss of MB% in LacY2-based RNE was observed only in the presence of the CTD (Fig. S6D), suggesting that the CTD negatively affects membrane binding of RNE, possibly by altering protein conformation. In fact, all ΔCTD RNE mutants we tested exhibited higher MB% than their CTD-containing counterparts (Fig. S6A-B). 

(b) When using mEos3.2 reporter only, LacY2 and LacY6 both increase the diffusion of mEos3.2 compared to MTS. However, when inserting the LacY transmembrane sequence into RNase E or RNase E without CTD, only the LacY2 increases the diffusion of RNase E. This should also be discussed. 

Thank you for raising this point. As the reviewer pointed out, as the membrane motifs, both LacY2 and LacY6 diffuse faster than the MTS, but when they are fused to RNE, only LacY2-based RNE diffuses faster than MTS-based RNE. We speculate that it is possibly due to a structural reason—having four (large) LacY6 in a tetrameric arrangement may cancel out the original fast-diffusing property of LacY6. We added this idea in the result section:

This result may be due to the high TM load (24 helices) created by four LacY6 anchors in the RNE tetramer. Although all constructs are tetrameric, the 24-helix load (LacY6), compared with 8 (LacY2) and 4 (MTS), likely enlarges the membrane-embedded footprint and increases drag, thereby changing the mobility advantages assessed as standalone membrane anchors.

(2) The authors interpret that in some cases the increase in the diffusion coefficient is related to the increase in the cytoplasm localization portion, such as for the LacY2 inserted RNase E with CTD, which is rational. However, the authors can directly measure the diffusion coefficient of the membrane and cytoplasm portion of RNase E by classifying the trajectories based on their localizations first, rather than just the ensemble calculation. 

Thank you for this suggestion. Currently, because of the 2D projection effect from imaging, we cannot clearly distinguish which individual tracks are from the cytoplasm or from the inner membrane based on the localization. Therefore, we are unable to assign individual tracks as membrane-bound or cytoplasmic. However, we can demonstrate that the xNorm data can be separated into two different spatial populations based on the diffusion coefficient. D. That is we can plot xNorm of slow tracks vs xNorm of fast tracks. This analysis showed that the slow tracks have LacY-like xNorm profiles while the fast tracks have LacZ-like xNorm profiles, also quantitatively supporting our MB% fitting results. We have added this analysis to Figure S2.

(3) The error bars of the diffusion coefficient and MB% are all SEM from bootstrapping, which are very small. I am wondering how much of the difference is simply due to a batch effect. Were the data mixed from multiple biological replicates? The number of biological replicates should also be reported. 

Thank you for raising this point. In the original manuscript, we reported the number of tracks analyzed and noted that all data was from at least three separate biological replicates (measurements were repeated at least three different days). Furthermore, in the revised manuscript, we have provided the number of cells imaged in Table S6. 

(4) Some figures lack p-values, such as Figures 4 and 5C-D. Also, adding p-values directly to the bar graphs will make it easier to read. 

Thank you for checking these details. We added p values in the graphs showing k_d1 and k_d2 (Table S7).

Reviewer #2 (Recommendations for the authors): 

Minor and technical points: 

(1) Clarity and flow will be improved if each section first highlights the objective for the experiments that are described (e.g., line 240). 

Thank you for the suggestion. We addressed this point by editing the beginning of each subsection in the Results. 

(2) Line 272 (and elsewhere)."1.33-times faster is wrong". The authors mean 33% faster (from 0.075 to 1, see Figure 4G), and not 133% faster. Needs fixing. 

Thanks for pointing this out. We changed this as well as other incidences where we talk about the fold difference. For example, this particular incidence was changed to:

Indeed, in the absence of the CTD, we found that the D of LacY2-based RNE was 1.33 ± 0.01 times as fast as the MTS-based RNE. 

(3) The authors need to consider the fitting of two species on their D population. e.g., how will a 93% - 7% split between diffusive species would have looked for the distribution in S4B? Note also the L1 profile in Fig S4C - while it is not hugely different from Figure S4B, the analysis gives a 41% amplitude for the fast-diffusing species. The 2-species analysis can also be used on some of the samples with much higher cytoplasmic components. Further, tracks that are in the more central region can be analysed to see whether the fast-diffusing species increase in amplitude. 

Thank you for this comment. The D histograms of L1 and RNase E show a dominant peak at around 0.015, but L1 has a residual population in the shoulder (note the difference between L1’s experimental data and D1 fit, a yellow line in now Figure S3B). This residual shoulder population is absent in the D histogram of RNase E. We also performed two-species analysis as suggested by the reviewer and provided the result in Figure S3C. The analysis shows that the two-population fit (black line) is very close to one one-population fit (yellow line). While we agree with the reviewer that subpopulation analysis is helpful for other proteins that show <90% MB% (>10% significant cytoplasmic population). we found it useful to divide xNorm histogram into two populations based on the diffusivity (rather than doing two-population fit to the D histogram, which does not have spatial information). This analysis, shown in Figure S2, supports our MB% fit results.

(4) The authors suggest that the sequestration of RNaseE to the membrane limits its interaction with cytoplasmic mRNAs, and may increase mRNA lifetime. While this is true and supported by the authors' preprint (Ref15), it will also be good to consider (and discuss) that highly-transcribed regions are in the nucleoid periphery (and thus close to the membrane) and that ribosomes/polysomes are likewise predominantly peripheral (coregulation of transcription/translation) and membrane proximal. 

This is an interesting point, which we appreciate very much. The lacZ gene, when induced, is shown to move to the nucleoid periphery (Yang et al. 2019, Nat Comm). Also, in our preprint (Ref 15), we engineered to have lacZ closer to the membrane, by translationally fusing it to lacY. However, the degradation rate of lacZ mRNA was not enhanced by the proximity to the membrane (for both k<Sub>d1</sub> and k_d2). For lacZ mRNA, we mainly see the change in k_d1 when RNE localization changes. We think it is due to the slow diffusion of the nascent mRNA (attached to the chromosome) and the slow diffusion of membrane-bound RNE, such that regardless of the location of the nascent mRNA, the degradation by the membrane-bound RNE is inefficient. Only when RNE is free diffusing in the cytoplasm, it seems to increase k_d1 (the decay of nascent mRNAs).

Reviewer #3 (Recommendations for the authors):

(1) It will increase the clarity of the manuscript if the authors can provide better nomenclatures for different constructs, such as for different membrane targeting sequences fused to mEos3.2, full-length RNase E, or CDT truncated RNaseE. 

Thank you for this suggestion. We agree that many constructions were discussed, and their naming can be confusing. To help with clarity, we have abbreviated RNase E as RNE throughout the text where appropriate. 

(2) Line 342, Figure S7D should be cited instead of S6D. 

Thank you for finding this error. We made a proper change in the revised manuscript.

Author response:

Reviewer #1 (Public review):

Summary:

The authors describe the results of a single study designed to investigate the extent to which horizontal orientation energy plays a key role in supporting view-invariant face recognition. The authors collected behavioral data from adult observers who were asked to complete an old/new face matching task by learning broad-spectrum faces (not orientation filtered) during a familiarization phase and subsequently trying to label filtered faces as previously seen or novel at test. This data revealed a clear bias favoring the use of horizontal orientation energy across viewpoint changes in the target images. The authors then compared different ideal observer models (cross-correlations between target and probe stimuli) to examine how this profile might be reflected in the image-level appearance of their filtered images. This revealed that a model looking for the best matching face within a viewpoint differed substantially from human data, exhibiting a vertical orientation bias for extreme profiles. However, a model forced to match targets to probes at different viewing angles exhibited a consistent horizontal bias in much the same manner as human observers.

Strengths:

I think the question is an important one: The horizontal orientation bias is a great example of a low-level image property being linked to high-level recognition outcomes, and understanding the nature of that connection is important. I found the old/new task to be a straightforward task that was implemented ably and that has the benefit of being simple for participants to carry out and simple to analyze. I particularly appreciated that the authors chose to describe human data via a lower-dimensional model (their Gaussian fits to individual data) for further analysis. This was a nice way to express the nature of the tuning function, favoring horizontal orientation bias in a way that makes key parameters explicit. Broadly speaking, I also thought that the model comparison they include between the view-selective and view-tolerant models was a great next step. This analysis has the potential to reveal some good insights into how this bias emerges and ask finegrained questions about the parameters in their model fits to the behavioral data.

We thank the reviewer for their positive appraisal of the importance of our research question as well as of the soundness of our approach to it.

Weaknesses:

I will start with what I think is the biggest difficulty I had with the paper. Much as I liked the model comparison analysis, I also don't quite know what to make of the view-tolerant model. As I understand the authors' description, the key feature of this model is that it does not get to compare the target and probe at the same yaw angle, but must instead pick a best match from candidates that are at different yaws. While it is interesting to see that this leads to a very different orientation profile, it also isn't obvious to me why such a comparison would be reflective of what the visual system is probably doing. I can see that the view-specific model is more or less assuming something like an exemplar representation of each face: You have the opportunity to compare a new image to a whole library of viewpoints, and presumably it isn't hard to start with some kind of first pass that identifies the best matching view first before trying to identify/match the individual in question. What I don't get about the view-tolerant model is that it seems almost like an anti-exemplar model: You specifically lack the best viewpoint in the library but have to make do with the other options. Again, this is sort of interesting and the very different behavior of the model is neat to discuss, but it doesn't seem easy to align with any theoretical perspective on face recognition. My thinking here is that it might be useful to consider an additional alternate model that doesn't specifically exclude the best-matching viewpoint, but perhaps condenses appearance across views into something like a prototype. I could even see an argument for something like the yaw-averages presented earlier in the manuscript as the basis for such a model, but this might be too much of a stretch. Overall, what I'd like to see is some kind of alternate model that incorporates the existence of the best-match viewpoint somehow, but without the explicit exemplar structure of the view-specific model.

The view-tolerant model was designed so that identity needed to be abstracted away from variations in yaw to support face recognition. We believe this model aligns with the notion of tolerant recognition.

The tolerance of identity recognition is presumably empowered by the internal representation of the natural statistics of identity, i.e. the stable traits and (idiosyncratic) variability of a face, which builds up through the varied encounters with a given face (Burton, Jenkins et al. 2005, Burton, Jenkins and Schweinberger 2011, Jenkins and Burton 2011, Jenkins, White et al. 2011, Burton, Kramer et al. 2016, Menon, Kemp and White 2018).

The average of various images of a face provides its appearance distribution (i.e., variability) and central tendency (i.e., stable properties; Figure 1) and could be used as a reasonable proxy of its natural statistical properties (Burton, Jenkins et al. 2005). We thus believe that the alternate model proposed by the reviewer is relevant to existing theories of face identity recognition and agree that our current model observers do not fully capture this aspect. It is thus an excellent idea to examine the orientation tuning profile of a model observer that compares a specific view of a face to the average encompassing all views of a face identity. Since the horizontal range is proposed to carry the view-stable cues to identity, we expect that such a ‘viewpoint-average’ model observer will perform best with horizontally filtered faces and that its orientation tuning profile will significantly predict human performance across views. We expect the viewpointtolerant and viewpoint-average observers will behave similarly as they manifest the stability of the horizontal identity cues across variations in viewpoint.

Besides this larger issue, I would also like to see some more details about the nature of the crosscorrelation that is the basis for this model comparison. I mostly think I get what is happening, but I think the authors could expand more on the nature of their noise model to make more explicit what is happening before these cross-correlations are taken. I infer that there is a noise-addition step to get them off the ceiling, but I felt that I had to read between the lines a bit to determine this.

The view-selective model responded correctly whenever successfully matching a given face identity at a specific viewpoint to itself. Since there was an exact match in each trial, resulting in uninformative ceiling performance, we decreased the signal-to-noise ratio (SNR) of the target and probe images to .125 (face RMS contrast: .01; noise RMS contrast: .08). In every trial, target and probe faces were each combined with 10 different random noise patterns. SNR was adjusted so that the overall performance of the view-selective model was in the range of human performance. We will describe these important aspects in the methods and add a supplemental with the graphic illustration of the d’ distributions of each model and human observers.

Another thing that I think is worth considering and commenting on is the stimuli themselves and the extent to which this may limit the outcomes of their behavioral task. The use of the 3D laserscanned faces has some obvious advantages, but also (I think) removes the possibility for pigmentation to contribute to recognition, removes the contribution of varying illumination and expression to appearance variability, and perhaps presents observers with more homogeneous faces than one typically has to worry about. I don't think these negate the current results, but I'd like the authors to expand on their discussion of these factors, particularly pigmentation. Naively, surface color and texture seem like they could offer diagnostic cues to identity that don't rely so critically on horizontal orientations, so removing these may mean that horizontal bias is particularly evident when face shape is the critical cue for recognition.

We indeed got rid of surface color by converting images to gray scales. While we acknowledge that the conversion to grayscales may have removed one potential source of surface information, it is unlikely that our stimuli fully eliminated the contribution of surface pigmentation in our study. Pigmentation refers to all surface reflectance property (Russell, Sinha et al. 2006) and hue (color) is only one surface cue among others. The grayscaled 3D laser scanned faces used here still contained natural variations in crucial surface cues such as skin albedo (i.e., how light or dark the surface appears) and texture (i.e., spatial variation in how light is reflected). Both color and grayscale stimuli (2D face pictures or 3D laser scanned faces like ours) have actually been used to disentangle the role of shape and surface cues to identity recognition (e.g., Troje and Bulthoff 1996, Vuong, Peissig et al. 2005, Russell, Sinha et al. 2006, Russell, Biederman et al. 2007, Jiang, Dricot et al. 2009).

More fundamentally, we demonstrated that the diagnosticity of the horizontal range of face information is not restricted to the transmission of shape cues. Our recent work has indeed shown that the processing of both face shape and surface most critically relies on horizontal information (Dumont, Roux-Sibilon and Goffaux 2024).

Reviewer #2 (Public review):

This study investigates the visual information that is used for the recognition of faces. This is an important question in vision research and is critical for social interactions more generally. The authors ask whether our ability to recognise faces, across different viewpoints, varies as a function of the orientation information available in the image. Consistent with previous findings from this group and others, they find that horizontally filtered faces were recognised better than vertically filtered faces. Next, they probe the mechanism underlying this pattern of data by designing two model observers. The first was optimised for faces at a specific viewpoint (viewselective). The second was generalised across viewpoints (view-tolerant). In contrast to the human data, the view-specific model shows that the information that is useful for identity judgements varies according to viewpoint. For example, frontal face identities are again optimally discriminated with horizontal orientation information, but profiles are optimally discriminated with more vertical orientation information. These findings show human face recognition is biased toward horizontal orientation information, even though this may be suboptimal for the recognition of profile views of the face.

One issue in the design of this study was the lowering of the signal-to-noise ratio in the viewselective observer. This decision was taken to avoid ceiling effects. However, it is not clear how this affects the similarity with the human observers.

The view-selective model responded correctly whenever successfully matching a given face identity at a specific viewpoint to itself. Since there was an exact match in each trial, resulting in uninformative ceiling performance, we decreased the signal-to-noise ratio (SNR) of the target and probe images to .125 (face RMS contrast: .01; noise RMS contrast: .08). In every trial, target and probe faces were each combined with 10 different random noise patterns. SNR was adjusted so that the overall performance of the view-selective model was in the range of human performance. We will describe these important aspects in the methods and add a supplemental with the graphic illustration of the d’ distributions of each model and human observers.

Another issue is the decision to normalise image energy across orientations and viewpoints. I can see the logic in wanting to control for these effects, but this does reflect natural variation in image properties. So, again, I wonder what the results would look like without this step.

Energy of natural images is disproportionately distributed across orientations (e.g., Hansen, Essock et al. 2003). Images of faces cropped from their background as used here contain most of their energy in the horizontal range (Keil 2009, Goffaux and Greenwood 2016, Goffaux 2019). If not normalized after orientation filtering, such uneven distribution of energy would boost recognition performance in the horizontal range across views. Normalization was performed across our experimental conditions merely to avoid energy from explaining the influence of viewpoint on the orientation tuning profile.

We are not aware of any systematic natural variations of energy across face views. To address this, we measured face average energy (i.e., RMS contrast) in the original stimulus set, i.e., before the application of any image processing or manipulation. Background pixels were excluded from these image analyses. Across yaws, we found energy to range between .11 and .14 on a 0 to 1 grayscale. This is moderate compared to the range of energy variations we measured across identities (from .08 to .18). This suggests that variations in energy across viewpoints are moderate compared to variations related to identity. It is unclear whether these observations are specific to our stimulus set or whether they are generalizable to faces we encounter in everyday life. They, however, indicate that RMS contrast did not substantially vary across views in the present study and suggest that RMS normalization is unlikely to have affected the influence of viewpoint on recognition performance.

Nonetheless, we acknowledge the importance of this issue regarding the trade-off between experimental control and stimulus naturalness, and we will refer to it explicitly in the methods section.

Despite the bias toward horizontal orientations in human observers, there were some differences in the orientation preference at each viewpoint. For example, frontal faces were biased to horizontal (90 degrees), but other viewpoints had biases that were slightly off horizontal (e.g., right profile: 80 degrees, left profile: 100 degrees). This does seem to show that differences in statistical information at different viewpoints (more horizontal information for frontal and more vertical information for profile) do influence human perception. It would be good to reflect on this nuance in the data.

Indeed, human performance data indicates that while identity recognition remains tuned to horizontal information, horizontal tuning shows some variation across viewpoints. We primarily focused on the first aspect because of its direct relevance to our research objective, but also discussed the second aspect: with yaw rotation, certain non-horizontal morphological features such as the jaw line or nose bridge, etc. may increasingly contribute to identity recognition, whereas at frontal or near frontal views, features are mostly horizontally-oriented (e.g., Keil 2008, Keil 2009). We will relate this part of the discussion more explicitly to the observation of the fluctuation of the peak location as a function of yaw.

Author response:

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

Reviewer 1:

The authors frequently refer to their predictions and theory as being causal, both in the manuscript and in their response to reviewers. However, causal inference requires careful experimental design, not just statistical prediction. For example, the claim that "algorithmic differences between those with BPD and matched healthy controls" are "causal" in my opinion is not warranted by the data, as the study does not employ experimental manipulations or interventions which might predictably affect parameter values. Even if model parameters can be seen as valid proxies to latent mechanisms, this does not automatically mean that such mechanisms cause the clinical distinction between BPD and CON, they could plausibly also refer to the effects of therapy or medication. I recommend that such causal language, also implicit to expressions like "parameter influences on explicit intentional attributions", is toned down throughout the manuscript.

Thankyou for this chance to be clearer in the language. Our models and paradigm introduce a from of temporal causality, given that latent parameter distributions are directly influenced by latent parameter estimates at a previous point in time (self-uncertainty and other uncertainty directly governs social contagion). Nevertheless, we appreciate the reviewers perspective and have now toned down the language to reflect this.

Abstract:

‘Our model makes clear predictions about the mechanisms of social information generalisation concerning both joint and individual reward.’

Discussion:

‘We can simulate this by modelling a framework that incorporates priors based on both self and a strong memory impression of a notional other (Figure S3).’

‘We note a strength of this work is the use of model comparison to understand algorithmic differences between those with BPD and matched healthy controls.’

Although the authors have now much clearer outlined the stuy's aims, there still is a lack of clarity with respect to the authors' specific hypotheses. I understand that their primary predictions about disruptions to self-other generalisation processes underlying BPD are embedded in the four main models that are tested, but it is still unclear what specific hypotheses the authors had about group differences with respect to the tested models. I recommend the authors specify this in the introduction rather than refering to prior work where the same hypotheses may have been mentioned.

Thankyou for this further critique which has enabled us to more cleary refine our introduction. We have now edited our introduction to be more direct about our hypotheses, that these hypotheses are instantiated into formal models, and what our predictions were. We have also included a small section on how previous predictions from other computational assessments of BPD link to our exploratory work, and highlighted this throughout the manuscript.

‘This paper seeks to address this gap by testing explicitly how disruptions in self-other generalization processes may underpin interpersonal disruptions observed in BPD. Specifically, our hypotheses were: (i) healthy controls will demonstrate evidence for both self-insertion and social contagion, integrating self and other information during interpersonal learning; and (ii) individuals with BPD will exhibit diminished self-other integration, reflected in stronger evidence for observations that assume distinct self-other representations.

We tested these hypotheses by designing a dynamic, sequential, three-phase Social Value Orientation (Murphy & Ackerman, 2014) paradigm—the Intentions Game—that would provide behavioural signatures assessing whether BPD differed from healthy controls in these generalization processes (Figure 1A). We coupled this paradigm with a lattice of models (M1-M4) that distinguish between self-insertion and social contagion (Figure 1B), and performed model comparison:

M1. Both self-to-other (self-insertion) and other-to-self (social contagion) occur before and after learning M2. Self-to-other transfer only occurs M3. Other-to-self transfer only occurs M4. Neither transfer process, suggesting distinct self-other representations

We additionally ran exploratory analysis of parameter differences and model predictions between groups following from prior work demonstrating changes in prosociality (Hula et al., 2018), social concern (Henco et al., 2020), belief stability (Story et al., 2024a), and belief updating (Story, 2024b) in BPD to understand whether discrepancies in self-other generalisation influences observational learning. By clearly articulating our hypotheses, we aim to clarify the theoretical contribution of our findings to existing literature on social learning, BPD, and computational psychiatry.’

Caveats should also be added about the exploratory nature of the many parameter group comparisons. If there are any predictions about group differences that can be made based on prior literature, the authors should make such links clear.

Thank you for this. We have now included caveats in the text to highlight the exploratory nature of these group comparisons, and added direct links to relevant literature where able:

Introduction

‘We additionally ran exploratory analysis of parameter differences and model predictions between groups following from prior work demonstrating changes in prosociality (Hula et al., 2018), social concern (Henco et al., 2020), belief stability (Story et al., 2024a), and belief updating (Story, 2024b) in BPD to understand whether discrepancies in self-other generalisation influences observational learning. By clearly articulating our hypotheses, we aim to clarify the theoretical contribution of our findings to existing literature on social learning, BPD, and computational psychiatry.’

Model Comparison

‘We found that CON participants were best fit at the group level by M1 (Frequency = 0.59, Exceedance Probability = 0.98), whereas BPD participants were best fit by M4 (Frequency = 0.54, Exceedance Probability = 0.86; Figure 2A). This suggests CON participants are best fit by a model that fully integrates self and other when learning, whereas those with BPD are best explained as holding disintegrated and separate representations of self and other that do not transfer information back and forth.

We first explore parameters between separate fits (see Methods). Later, in order to assuage concerns about drawing inferences from different models, we examined the relationships between the relevant parameters when we forced all participants to be fit to each of the models (in a hierarchical manner, separated by group). In sum, our model comparison is supported by convergence in parameter values when comparisons are meaningful (see Supplementary Materials). We refer to both types of analysis below.’

Phase 2 analysis

‘Prior work predicts those with BPD should focus more intently on public social information, rather than private information that only concerns one party (Henco et al., 2020). In BPD participants, only new beliefs about the relative reward preferences – mutual outcomes for both player - of partners differed (see Fig 2E): new median priors were larger than median preferences in phase 1 (mean = -0.47; = -6.10, 95%HDI: -7.60, -4.60).’

‘Models of moral preference learning (Story et al., 2024) predicts that BPD vs non-BPD participants have more rigid beliefs about their partners. We found that BPD participants were equally flexible around their prior beliefs about a partner’s relative reward preferences (= -1.60, 95%HDI: -3.42, 0.23), and were less flexible around their beliefs about a partner’s absolute reward preferences (=-4.09, 95%HDI: -5.37, -2.80), versus CON (Figure 2B).’

Phase 3 analysis

‘Prior work predicts that human economic preferences are shaped by observation (Panizza, et al., 2021; Suzuki et al. 2016; Yu et al, 2021), although little-to-no work has examined whether contagion differs for relative vs. absolute preferences. Associative models predict that social contagion may be exaggerated in BPD (Ereira et al., 2018).… As a whole, humans are more susceptible to changing relative preferences more than selfish, absolute reward preferences, and this is disrupted in BPD.’

Psychometric and Intentional Attribution analysis

‘Childhood trauma, persecution, and poor mentalising in BPD are all predicted to disrupt one’s ability to change (Fonagy & Luyten, 2009).’

‘Prior work has also predicted that partner-participant preference disparity influences mental state attributions (Barnby et al., 2022; Panizza et al., 2021).’

I'm not sure I understand why the authors, after adding multiple comparison correction, now list two kinds of p-values. To me, this is misleading and precludes the point of multiple comparison corrections, I therefore recommend they report the FDR-adjusted p-values only. Likewise, if a corrected p-value is greater than 0.05 this should not be interpreted as a result.

We have now adjusted the exploratory results to include only the FDR corrected values in the text.

‘We assessed conditional psychometric associations with social contagion under the assumption of M3 for all participants. We conducted partial correlation analyses to estimate relationships conditional on all other associations and retained all that survived bootstrapping (5000 reps), permutation testing (5000 reps), and subsequent FDR correction. When not controlled for group status, RGPTSB and CTQ scores were both moderately associated with MZQ scores (RGPTSB r = 0.41, 95%CI: 0.23, 0.60, p[fdr]=0.043; CTQ r = 0.354 95%CI: 0.13, 0.56, p[fdr]=0.02). This was not affected by group correction. CTQ scores were moderately and negatively associated with shifts in individualistic reward preferences (; r = -0.25, 95%CI: -0.46, -0.04, p[fdr]=0.03). This was not affected by group correction. MZQ scores were in turn moderately and negatively associated with shifts in prosocial-competitive preferences () between phase 1 and 3 (r = -0.26, 95%CI: -0.46, -0.06, p[fdr]=0.03). This was diminished when controlled for group status (r = 0.13, 95%CI: -0.34, 0.08, p[fdr]=0.20). Together this provides some evidence that self-reported trauma and self-reported mentalising influence social contagion (Fig S11). Social contagion under M3 was highly correlated with contagion under M1 demonstrating parsimony of outcomes across models (Fig S12).

Prior work has predicted that partner-participant preference disparity influences mental state attributions (Barnby et al., 2022; Panizza et al., 2021). We tested parameter influences on explicit intentional attributions in Phase 2 while controlling for group status. Attributions included the degree to which they believed their partner was motived by harmful intent (HI) and self-interest (SI). According with prior work (Barnby et al., 2022), greater disparity of absolute preferences before learning was associated on a trend level with reduced attributions of SI (<= -0.23, p[fdr]=0.08), and greater disparity of relative preferences before learning exaggerated attributions of HI = 0.21, p[fdr]=0.08), but did not survive correction (Figure S4B). This is likely due to partners being significantly less individualistic and prosocial on average compared to participants (= -5.50, 95%HDI: -7.60, -3.60; = 12, 95%HDI: 9.70, 14.00); partners are recognised as less selfish and more competitive.’

Can the authors please elaborate why the algorithm proposed to be employed by BPD is more 'entropic', especially given both their self-priors and posteriors about partners' preferences tended to be more precise than the ones used by CON? As far as I understand, there's nothing in the data to suggest BPD predictions should be more uncertain. In fact, this leads me to wonder, similarly to what another reviewer has already suggested, whether BPD participants generate self-referential priors over others in the same way CON participants do, they are just less favourable (i.e., in relation to oneself, but always less prosocial) - I think there is currently no model that would incorporate this possibility? It should at least be possible to explore this by checking if there is any statistical relationship between the estimated θ_ppt^m and 〖p(θ〗_par |D^0).

Thank you for this opportunity to be clearer in our wording. We belief the reviewer is referring to this line in the discussion: ‘In either case, the algorithm underlying the computational goal for BPD participants is far higher in entropy and emphasises a less stable or reliable process of inference.’

We note in the revised Figure 2 panel E and in the results that those with BPD under M4 show insertion along absolute reward (they still expect diminished selfishness in others), but neutral priors over relative reward (around 0, suggesting expectations of neither prosocial or competitive tendencies of others). Thus, θ_ppt^m (self preference) and θ_par^m (other preference) are tightly associated for absolute, but not relative reward.

In our wording, we meant that whether under model M4 or M1, those with BPD either show a neutral prior over relative reward (M4) or a prior with large variance over relative reward (M1), showing expectations of difference between themselves and their partner. In both cases, expectation about a partner’s absolute reward preferences is diminished vs. CON participants. We have strengthened our language in the discussion to clarify this:

‘In either case, the algorithm underlying the computational goal for BPD participants is far higher in uncertainty, whether through a neutral central tendency (M4) or large variance (M1) prior over relative reward in phase 2, and emphasises a less certain and reliable expectation about others.’

To note, social contagion under M3 was highly correlated with contagion under M1 (see Fig S11). This provides some preliminary evidence that trauma impacts beliefs about individualism directly, whereas trauma and persecutory beliefs impact beliefs about prosociality through impaired trait mentalising" - I don't understand what the authors mean by this, can they please elaborate and add some explanation to the main text?

We have now clarified this in the text:

‘Together this provides some evidence that self-reported trauma and self-reported mentalising influence social contagion (Fig S11). Social contagion under M3 was highly correlated with contagion under M1 demonstrating parsimony of outcomes across models (Fig S12).’

I noted that at least some of the newly added references have not been added to the bibliography (e.g., Hitchcock et al. 2022).

Thankyou for noticing this omission. We have now ensured all cited works are in the reference list.

Reviewer 2:

The paper is not based on specific empirical hypotheses formulated at the outset, but, rather, it uses an exploratory approach. Indeed, the task is not chosen in order to tackle specific empirical hypotheses. This, in my view, is a limitation since the introduction reads a bit vague and it is not always clear which gaps in the literature the paper aims to fill. As a further consequence, it is not always clear how the findings speak to previous theories on the topic.’

As I wrote in the public review, however, I believe that an important limitation of this work is that it was not based on testing specific empirical hypotheses formulated at the outset, and on selecting the experimental paradigm accordingly. This is a limitation because it is not always clear which gaps in the literature the paper aims to fill. As a consequence, although it has improved substantially compared to the previous version, the introduction remains a bit vague. As a further consequence, it is not always clear how the findings speak to previous theories on the topic. Still, despite this limitation, the paper has many strengths, and I believe it is now ready for publication

Thank you for this further critique. We appreciate your appraisal that the work has improved substantially and is ready for publication. We nevertheless have opted to clarify our introduction and aprior predictions throughout the manuscript (please see response to Reviewer 1).

Reviewer 3:

Although the authors note that their approach makes "clear and transparent a priori predictions," the paper could be improved by providing a clear and consolidated statement of these predictions so that the results could be interpreted vis-a-vis any a priori hypotheses.

In line with comments from both Reviewer 1 and 2, we have clarified our introduction to make it clear what our aprior predictions and hypotheses are about our core aims and exploratory analyses (see response to Reviewer 1).

The approach of using a partial correlation network with bootstrapping (and permutation) was interesting, but the logic of the analysis was not clearly stated. In particular, there are large group (Table 1: CON vs. BPD) differences in the measures introduced into this network. As a result, it is hard to understand whether any partial correlations are driven primarily by mean differences in severity (correlations tend to be inflated in extreme groups designs due to the absence of observation in middle of scales forming each bivariate distribution). I would have found these exploratory analyses more revealing if group membership was controlled for.

Thank you for this chance to be clearer in our methods. We have now written a more direct exposition of this exploratory method:

‘Exploratory Network Analysis

To understand the individual differences of trait attributes (MZQ, RGPTSB, CTQ) with other-to-self information transfer () across the entire sample we performed a network analysis (Borsboom, 2021). Network analysis allows for conditional associations between variables to be estimated; each association is controlled for by all other associations in the network. It also allows for visual inspection of the conditional relationships to get an intuition for how variables are interrelated as a whole (see Fig S11). We implemented network analysis with the bootNet package in r using the ‘estimateNetwork’ function with partial correlations (Epskamp, Borsboom & Fried, 2018). To assess the stability of the partial correlations we further implemented bootstrap resampling with 5000 repetitions using the ‘bootnet’ function. We then additionally shuffled the data and refitted the network 5000 times to determine a p_permuted value; this indicates the probability that a conditional relationship in the original network was within the null distribution of each conditional relationship. We then performed False Discovery Rate correction on the resulting p-values. We additionally controlled for group status for all variables in a supplementary analysis (Table S4).’

We have also further corrected for group status and reported these results as a supplementary table, and also within the main text alongside the main results. We have opted to relegate Figure 4 into a supplementary figure to make the text clearer.

‘We explored conditional psychometric associations with social contagion under the assumption of M3 for all participants (where everyone is able to be influenced by their partner). We conducted partial correlation analyses to estimate relationships conditional on all other associations and retained all that survived bootstrapping (5000 reps), permutation testing (5000 reps), and subsequent FDR correction. When not controlled for group status, RGPTSB and CTQ scores were both moderately associated with MZQ scores (RGPTSB r = 0.41, 95%CI: 0.23, 0.60, p[fdr]=0.043; CTQ r = 0.354 95%CI: 0.13, 0.56, p[fdr]=0.02). This was not affected by group correction. CTQ scores were moderately and negatively associated with shifts in individualistic reward preferences (; r = -0.25, 95%CI: -0.46, -0.04, p[fdr]=0.03). This was not affected by group correction. MZQ scores were in turn moderately and negatively associated with shifts in prosocial-competitive preferences () between phase 1 and 3 (r = -0.26, 95%CI: -0.46, -0.06, p[fdr]=0.03). This was diminished when controlled for group status (r = 0.13, 95%CI: -0.34, 0.08, p[fdr]=0.20). Together this provides some evidence that self-reported trauma and self-reported mentalising influence social contagion (Fig S11). Social contagion under M3 was highly correlated with contagion under M1 demonstrating parsimony of outcomes across models (Fig S12).’

Discussion first para: "effected -> affected"

Thanks for spotting this. We have now changed it.

Add "s" to "participant: "Notably, despite differing strategies, those with BPD achieved similar accuracy to CON participant."

We have now changed this.

Author response:

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

Reviewer #1 (Public review):

Summary:

Measurement of BOLD MR imaging has regularly found regions of the brain that show reliable suppression of BOLD responses during specific experimental testing conditions. These observations are to some degree unexplained, in comparison with more usual association between activation of the BOLD response and excitatory activation of the neurons (most tightly linked to synaptic activity) in the same brain location. This paper finds two patients whose brains were tested with both non-invasive functional MRI and with invasive insertion of electrodes, which allowed the direct recording of neuronal activity. The electrode insertions were made within the fusiform gyrus, which is known to process information about faces, in a clinical search for the sites of intractable epilepsy in each patient. The simple observation is that the electrode location in one patient showed activation of the BOLD response and activation of neuronal firing in response to face stimuli. This is the classical association. The other patient showed an informative and different pattern of responses. In this person, the electrode location showed a suppression of the BOLD response to face stimuli and, most interestingly, an associated suppression of neuronal activity at the electrode site.

Strengths:

Whilst these results are not by themselves definitive, they add an important piece of evidence to a long-standing discussion about the origins of the BOLD response. The observation of decreased neuronal activation associated with negative BOLD is interesting because, at various times, exactly the opposite association has been predicted. It has been previously argued that if synaptic mechanisms of neuronal inhibition are responsible for the suppression of neuronal firing, then it would be reasonable

Weaknesses:

The chief weakness of the paper is that the results may be unique in a slightly awkward way. The observation of positive BOLD and neuronal activation is made at one brain site in one patient, while the complementary observation of negative BOLD and neuronal suppression actually derives from the other patient. Showing both effects in both patients would make a much stronger paper.

We thank reviewer #1 for their positive evaluation of our paper. Obviously, we agree with the reviewer that the paper would be much stronger if BOTH effects – spike increase and decrease – would be found in BOTH patients in their corresponding fMRI regions (lateral and medial fusiform gyrus) (also in the same hemisphere). Nevertheless, we clearly acknowledge this limitation in the (revised) version of the manuscript (p.8: Material and Methods section).

Note that with respect to the fMRI data, our results are not surprising, as we indicate in the manuscript: BOLD increases to faces (relative to nonface objects) are typically found in the LatFG and BOLD decreases in the medialFG (in the revised version, we have added the reference to an early neuroimaging paper that describes this dissociation clearly:

Pelphrey, K. A., Mack, P. B., Song, A., Güzeldere, G., & McCarthy, G. Faces evoke spatially differentiated patterns of BOLD activation and deactivation. Neuroreport 14, 955–959 (2003).

This pattern of increase/decrease in fMRI can be appreciated in both patients on Figure 2, although one has to consider both the transverse and coronal slices to appreciate it.

Regarding electrophysiological data, in the current paper, one could think that P1 shows only increases to faces, and P2 would show only decreases (irrespective of the region). However, that is not the case since 11% of P1’s face-selective units are decreases (89% are increases) and 4% of P2’s face-selective units are increases. This has now been made clearer in the revised manuscript (p.5).

As the reviewer is certainly aware, the number and positions of the electrodes are based on strict clinical criteria, and we will probably never encounter a situation with two neighboring (macro-micro hybrid electrodes), one with microelectrodes ending up in the lateral MidFG, the other in the medial MidFG, in the same patient. If there is no clinical value for the patient, this cannot be done.

The only thing we can do is to strengthen these results in the future by collecting data on additional patients with an electrode either in the lateral or the medial FG, together with fMRI. But these are the only two patients we have been able to record so far with electrodes falling unambiguously in such contrasted regions and with large (and comparable) measures.

While we acknowledge that the results may be unique because of the use of 2 contrasted patients only (and this is why the paper is a short report), the data is compelling in these 2 cases, and we are confident that it will be replicated in larger cohorts in the future.

Finally, information regarding ethics approval has been provided in the paper.

Reviewer #2 (Public review):

Summary:

This is a short and straightforward paper describing BOLD fMRI and depth electrode measurements from two regions of the fusiform gyrus that show either higher or lower BOLD responses to faces vs. objects (which I will call face-positive and facenegative regions). In these regions, which were studied separately in two patients undergoing epilepsy surgery, spiking activity increased for faces relative to objects in the face-positive region and decreased for faces relative to objects in the face-negative region. Interestingly, about 30% of neurons in the face-negative region did not respond to objects and decreased their responses below baseline in response to faces (absolute suppression).

Strengths:

These patient data are valuable, with many recording sessions and neurons from human face-selective regions, and the methods used for comparing face and object responses in both fMRI and electrode recordings were robust and well-established. The finding of absolute suppression could clarify the nature of face selectivity in human fusiform gyrus since previous fMRI studies of the face-negative region could not distinguish whether face < object responses came from absolute suppression, or just relatively lower but still positive responses to faces vs. objects.

Weaknesses:

The authors claim that the results tell us about both 1) face-selectivity in the fusiform gyrus, and 2) the physiological basis of the BOLD signal. However, I would like to see more of the data that supports the first claim, and I am not sure the second claim is supported.

(1) The authors report that ~30% of neurons showed absolute suppression, but those data are not shown separately from the neurons that only show relative reductions. It is difficult to evaluate the absolute suppression claim from the short assertion in the text alone (lines 105-106), although this is a critical claim in the paper.

We thank reviewer #2 for their positive evaluation of our paper. We understand the reviewer’s point, and we partly agree. Where we respectfully disagree is that the finding of absolute suppression is critical for the claim of the paper: finding an identical contrast between the two regions in terms of RELATIVE increase/decrease of face-selective activity in fMRI and spiking activity is already novel and informative. Where we agree with the reviewer is that the absolute suppression could be more documented: it wasn’t, due to space constraints (brief report). We provide below an example of a neuron showing absolute suppression to faces (P2), as also requested in the recommendations to authors. In the frequency domain, there is only a face-selective response (1.2 Hz and harmonics) but no significant response at 6 Hz (common general visual response). In the time-domain, relative to face onset, the response drops below baseline level. It means that this neuron has baseline (non-periodic) spontaneous spiking activity that is actively suppressed when a face appears.

Author response image 1.

(2) I am not sure how much light the results shed on the physiological basis of the BOLD signal. The authors write that the results reveal "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain" (line 120). But I think to make this claim, you would need a region that exclusively had neurons showing absolute suppression, not a region with a mix of neurons, some showing absolute suppression and some showing relative suppression, as here. The responses of both groups of neurons contribute to the measured BOLD signal, so it seems impossible to tell from these data how absolute suppression per se drives the BOLD response.

It is a fact that we find both kinds of responses in the same region. We cannot tell with this technique if neurons showing relative vs. absolute suppression of responses are spatially segregated for instance (e.g., forming two separate sub-regions) or are intermingled. And we cannot tell from our data how absolute suppression per se drives the BOLD response. In our view, this does not diminish the interest and originality of the study, but the statement "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain” has been rephrased in the revised manuscript: "that BOLD decreases can be due to relative, or absolute (or a combination of both), spike suppression in the human brain”.

Reviewer #3 (Public review):

In this paper the authors conduct two experiments an fMRI experiment and intracranial recordings of neurons in two patients P1 and P2. In both experiments, they employ a SSVEP paradigm in which they show images at a fast rate (e.g. 6Hz) and then they show face images at a slower rate (e.g. 1.2Hz), where the rest of the images are a variety of object images. In the first patient, they record from neurons over a region in the mid fusiform gyrus that is face-selective and in the second patient, they record neurons from a region more medially that is not face selective (it responds more strongly to objects than faces). Results find similar selectivity between the electrophysiology data and the fMRI data in that the location which shows higher fMRI to faces also finds face-selective neurons and the location which finds preference to non faces also shows non face preferring neurons.

Strengths:

The data is important in that it shows that there is a relationship between category selectivity measured from electrophysiology data and category-selective from fMRI. The data is unique as it contains a lot of single and multiunit recordings (245 units) from the human fusiform gyrus - which the authors point out - is a humanoid specific gyrus.

Weaknesses:

My major concerns are two-fold:

(i) There is a paucity of data; Thus, more information (results and methods) is warranted; and in particular there is no comparison between the fMRI data and the SEEG data.

We thank reviewer #3 for their positive evaluation of our paper. If the reviewer means paucity of data presentation, we agree and we provide more presentation below, although the methods and results information appear as complete to us. The comparison between fMRI and SEEG is there, but can only be indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance). In addition, our manuscript aims at providing a short empirical contribution to further our understanding of the relationship between neural responses and BOLD signal, not to provide a model of neurovascular coupling.

(ii) One main claim of the paper is that there is evidence for suppressed responses to faces in the non-face selective region. That is, the reduction in activation to faces in the non-face selective region is interpreted as a suppression in the neural response and consequently the reduction in fMRI signal is interpreted as suppression. However, the SSVEP paradigm has no baseline (it alternates between faces and objects) and therefore it cannot distinguish between lower firing rate to faces vs suppression of response to faces.

We understand the concern of the reviewer, but we respectfully disagree that our paradigm cannot distinguish between lower firing rate to faces vs. suppression of response to faces. Indeed, since the stimuli are presented periodically (6 Hz), we can objectively distinguish stimulus-related activity from spontaneous neuronal firing. The baseline corresponds to spikes that are non-periodic, i.e., unrelated to the (common face and object) stimulation. For a subset of neurons, even this non-periodic baseline activity is suppressed, above and beyond the suppression of the 6 Hz response illustrated on Figure 2. We mention it in the manuscript, but we agree that we do not present illustrations of such decrease in the time-domain for SU, which we did not consider as being necessary initially (please see below for such presentation).

(1) Additional data: the paper has 2 figures: figure 1 which shows the experimental design and figure 2 which presents data, the latter shows one example neuron raster plot from each patient and group average neural data from each patient. In this reader's opinion this is insufficient data to support the conclusions of the paper. The paper will be more impactful if the researchers would report the data more comprehensively.

We answer to more specific requests for additional evidence below, but the reviewer should be aware that this is a short report, which reaches the word limit. In our view, the group average neural data should be sufficient to support the conclusions, and the example neurons are there for illustration. And while we cannot provide the raster plots for a large number of neurons, the anonymized data is made available at:

(a) There is no direct comparison between the fMRI data and the SEEG data, except for a comparison of the location of the electrodes relative to the statistical parametric map generated from a contrast (Fig 2a,d). It will be helpful to build a model linking between the neural responses to the voxel response in the same location - i.e., estimate from the electrophysiology data the fMRI data (e.g., Logothetis & Wandell, 2004).

As mentioned above the comparison between fMRI and SEEG is indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance) and would not allow to make such a model.

(b) More comprehensive analyses of the SSVEP neural data: It will be helpful to show the results of the frequency analyses of the SSVEP data for all neurons to show that there are significant visual responses and significant face responses. It will be also useful to compare and quantify the magnitude of the face responses compared to the visual responses.

The data has been analyzed comprehensively, but we would not be able to show all neurons with such significant visual responses and face-selective responses.

(c) The neuron shown in E shows cyclical responses tied to the onset of the stimuli, is this the visual response?

Correct, it’s the visual response at 6 Hz.

If so, why is there an increase in the firing rate of the neuron before the face stimulus is shown in time 0?

Because the stimulation is continuous. What is displayed at 0 is the onset of the face stimulus, with each face stimulus being preceded by 4 images of nonface objects.

The neuron's data seems different than the average response across neurons; This raises a concern about interpreting the average response across neurons in panel F which seems different than the single neuron responses

The reviewer is correct, and we apologize for the confusion. This is because the average data on panel F has been notch-filtered for the 6 Hz (and harmonic responses), as indicated in the methods (p.11): ‘a FFT notch filter (filter width = 0.05 Hz) was then applied on the 70 s single or multi-units time-series to remove the general visual response at 6 Hz and two additional harmonics (i.e., 12 and 18 Hz)’.

Here is the same data without the notch-filter (the 6Hz periodic response is clearly visible):

Author response image 2.

For sake of clarity, we prefer presenting the notch-filtered data in the paper, but the revised version makes it clear in the figure caption that the average data has been notch-filtered.

(d) Related to (c) it would be useful to show raster plots of all neurons and quantify if the neural responses within a region are homogeneous or heterogeneous. This would add data relating the single neuron response to the population responses measured from fMRI. See also Nir 2009.

We agree with the reviewer that this is interesting, but again we do not think that it is necessary for the point made in the present paper. Responses in these regions appear rather heterogenous, and we are currently working on a longer paper with additional SEEG data (other patients tested for shorter sessions) to define and quantify the face-selective neurons in the MidFusiform gyrus with this approach (without relating it to the fMRI contrast as reported here).

(e) When reporting group average data (e.g., Fig 2C,F) it is necessary to show standard deviation of the response across neurons.

We agree with the reviewer and have modified Figure 2 accordingly in the revised manuscript.

(f) Is it possible to estimate the latency of the neural responses to face and object images from the phase data? If so, this will add important information on the timing of neural responses in the human fusiform gyrus to face and object images.

The fast periodic paradigm to measure neural face-selectivity has been used in tens of studies since its original reports:

• in EEG: Rossion et al., 2015: https://doi.org/10.1167/15.1.18

• in SEEG: Jonas et al., 2016: https://doi.org/10.1073/pnas.1522033113

In this paradigm, the face-selective response spreads to several harmonics (1.2 Hz, 2.4 Hz, 3.6 Hz, etc.) (which are summed for quantifying the total face-selective amplitude). This is illustrated below by the averaged single units’ SNR spectra across all recording sessions for both participants.

Author response image 3.

There is no unique phase-value, each harmonic being associated with a phase-value, so that the timing cannot be unambiguously extracted from phase values. Instead, the onset latency is computed directly from the time-domain responses, which is more straightforward and reliable than using the phase. Note that the present paper is not about the specific time-courses of the different types of neurons, which would require a more comprehensive report, but which is not necessary to support the point made in the present paper about the SEEG-fMRI sign relationship.

(g) Related to (e) In total the authors recorded data from 245 units (some single units and some multiunits) and they found that both in the face and nonface selective most of the recoded neurons exhibited face -selectivity, which this reader found confusing: They write “ Among all visually responsive neurons, we found a very high proportion of face-selective neurons (p < 0.05) in both activated and deactivated MidFG regions (P1: 98.1%; N = 51/52; P2: 86.6%; N = 110/127)’. Is the face selectivity in P1 an increase in response to faces and P2 a reduction in response to faces or in both it’s an increase in response to faces

Face-selectivity is defined as a DIFFERENTIAL response to faces compared to objects, not necessarily a larger response to faces. So yes, face-selectivity in P1 is an increase in response to faces and P2 a reduction in response to faces.

Additional methods

(a) it is unclear if the SSVEP analyses of neural responses were done on the spikes or the raw electrical signal. If the former, how is the SSVEP frequency analysis done on discrete data like action potentials?

The FFT is applied directly on spike trains using Matlab’s discrete Fourier Transform function. This function is suitable to be applied to spike trains in the same way as to any sampled digital signal (here, the microwires signal was sampled at 30 kHz, see Methods).

In complementary analyses, we also attempted to apply the FFT on spike trains that had been temporally smoothed by convolving them with a 20ms square window (Le Cam et al., 2023, cited in the paper ). This did not change the outcome of the frequency analyses in the frequency range we are interested in. We have also added one sentence with information in the methods section about spike detection (p.10).

(b) it is unclear why the onset time was shifted by 33ms; one can measure the phase of the response relative to the cycle onset and use that to estimate the delay between the onset of a stimulus and the onset of the response. Adding phase information will be useful.

The onset time was shifted by 33ms because the stimuli are presented with a sinewave contrast modulation (i.e., at 0ms, the stimulus has 0% contrast). 100% contrast is reached at half a stimulation cycle, which is 83.33ms here, but a response is likely triggered before reaching 100% contrast. To estimate the delay between the start of the sinewave (0% contrast) and the triggering of a neural response, we tested 7 SEEG participants with the same images presented in FPVS sequences either as a sinewave contrast (black line) modulation or as a squarewave (i.e. abrupt) contrast modulation (red line). The 33ms value is based on these LFP data obtained in response to such sinewave stimulation and squarewave stimulation of the same paradigm. This delay corresponds to 4 screen refresh frames (120 Hz refresh rate = 8.33ms by frame) and 35% of the full contrast, as illustrated below (please see also Retter, T. L., & Rossion, B. (2016). Uncovering the neural magnitude and spatio-temporal dynamics of natural image categorization in a fast visual stream. Neuropsychologia, 91, 9–28).

Author response image 4.

(2) Interpretation of suppression:

The SSVEP paradigm alternates between 2 conditions: faces and objects and has no baseline; In other words, responses to faces are measured relative to the baseline response to objects so that any region that contains neurons that have a lower firing rate to faces than objects is bound to show a lower response in the SSVEP signal. Therefore, because the experiment does not have a true baseline (e.g. blank screen, with no visual stimulation) this experimental design cannot distinguish between lower firing rate to faces vs suppression of response to faces.

The strongest evidence put forward for suppression is the response of non-visual neurons that was also reduced when patients looked at faces, but since these are non-visual neurons, it is unclear how to interpret the responses to faces.

We understand this point, but how does the reviewer know that these are non-visual neurons? Because these neurons are located in the visual cortex, they are likely to be visual neurons that are not responsive to non-face objects. In any case, as the reviewer writes, we think it’s strong evidence for suppression.

We thank all three reviewers for their positive evaluation of our paper and their constructive comments.

Author response:

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

Zhang et al. addressed the question of whether advantageous and disadvantageous inequality aversion can be vicariously learned and generalized. Using an adapted version of the ultimatum game (UG), in three phases, participants first gave their own preference (baseline phase), then interacted with a "teacher" to learn their preference (learning phase), and finally were tested again on their own (transfer phase). The key measure is whether participants exhibited similar choice preferences (i.e., rejection rate and fairness rating) influenced by the learning phase, by contrasting their transfer phase and baseline phase. Through a series of statistical modeling and computational modeling, the authors reported that both advantageous and disadvantageous inequality aversion can indeed be learned (Study 1), and even be generalised (Study 2).

Strengths:

This study is very interesting, it directly adapted the lab's previous work on the observational learning effect on disadvantageous inequality aversion, to test both advantageous and disadvantageous inequality aversion in the current study. Social transmission of action, emotion, and attitude have started to be looked at recently, hence this research is timely. The use of computational modeling is mostly appropriate and motivated. Study 2, which examined the vicarious inequality aversion in conditions where feedback was never provided, is interesting and important to strengthen the reported effects. Both studies have proper justifications to determine the sample size.

Weaknesses:

Despite the strengths, a few conceptual aspects and analytical decisions have to be explained, justified, or clarified.

INTRODUCTION/CONCEPTUALIZATION

(1) Two terms seem to be interchangeable, which should not, in this work: vicarious/observational learning vs preference learning. For vicarious learning, individuals observe others' actions (and optionally also the corresponding consequence resulting directly from their own actions), whereas, for preference learning, individuals predict, or act on behalf of, the others' actions, and then receive feedback if that prediction is correct or not. For the current work, it seems that the experiment is more about preference learning and prediction, and less so about vicarious learning. The intro and set are heavily around vicarious learning, and later the use of vicarious learning and preference learning is rather mixed in the text. I think either tone down the focus on vicarious learning, or discuss how they are different. Some of the references here may be helpful: (Charpentier et al., Neuron, 2020; Olsson et al., Nature Reviews Neuroscience, 2020; Zhang & Glascher, Science Advances, 2020)

We are appreciative of the Reviewer for raising this question and providing the reference. In response to this comment we have elected to avoid, in most cases, use of the term ‘vicarious’ and instead focus the paper on learning of others’ preferences (without specific commitment to various/observational learning per se). These changes are reflected throughout all sections of the revised manuscript, and in the revised title. We believe this simplified terminology has improved the clarity of our contribution.

EXPERIMENTAL DESIGN

(2) For each offer type, the experiment "added a uniformly distributed noise in the range of (-10 ,10)". I wonder what this looks like? With only integers such as 25:75, or even with decimal points? More importantly, is it possible to have either 70:30 or 90:10 option, after adding the noise, to have generated an 80:20 split shown to the participants? If so, for the analyses later, when participants saw the 80:20 split, which condition did this trial belong to? 70:30 or 90:10? And is such noise added only to the learning phase, or also to the baseline/transfer phases? This requires some clarification.

We thank the Reviewer for pointing this out. The uniformly distributed noise was added to all three phases to make the proposers’ behavior more realistic. This added noise was rounded to integer numbers, constrained from -9 to 9, which means in both 70:30 and 90:10 offer types, an 80:20 split could not occur. We have made this feature of our design clear in the Method section Line 524 ~ 528:

“In all task phases, we added uniformly distributed noise to each trial’s offer (ranging from -9 to 9, inclusive, rounding to the nearest integer) such that the random amount added (or subtracted) from the Proposer’s share was subtracted (or added) to the Receiver’s share. We adopted this manipulation to make the proposers’ behavior appear more realistic. The orders of offers participants experienced were fully randomized within each experiment phase. ”

(3) For the offer conditions (90:10, 70:30, 50:50, 30:70, 10:90) - are they randomized? If so, how is it done? Is it randomized within each participant, and/or also across participants (such that each participant experienced different trial sequences)? This is important, as the order especially for the learning phase can largely impact the preference learning of the participants.

We agree with the Reviewer the order in which offers are experienced could be very important. The order of the conditions was randomized independently for each participant (i.e. each participant experienced different trial sequences). We made this point clear in the Methods part. Line 527 ~ 528:

“The orders of offers participants experienced were fully randomized within each experiment phase.”

STATISTICAL ANALYSIS & COMPUTATIONAL MODELING

(4) In Study 1 DI offer types (90:10, 70:30), the rejection rate for DI-AI averse looks consistently higher than that for DI averse (ie, the blue line is above the yellow line). Is this significant? If so, how come? Since this is a between-subject design, I would not anticipate such a result (especially for the baseline). Also, for the LME results (eg, Table S3), only interactions were reported but not the main results.

We thank the Reviewer for pointing out this feature of the results. Prompted by this comment, we compared the baseline rejection rates between two conditions for these two offer types, finding in Experiment 1 that rejection rates in the DI-AI-averse condition were significantly higher than in the DI-averse condition (DI-AI-averse vs. DI-averse; Offer 90:10, β = 0.13, p < 0.001, Offer 70:30, β = 0.09, p < 0.034). We agree with the Reviewer that there should, in principle, be no difference between the experiences of participants in these two conditions is identical in the Baseline phase. However, we did not observe these difference in baseline preferences in Experiment 2 (DI-AI-averse vs. DI-averse; Offer 90:10, β = 0.07, p < 0.100, Offer 70:30, β = 0.05, p < 0.193). On the basis of the inconsistency of this effect across studies we believe this is a spurious difference in preferences stemming from chance.

Regarding the LME results, the reason why only interaction terms are reported is due to the specification of the model and the rationale for testing.

Taking the model reported in Table S3 as an example—a logistic model which examines Baseline phase rejection rates as a function of offer level and condition—the between-subject conditions (DI-averse and DI-AI-averse) are represented by dummy-coded variables. Similarly, offer types were also dummy-coded, such that each of the five columns (90:10, 70:30, 50:50, 30:70, and 10:90) correspond corresponded to a particular offer type. This model specification yields ten interaction terms (i.e., fixed effects) of interest—for example, the “DI-averse × Offer 90:10” indicates baseline rejection rates for 90:10 offers in DI-averse condition. Thus, to compare rejection rates across specific offer types, we estimate and report linear contrasts between these resultant terms. We have clarified the nature of these reported tests in our revised Results—for example, line189-190: “linear contrasts; e.g. 90:10 vs 10:90, all Ps<0.001, see Table S3 for logistic regression coefficients for rejection rates).

Also in response to this comment that and a recommendation from Reviewer 2 (see below), we have revised our supplementary materials to make each model specification clearer as SI line 25:

“RejectionRate ~ 0 + (Disl + Advl):(Offer10 + Offer30 + Offer50 + Offer70 + Offer90) + (1|Subject)”

(5) I do not particularly find this analysis appealing: "we examined whether participants' changes in rejection rates between Transfer and Baseline, could be explained by the degree to which they vicariously learned, defined as the change in punishment rates between the first and last 5 trials of the Learning phase." Naturally, the participants' behavior in the first 5 trials in the learning phase will be similar to those in the baseline; and their behavior in the last 5 trials in the learning phase would echo those at the transfer phase. I think it would be stronger to link the preference learning results to the change between the baseline and transfer phase, eg, by looking at the difference between alpha (beta) at the end of the learning phase and the initial alpha (beta).

Thanks for pointing this out. Also, considering the comments from Reviewer 2 concerning the interpretation of this analysis, we have elected to remove this result from our revision.

(6) I wonder if data from the baseline and transfer phases can also be modeled, using a simple Fehr-Schimdt model. This way, the change in alpha/beta can also be examined between the baseline and transfer phase.

We agree with the Reviewer that a simplified F-S model could be used, in principle, to characterize Baseline and Transfer phase behavior, but it is our view that the rejection rates provide readers with the clearest (and simplest) picture of how participants are responding to inequity. Put another way, we believe that the added complexity of using (and explaining) a new model to characterize simple, steady-state choice behavior (within these phases) would not be justified or add appreciable insights about participants’ behavior.

(7) I quite liked Study 2 which tests the generalization effect, and I expected to see an adapted computational modeling to directly reflect this idea. Indeed, the authors wrote, "[...] given that this model [...] assumes the sort of generalization of preferences between offer types [...]". But where exactly did the preference learning model assume the generalization? In the methods, the modeling seems to be only about Study 1; did the authors advise their model to accommodate Study 2? The authors also ran simulation for the learning phase in Study 2 (Figure 6), and how did the preference update (if at all) for offers (90:10 and 10:90) where feedback was not given? Extending/Unpacking the computational modeling results for Study 2 will be very helpful for the paper.

We are appreciative of the Reviewer’s positive impression of Experiment 2. Upon reflection, we realize that our original submission was not clear about the modeling done in Experiment 2, and we should clarify here that we did also fit the Preference Inference model to this dataset. As in Experiment 1, this model assumes that the participants have a representation of the teacher’s preference as a Fehr-Schmidt form utility function and infer the Teacher’s Envy and Guilt parameters through learning. The model indicates that, on the basis of experience with the Teacher’s preferences on moderately unfair offers (i.e., offer 70:30 and offer 30:70), participants can successfully infer these guess of these two parameters, and in turn, compute Fehr-Schmidt utility to guide their decisions in the extreme unfair offers (i.e., offer 90:10 and offer 10:90).

In response to this comment, we have made this clearer in our Results (Line 377-382):

“Finally, following Experiment 1, we fit a series of computational models of Learning phase choice behavior, comparing the goodness-of-fit of the four best-fitting models from Experiment 1 (see Methods). As before, we found that the Preference Inference model provided the best fit of participants’ Learning Phase behavior (Figure S1a, Table S12). Given that this model is able to infer the Teacher’s underlying inequity-averse preferences (rather than learns offer-specific rejection preferences), it is unsurprising that this model best describes the generalization behavior observed in Experiment 2.”

and in our revised Methods (Line 551-553)

“We considered 6 computational models of Learning Phase choice behavior, which we fit to individual participants’ observed sequences of choices, in both Experiments 1 and 2, via Maximum Likelihood Estimation”

Reviewer #2 (Public review):

Summary:

This study investigates whether individuals can learn to adopt egalitarian norms that incur a personal monetary cost, such as rejecting offers that benefit them more than the giver (advantageous inequitable offers). While these behaviors are uncommon, two experiments demonstrate that individuals can learn to reject such offers through vicarious learning - by observing and acting in line with a "teacher" who follows these norms. The authors use computational modelling to argue that learners adopt these norms through a sophisticated process, inferring the latent structure of the teacher's preferences, akin to theory of mind.

Strengths:

This paper is well-written and tackles a critical topic relevant to social norms, morality, and justice. The findings, which show that individuals can adopt just and fair norms even at a personal cost, are promising. The study is well-situated in the literature, with clever experimental design and a computational approach that may offer insights into latent cognitive processes. Findings have potential implications for policymakers.

Weaknesses:

Note: in the text below, the "teacher" will refer to the agent from which a participant presumably receives feedback during the learning phase.

(1) Focus on Disadvantageous Inequity (DI): A significant portion of the paper focuses on responses to Disadvantageous Inequitable (DI) offers, which is confusing given the study's primary aim is to examine learning in response to Advantageous Inequitable (AI) offers. The inclusion of DI offers is not well-justified and distracts from the main focus. Furthermore, the experimental design seems, in principle, inadequate to test for the learning effects of DI offers. Because both teaching regimes considered were identical for DI offers the paradigm lacks a control condition to test for learning effects related to these offers. I can't see how an increase in rejection of DI offers (e.g., between baseline and generalization) can be interpreted as speaking to learning. There are various other potential reasons for an increase in rejection of DI offers even if individuals learn nothing from learning (e.g. if envy builds up during the experiment as one encounters more instances of disadvantageous fairness).

We are appreciative of the Reviewer’s insight here and for the opportunity to clarify our experimental logic. We included DI offers in order to 1) expose participants to the full spectrum of offer types, and avoid focusing participants exclusively upon AI offers, which might result in a demand characteristic and 2) to afford exploration of how learning dynamics might differ in DI context s—which was, to some extent, examined in our previous study (FeldmanHall, Otto, & Phelps, 2018)—versus AI contexts. Furthermore, as this work builds critically on our previous study, we reasoned that replicating these original findings (in the DI context) would be important for demonstrating the generality of the learning effects in the DI context across experimental settings. We now remark on this point in our revised Introduction Line 129 ~132:

“In addition, to mechanistically probe how punitive preferences are acquired in Adv-I and Dis-I contexts—in turn, assessing the replicability of our earlier study investigating punitive preference acquisition in the Dis context—we also characterize trial-by-trial acquisition of punitive behavior with computational models of choice.”

(2) Statistical Analysis: The analysis of the learning effects of AI offers is not fully convincing. The authors analyse changes in rejection rates within each learning condition rather than directly comparing the two. Finding a significant effect in one condition but not the other does not demonstrate that the learning regime is driving the effect. A direct comparison between conditions is necessary for establishing that there is a causal role for the learning regime.

We agree with the Reviewer and upon reflection, believe that direct comparisons between conditions would be helpful to support the claim that the different learning conditions are responsible for the observed learning effects. In brief, these specific tests buttress the idea that exposure to AI-averse preferences result in increases in AI punishment rates in the Transfer phase (over and above the rates observed for participants who were only exposed to DI-averse preferences).

Accordingly, our revision now reports statistics concerning the differences between conditions for AI offers in Experiment 1 (Line 198~ 207):

“Importantly, when comparing these changes between the two learning conditions, we observed significant differences in rejection rates for Adv-I offers: compared to exposure to a Teacher who rejected only Dis-I offers, participants exposed to a Teacher who rejected both Dis-I and Adv-I offers were more likely to reject Adv-I offers and rated these offers more unfair. This difference between conditions was evident in both 30:70 offers (Rejection rates: β(SE) = 0.10(0.04), p = 0.013; Fairness ratings: β(SE) = -0.86(0.17), p < 0.001) and 10:90 offers (Rejection rates: β(SE) = 0.15(0.04), p < 0.001, Fairness ratings: β(SE) = -1.04(0.17), p < 0.001). As a control, we also compared rejection rates and fairness rating changes between conditions in Dis-I offers (90:10 and 30:70) and Fair offers (i.e., 50:50) but observed no significant difference (all ps > 0.217), suggesting that observing an Adv-I-averse Teacher’s preferences did not influence participants’ behavior in response to Dis-I offers.”

Line 222 ~ 230:

“A mixed-effects logistic regression revealed a significant larger (positive) effect of trial number on rejection rates of Adv-I offers for the Adv-Dis-I-Averse condition compared to the Dis-I-Averse condition. This relative rejection rate increase was evident both in 30:70 offers (Table S7; β(SE) = -0.77(0.24), p < 0.001) and in 10:90 offers (β(SE) = -1.10(0.33), p < 0.001). In contrast, comparing Dis-I and Fairness offers when the Teacher showed the same tendency to reject, we found no significant difference between the two conditions (90:10 splits: β(SE)=-0.48(0.21),p=0.593;70:30 splits: β(SE)=-0.01(0.14),p=0.150; 50:50 splits: β(SE)=-0.00(0.21),p=0.086). In other words, participants by and large appeared to adjust their rejection choices in accordance with the Teacher’s feedback in an incremental fashion.”

And in Experiment 2 Line 333 ~ 345:

“Similar to what we observed in Experiment 1 (Figure 4a), Compared to the participants in the Dis-I-Averse Condition, participants in the Adv-I-Averse Condition increased their rates of rejection of extreme Adv-I offerers (i.e., 10:90) in the Transfer Phase, relative to the Baseline phase (β(SE) = -0.12(0.04), p < 0.004; Table S9), suggesting that participants’ learned (and adopted) Adv-I-averse preferences, generalized from one specific offer type (30:70) to an offer types for which they received no Teacher feedback (10:90). Examining extreme Dis-I offers where the Teacher exhibited identical preferences across the two learning conditions, we found no difference in the Changes of Rejection Rates from Baseline to Transfer phase between conditions (β(SE) = -0.05(0.04), p < 0.259). Mirroring the observed rejection rates (Figure 4b), relative to the Dis-I-Averse Condition, participants’ fairness ratings for extreme Adv-I offers increased more from the Baseline to Transfer phase in the Adv-Dis-I-Averse Condition than in the Dis-I-Averse condition (β(SE) = -0.97(0.18), p < 0.001), but, importantly, changes in fairness ratings for extreme Dis-I offers did not differ significantly between learning conditions (β(SE) = -0.06(0.18), p < 0.723)”

Line 361 ~ 368:

“Examining the time course of rejection rates in Adv-I-contexts during the Learning phase (Figure 5) revealed that participants learned over time to punish mildly unfair 30:70 offers, and these punishment preferences generalized to more extreme offers (10:90). Specifically, compared to the Dis-I-Averse Condition, in the Adv-Dis-I-Averse condition we observed a significant larger trend of increase in rejections rates for 10:90 (Adv-I) offers (Figure 5, β(SE) = -0.81(0.26), p < 0.002 mixed-effects logistic regression, see Table S10). Again, when comparing the rejection rate increase in the extremely Dis-I offers (90:10), we didn’t find significant difference between conditions (β(SE) = -0.25(0.19), p < 0.707).”

(3) Correlation Between Learning and Contagion Effects:

The authors argue that correlations between learning effects (changes in rejection rates during the learning phase) and contagion effects (changes between the generalization and baseline phases) support the idea that individuals who are better aligning their preferences with the teacher also give more consideration to the teacher's preferences later during generalization phase. This interpretation is not convincing. Such correlations could emerge even in the absence of learning, driven by temporal trends like increasing guilt or envy (or even by slow temporal fluctuations in these processes) on behalf of self or others. The reason is that the baseline phase is temporally closer to the beginning of the learning phase whereas the generalization phase is temporally closer to the end of the learning phase. Additionally, the interpretation of these effects seems flawed, as changes in rejection rates do not necessarily indicate closer alignment with the teacher's preferences. For example, if the teacher rejects an offer 75% of the time then a positive 5% learning effect may imply better matching the teacher if it reflects an increase in rejection rate from 65% to 70%, but it implies divergence from the teacher if it reflects an increase from 85% to 90%. For similar reasons, it is not clear that the contagion effects reflect how much a teacher's preferences are taken into account during generalization.

This comment is very similar to a previous comment made by Reviewer 1, who also called into question the interpretability of these correlations. In response to both of these comments we have elected to remove these analyses from our revision.

(4) Modeling Efforts: The modelling approach is underdeveloped. The identification of the "best model" lacks transparency, as no model-recovery results are provided, and fits for the losing models are not shown, leaving readers in the dark about where these models fail. Moreover, the reinforcement learning (RL) models used are overly simplistic, treating actions as independent when they are likely inversely related (for example, the feedback that the teacher would have rejected an offer provides feedback that rejection is "correct" but also that acceptance is "an error", and the later is not incorporated into the modelling). It is unclear if and to what extent this limits current RL formulations. There are also potentially important missing details about the models. Can the authors justify/explain the reasoning behind including these variants they consider? What are the initial Q-values? If these are not free parameters what are their values?

We are appreciative of the Reviewer for identifying these potentially unaddressed questions.

The RL models we consider in the present study are naïve models which, in our previous study (FeldmanHall, Otto, & Phelps, 2018), we found to capture important aspects of learning. While simplistic, we believed these models serve as a reasonable baseline for evaluating more complex models, such as the Preference Inference model. We have made this point more explicit in our revised Introduction, Line 129 ~ 132:

“In addition, to mechanistically probe how punitive preferences may be acquired in Adv-I and Dis-I contexts—in turn, assessing the replicability of our earlier study investigating punitive preference acquisition in the Dis-I context—we also characterize trial-by-trial acquisition of punitive behavior with computational models of choice.”

Again, following from our previous modeling of observational learning (FeldmanHall et al., 2018), we believe that the feedback the Teacher provides here is ideally suited to the RL formalism. In particular, when the teacher indicates that the participant’s choice is what they would have preferred, the model receives a reward of ‘1’ (e.g., the participant rejects and the Teacher indicates they would preferred rejection, resulting in a positive prediction error) otherwise, the model receives a reward of ‘0’ (e.g., the participant accepts and the Teacher indicates they would preferred rejection, resulting in a negative prediction error), indicating that the participant did not choose in accordance with the Teacher’s preferences. Through an error driven learning process, these models provide a naïve way of learning to act in accordance with the Teacher’s preferences.

Regarding the requested model details: When treating the initial values as free parameters (model 5), we set Q(reject, offertype) as free values in [0,1] and Q(accept,offertype) as 0.5. This setting can capture participants' initial tendency to reject or accept offers from this offer type. When the initial values are fixed, for all offer types we set Q(reject, offertype) = Q(accept,offertype) = 0.5. In practice, when the initial values are fixed, setting them to 0.5 or 0 doesn’t make much difference. We have clarified these points in our revised Methods, Line 275 ~ 576:

“We kept the initial values fixed in this model, that is Q₀(reject,offertype) =0.5, (offertype ∈ 90:10, 70:30, 50:50, 30:70, 10:90)”

And Line 582 ~ 584:

“Formally, this model treats Q₀(reject,offertype) =0.5, (offertype ∈ 90:10, 70:30, 50:50, 30:70, 10:90) as free parameters with values between 0 and 1.”

(5) Conceptual Leap in Modeling Interpretation: The distinction between simple RL models and preference-inference models seems to hinge on the ability to generalize learning from one offer to another. Whereas in the RL models learning occurs independently for each offer (hence to cross-offer generalization), preference inference allows for generalization between different offers. However, the paper does not explore RL models that allow generalization based on the similarity of features of the offers (e.g., payment for the receiver, payment for the offer-giver, who benefits more). Such models are more parsimonious and could explain the results without invoking a theory of mind or any modelling of the teacher. In such model versions, a learner learns a functional form that allows to predict the teacher's feedback based on said offer features (e.g., linear or quadratic form). Because feedback for an offer modulates the parameters of this function (feature weights) generalization occurs without necessarily evoking any sophisticated model of the other person. This leaves open the possibility that RL models could perform just as well or even show superiority over the preference learning model, casting doubt on the authors' conclusions. Of note: even the behaviourists knew that as Little Albert was taught to fear rats, this fear generalized to rabbits. This could occur simply because rabbits are somewhat similar to rats. But this doesn't mean little Alfred had a sophisticated model of animals he used to infer how they behave.

We are appreciative of the Reviewer for their suggestion of an alternative explanation for the observed generalization effects. Our understanding of the suggestion, put simply, put simply, is that an RL model could capture the observed generalization effects if the model were to learn and update a functional form of the Teacher’s rejection preferences using an RL-like algorithm. This idea is similar, conceptually to our account of preference learning whereby the learner has a representation of the teacher’s preferences. In our experiment the offer is in the range of [0-100], the crux of this idea is why the participants should take the functional form (either v-shaped or quadratic) with the minimum at 50. This is important because, at the beginning of the learning phase, the rejection rates are already v-shaped with 50 as its minimum. The participants do not need to adjust the minimum of this functional form. Thus, if we assume that the participants represent the teacher’s rejection rate as a v-shape function with a minimum at [50,50], then this very likely implies that the participants have a representation that the teacher has a preference for fairness. Above all, we agree that with suitable setup of the functional form, one could implement an RL model to capture the generalization effects, without presupposing an internal “model” of the teacher’s preferences.

However, there is another way of modeling the generalization effect by truly “model-free” similarity-based Reinforcement learning. In this approach, we do not assume any particular functional form of the teacher’s preferences, but rather, assumes that experience acquired in one offer type can be generalized to offers that are close (i.e., similar) to the original offer. Accordingly, we implement this idea using a simple RL model in which the action values for each offer type is updated by a learning rate that is scaled by the distance between that offer and the experienced offer (i.e., the offer that generated the prediction error). This learning rate is governed by a Gaussian distribution, similar to the case in the Gaussian process regression (cf. Chulz, Speekenbrink, & Krause, 2018). The initial value of the ‘Reject’ action, for each offer , is set to a free parameter between 0 and 1, and the initial value for the 'Accept’ action was set to 0.5. The results show that even though this model exhibits the trend of increasing rejection rates observed in the AI-DI punish condition, the initial preferences (i.e., starting point of learning) diverges markedly from the Learning phase behavior we observed in Experiment 1:

Author response image 1.

This demonstrated that the participant at least maintains a representation of the teacher’s preference at the beginning. That is, they have prior knowledge about the shape of this preference. We incorporated this property into the model, that is, we considered a new model that assumes v-shaped starting values for rejection with two parameters, alpha and beta, governing the slope of this v-shaped function (this starting value actually mimics the shape of the preference functions of the Fehr-Schmidt model). We found that this new model (which we term the “Model RL Sim Vstart”) provided a satisfactory qualitative fit of the Transfer phase learning curves in Experiment 1 (see below).

Author response image 2.

However, we didn’t adopt this model as the best model for the following reasons. First, this model yielded a larger AIC value (indicating worse quantitative fit) compared to our preference Inference model in both Experiments 1 and 2, likely owing to its increased complexity (5 free parameters versus 4 in the Preference Inference model). Accordingly, we believe that inclusion of this model in our revised submission would be more distracting than helpful on account of the added complexity of explaining and justifying these assumptions, and of course its comparatively poor goodness of fit (relative to the preference inference model).

(6) Limitations of the Preference-Inference Model: The preference-inference model struggles to capture key aspects of the data, such as the increase in rejection rates for 70:30 DI offers during the learning phase (e.g. Figure 3A, AI+DI blue group). This is puzzling.

Thinking about this I realized the model makes quite strong unintuitive predictions that are not examined. For example, if a subject begins the learning phase rejecting the 70:30 offer more than 50% of the time (meaning the starting guilt parameter is higher than 1.5), then overleaning the tendency to reject will decrease to below 50% (the guilt parameter will be pulled down below 1.5). This is despite the fact the teacher rejects 75% of the offers. In other words, as learning continues learners will diverge from the teacher. On the other hand, if a participant begins learning to tend to accept this offer (guilt < 1.5) then during learning they can increase their rejection rate but never above 50%. Thus one can never fully converge on the teacher. I think this relates to the model's failure in accounting for the pattern mentioned above. I wonder if individuals actually abide by these strict predictions. In any case, these issues raise questions about the validity of the model as a representation of how individuals learn to align with a teacher's preferences (given that the model doesn't really allow for such an alignment).

In response to this comment we explain our efforts to build a new model that might be able conceptually resolves the issue identified by the Reviewer.

The key intuition guiding the Preference inference model is a Bayesian account of learning which we aimed to further simplify. In this setting, a Bayesian learner maintains a representation of the teacher’s inequity aversion parameters and updates it according to the teacher’s (observed) behavior. Intuitively, the posterior distribution shifts to the likelihood of the teacher’s action. On this view, when the teacher rejects, for instance, an AI offer, the learner should assign a higher probability to larger values of the Guilt parameter, and in turn the learner should change their posterior estimate to better capture the teacher’s preferences.

In the current study, we simplified this idea, implementing this sort of learning using incremental “delta rule” updating (e.g. Equation 8 of the main text). Then the key question is to define the “teaching signal”. Assuming that the teacher rejects an offer 70:30, based on Bayesian reasoning, the teacher’s envy parameter (α) is more likely to exceed 1.5 (computed as 30/(50-30), per equation 7) than to be smaller than 1.5. Thus, 1.5, which is then used in equation 8 to update α, can be thought of as a teaching signal. We simply assumed that if the initial estimate is already greater than 1.5, which means the prior is consistent with the likelihood, no updating would occur. This assumption raises the question of how to set the learning rate range. In principle, an envy parameter that is larger than 1.5 should be the target of learning (i.e., the teaching signal), and thus our model definition allows the learning rate to be greater than 1, incorporating this possibility.

Our simplified preference inference model has already successfully captured some key aspects of the participants’ learning behavior. However, it may fail in the following case: assume that the participant has an initial estimate of 1.51 for the envy parameter (β). Let’s say this corresponds to a rejection rate of 60%. Thus, no matter how many times the teacher rejects the offer 70:30, the participant’s estimate of the envy parameter remains the same, but observing only one offer acceptance would decrease this estimate, and in turn, would decrease the model’s predicted rejection rate. We believe this is the anomalous behavior—in 70:30 offers—identified by the Reviewer which the model does not appear able to recreate participants’ in these offers.

This issue actually touches the core of our model specification, that is, the choosing of the teaching signal. As we chose 1.5 as the teaching signal—i.e. lower bound on whenever the teacher rejects or accepts an offer of 70:30, a very small deviation of 1.5 would fail one part of updating. One way to mitigate this problem would be to choose a lower bound for α greater than 1.5, such that when the Teacher rejects a 70:30 offer, we assign a number greater than 1.5 (by ‘hard-coding’ this into the model via modification of equation 7). One sensible candidate value could be the middle point between 1.5 and 10 (the maximum value of α per our model definition). Intuitively, the model of this setting could still pull up the value of α to 1.51 when the teacher rejects 70:30, thus alleviating (but not completely eliminating) the anomaly.

We fitted this modified Preference Inference model to the data from Experiment 1 (see Author response image 3 below) and found that even though this model has a smaller AIC (and thus better quantitative fit than the original Preference Inference model), it still doesn’t fully capture the participants’ behavior for 70:30 offers.

Author response image 3.

Accordingly, rather than revising our model to include an unprincipled ‘kludge’ to account for this minor anomaly in the model behavior, we have opted to report our original model in our revision as we still believe it parsimoniously captures our intuitions about preference learning and provides a better fit to the observed behavior than the other RL models considered in the present study.

Reviewer #1 (Recommendations for the authors):

(1) I do not particularly prefer the acronyms AI and DI for disadvantageous inequity and advantageous inequity. Although they have been used in the literature, not every single paper uses them. More importantly, AI these days has such a strong meaning of artificial intelligence, so when I was reading this, I'd need to very actively inhibit this interpretation. I believe for the readability for a wider readership of eLife, I would advise not to use AI/DI here, but rather use the full terms.

We thank the Reviewer for this suggestion. As the full spelling of the two terms are somewhat lengthy, and appear frequently in the figures, we have elected to change the abbreviations for disadvantageous inequity and advantageous inequity to Dis-I and Adv-I, respectively in the main text and the supplementary information. We still use AI/DI in the response letter to make the terminology consistent.

(2) Do "punishment rate" and "rejection rate" mean the same? If so, it would be helpful to stick with one single term, eg, rejection rate.

We thank the Reviewer for this suggestion. As these terms have the same meaning, we have opted to use the term “rejection rate” throughout the main text.

(3) For the linear mixed effect models, were other random effect structures also considered (eg, random slops of experimental conditions)? It might be worth considering a few model specifications and selecting the best one to explain the data.

Thanks for this comment. Following established best practices (Barr, Levy, Scheepers, & Tily, 2013) we have elected to use a maximal random effects structure, whereby all possible predictor variables in the fixed effects structure also appear in the random effects structure.

(4) For equation (4), the softmax temperature is denoted as tau, but later in the text, it is called gamma. Please make it consistent.

We are appreciative of the Reviewer’s attention to detail. We have corrected this error.

Reviewer #2 (Recommendations for the authors):

(1) Several Tables in SI are unclear. I wasn't clear if these report raw probabilities of coefficients of mixed models. For any mixed models, it would help to give the model specification (e.g., Walkins form) and explain how variables were coded.

We are appreciative of the Reviewer’s attention to detail. We have clarified, in the captions accompanying our supplemental regression tables, that these coefficients represent log-odds. Regretfully we are unaware of the “Walkins form” the Reviewer references (even after extensive searching of the scientific literature). However, in our new revision we do include lme4 model syntax in our supplemental information which we believe will be helpful for readers seeking replicate our model specification.

(2) In one of the models it was said that the guilt and envy parameters were bounded between 0-1 but this doesn't make sense and I think values outside this range were later reported.

We are again appreciative of the Reviewer’s attention to detail. This was an error we have corrected— the actual range is [0,10].

(3) It is unclear if the model parameters are recoverable.

In response to this comment our revision now reports a basic parameter recovery analysis for the winning Preference Inference model. This is reported in our revised Methods:

“Finally, to verify if the free parameters of the winning model (Preference Inference) are recoverable, we simulated 200 artificial subjects, based on the Learning Phase of Experiment 1, with free parameters randomly chosen (uniformly) from their defined ranges. We then employed the same model-fitting procedure as described above to estimate these parameter value, observing that parameters. We found that all parameters of the model can be recovered (see Figure S2).”

And scatter plots depicting these simulated (versus recovered) parameters are given in Figure S2 of our revised Supplementary Information:

(4) I was confused about what Figure S2 shows. The text says this is about correlating contagious effects for different offers but the captions speak about learning effects. This is an important aspect which is unclear.

We have removed this figure in response to both Reviewers’ comments about the limited insights that can be drawn on the basis of these correlations.

Author response:

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

Reviewer #1 (Public review):

Summary:

The aim of this paper is to develop a simple method to quantify fluctuations in the partitioning of cellular elements. In particular, they propose a flow-cytometry-based method coupled with a simple mathematical theory as an alternative to conventional imaging-based approaches.

Strengths:

The approach they develop is simple to understand and its use with flow-cytometry measurements is clearly explained. Understanding how the fluctuations in the cytoplasm partition vary for different kinds of cells is particularly interesting.

Weaknesses:

The theory only considers fluctuations due to cellular division events. This seems a large weakness because it is well known that fluctuations in cellular components are largely affected by various intrinsic and extrinsic sources of noise and only under particular conditions does partitioning noise become the dominant source of noise.

We thank the Reviewer for her/his evaluation of our manuscript. The point raised is indeed a crucial one. In a cell division cycle, there are at least three distinct sources of noise that affect component numbers [1] :

(1) Gene expression and degradation, which determine component numbers fluctuations during cell growth.

(2) Variability in cell division time, which depending on the underlying model may or may not be a function of protein level and gene expression.

(3) Noise in the partitioning/inheritance of components between mother and daughter cells.

Our approach specifically addresses the latter, with the goal of providing a quantitative measure of this noise source. For this reason, in the present work, we consider homogeneous cancer cell populations that could be considered to be stationary from a population point-of-view. By tracking the time evolution of the distribution of tagged components via live fluorescent markers, we aim at isolating partitioning noise effects. However, as noted by the Reviewer, other sources of noise are present, and depending on the considered system the relative contributions of the different sources may change. Thus, we agree that a quantification of the effect of the various noise sources on the accuracy of our measurements will improve the reliability of our method.

In this respect, assuming independence between noise sources, we reasoned that variability in cell cycle length would affect the timing of population emergence but not the intrinsic properties of those populations (e.g., Gaussian variance). To test this hypothesis, we conducted a preliminary set of simulations in which cell division times were drawn from an Erlang distribution (mean = 18 h, k=4k = 4k=4). The results, showing the behavior of the mean and variance of the component distributions across generations, are presented in Supplementary Information - Figure 1. Under the assumption of independence between different noise sources, no significant effects were observed even for high asymmetries of the partitioning distribution.

Next, we quantified the accuracy of our measurements in the presence of cross-talks between the various noise sources.Indeed, cells may adopt different growth and division strategies, which can be grouped into three categories based on what triggers division:

● Sizer-like cells divide upon reaching a certain size;

● Timer-like cells divide after a fixed time (corresponding to the previously treated case with independent noise);

● Adder-like cells divide once their volume has increased by a finite amount.

A detailed discussion of these strategies, including their mathematical formulation, can be found in [2]. Here we have assumed that cells follow a sizer-like model. In this way, we study a system in which cells with a higher number of components have shorter division times. Hence, older (newer) generations are emptied (populated) starting from higher values.

As can be observed, higher levels of division asymmetry increase the fluctuations of the system relative to the analytically expected behavior, particularly in later generations.

The result in Supplementary Information - Figure 3 demonstrates the robustness of our method, as the estimates remain within the pre-established experimental error margin. We have now discussed this aspect both in the main and in the Supplementary Information and thank the Reviewer for pointing it out.

(1) Soltani, Mohammad, et al. "Intercellular variability in protein levels from stochastic expression and noisy cell cycle processes." PLoS computational biology 12.8 (2016): e1004972.

(2) Mattia Miotto, Simone Scalise, Marco Leonetti, Giancarlo Ruocco, Giovanna Peruzzi, and Giorgio Gosti. A size-dependent division strategy accounts for leukemia cell size heterogeneity. Communications Physics, 7(1):248, 2024.

Reviewer #2 (Public review):

Summary:

The authors present a combined experimental and theoretical workflow to study partitioning noise arising during cell division. Such quantifications usually require time-lapse experiments, which are limited in throughput. To bypass these limitations, the authors propose to use flow-cytometry measurements instead and analyse them using a theoretical model of partitioning noise. The problem considered by the authors is relevant and the idea to use statistical models in combination with flow cytometry to boost statistical power is elegant. The authors demonstrate their approach using experimental flow cytometry measurements and validate their results using time-lapse microscopy. However, while I appreciate the overall goal and motivation of this work, I was not entirely convinced by the strength of this contribution. The approach focuses on a quite specific case, where the dynamics of the labelled component depend purely on partitioning. As such it seems incompatible with studying the partitioning noise of endogenous components that exhibit production/turnover. The description of the methods was partly hard to follow and should be improved. In addition, I have several technical comments, which I hope will be helpful to the authors.

We are grateful to the Reviewer for the comments. Indeed, both partitioning and production turnover noise are in general fundamental processes. At present the only way to consider them together are time-consuming and costly transfection/microscopy/tracking experiments. In this work, we aimed at developing a method to effectively pinpoint the first component, i.e. partitioning noise thus we opted to separate the two different noise sources.

Below, we provided a point-by-point response that we hope will clarify all raised concerns.

Comments:

(1) In the theoretical model, copy numbers are considered to be conserved across generations. As a consequence, concentrations will decrease over generations due to dilution. While this consideration seems plausible for the considered experimental system, it seems incompatible with components that exhibit production and turnover dynamics. I am therefore wondering about the applicability/scope of the presented approach and to what extent it can be used to study partitioning noise for endogenous components. As presented, the approach seems to be limited to a fairly small class of experiments/situations.

We see the Reviewer's point. Indeed, we are proposing a high-throughput and robust procedure to measure the partitioning/inheritance noise of cell components through flow cytometry time courses. By using live-cell staining of cellular compounds, we can track the effect of partitioning noise on fluorescence intensity distribution across successive generations. This specific procedure is purposely optimized to isolate partitioning noise from other sources and, as it is, can not track endogenous components or dyes that require fixation. While this certainly poses limits to the proposed approach, there are numerous contexts in which our methodology could be used to explore the role of asymmetric inheritance. Among others, (i) investigating how specific organelles are differentially partitioned and how this influences cellular behavior could provide deeper insights into fundamental biological processes: asymmetric segregation of organelles is a key factor in cell differentiation, aging, and stress response. During cell division, organelles such as mitochondria, the endoplasmic reticulum, lysosomes, peroxisomes, and centrosomes can be unequally distributed between daughter cells, leading to functional differences that influence their fate. For instance, Kajaitso et al. [1] proposed that asymmetric division of mitochondria in stem cells is associated with the retention of stemness traits in one daughter cell and differentiation in the other. As organisms age, stem cells accumulate damage, and to prevent exhaustion and compromised tissue function, cells may use asymmetric inheritance to segregate older or damaged subcellular components into one daughter cell. (ii) Asymmetric division has also been linked to therapeutic resistance in Cancer Stem Cells [2]. Although the functional consequences are not yet fully determined, the asymmetric inheritance of mitochondria is recognized as playing a pivotal role [3]. Another potential application of our methodology may be (iii) the inheritance of lysosomes, which, together with mitochondria, appears to play a crucial role in determining the fate of human blood stem cells [4]. Furthermore, similar to studies conducted on liquid tumors [5][6], our approach could be extended to investigate cell growth dynamics and the origins of cell size homeostasis in adherent cells [7][8][9]. The aforementioned cases of study can be readily addressed using our approach that in general is applicable whenever live-cell dyes can be used. We have added a discussion of the strengths and limitations of the method in the Discussion section of the revised version of the manuscript

(1) Katajisto, Pekka, et al. "Asymmetric apportioning of aged mitochondria between daughter cells is required for stemness." Science 348.6232 (2015): 340-343.

(2) Hitomi, Masahiro, et al. "Asymmetric cell division promotes therapeutic resistance in glioblastoma stem cells." JCI insight 6.3 (2021): e130510.

(3) García-Heredia, José Manuel, and Amancio Carnero. "Role of mitochondria in cancer stem cell resistance." Cells 9.7 (2020): 1693.

(4) Loeffler, Dirk, et al. "Asymmetric organelle inheritance predicts human blood stem cell fate." Blood, The Journal of the American Society of Hematology 139.13 (2022): 2011-2023.

(5) Miotto, Mattia, et al. "Determining cancer cells division strategy." arXiv preprint arXiv:2306.10905 (2023).

(6) Miotto, Mattia, et al. "A size-dependent division strategy accounts for leukemia cell size heterogeneity." Communications Physics 7.1 (2024): 248.

(7) Kussell, Edo, and Stanislas Leibler. "Phenotypic diversity, population growth, and information in fluctuating environments." Science 309.5743 (2005): 2075-2078.

(8) McGranahan, Nicholas, and Charles Swanton. "Clonal heterogeneity and tumor evolution: past, present, and the future." Cell 168.4 (2017): 613-628.

(9) De Martino, Andrea, Thomas Gueudré, and Mattia Miotto. "Exploration-exploitation tradeoffs dictate the optimal distributions of phenotypes for populations subject to fitness fluctuations." Physical Review E 99.1 (2019): 012417.

(2) Similar to the previous comment, I am wondering what would happen in situations where the generations could not be as clearly identified as in the presented experimental system (e.g., due to variability in cell-cycle length/stage). In this case, it seems to be challenging to identify generations using a Gaussian Mixture Model. Can the authors comment on how to deal with such situations? In the abstract, the authors motivate their work by arguing that detecting cell divisions from microscopy is difficult, but doesn't their flow cytometry-based approach have a similar problem?

The point raised is an important one, as it highlights the fundamental role of the gating strategy. The ability to identify the distribution of different generations using the Gaussian Mixture Model (GMM) strongly depends on the degree of overlap between distributions. The more the distributions overlap, the less capable we are of accurately separating them.

The extent of overlap is influenced by the coefficients of variation (CV) of both the partitioning distribution function and the initial component distribution. Specifically, the component distribution at time t results from the convolution of the component distribution itself at time t−1 and the partitioning distribution function. Therefore, starting with a narrow initial component distribution allows for better separation of the generation peaks. The balance between partitioning asymmetry and the width of the initial component distribution is thus crucial.

As shown in Supplementary Information - Figure 5, increasing the CV of either distribution reduces the ability to distinguish between different generations.

However, the variance of the initial distribution cannot be reduced arbitrarily. While selecting a narrow distribution facilitates a better reconstruction of the distributions, it simultaneously limits the number of cells available for the experiment. Therefore, for components exhibiting a high level of asymmetry, further narrowing of the initial distribution becomes experimentally impractical.

In such cases, an approach previously tested on liquid tumors [1] involves applying the Gaussian Mixture Model (GMM) in two dimensions by co-staining another cellular component with lower division asymmetry.

Regarding time-lapse fluorescence microscopy, the main challenge lies not in disentangling the interplay of different noise sources, but rather in obtaining sufficient statistical power from experimental data. While microscopy provides detailed insights into the division process and component partitioning, its low throughput limits large-scale statistical analyses. Current segmentation algorithms still perform poorly in crowded environments and with complex cell shapes, requiring a substantial portion of the image analysis pipeline to be performed manually, a process that is time-consuming and difficult to scale. In contrast, our cytometry-based approach bypasses this analysis bottleneck, as it enables a direct population-wide measurement of the system's evolution. We have added a detailed discussion of this argument in the Supplementary Material of the manuscript and added a clarification of the role of the gating strategy in the main text.

(1) Peruzzi, Giovanna, et al. "Asymmetric binomial statistics explains organelle partitioning variance in cancer cell proliferation." Communications Physics 4.1 (2021): 188.

(3) I could not find any formal definition of division asymmetry. Since this is the most important quantity of this paper, it should be defined clearly.

We thank the Reviewer for the note. With division asymmetry we refer to a quantity that reflects how similar two daughter cells are likely to be in terms of inherited components after a division process. We opted to measure it via the coefficient of variation (root squared variance divided by the mean) of the partitioning fraction distribution. We have amended this lack of definition in the reviewed version of the manuscript.

(4) The description of the model is unclear/imprecise in several parts. For instance, it seems to me that the index "i" does not really refer to a cell in the population, but rather a subpopulation of cells that has undergone a certain number of divisions. Furthermore, why is the argument of Equation 11 suddenly the fraction f as opposed to the component number? I strongly recommend carefully rewriting and streamlining the model description and clearly defining all quantities and how they relate to each other.

We have amending the text carefully to avoid double naming of variables and clarifying each computation passage. In equation 11 the variable f refers to the fluorescent intensity, but the notation will be changed to increase clarity.

(5) Similarly, I was not able to follow the logic of Section D. I recommend carefully rewriting this section to make the rationale, logic, and conclusions clear to the reader.

We have updated the manuscript clarifying the scope of section D and its results. In brief, Section A presents a general model to derive the variance of the partitioning distribution from flow cytometry time-course data without making any assumptions about the shape of the distribution itself. In Section D, our goal is to interpret the origin of asymmetry and propose a possible form for the partitioning distribution. Since the dyes used bind non-specifically to cytoplasmic amines, the tagged proteins are expected to be uniformly distributed throughout the cytoplasm and present in large numbers. Given these assumptions the least complex model for division follows the binomial distribution, with a parameter that measures the bias in the process. Therefore, we performed a similar computation to that in Section A, which allows us to estimate not only the variance but also the degree of biased asymmetry. Finally, we fitted the data to this new model and proposed an experimental interpretation of the results.

(6) Much theoretical work has been done recently to couple cell-cycle variability to intracellular dynamics. While the authors neglect the latter for simplicity, it would be important to further discuss these approaches and why their simplified model is suitable for their particular experiments.

We agree with the Reviewer, we have added a discussion on this topic in the Introduction and Discussion sections of the main text.

(7) In the discussion the authors note that the microscopy-based estimates may lead to an overestimation of the fluctuations due to limited statistics. I could not follow that reasoning. Due to the gating in the flow cytometry measurements, I could imagine that the resulting populations are more stringently selected as compared to microscopy. Could that also be an explanation? More generally, it would be interesting to see how robust the results are in terms of different gating diameters.

The Reviewer is right on the importance of the sorting procedure. As already discussed in a previous point, the gating strategy we employed plays a fundamental role: it reduces the overlap of fluorescence distributions as generations progress, enables the selection of an initial distribution distinct from the fluorescence background, allowing for longer tracking of proliferation, and synchronizes the initial population. The narrower the initial distribution, the more separated the peaks of different generations will be. However, this also results in a smaller number of cells available for the experiment, requiring a careful balance between precision and experimental feasibility. A similar procedure, although it would certainly limit the estimation error, would be impracticable In the case of microscopy. Indeed, the primary limitation and source of error is the number of recorded events. Our pipeline allowed us to track on the order of hundreds of division dynamics, but the analysis time scales non-linearly with the number of events. Significantly increasing the dataset would have been extremely time-consuming. Reducing the analysis to cells with similar fluorescence, although theoretically true, would have reduced the statistics to a level where the sampling error would drastically dominate the measure. Moreover, different experiments would have been hardly comparable, since different fluorescences could map in equally sized cells. In light of these factors, we expect higher CV for the microscopy measure than for flow cytometry’s ones. In the plots below, we show the behaviour of the mean and the standard deviation of N numbers sampled from a gaussian distribution N(0,1) as a function of the sampling number N. The higher is N the closer the sampled distribution will be to the true one. The region in the hundreds of samples is still very noisy, but to do much better we would have to reach the order of thousands. We have added a discussion on these aspects in the reviewed version of the manuscript, with a deeper description of the importance of the sorting procedure in the Supplementary Material. .

Author response image 1.

Standard deviation and mean value of a distribution of points sampled from a Gaussian distribution with mean 0 and standard deviation 1, versus the number of samples, N. Increasing N leads to a closer approximation of the expected values. In orange is highlighted the Microscopy Working Region (Microscopy WR) which corresponds to the number of samples we are able to reach with microscopy experiments. In yellow the region we would have to reach to lower the estimating error, which is although very expensive in terms of analysis time.

(7) It would be helpful to show flow cytometry plots including the identified subpopulations for all cell lines, currently, they are shown only for HCT116 cells. More generally, very little raw data is shown.

We have provided the requested plots for the other cell lines together with additional raw data coming from simulations in the Supplementary Material.

(8) The title of the manuscript could be tailored more to the considered problem. At the moment it is very generic.

We see the Reviewer point. The proposed title aims at conveying the wide applicability of the presented approach, which ultimately allows for the assessment of the levels of fluctuations in the levels of the cellular components at division. This in turn reflects the asymmetricity in the division.

Reviewer #1 (Recommendations for the authors):

(1) I am quite concerned about the fact that the theory only considers fluctuations due to cellular division events since intrinsic and extrinsic noise sources are often dominant. I suggest that the authors simulate a full model of cell growth and division (that accounts for fluctuations in gene expression, cell-cycle dynamics, and cell division to generate a controlled synthetic dataset and then use this as input to their method to understand how robust are their results to the influence of noise sources other than partitioning.

We thank the reviewer for the suggestions and following his advice we performed two sets of simulations in which we took into account the effect of the other noise sources. A detailed description of the results and the methods has been added to the Supplementary Material, while the topic has also been assessed in the main text. A cell proliferation cycle is affected by different sources of variability: (i) production and degradation processes of molecules; (ii) variability in length of the cell cycle; (iii) partitioning noise, which identifies asymmetric inheritance of components between the two daughter cells. However, the experimental approach and the model have been formulated to specifically address the effects of partitioning noise. Indeed, since we are dealing with components tagged via live fluorescent markers, production of new fluorophores is impossible and can therefore be discarded. Instead, the degradation process is a global effect that influences the behavior of the mean of the distribution in a time-dependent manner. However, by looking at the experimental data in Figure 1 of the main text, no significant depletion of fluorescence is observed, or at least it is hidden by the experimental fluctuations of the measure. Instead, a more careful evaluation has to be done for what concerns fluctuation in cell cycle length. We conducted two sets of simulations. In the first, we assumed the independence between fluctuations in cell cycle length and partitioning noise.

Cell’s division time was extracted from an Erlang distribution (mean = 18 , k = 4) and the results, showing the behavior of the mean and variance of the component distributions across generations, are presented in Supplementary Information - Figure 1. Under the assumption of independence between different noise sources, no significant effects were observed even for high asymmetries of the partitioning distribution. The second set of simulations considered a situation in which the cell’s components and division time are coupled. We assumed a sizer-like division strategy for which bigger cells have a shorter division time and the results of the simulations are shown in Supplementary Information - Figure 2.

As can be observed, higher levels of division asymmetry increase the fluctuations of the system relative to the analytically expected behavior, particularly in later generations.

The result in Supplementary Information - Figure 3 demonstrates the robustness of our method, as the estimates remain within the pre-established experimental error margin. However, a detailed description of this topic has been provided in the Supplementary Information and into the main text.

(2) I find the use of the Cauchy distribution somewhat odd since this does not have a finite mean or a variance and I suspect it is unlikely this mimics a naturally measurable distribution in their experiments. This should either be justified biologically or else replaced by a more realistic distribution.

Following the reviewer’s suggestion, we have changed the distribution to Gaussian one.

(3) There is a large body of literature on gene expression models that incorporate a large amount of detail including cell-cycle dynamics and cell division which are relevant to their discussion but not referenced. I suggest they read the following and see how to incorporate at least some of them in their discussion:

Frequency domain analysis of fluctuations of mRNA and protein copy numbers within a cell lineage: theory and experimental validation., Physical Review X, 11.2 (2021): 021032.

Exact solution of stochastic gene expression models with bursting, cell cycle and replication dynamics., Physical Review E, 101.3 (2020): 032403.

Coupling gene expression dynamics to cell size dynamics and cell cycle events: Exact and approximate solutions of the extended telegraph model., Iscience, 26.1 (2023).

Models of protein production along the cell cycle: An investigation of possible sources of noise., Plos one, 15.1 (2020): e0226016.

Sources, propagation and consequences of stochasticity in cellular growth., Nature communications, 9(1), 4528

Intrinsic and extrinsic noise of gene expression in lineage trees., Scientific Reports, 9.1 (2019): 474.

We thank the Reviewer for the provided articles. We enlarged both introduction and discussion commenting on them, also in response to the second Reviewer comments.

Reviewer #2 (Recommendations for the authors):

(1) Even when it is used only during simulation for the sake of illustration, the Cauchy distribution is a somewhat unfortunate choice as its moments do not exist and hence, the authors' approach would not apply. I would recommend using another distribution instead.

Following the Reviewer’s suggestion we have changed the distribution to Gaussian ones.

(2) "cells population" should be "cell population".

We have amended this mistake in the text.

Author Response

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

Reviewer #1:

Concerns Public Review:

1)The framing of 'infinite possible types of conflict' feels like a strawman. While they might be true across stimuli (which may motivate a feature-based account of control), the authors explore the interpolation between two stimuli. Instead, this work provides confirmatory evidence that task difficulty is represented parametrically (e.g., consistent with literatures like n-back, multiple object tracking, and random dot motion). This parametric encoding is standard in feature-based attention, and it's not clear what the cognitive map framing is contributing.

Suggestion:

1) 'infinite combinations'. I'm frankly confused by the authors response. I don't feel like the framing has changed very much, besides a few minor replacements. Previous work in MSIT (e.g., by the author Zhongzheng Fu) has looked at whether conflict levels are represented similarly across conflict types using multivariate analyses. In the paper mentioned by Ritz & Shenhav (2023), the authors looked at whether conflict levels are represented similarly across conflict types using multivariate analyses. It's not clear what this paper contributes theoretically beyond the connections to cognitive maps, which feel like an interpretative framework rather than a testable hypothesis (i.e., these previous paper could have framed their work as cognitive maps).

Response: We acknowledge the limitations inherent in our experimental design, which prevents us from conducting a strict test of the cognitive space view. In our previous revision, we took steps to soften our conclusions and emphasize these limitations. However, we still believe that our study offers valuable and novel insights into the cognitive space, and the tests we conducted are not merely strawman arguments.

Specifically, our study aimed to investigate the fundamental principles of the cognitive space view, as we stated in our manuscript that “the representations of different abstract information are organized continuously and the representational geometry in the cognitive space is determined by the similarity among the represented information (Bellmund et al., 2018)”. While previous research has applied multivariate analyses to understand cognitive control representation, no prior studies had directedly tested the two key hypotheses associated with cognitive space: (1) that cognitive control representation across conflict types is continuous, and (2) that the similarity among representations of different conflict types is determined by their external similarity.

Our study makes a unique contribute by directly testing these properties through a parametric manipulation of different conflict types. This approach differs significantly from previous studies in two ways. First, our parametric manipulation involves more than two levels of conflict similarity, enabling us to directly test the two critical hypotheses mentioned above. Unlike studies such as Fu et al. (2022) and other that have treated different conflict types categorically, we introduced a gradient change in conflict similarity. This differentiation allowed us to employ representational similarity analysis (RSA) over the conflict similarity, which goes beyond mere decoding as utilized in prior work (see more explanation below for the difference between Fu et al., 2022 and our study [1]).

Second, our parametric manipulation of conflict types differs from previous studies that have manipulated task difficulty, and the modulation of multivariate pattern similarity observed in our study could not be attributed by task difficulty. Previous research, including the Ritz & Shenhav (2023) (see below explanation[2]), has primarily shown that task difficulty modulates univoxel brain activation. A recent work by Wen & Egner (2023) reported a gradual change in the multivariate pattern of brain activations across a wide range of frontoparietal areas, supporting the reviewer’s idea that “task difficulty is represented parametrically”. However, we do not believe that our results reflect the task difficulty representation. For instance, in our study, the spatial Stroop-only and Simon-only conditions exhibited similar levels of difficulty, as indicated by their relatively comparable congruency effects (Fig. S1). Despite this similarity in difficulty, we found that the representational similarity between these two conditions was the lowest (see revised Fig. S4, the most off-diagonal value). This observation aligns more closely with our hypothesis that these two conditions are most dissimilar in terms of their conflict types.

[1] Fu et al. (2022) offers important insights into the geometry of cognitive space for conflict processing. They demonstrated that Simon and flanker conflicts could be distinguished by a decoder that leverages the representational geometry within a multidimensional space. However, their model of cognitive space primarily relies on categorical definitions of conflict types (i.e., Simon versus flanker), rather than exploring a parametric manipulation of these conflict types. The categorical manipulations make it difficult to quantify conceptual similarity between conflict types and hence limit the ability to test whether neural representations of conflict capture conceptual similarity. To the best of our knowledge, no previous studies have manipulated the conflict types parametrically. This gap highlights a broader challenge within cognitive science: effectively manipulating and measuring similarity levels for conflicts, as well as other high-level cognitive processes, which are inherently abstract. We therefore believe our parametric manipulation of conflict types, despite its inevitable limitations, is an important contribution to the literature.

We have incorporated the above statements into our revised manuscript: Methodological implications. Previous studies with mixed conflicts have applied mainly categorical manipulations of conflict types, such as the multi-source interference task (Fu et al., 2022) and color Stroop-Simon task (Liu et al., 2010). The categorical manipulations make it difficult to quantify conceptual similarity between conflict types and hence limit the ability to test whether neural representations of conflict capture conceptual similarity. To the best of our knowledge, no previous studies have manipulated the conflict types parametrically. This gap highlights a broader challenge within cognitive science: effectively manipulating and measuring similarity levels for conflicts, as well as other high-level cognitive processes, which are inherently abstract. The use of an experimental paradigm that permits parametric manipulation of conflict similarity provides a way to systematically investigate the organization of cognitive control, as well as its influence on adaptive behaviors.

[2] The work by Ritz & Shenhav (2023) indeed applied multivariate analyses, but they did not test the representational similarity across different levels of task difficulty in a similar way as our investigation into different levels of conflict types, neither did they manipulated conflict types as our study. They first estimated univariate brain activations that were parametrically scaled by task difficulty (e.g., target coherence), yielding one map of parameter estimates (i.e., encoding subspace) for each of the target coherence and distractor congruence. The multivoxel patterns from the above maps were correlated to test whether the target coherence and distractor congruence share the similar neural encoding. It is noteworthy that the encoding of task difficulty in their study is estimated at the univariate level, like the univariate parametric modulation analysis in our study. The representational similarity across target coherence and distractor congruence was the second-order test and did not reflect the similarity across different difficulty levels. Though, we have found another study (Wen & Egner, 2023) that has directly tested the representational similarity across different levels of task difficulty, and they observed a higher representational similarity between conditions with similar difficulty levels within a wide range of brain regions.

Reference:

Wen, T., & Egner, T. (2023). Context-independent scaling of neural responses to task difficulty in the multiple-demand network. Cerebral Cortex, 33(10), 6013-6027. https://doi.org/10.1093/cercor/bhac479

Fu, Z., Beam, D., Chung, J. M., Reed, C. M., Mamelak, A. N., Adolphs, R., & Rutishauser, U. (2022). The geometry of domain-general performance monitoring in the human medial frontal cortex. Science (New York, N.Y.), 376(6593), eabm9922. https://doi.org/10.1126/science.abm9922

Ritz, H., & Shenhav, A. (2023). Orthogonal neural encoding of targets and distractors supports multivariate cognitive control. https://doi.org/10.1101/2022.12.01.518771 Another issue is suggesting mixtures between two types of conflict may be many independent sources of conflict. Again, this feels like the strawman. There's a difference between infinite combinations of stimuli on the one hand, and levels of feature on the other hand. The issue of infinite stimuli is why people have proposed feature-based accounts, which are often parametric, eg color, size, orientation, spatial frequency. Mixing two forms of conflict is interesting, but the task limitations (i.e., highly correlated features) prevent an analysis of whether these are truly mixed (or eg reflect variations on just one of the conflict types). Without being able to compare a mixture between types vs levels of only one type, it's not clear what you can draw from these results re: how these are combined (and not clear how it reconciles the debate between general and specific).

Response: As the reviewer pointed out, a feature (or a parameterization) is an efficient way to encode potentially infinite stimuli. This is the same idea as our hypothesis: different conflict types are represented in a cognitive space akin to concrete features such as a color spectrum. This concept can be illustrated in the figure below.

Author response image 1.

We would like to clarify that in our study we have manipulated five levels of conflict types, but they all originated from two fundamental sources: vertically spatial Stroop and horizontally Simon conflicts. We agree that the mixture of these two sources does not inherently generate additional conflict sources. However, this mixture does influence the similarity among different conflict conditions, which provides essential variability that is crucial for testing the core hypotheses (i.e., continuity and similarity modulation, see the response above) of the cognitive space view. This clarification is crucial as the reviewer’s impression might have been influenced by our introduction, where we repeatedly emphasized multiple sources of conflicts. Our aim in the introduction was to outline a broader conceptual framework, which might not directly reflect the specific design of our current study. Recognizing the possibility of misinterpretation, we have adjusted our introduction and discussion to place less emphasis on the variety of possible conflict sources. For example, we have removed the expression “The large variety of conflict sources implies that there may be innumerable number of conflict conditions” from the introduction. As we have addressed in the previous response, the observed conflict similarity effect could not be attributed to merely task difficulty. Similarly, the mixture of spatial Stroop and Simon conflicts should not be attributed to one conflict source only; doing so would oversimplify it to an issue of task difficulty, as it would imply that our manipulation of conflict types merely represented varying levels of a single conflict, akin to manipulating task difficulty when everything else being equal. Importantly, the mixed conditions differ from variations along a single conflict source in that they also incorporate components of the other conflict source, thereby introducing difference beyond that would be found within variances of a single conflict source. There are a few additional evidence challenging the single dimension assumption. In our previous revisions, we compared model fittings between the Cognitive-Space model and the Stroop-/Simon-only models, and results showed that the CognitiveSpace model (BIC = 5377093) outperformed the Stroop-Only (BIC = 5377122) and Simon-Only (BIC = 5377096) models. This suggests that mixed conflicts might not be solely reflective of either Stroop or Simon sources, although we did not include these results due to concerns raised by reviewers about the validity of such comparisons, given the high anticorrelation between the two dimensions. Furthermore, Fu et al. (2022) demonstrated that the mixture of Simon and Flanker conflicts (the sf condition) is represented as the vector sum of the Flanker and Simon dimensions within their space model, indicating a compositional nature. Similarly, our mixed conditions are combinations of Stroop and Simon conflicts, and it is plausible that these mixtures represent a fusion of both Stroop and Simon components, rather than just one. Thus, we disagree that the mixture of conflicts is a strawman. In response to this concern, we have included a statement in our limitation section: “Another limitation is that in our design, the spatial Stroop and Simon effects are highly anticorrelated. This constraint may make the five conflict types represented in a unidimensional space (e.g., a circle) embedded in a 2D space. This limitation also means we cannot conclusively rule out the possibility of a real unidimensional space driven solely by spatial Stroop or Simon conflicts. However, this appears unlikely, as it would imply that our manipulation of conflict types merely represented varying levels of a single conflict, akin to manipulating task difficulty when everything else being equal. If task difficulty were the primary variable, we would expect to see greater representational similarity between task conditions of similar difficulty, such as the Stroop and Simon conditions, which demonstrates comparable congruency effects (see Fig. S1). Contrary to this, our findings reveal that the Stroop-only and Simon-only conditions exhibit the lowest representational similarity (Fig. S4). Furthermore, Fu et al. (2022) has shown that the representation of mixtures of Simon and Flanker conflicts was compositional, rather than reflecting single dimension, which also applies to our cases.”

My recommendation would be to dramatically rewrite to reduce the framing of this providing critical evidence in favor of cognitive maps, and being more overt about the limitations of this task. However, the authors are not required to make further revisions in eLife's new model, and it's not clear how my scores would change if they made those revisions (ie the conceptual limitations would remain, the claims would just now match the more limited scope).

Response: With the above rationales and the adjustments we have made in the manuscripts, we believe that we have thoroughly acknowledged and articulated the limitations of our study. Therefore, we have decided against a complete rewrite of the manuscript.

Public Review:

2) The representations within DLPFC appear to treat 100% Stoop and (to a lesser extent) 100% Simon differently than mixed trials. Within mixed trials, the RDM within this region don't strongly match the predictions of the conflict similarity model. It appears that there may be a more complex relationship encoded in this region.

Suggestion:

2) RSMs in the key region of interest. I don't really understand the authors response here either. e.g,. 'It is essential to clarify that our conclusions were based on the significant similarity modulation effect identified in our statistical analysis using the cosine similarity model, where we did not distinguish between the within-Stroop condition and the other four within-conflict conditions (Fig. 7A, now Fig. 8A). This means that the representation of conflict type was not biased by the seemingly disparities in the values shown here'. In Figure 1C, it does look like they are testing this model.

It seems like a stronger validation would test just the mixture trials (i.e., ignoring Simon-only and stroop-only). However, simon/stroop-only conditions being qualitatively different does beg the question of whether these are being represented parametrically vs categorically.

Response: We apologize for the confusion caused by our previous response. To clarify, our conclusions have been drawn based on the robust conflict similarity effect.

The conflict similarity regressor is defined by higher values in the diagonal cells (representing within-conflict similarity) than the off-diagonal cells (indicating between-conflict similarity), as illustrated in Fig. 1C and Fig. 8A (now Fig. 4B). It is important to note that this regressor may not be particularly sensitive to the variations within the diagonal cells. Our previous response aimed to emphasize that the inconsistencies observed along the diagonal do not contradict our core hypothesis regarding the conflict similarity effect.

We recognized that since the visualization in Fig. S4, based on the raw RSM (i.e., Pearson correlation), may have been influenced by other regressors in our model than the conflict similarity effect. To reflect pattern similarity with confounding factors controlled for, we have visualized the RSM by including only the fixed effect of the conflict similarity and the residual while excluding all other factors. As shown in the revised Figure S4, the difference between the within-Stroop and other diagonal cells was greatly reduced. Instead, it revealed a clear pattern where that the diagonal values were higher than the off-diagonal values in the incongruent condition, aligning with our hypothesis regarding the conflict similarity modulator. Although some visual distinctions persist within the five diagonal cells (e.g., in the incongruent condition, the Stroop, Simon, and StMSmM conditions appear slightly lower than StHSmL and StLSmM conditions), follow-up one-way ANOVAs among these five diagonal conditions showed no significant differences. This held true for both incongruent and congruent conditions, with Fs < 1. Thus, we conclude that there is no strong evidence supporting the notion that Simon- and spatial Stroop-only conditions are systematically different from other conflict types. As a result, we decided not to exclude these two conflict types from analysis.

Author response image 2.

The stronger conflict type similarity effect in incongruent versus congruent conditions. Shown are the summary representational similarity matrices for the right 8C region in incongruent (left) and congruent (right) conditions, respectively. Each cell represents the averaged Pearson correlation (after regressing out all factors except the conflict similarity) of cells with the same conflict type and congruency in the 1400×1400 matrix. Note that the seemingly disparities in the values of withinconflict cells (i.e., the diagonal) did not reach significance for either incongruent or congruent trials, Fs < 1.

Public Review:

3) To orthogonalized their variables, the authors need to employ a complex linear mixed effects analysis, with a potential influence of implementation details (e.g., high-level interactions and inflated degrees of freedom).

Suggestion:

3) The DF for a mixed model should not be the number of observations minus the number of fixed effects. The gold standard is to use satterthwaite correction (e.g. in Matlab, fixedEffects(lme,'DFMethod','satterthwaite')), or number of subjects - number of fixed effects (i.e. you want to generalize to new subjects, not just new samples from the same subjects). Honestly, running a 4-way interaction probably is probably using more degrees of freedom than are appropriate given the number of subjects.

Response: We concur with the reviewer’s comment that our previous estimation of degrees of freedom (DFs) was inaccurate. Following your suggestion, we have now applied the “Satterthwaite” approach to approximate the DFs for all our linear mixed effect model analyses. This adjustment has led to the correction of both DFs and p values. In the Methods section, we have mentioned this revision.

“We adjusted the t and p values with the degrees of freedom calculated through the Satterthwaite approximation method (Satterthwaite, 1946). Of note, this approach was applied to all the mixed-effect model analyses in this study.”

The application of this method has indeed resulted in a reduction of our statistical significance. However, our overall conclusions remained robust. Instead of the highly stringent threshold used in our previous version (Bonferonni corrected p < .0001), we have now adopted a relatively more lenient threshold of Bonferonni correction at p < 0.05, which is commonly employed in the literature. Furthermore, it is worth noting that the follow-up criteria 2 and 3 are inherently second-order analyses. Criterion 2 involves examining the interaction effect (conflict similarity effect difference between incongruent and congruent conditions), and criterion 3 involves individual correlation analyses. Due to their second-order nature, these criteria inherently have lower statistical power compared to criterion 1 (Blake & Gangestad, 2020). We thus have applied a more lenient but still typically acceptable false discovery rate (FDR) correction to criteria 2 and 3. This adjustment helps maintain the rigor of our analysis while considering the inherent differences in statistical power across the various criteria. We have mentioned this revision in our manuscript:

“We next tested whether these regions were related to cognitive control by comparing the strength of conflict similarity effect between incongruent and congruent conditions (criterion 2) and correlating the strength to behavioral similarity modulation effect (criterion 3). Given these two criteria pertain to second-order analyses (interaction or individual analyses) and thus might have lower statistical power (Blake & Gangestad, 2020), we applied a more lenient threshold using false discovery rate (FDR) correction (Benjamini & Hochberg, 1995) on the above-mentioned regions.”

With these adjustments, we consistently identified similar brain regions as observed in our previous version. Specifically, we found that only the right 8C region met the three criteria in the conflict similarity analysis. In addition, the regions meeting the criteria for the orientation effect included the FEF and IP2 in left hemisphere, and V1, V2, POS1, and PF in the right hemisphere. We have thoroughly revised the description of our results, updated the figures and tables in both the revised manuscript and supplementary material to accurately reflect these outcomes.

Reference:

Blake, K. R., & Gangestad, S. (2020). On Attenuated Interactions, Measurement Error, and Statistical Power: Guidelines for Social and Personality Psychologists. Pers Soc Psychol Bull, 46(12), 1702-1711. https://doi.org/10.1177/0146167220913363

Minor:

1. Figure 8 should come much earlier (e.g, incorporated into Figure 1), and there should be consistent terms for 'cognitive map' and 'conflict similarity'.

Response: We appreciate this suggestion. Considering that Figure 7 (“The crosssubject RSA model and the rationale”) also describes the models, we have merged Figure 7 and 8 and moved the new figure ahead, before we report the RSA results. Now you could find it in the new Figure 4, see below. We did not incorporate them into Figure 1 since Figure 1 is already too crowded.

Author response image 3.

Fig. 4. Rationale of the cross-subject RSA model and the schematic of key RSMs. A) The RSM is calculated as the Pearson’s correlation between each pair of conditions across the 35 subjects. For 17 subjects, the stimuli were displayed on the top-left and bottom-right quadrants, and they were asked to respond with left hand to the upward arrow and right hand to the downward arrow. For the other 18 subjects, the stimuli were displayed on the top-right and bottom-left quadrants, and they were asked to respond with left hand to the downward arrow and right hand to the upward arrow. Within each subject, the conflict type and orientation regressors were perfectly covaried. For instance, the same conflict type will always be on the same orientation. To de-correlate conflict type and orientation effects, we conducted the RSA across subjects from different groups. For example, the bottom-right panel highlights the example conditions that are orthogonal to each other on the orientation, response, and Simon distractor, whereas their conflict type, target and spatial Stroop distractor are the same. The dashed boxes show the possible target locations for different conditions. (B) and (C) show the orthogonality between conflict similarity and orientation RSMs. The within-subject RSMs (e.g., Group1-Group1) for conflict similarity and orientation are all the same, but the cross-group correlations (e.g., Group2-Group1) are different. Therefore, we can separate the contribution of these two effects when including them as different regressors in the same linear regression model. (D) and (E) show the two alternative models. Like the cosine model (B), within-group trial pairs resemble betweengroup trial pairs in these two models. The domain-specific model is an identity matrix. The domaingeneral model is estimated from the absolute difference of behavioral congruency effect, but scaled to 0 (lowest similarity) – 1 (highest similarity) to aid comparison. The plotted matrices in B-E include only one subject each from Group 1 and Group 2. Numbers 1-5 indicate the conflict type conditions, for spatial Stroop, StHSmL, StMSmM, StLSmH, and Simon, respectively. The thin lines separate four different sub-conditions, i.e., target arrow (up, down) × congruency (incongruent, congruent), within each conflict type.

In our manuscript, the term “cognitive map/space” was used when explaining the results in a theoretical perspective, whereas the “conflict similarity” was used to describe the regressor within the RSA. These terms serve distinct purposes in our study and cannot be interchangeably substituted. Therefore, we have retained them in their current format. However, we recognize that the initial introduction of the “Cognitive-Space model” may have appeared somewhat abrupt. To address this, we have included a brief explanatory note: “The model described above employs the cosine similarity measure to define conflict similarity and will be referred to as the Cognitive-Space model.”

Author response:

The following is the authors’ response to the previous reviews

Editor's note:

Thank you for taking time and efforts to improve this study. After re-review, two reviewers have a consensus that the connections the fatty acids and sperm motility is still ambiguous. Thus, I recommend to further tone down this conclusion consistently in the title and the text pointed out by reviewers before making a final version of record.

We sincerely appreciate the considerable time and effort you and the reviewers devoted to evaluating our manuscript. We have revised the title and text to express the relationship between fatty acids and sperm motility more consistently and toned down. With these revisions, we would like to proceed with publishing the manuscript as the Version of Record (VoR). Thank you very much for your guidance in improving our study.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this revised report, Yamanaka and colleagues investigate a proposed mechanism by which testosterone modulates seminal plasma metabolites in mice. Based on limited evidence in previous versions of the report, the authors softened the claim that oleic acid derived from seminal vesicle epithelium strongly affects linear progressive motility in isolated cauda epididymal sperm in vitro. Though the report still contains somewhat ambiguous references to the strength of the relationship between fatty acids and sperm motility.

Strengths:

Often, reported epidydimal sperm from mice have lower percent progressive motility compared with sperm retrieved from the uterus or by comparison with human ejaculated sperm. The findings in this report may improve in vitro conditions to overcome this problem, as well as add important physiological context to the role of reproductive tract glandular secretions in modulating sperm behaviors. The strongest observations are related to the sensitivity of seminal vesicle epithelial cells to testosterone. The revisions include the addition of methodological detail, modified language to reflect the nuance of some of the measurements, as well as re-performed experiments with more appropriate control groups. The findings are likely to be of general interest to the field by providing context for follow-on studies regarding the relationship between fatty acid beta oxidation and sperm motility pattern.

Weaknesses:

The connection between media fatty acids and sperm motility pattern remains inconclusive.

We would like to express our sincere gratitude to the judges for their cooperation in reviewing the manuscript and for your helpful comments, which were instrumental in improving manuscript.

Reviewer #2 (Public review):

Using a combination of in vivo studies with testosterone-inhibited and aged mice with lower testosterone levels as well as isolated mouse and human seminal vesicle epithelial cells the authors show that testosterone induces an increase in glucose uptake. They find that testosterone induces a difference in gene expression with a focus on metabolic enzymes. Specifically, they identify increased expression of enzymes regulating cholesterol and fatty acid synthesis, leading to increased production of 18:1 oleic acid. The revised version strengthens the role of ACLY as the main regulator of seminal vesicle epithelial cell metabolic programming. The authors propose that fatty acids are secreted by seminal vesicle epithelial cells and are taken up by sperm, positively affecting sperm function. A lipid mixture mimicking the lipids secreted by seminal vesicle epithelial cells, however, only has a small and mostly non-significant effect on sperm motility, suggesting the authors were not apply to pinpoint the seminal vesicle fluid component that positively affects sperm function.

We greatly appreciate the reviewer’s thoughtful comments and time spent reviewing this manuscript. The relationship between lipids such as fatty acids and sperm motility remains unclear in the current dataset. Therefore, before finalizing the manuscript, we revised the title and text, as suggested by the reviewers, to express this conclusion more cautiously and consistently.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Some additional comments are provided below to aid the authors in improving the quality of the work:

Major Comments:

(1) In the newly added supplemental figure 5, the authors note that the percentage data were arcisine transformed prior to statistical analysis without providing any other justification. This seems strange, especially for such a small sample size. It seems more appropriate for the authors to use a nonparametric test. Forcing symmetry without knowing what the shape of the true distribution is makes the ANOVA hard to interpret. Additionally, why use pairwise comparisons rather than comparing each group to the control (LM 0%). Also, note that the graphs are not individually labeled to distinguish them in the legend (A, B, C, etc.). Ultimately, the treatment differences don't seem that meaningful, even if the authors were able to observe statistical significance with the somewhat over-manipulated method of analysis.

Ultimately, the conclusion of this experiment (Supplemental figure 5) remains unchanged, but we agree that the relationship between fatty acids and sperm motility remains unclear. Therefore, before finalizing the manuscript, we revised the title and text as pointed out by the reviewers to express this conclusion more cautiously and consistently throughout the manuscript.

Arcsin transform is commonly used for percentage data [Zar, J.H. 2010. Biostatistical analysis., McDonald, J.H. 2014. Handbook of biological statistics.]. If the values are low or high, such as 0 to 30% or 70 to 100%, without arcsine transformation will result in a large deviation from the normality of the data. However, even if such a conversion is performed, it does not necessarily mean that the assumptions of normality and homogeneity of variance, which are prerequisites for parametric statistical analysis methods, are satisfied.

Given the small sample size and the possibility of non-normal data, we performed Shapiro–Wilk tests for each group (n = 6) and found no departure from normality (all p > 0.1). Q–Q plots and Levene’s test (p > 0.1) likewise supported the assumptions of ANOVA. Following the reviewer’s recommendation, we repeated the analysis with a Kruskal–Wallis test followed by Dunn’s post-hoc comparisons (Bonferroni corrected). Both approaches led to the same conclusions, with non-parametric p-values equal to or smaller than the parametric ones. In the revised manuscript we now report ANOVA as the primary analysis. The author response image includes effect sizes with 95 % confidence intervals, and provide the non-parametric results for transparency.

Author response image 1.

Results of reanalysis of supplementary Figure 5 using nonparametric tests and effect sizes with 95% confidence intervals. Upper part; Differences between groups were assessed by Kruskal–Wallis test, differences among values were analyzed by Dunn’s post-hoc comparisons (Bonferroni corrected) for multiple comparisons. Different letters represent significantly different groups. Lower part; The effect sizes with 95 % confidence intervals. For example, Cliff's Δ = -1 (95% CI ~ -0.6) in VSL's “LM 0 vs LM1” means that LM 1% values exceed LM 0 %values in all pairs.

(2) I appreciate that the authors toned down the interpretation of the effects of seminal plasma metabolites on sperm motility with a cautionary statement on Lines 397-405 and Line 259. However, they send mixed signals with the title of the report: "Testosterone-Induced Metabolic Changes in Seminal Vesicle Epithelial cells Alter Plasma Components to Enhance Sperm Motility", and on line 265 when the say "ACLY expression is upregulated by testosterone and is essential for the metabolic shift of seminal vesicle epithelial cells that mediates sperm linear motility".

The wording has been softened overall. The title has been changed to “Testosterone-Induced Metabolic Changes in Seminal Vesicle Epithelium Modify Seminal Plasma Components with Potential to Improve Sperm Motility” In the results (lines 265-266), we have stated that “ACLY expression is upregulated by testosterone and is essential for the metabolic shift that is associated with increased linear motility” without implying a causal relationship.

Minor Comments:

(1) Typo on line 31: "understanding the male fertility mechanisms and may perspective for the development of potential biomarkers of male fertility and advance in the treatment of male infertility."

We have made the following corrections. “These findings suggest that testosterone-dependent lipid remodeling may contribute to sperm straight-line motility, and further functional verification is required.”

(2) Line 193: the statement is confusing "Therefore, we analyzed mitochondrial metabolism using a flux analyzer, predicting that more glucose is metabolized, pyruvate is metabolized from phosphoenolpyruvic acid through glycolysis in response to testosterone, and is further metabolized in the mitochondria." For example, 'Metabolized through glycolysis' is an ambiguous way to describe the pyruvate kinase reaction. Additionally, phosphoenolpyruvate has three acid ionizable groups, two of which have pKa's well below physiological pH, so phosphoenolpyruvate is the correct intermediate rather than phosphoenolpyruvic acid. The authors make similar mistakes with other organic acids such as citric acid.

Rewritten as “We therefore examined cellular energy metabolism with a flux analyzer, anticipating that testosterone would elevate glycolytic flux, thereby producing more pyruvate from phosphoenolpyruvate. Because extracellular pyruvate levels simultaneously declined, we inferred that the cells had an increased pyruvate demand and, at that time, hypothesized that the excess pyruvate would enter the mitochondria to support enhanced oxidative metabolism.” (lines 193-198)

The organic acids are now referenced in their appropriate forms (e.g., citrate, phosphoenolpyruvate).

(3) Line: 271: "Acly" should be all capitalized to "ACLY". The report mixes capitalizing through out and could be more consistent.

We appreciate the reviewer’s attention to nomenclature and have standardized the manuscript accordingly. Proteins are written in Roman letters, all in capital letters. Mouse gene symbols: italics, first letter capitalize.

Reviewer #2 (Recommendations for the authors):

Major comments:

(1) 'Once capacitation is complete, sperm cannot maintain that state for a long time'. The publications cited by the author do not support that statement and this reviewer also does not agree. Lower fertilization efficiency from in vitro capacitated epidydimal sperm does not have to mean capacitation is reversed, it can simply mean in vitro capacitation conditions not accurately mimic capacitation in vivo.

We thank the reviewer for pointing this out and would like to clarify our position. Our statement does not suggest a "reversal" of active capacitation. Rather, it reflects the well-documented fact that capacitation is a transient process. Sperm that undergo capacitation too early cannot maintain that state for long enough to retain their ability to fertilize at the moment and location of fertilization in vivo.

(2) How do the authors explain the discrepancy between the results shown in Fig. S1E, the increase in sperm motility upon mixing of sperm with SVF and the results reported in Li et al 2025. Mentioning decapacitating factors without further explanation is insufficient.

We appreciate the reviewer's feedback pointing out the need for a clearer explanation.

Seminal plasma is inherently binary, containing both decapacitation factors that delay or inhibit capacitation and nutrient substrates that promote sperm motility.

In vivo, it is believed that the coating of sperm by decapacitation factors is removed by uterine fluid and albumin as it passes through the female reproductive tract [PMID: 22827391, PMID: 24274412]. In contrast, standard fertilization culture media lack a clearance pathway, so decapacitating factors are retained throughout the culture period. As a result, the cleavage rate after in vitro fertilization using sperm exposed to seminal vesicle fluid decreased dramatically.

Lipids, such as fatty acids, increased sperm motility without directly inducing markers of fertilization. These results suggest that the enhancement of motility by lipids is functionally distinct from the capacitation-inhibiting function of seminal plasma proteins. The data from this study are consistent with the biphasic model. Specifically, decapacitation factors temporarily stabilize the sperm membrane, preventing early capacitation. Meanwhile, lipids enhance sperm motility, enabling them to rapidly pass through the hostile uterine environment.

(3) This reviewer does not see the merit in including a lipid mixture motility experiment compared to using OA alone. The increase in motility is still small and far from comparable to the motility increase with seminal vesicle fluid. In this reviewer's opinion the experiment is still inconclusive and should not be highlighted in the manuscript title.

The wording has been softened overall. The title has been changed to “Testosterone-Induced Metabolic Changes in Seminal Vesicle Epithelium Modify Seminal Plasma Components with Potential to Improve Sperm Motility”. (Please see also Reviewer 1's main comment 1)

Minor comments:

(1) 'This change includes a large amplitude of flagella' does not make sense. Please correct.

The following corrections have been made. “This change is characterized by large-amplitude flagellar beating.” (lines 44-45)

Author response:

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

To the Senior Editor and the Reviewing Editor:

We sincerely appreciate the valuable comments provided by the reviewers, the reviewing editor, and the senior editor. Based on our last response and revision, we are confused by the two limitations noted in the eLife assessment. 

(1) benchmarking against comparable methods is limited.

In our last revision, we added the comparison experiments with TNDM, as the reviewers requested. Additionally, it is crucial to emphasize that our evaluation of decoding capabilities of behaviorally relevant signals has been benchmarked against the performance of the ANN on raw signals, which, as Reviewer #1 previously noted, nearly represents the upper limit of performance. Consequently, we believe that our benchmarking methods are sufficiently strong.

(2) some observations may be a byproduct of their method, and may not constitute new scientific observations.

We believe that our experimental results are sufficient to demonstrate that our conclusions are not byproducts of d-VAE based on three reasons:

(1) The d-VAE, as a latent variable model, adheres to the population doctrine, which posits that latent variables are responsible for generating the activities of individual neurons. The goal of such models is to maximize the explanation of the raw signals. At the signal level, the only criterion we can rely on is neural reconstruction performance, in which we have achieved unparalleled results. Thus, it is inappropriate to focus on the mixing process during the model's inference stage while overlooking the crucial de-mixing process during the generation stage and dismissing the significance of our neural reconstruction results. For more details, please refer to the first point in our response to Q4 from Reviewer #4.

(2) The criterion that irrelevant signals should contain minimal information can effectively demonstrate that our conclusions are not by-products of d-VAE. Unfortunately, the reviewers seem to have overlooked this criterion. For more details, please refer to the third point in our response to Q4 from Reviewer #4

(3) Our synthetic experimental results also substantiate that our conclusions are not byproducts of d-VAE. However, it appears the reviewers did not give these results adequate consideration. For more details, please refer to the fourth point in our response to Q4 from Reviewer #4.

Furthermore, our work presents not just "a useful method" but a comprehensive framework. Our study proposes, for the first time, a framework for defining, extracting, and validating behaviorally relevant signals. In our current revision, to clearly distinguish between d-VAE and other methods, we have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem. To our knowledge, current methods have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals. Similarly, existing research has not yet defined and validated behaviorally relevant signals. For more details, please refer to our response to Q1 from Reviewer #4.

Based on these considerations, we respectfully request that you reconsider the eLife assessment of our work. We greatly appreciate your time and attention to this matter.

The main revisions made to the manuscript are as follows:

(1) We have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem, enabling a clearer distinction between d-VAE and other models.

(2) We have moderated the assertion about linear readout to highlight its conjectural nature and have broadened the discussion regarding this conclusion. 

(3) We have elaborated on the model details of d-VAE and have removed the identifiability claim.

To Reviewer #1

Q1: “As reviewer 3 also points out, I would, however, caution to interpret this as evidence for linear read-out of the motor system - your model performs a non-linear transformation, and while this is indeed linearly decodable, the motor system would need to do something similar first to achieve the same. In fact to me it seems to show the opposite, that behaviour-related information may not be generally accessible to linear decoders (including to down-stream brain areas).”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by linear decoders or downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our opinion, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

Q2: “As in my initial review, I would also caution against making strong claims about identifiability although this work and TNDM seem to show that in practise such methods work quite well. CEBRA, in contrast, offers some theoretical guarantees, but it is not a generative model, so would not allow the type of analysis done in this paper. In your model there is a para,eter \alpha to balance between neural and behaviour reconstruction. This seems very similar to TNDM and has to be optimised - if this is correct, then there is manual intervention required to identify a good model.”

Thank you for your comments. 

Considering your concerns about our identifiability claims and the fact that identifiability is not directly relevant to the core of our paper, we have removed content related to identifiability.

Firstly, our model is based on the pi-VAE, which also has theoretical guarantees. However, it is important to note that all such theoretical guarantees (including pi-VAE and CEBRA) are based on certain assumptions that cannot be validated as the true distribution of latent variables remains unknown.

Secondly, it is important to clarify that the identifiability of latent variables does not impact the conclusions of this paper, nor does this paper make specific conclusions about the model's latent variables. Identifiability means that distinct latent variables correspond to distinct observations. If multiple latent variables can generate the same observation, it becomes impossible to determine which one is correct given the observation, which leads to the issue of nonidentifiability. Notably, our analysis focuses on the generated signals, not the latent variables themselves, and thus the identifiability of these variables does not affect our findings. 

Our approach, dedicated to extracting these signals, distinctly differs from methods such as TNDM, which focuses on extracting behaviorally relevant latent dynamics. To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝑥# denotes generated behaviorally-relevant signals, 𝑥 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓).  Other studies have not explicitly proposed extracting behaviorally-relevant signals, nor have they identified and addressed the key challenges involved in extracting relevant signals. Consequently, our approach is distinct from other methods.

Thank you for your valuable feedback.

Q3: “Somewhat related, I also found that the now comprehensive comparison with related models shows that the using decoding performance (R2) as a metric for model comparison may be problematic: the R2 values reported in Figure 2 (e.g. the MC_RTT dataset) should be compared to the values reported in the neural latent benchmark, which represent well-tuned models (e.g. AutoLFADS). The numbers (difficult to see, a table with numbers in the appendix would be useful, see: https://eval.ai/web/challenges/challenge-page/1256/leaderboard) seem lower than what can be obtained with models without latent space disentanglement. While this does not necessarily invalidate the conclusions drawn here, it shows that decoding performance can depend on a variety of model choices, and may not be ideal to discriminate between models. I'm also surprised by the low neural R2 for LFADS I assume this is condition-averaged) - LFADS tends to perform very well on this metric.”

Thank you for your comments. The dataset we utilized is not from the same day as the neural latent benchmark dataset. Notably, there is considerable variation in the length of trials within the RTT paradigm, and the dataset lacks explicit trial information, rendering trial-averaging unsuitable. Furthermore, behaviorally relevant signals are not static averages devoid of variability; even behavioral data exhibits variability. We computed the neural R2 using individual trials rather than condition-averaged responses. 

Thank you for your valuable feedback.

Q4: “One statement I still cannot follow is how the prior of the variational distribution is modelled. You say you depart from the usual Gaussian prior, but equation 7 seems to suggest there is a normal prior. Are the parameters of this distribution learned? As I pointed out earlier, I however suspect this may not matter much as you give the prior a very low weight. I also still am not sure how you generate a sample from the variational distribution, do you just draw one for each pass?”

Thank you for your questions.

The conditional distribution of prior latent variables 𝑝%(𝒛|𝒚) is a Gaussian distribution, but the distribution of prior latent variables 𝑝(𝒛) is a mixture Gaussian distribution. The distribution of prior latent variables 𝑝(𝒛) is:

where denotes the empirical distribution of behavioral variables

𝒚, and 𝑁 denotes the number of samples, 𝒚(𝒊) denotes the 𝒊th sample, δ(⋅) denotes the Dirac delta function, and 𝑝%(𝒛|𝒚) denotes the conditional distribution of prior latent variables given the behavioral variables parameterized by network 𝑚. Based on the above equation, we can see that 𝑝(𝒛) is not a Gaussian distribution, it is a Gaussian mixture model with 𝑁 components, which is theoretically a universal approximator of continuous probability densities.

Learning this prior is important, as illustrated by our latent variable visualizations, which are not a Gaussian distribution. Upon conducting hypothesis testing for both latent variables and behavioral variables, neither conforms to Gaussian distribution (Lilliefors test and Kolmogorov-Smirnov test). Consequently, imposing a constraint on the latent variables towards N(0,1) is expected to affect performance adversely.

Regarding sampling, during training process, we draw only one sample from the approximate posterior distribution . It is worth noting that drawing multiple samples or one sample for each pass does not affect the experimental results. After training, we can generate a sample from the prior by providing input behavioral data 𝒚(𝒊) and then generating corresponding samples via and . To extract behaviorally-relevant signals from raw signals, we use and .

Thank you for your valuable feedback.

Q5: “(1) I found the figures good and useful, but the text is, in places, not easy to follow. I think the manuscript could be shortened somewhat, and in some places more concise focussed explanations would improve readability.

(2) I would not call the encoding "complex non-linear" - non-linear is a clear term, but complex can mean many things (e.g. is a quadratic function complex?) ”

Thank you for your recommendation. We have revised the manuscript for enhanced clarity.  We call the encoding “complex nonlinear” because neurons encode information with varying degrees of nonlinearity, as illustrated in Fig. 3b, f, and Fig. S3b.

Thank you for your valuable feedback.

To Reviewer #2

Q1: “I still remain unconvinced that the core findings of the paper are "unexpected". In the response to my previous Specific Comment #1, they say "We use the term 'unexpected' due to the disparity between our findings and the prior understanding concerning neural encoding and decoding." However, they provide no citations or grounding for why they make those claims. What prior understanding makes it unexpected that encoding is more complex than decoding given the entropy, sparseness, and high dimensionality of neural signals (the "encoding") compared to the smoothness and low dimensionality of typical behavioural signals (the "decoding")?” 

Thank you for your comments. We believe that both the complexity of neural encoding and the simplicity of neural decoding in motor cortex are unexpected.

The Complexity of Neural Encoding: As noted in the Introduction, neurons with small R2 values were traditionally considered noise and consequently disregarded, as detailed in references [1-3]. However, after filtering out irrelevant signals, we discovered that these neurons actually contain substantial amounts of behavioral information, previously unrecognized. Similarly, in population-level analyses, neural signals composed of small principal components (PCs) are often dismissed as noise, with analyses typically utilizing only between 6 and 18 PCs [4-10]. Yet, the discarded PC signals nonlinearly encode significant amounts of information, with practically useful dimensions found to range between 30 and 40—far exceeding the usual number analyzed. These findings underscore the complexity of neural encoding and are unexpected.

The Simplicity of Neural Decoding: In the motor cortex, nonlinear decoding of raw signals has been shown to significantly outperform linear decoding, as evidenced in references [11,12]. Interestingly, after separating behaviorally relevant and irrelevant signals, we observed that the linear decoding performance of behaviorally relevant signals is nearly equivalent to that of nonlinear decoding—a phenomenon previously undocumented in the motor cortex. This discovery is also unexpected.

Thank you for your valuable feedback.

(1) Georgopoulos, Apostolos P., Andrew B. Schwartz, and Ronald E. Kettner. "Neuronal population coding of movement direction." Science 233.4771 (1986): 1416-1419.

(2) Hochberg, Leigh R., et al. "Reach and grasp by people with tetraplegia using a neurally controlled robotic arm." Nature 485.7398 (2012): 372-375. 

(3) Inoue, Yoh, et al. "Decoding arm speed during reaching." Nature communications 9.1 (2018): 5243.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(7) Sadtler, Patrick T., et al. "Neural constraints on learning." Nature 512.7515 (2014): 423426.

(8) Golub, Matthew D., et al. "Learning by neural reassociation." Nature neuroscience 21.4 (2018): 607-616.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

(11) Glaser, Joshua I., et al. "Machine learning for neural decoding." Eneuro 7.4 (2020).

(12) Willsey, Matthew S., et al. "Real-time brain-machine interface in non-human primates achieves high-velocity prosthetic finger movements using a shallow feedforward neural network decoder." Nature Communications 13.1 (2022): 6899.

Q2: “I still take issue with the premise that signals in the brain are "irrelevant" simply because they do not correlate with a fixed temporal lag with a particular behavioural feature handchosen by the experimenter. In the response to my previous review, the authors say "we employ terms like 'behaviorally-relevant' and 'behaviorally-irrelevant' only regarding behavioral variables of interest measured within a given task, such as arm kinematics during a motor control task.". This is just a restatement of their definition, not a response to my concern, and does not address my concern that the method requires a fixed temporal lag and continual decoding/encoding. My example of reward signals remains. There is a huge body of literature dating back to the 70s on the linear relationships between neural and activity and arm kinematics; in a sense, the authors have chosen the "variable of interest" that proves their point. This all ties back to the previous comment: this is mostly expected, not unexpected, when relating apparently-stochastic, discrete action potential events to smoothly varying limb kinematics.”

Thank you for your comments. 

Regarding the experimenter's specification of behavioral variables of interest, we followed common practice in existing studies [1, 2]. Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [3-5]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [68].

Concerning the issue of rewards, in the paper you mentioned [9], the impact of rewards occurs after the reaching phase. It's important to note that in our experiments, we analyze only the reaching phase, without any post-movement phase. 

If the impact of rewards can be stably reflected in the signals in the reaching phase of the subsequent trial, and if the reward-induced signals do not interfere with decoding—since these signals are harmless for decoding and beneficial for reconstruction—our model is likely to capture these signals. If the signals induced by rewards during the reaching phase are randomly unstable, our model will likely be unable to capture them.

If the goal is to extract post-movement neural activity from both rewarded and unrewarded trials, and if the neural patterns differ between these conditions, one could replace the d-VAE's regression loss, used for continuous kinematics decoding, with a classification loss tailored to distinguish between rewarded and unrewarded conditions.

To clarify the definition, we have revised it in the manuscript. Specifically, before a specific definition, we briefly introduce the relevant signals and irrelevant signals. Behaviorally irrelevant signals refer to those not directly associated with the behavioral variables of interest and may include noise or signals from variables of no interest. In contrast, behaviorally relevant signals refer to those directly related to the behavioral variables of interest. For instance, rewards in the post-movement phase are not directly related to behavioral variables (kinematics) in the reaching movement phase.

It is important to note that our definition of behaviorally relevant signals not only includes decoding capabilities but also specific requirement at the signal level, based on two key requirements:

(1) they should closely resemble raw signals to preserve the underlying neuronal properties without becoming so similar that they include irrelevant signals. (encoding requirement), and  (2) they should contain behavioral information as much as possible (decoding requirement). Signals that meet both requirements are considered effective behaviorally relevant signals. In our study, we assume raw signals are additively composed of behaviorally-relevant and irrelevant signals. We define irrelevant signals as those remaining after subtracting relevant signals from raw signals. Therefore, we believe our definition is clearly articulated. 

Thank you for your valuable feedback.

(1) Sani, Omid G., et al. "Modeling behaviorally relevant neural dynamics enabled by preferential subspace identification." Nature Neuroscience 24.1 (2021): 140-149.

(2) Buetfering, Christina, et al. "Behaviorally relevant decision coding in primary somatosensory cortex neurons." Nature neuroscience 25.9 (2022): 1225-1236.

(3) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(4) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(5) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(6) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(7) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(8) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(9) Ramkumar, Pavan, et al. "Premotor and motor cortices encode reward." PloS one 11.8 (2016): e0160851.

Q3: “The authors seem to have missed the spirit of my critique: to say "linear readout is performed in motor cortex" is an over-interpretation of what their model can show.”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our view, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Regarding the question of whether the brain employs linear readout, given the limitations of current observational methods and our incomplete understanding of brain mechanisms, it is challenging to ascertain whether the brain employs a linear readout. In many cortical areas, linear decoders have proven to be sufficiently accurate. Consequently, numerous studies [4, 5, 6], including the one you referenced [4], directly employ linear decoders to extract information and formulate conclusions based on the decoding results. Contrary to these approaches, our research has compared the performance of linear and nonlinear decoders on behaviorally relevant signals and found their decoding performance is comparable. Considering both the decoding accuracy and model complexity, our results suggest that the motor cortex may utilize linear readout to decode information from relevant signals. Given the current technological limitations, we consider it reasonable to analyze collected data to speculate on the potential workings of the brain, an approach that many studies have also embraced [7-10]. For instance, a study [7] deduces strategies the brain might employ to overcome noise by analyzing the structure of recorded data and decoding outcomes for new stimuli.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

(4) Jurewicz, Katarzyna, et al. "Irrational choices via a curvilinear representational geometry for value." bioRxiv (2022): 2022-03.

(5) Hong, Ha, et al. "Explicit information for category-orthogonal object properties increases along the ventral stream." Nature neuroscience 19.4 (2016): 613-622.

(6) Chang, Le, and Doris Y. Tsao. "The code for facial identity in the primate brain." Cell 169.6 (2017): 1013-1028.

(7) Ganmor, Elad, Ronen Segev, and Elad Schneidman. "A thesaurus for a neural population code." Elife 4 (2015): e06134.

(8) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

Q4: “Agreeing with my critique is not sufficient; please provide the data or simulations that provides the context for the reference in the fano factor. I believe my critique is still valid.”

Thank you for your comments. As we previously replied, Churchland's research examines the variability of neural signals across different stages, including the preparation and execution phases, as well as before and after the target appears. Our study, however, focuses exclusively on the movement execution phase. Consequently, we are unable to produce comparative displays similar to those in his research. Intuitively, one might expect that the variability of behaviorally relevant signals would be lower; however, since no prior studies have accurately extracted such signals, the specific FF values of behaviorally relevant signals remain unknown. Therefore, presenting these values is meaningful, and can provide a reference for future research. While we cannot compare FF across different stages, we can numerically compare the values to the Poisson count process. An FF of 1 indicates a Poisson firing process, and our experimental data reveals that most neurons have an FF less than 1, indicating that the variance in firing counts is below the mean.  Thank you for your valuable feedback.

To Reviewer #4

Q1: “Overall, studying neural computations that are behaviorally relevant or not is an important problem, which several previous studies have explored (for example PSID in (Sani et al. 2021), TNDM in (Hurwitz et al. 2021), TAME-GP in (Balzani et al. 2023), pi-VAE in (Zhou and Wei 2020), and dPCA in (Kobak et al. 2016), etc). However, this manuscript does not properly put their work in the context of such prior works. For example, the abstract states "One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive", which is not the case given that these prior works have done that. The same is true for various claims in the main text, for example "Furthermore, we found that the dimensionality of primary subspace of raw signals (26, 64, and 45 for datasets A, B, and C) is significantly higher than that of behaviorally-relevant signals (7, 13, and 9), indicating that using raw signals to estimate the neural dimensionality of behaviors leads to an overestimation" (line 321). This finding was presented in (Sani et al. 2021) and (Hurwitz et al. 2021), which is not clarified here. This issue of putting the work in context has been brought up by other reviewers previously but seems to remain largely unaddressed. The introduction is inaccurate also in that it mixes up methods that were designed for separation of behaviorally relevant information with those that are unsupervised and do not aim to do so (e.g., LFADS). The introduction should be significantly revised to explicitly discuss prior models/works that specifically formulated this behavior separation and what these prior studies found, and how this study differs.”  

Thank you for your comments. Our statement about “One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive” is accurate. To our best knowledge, there is no prior works to do this work--- separating accurate behaviorally relevant neural signals at both single-neuron and single-trial resolution. The works you mentioned have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals, namely determining the optimal degree of similarity between the generated relevant signals and raw signals. Those works focus on the latent neural dynamics, rather than signal level.

To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝒙𝒓 denotes generated behaviorally-relevant signals, 𝒙 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓). All the works you mentioned did not have the key part 𝑅(𝒙𝒓).

Regarding the dimensionality estimation, the dimensionality of neural manifolds quantifies the degrees of freedom required to describe population activity without significant information loss.

There are two differences between our work and PSID and TNDM. 

First, the dimensions they refer to are fundamentally different from ours. The dimensionality we describe pertains to a linear subspace, where a neural dimension or neural mode or principal component basis, , with N representing the number of neurons. However, the vector length of a neural mode of PSID and our approach differs; PSID requires concatenating multiple time steps T, essentially making , TNDM, on the other hand, involves nonlinear dimensionality reduction, which is different from linear dimensionality reduction.

Second, we estimate neural dimensionality by explaining the variance of neural signals, whereas PSID and TNDM determine dimensionality through decoding performance saturation. It is important to note that the dimensionality at which decoding performance saturates may not accurately reflect the true dimensionality of neural manifolds, as some dimensions may contain redundant information that does not enhance decoding performance.

We acknowledge that while LFADS can generate signals that contain some behavioral information, it was not specifically designed to do so. Following your suggestion, we have removed this reference from the Introduction.

Thank you for your valuable feedback.

Q2: “Claims about linearity of "motor cortex" readout are not supported by results yet stated even in the abstract. Instead, what the results support is that for decoding behavior from the output of the dVAE model -- that is trained specifically to have a linear behavior readout from its embedding -- a nonlinear readout does not help. This result can be biased by the very construction of the dVAE's loss that encourages a linear readout/decoding from embeddings, and thus does not imply a finding about motor cortex.”

Thank you for your comments. We respectfully disagree with the notion that the ability of relevant signals to be linearly decoded is due to constraints that allow embedding to be linearly decoded. Embedding involves reorganizing or transforming the structure of original signals, and they can be linearly decoded does not mean the corresponding signals can be decoded linearly.

Let's clarify this with three intuitive examples:

Example 1: Image denoising is a well-established field. Whether employing supervised or blind denoising methods [1, 2], both can effectively recover the original image. This denoising process closely resembles the extraction of behaviorally relevant signals from raw signals. Consider if noisy images are not amenable to linear decoding (classification); would removing the noise enable linear decoding? The answer is no. Typically, the noise in images captured under normal conditions is minimal, yet even the clear images remain challenging to decode linearly.

Example 2: Consider the task of face recognition, where face images are set against various backgrounds, in this context, the pixels representing the face corresponds to relevant signals, while the background pixels are considered irrelevant. Suppose a network is capable of extracting the face pixels and the resulting embedding can be linearly decoded. Can the face pixels themselves be linearly decoded? The answer is no. If linear decoding of face pixels were feasible, the challenging task of face recognition could be easily resolved by merely extracting the face from the background and training a linear classifier.

Example 3: In the MNIST dataset, the background is uniformly black, and its impact is minimal. However, linear SVM classifiers used directly on the original pixels significantly underperform compared to non-linear SVMs.

In summary, embedding involves reorganizing the structure of the original signals through a feature transformation function. However, the reconstruction process can recover the structure of the original signals from the embedding. The fact that the structure of the embedding can be linearly decoded does not imply that the structure of the original signals can be linearly decoded in the same way. It is inappropriate to focus on the compression process without equally considering the reconstruction process.

Thank you for your valuable feedback.

(1) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(2) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

Q3: “Related to the above, it is unclear what the manuscript means by readout from motor cortex. A clearer definition of "readout" (a mapping from what to what?) in general is needed. The mapping that the linearity/nonlinearity claims refer to is from the *inferred* behaviorally relevant neural signals, which themselves are inferred nonlinearly using the VAE. This should be explicitly clarified in all claims, i.e., that only the mapping from distilled signals to behavior is linear, not the whole mapping from neural data to behavior. Again, to say the readout from motor cortex is linear is not supported, including in the abstract.” 

Thank you for your comments. We have revised the manuscript to make it more clearly. Thank you for your valuable feedback.

Q4: “Claims about individual neurons are also confounded. The d-VAE distilling processing is a population level embedding so the individual distilled neurons are not obtainable on their own without using the population data. This population level approach also raises the possibility that information can leak from one neuron to another during distillation, which is indeed what the authors hope would recover true information about individual neurons that wasn't there in the recording (the pixel denoising example). The authors acknowledge the possibility that information could leak to a neuron that didn't truly have that information and try to rule it out to some extent with some simulations and by comparing the distilled behaviorally relevant signals to the original neural signals. But ultimately, the distilled signals are different enough from the original signals to substantially improve decoding of low information neurons, and one cannot be sure if all of the information in distilled signals from any individual neuron truly belongs to that neuron. It is still quite likely that some of the improved behavior prediction of the distilled version of low-information neurons is due to leakage of behaviorally relevant information from other neurons, not the former's inherent behavioral information. This should be explicitly acknowledged in the manuscript.”

Thank you for your comments. We value your insights regarding the mixing process. However, we are confident in the robustness of our conclusions. We respectfully disagree with the notion that the small R2 values containing significant information are primarily due to leakage, and we base our disagreement on four key reasons.

(1) Neural reconstruction performance is a reliable and valid criterion.

The purpose of latent variable models is to explain neuronal activity as much as possible. Given the fact that the ground truth of behaviorally-relevant signals, the latent variables, and the generative model is unknow, it becomes evident that the only reliable reference at the signal level is the raw signals. A crucial criterion for evaluating the reliability of latent variable models (including latent variables and generated relevant signals) is their capability to effectively explain the raw signals [1]. Consequently, we firmly maintain the belief that if the generated signals closely resemble the raw signals to the greatest extent possible, in accordance with an equivalence principle, we can claim that these obtained signals faithfully retain the inherent properties of single neurons. 

Reviewer #4 appears to focus on the compression (mixing) process without giving equal consideration to the reconstruction (de-mixing) process. Numerous studies have demonstrated that deep autoencoders can reconstruct the original signal very effectively. For example, in the field of image denoising, autoencoders are capable of accurately restoring the original image [2, 3]. If one persistently focuses on the fact of mixing and ignores the reconstruction （demix） process, even if the only criterion that we can rely on at the signal level is high, one still won't acknowledge it. If this were the case, many problems would become unsolvable. For instance, a fundamental criterion for latent variable models is their ability to explain the original data. If the ground truth of the latent variables remains unknown and the reconstruction criterion is disregarded, how can we validate the effectiveness of the model, the validity of the latent variables, or ensure that findings related to latent variables are not merely by-products of the model? Therefore, we disagree with the aforementioned notion. We believe that as long as the reconstruction performance is satisfactory, the extracted signals have successfully retained the characteristics of individual neurons.

In our paper, we have shown in various ways that our generated signals sufficiently resemble the raw signals, including visualizing neuronal activity (Fig. 2m, Fig. 3i, and Fig. S5), achieving the highest performance among competitors (Fig. 2d, h, l), and conducting control analyses. Therefore, we believe our results are reliable. 

(1) Cunningham, J.P. and Yu, B.M., 2014. Dimensionality reduction for large-scale neural recordings. Nature neuroscience, 17(11), pp.1500-1509.

(2) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(3) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

(2) There is no reason for d-VAE to add signals that do not exist in the original signals.

(1) Adding signals that does not exist in the small R2 neurons would decrease the reconstruction performance. This is because if the added signals contain significant information, they will not resemble the irrelevant signals which contain no information, and thus, the generated signals will not resemble the raw signals. The model optimizes towards reducing the reconstruction loss, and this scenario deviates from the model's optimization direction. It is worth mentioning that when the model only has reconstruction loss without the interference of decoding loss, we believe that information leakage does not happen. Because the model can only be optimized in a direction that is similar to the raw signals; adding non-existent signals to the generated signals would increase the reconstruction loss, which is contrary to the objective of optimization. 

(2) Information carried by these additional signals is redundant for larger R2 neurons, thus they do not introduce new information that can enhance the decoding performance of the neural population, which does not benefit the decoding loss.

Based on these two points, we believe the model would not perform such counterproductive and harmful operations.

(3) The criterion that irrelevant signals should contain minimal information can effectively rule out the leakage scenario.

The criterion that irrelevant signals should contain minimal information is very important, but it seems that reviewer #4 has continuously overlooked their significance. If the model's reconstruction is insufficient, or if additional information is added (which we do not believe will happen), the residuals would decode a large amount of information, and this criterion would exclude selecting such signals. To clarify, if we assume that x, y, and z denote the raw, relevant, and irrelevant signals of smaller R2 neurons, with x=y+z, and the extracted relevant signals become y+m, the irrelevant signals become z-m in this case. Consequently, the irrelevant signals contain a significant amount of information.

We presented the decoding R2 for irrelevant signals in real datasets under three distillation scenarios: a bias towards reconstruction (alpha=0, an extreme case where the model only has reconstruction loss without decoding loss), a balanced trade-off, and a bias towards decoding (alpha=0.9), as detailed in Table 1. If significant information from small R2 neurons leaks from large R2 neurons, the irrelevant signals should contain a large amount of information. However, our results indicate that the irrelevant signals contain only minimal information, and their performance closely resembles that of the model training solely with reconstruction loss, showing no significant differences (P > 0.05, Wilcoxon rank-sum test). When the model leans towards decoding, some useful information will be left in the residuals, and irrelevant signals will contain a substantial amount of information, as observed in Table 1, alpha=0.9. Therefore, we will not choose these signals for analysis.

In conclusion, the criterion that irrelevant signals should contain minimal information is a very effective measure to exclude undesirable signals.

Author response table 1.

Decoding R2 of irrelevant signals

(4) Synthetic experiments can effectively rule out the leakage scenario.

In the absence of ground truth data, synthetic experiments serve as an effective method for validating models and are commonly employed [1-3]. 

Our experimental results demonstrate that d-VAE can effectively extract neural signals that more closely resemble actual behaviorally relevant signals (Fig. S2g).  If there were information leakage, it would decrease the similarity to the ground truth signals, hence we have ruled out this possibility. Moreover, in synthetic experiments with small R2 neurons (Fig. S10), results also demonstrate that our model could make these neurons more closely resemble ground truth relevant signals and recover their information. 

In summary, synthetic experiments strongly demonstrate that our model can recover obscured neuronal information, rather than adding signals that do not exist.

(1) Pnevmatikakis, Eftychios A., et al. "Simultaneous denoising, deconvolution, and demixing of calcium imaging data." Neuron 89.2 (2016): 285-299.

(2) Schneider, Steffen, Jin Hwa Lee, and Mackenzie Weygandt Mathis. "Learnable latent embeddings for joint behavioural and neural analysis." Nature 617.7960 (2023): 360-368.

(3) Zhou, Ding, and Xue-Xin Wei. "Learning identifiable and interpretable latent models of high-dimensional neural activity using pi-VAE." Advances in Neural Information Processing Systems 33 (2020): 7234-7247.

Based on these four points, we are confident in the reliability of our results. If Reviewer #4 considers these points insufficient, we would highly appreciate it if specific concerns regarding any of these aspects could be detailed.

Thank you for your valuable feedback.

Q5: “Given the nuances involved in appropriate comparisons across methods and since two of the datasets are public, the authors should provide their complete code (not just the dVAE method code), including the code for data loading, data preprocessing, model fitting and model evaluation for all methods and public datasets. This will alleviate concerns and allow readers to confirm conclusions (e.g., figure 2) for themselves down the line.”

Thanks for your suggestion.

Our codes are now available on GitHub at https://github.com/eric0li/d-VAE. Thank you for your valuable feedback.

Q6: “Related to 1) above, the authors should explore the results if the affine network h(.) (from embedding to behavior) was replaced with a nonlinear ANN. Perhaps linear decoders would no longer be as close to nonlinear decoders. Regardless, the claim of linearity should be revised as described in 1) and 2) above, and all caveats should be discussed.”

Thank you for your suggestion. We appreciate your feasible proposal that can be empirically tested. Following your suggestion, we have replaced the decoding of the latent variable z to behavior y with a nonlinear neural network, specifically a neural network with a single hidden layer. The modified model is termed d-VAE2. We applied the d-VAE2 to the real data, and selected the optimal alpha through the validation set. As shown in Table 1, results demonstrate that the performance of KF and ANN remains comparable. Therefore, the capacity to linearly decode behaviorally relevant signals does not stem from the linear decoding of embeddings.

Author response table 2.

Decoding R2 of behaviorally relevant signals obtained by d-VAE2

Additionally, it is worth noting that this approach is uncommon and is considered somewhat inappropriate according to the Information Bottleneck theory [1]. According to the Information Bottleneck theory, information is progressively compressed in multilayer neural networks, discarding what is irrelevant to the output and retaining what is relevant. This means that as the number of layers increases, the mutual information between each layer's embedding and the model input gradually decreases, while the mutual information between each layer's embedding and the model output gradually increases. For the decoding part, if the embeddings that is not closest to the output (behaviors) is used, then these embeddings might contain behaviorally irrelevant signals. Using these embeddings to generate behaviorally relevant signals could lead to the inclusion of irrelevant signals in the behaviorally relevant signals.

To demonstrate the above statement, we conducted experiments on the synthetic data. As shown in Table 2, we present the performance (neural R2 between the generated signals and the ground truth signals) of both models at several alpha values around the optimal alpha of dVAE (alpha=0.9) selected by the validation set. The experimental results show that at the same alpha value, the performance of d-VAE2 is consistently inferior to that of d-VAE, and d-VAE2 requires a higher alpha value to achieve performance comparable to d-VAE, and the best performance of d-VAE2 is inferior to that of d-VAE.

Author response table 3.

Neural R2 between generated signals and real behaviorally relevant signals

Thank you for your valuable feedback.

(1) Shwartz-Ziv, Ravid, and Naftali Tishby. "Opening the black box of deep neural networks via information." arXiv preprint arXiv:1703.00810 (2017).

Q7: “The beginning of the section on the "smaller R2 neurons" should clearly define what R2 is being discussed. Based on the response to previous reviewers, this R2 "signifies the proportion of neuronal activity variance explained by the linear encoding model, calculated using raw signals". This should be mentioned and made clear in the main text whenever this R2 is referred to.”

Thank you for your suggestion. We have made the modifications in the main text. Thank you for your valuable feedback.

Q8: “Various terms require clear definitions. The authors sometimes use vague terminology (e.g., "useless") without a clear definition. Similarly, discussions regarding dimensionality could benefit from more precise definitions. How is neural dimensionality defined? For example, how is "neural dimensionality of specific behaviors" (line 590) defined? Related to this, I agree with Reviewer 2 that a clear definition of irrelevant should be mentioned that clarifies that relevance is roughly taken as "correlated or predictive with a fixed time lag". The analyses do not explore relevance with arbitrary time lags between neural and behavior data.”

Thanks for your suggestion. We have removed the “useless” statements and have revised the statement of “the neural dimensionality of specific behaviors” in our revised manuscripts.

Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [1-3]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [4-6]. To clarify the definition, we have revised the definition in our manuscript. For details, please refer to the response to Q2 of reviewer #2 and our revised manuscript. We believe our definition is clearly articulated.

Thank you for your valuable feedback.

(1) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(2) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(3) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239. 

Q9: “CEBRA itself doesn't provide a neural reconstruction from its embeddings, but one could obtain one via a regression from extracted CEBRA embeddings to neural data. In addition to decoding results of CEBRA (figure S3), the neural reconstruction of CEBRA should be computed and CEBRA should be added to Figure 2 to see how the behaviorally relevant and irrelevant signals from CEBRA compare to other methods.”

Thank you for your question. Modifying CEBRA is beyond the scope of our work. As CEBRA is not a generative model, it cannot obtain behaviorally relevant and irrelevant signals, and therefore it lacks the results presented in Fig. 2. To avoid the same confusion encountered by reviewers #3 and #4 among our readers, we have opted to exclude the comparison with CEBRA. It is crucial to note, as previously stated, that our assessment of decoding capabilities has been benchmarked against the performance of the ANN on raw signals, which almost represents the upper limit of performance. Consequently, omitting CEBRA does not affect our conclusions.

Thank you for your valuable feedback.

Q10: “Line 923: "The optimal hyperparameter is selected based on the lowest averaged loss of five-fold training data." => why is this explained specifically under CEBRA? Isn't the same criteria used for hyperparameters of other methods? If so, clarify.”

Thank you for your question. The hyperparameter selection for CEBRA follows the practice of the original CEBRA paper. The hyperparameter selection for generative models is detailed in the Section “The strategy for selecting effective behaviorally-relevant signals”.  Thank you for your valuable feedback.

Author response:

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

Reviewer #1 (Public Review):

In this paper, the authors evaluate the utility of brain age derived metrics for predicting cognitive decline by performing a 'commonality' analysis in a downstream regression that enables the different contribution of different predictors to be assessed. The main conclusion is that brain age derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ('brain cognition') as an alternative suited to applications of cognitive decline. While this is less accurate overall than brain age, it explains more unique variance in the downstream regression.  

Importantly, in this revision, we clarified that we did not intend to use Brain Cognition as an alternative approach. This is because, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Here we made this point more explicit and further stated that the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. By examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. 

REVISED VERSION: while the authors have partially addressed my concerns, I do not feel they have addressed them all. I do not feel they have addressed the weight instability and concerns about the stacked regression models satisfactorily.

Please see our responses to Reviewer #1 Public Review #3 below

I also must say that I agree with Reviewer 3 about the limitations of the brain age and brain cognition methods conceptually. In particular that the regression model used to predict fluid cognition will by construction explain more variance in cognition than a brain age model that is trained to predict age. This suffers from the same problem the authors raise with brain age and would indeed disappear if the authors had a separate measure of cognition against which to validate and were then to regress this out as they do for age correction. I am aware that these conceptual problems are more widespread than this paper alone (in fact throughout the brain age literature), so I do not believe the authors should be penalised for that. However, I do think they can make these concerns more explicit and further tone down the comments they make about the utility of brain cognition. I have indicated the main considerations about these points in the recommendations section below. 

Thank you so much for raising this point. We now have the following statement in the introduction and discussion to address this concern (see below). 

Briefly, we made it explicit that, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. That is, the relationship between Brain Cognition and fluid cognition indicates the upper limit of Brain Age’s capability in capturing fluid cognition. More importantly, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age. And this is the third goal of this present study. 

From Introduction:

“Third and finally, certain variation in fluid cognition is related to brain MRI, but to what extent does Brain Age not capture this variation? To estimate the variation in fluid cognition that is related to the brain MRI, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in fluid cognition that is related to the brain MRI and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. This is, by design, the variation in fluid cognition explained by Brain Cognition should be higher or equal to that explained by Brain Age. Consequently, if we included Brain Cognition, Brain Age and chronological age in the same model to explain fluid cognition, we would be able to examine the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age. These unique effects of Brain Cognition, in turn, would indicate the amount of co-variation between brain MRI and fluid cognition that is missed by Brain Age.”

From Discussion:

“Third, by introducing Brain Cognition,  we showed the extent to which Brain Age indices were not able to capture the variation in fluid cognition that is related to brain MRI. More specifically, using Brain Cognition allowed us to gauge the variation in fluid cognition that is related to the brain MRI, and thereby, to estimate the upper limit of what Brain Age can do. Moreover, by examining what was captured by Brain Cognition, over and above Brain Age and chronological age via the unique effects of Brain Cognition, we were able to quantify the amount of co-variation between brain MRI and fluid cognition that was missed by Brain Age.

From our results, Brain Cognition, especially from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. As explained above, the unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.” 

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. I have some comments that I believe the authors ought to address, which mostly relate to clarity and interpretation 

Reviewer #1 Public Review #1

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. I would suggest the authors nuance their discussion to provide broader considerations of the utility of their method and on the limits of interpretation of brain age models more generally. 

Thank you for your comments on this issue. 

We now discussed the broader consideration in detail:

(1) the consistency between our findings on fluid cognition and other recent works on brain disorders, 

(2) the difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021)

and 

(3) suggested solutions we and others made to optimise the utility of Brain Age for both cognitive functioning and brain disorders.

From Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance,  combining different MRI modalities into the prediction models, similar to our stacked models, ocen leads to the highest performance of age prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). We consider the former as a normative type of study and the lader as a case-control type of study (Insel et al., 2010; Marquand et al., 2016). Those case-control Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. On the one hand, this means that case-control studies treat Brain Age as a method to detect anomalies in the neurological/psychological group (Hahn et al., 2021). On the other hand, this also means that case-control studies have to ignore underfided models when applied prediction models built from largely healthy participants to participants with neurological/psychological disorders (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other normative studies focusing on cognitive functioning often build age prediction models from MRI data of largely healthy participants and apply the built age prediction models to participants who are also largely healthy. Accordingly, the age prediction models for explaining cognitive functioning in normative studies, while not allowing us to detect group-level anomalies, do not suffer from being under-fided. This unfortunately might limit the generalisability of our study into just the normative type of study. Future work is still needed to test the utility of brain age in the case-control case.”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder. 

As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest.

Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

Reviewer #1 Public Review #2

Second, from a methods perspective, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand how the stacked regression models were constructed. I would request that the authors provide more information to enable the reader to beUer understand the stacked regression models used to ensure that these models are not overfit. 

Thank you for allowing us an opportunity to clarify our stacked model. We made additional clarification to make this clearer (see below). We wanted to confirm that we did not use test sets to build a stacked model in both lower and higher levels of the Elastic Net models. Test sets were there just for testing the performance of the models.  

From Methods:

“We used nested cross-validation (CV) to build these prediction models (see Figure 7). We first split the data into five outer folds, leaving each outer fold with around 100 participants. This number of participants in each fold is to ensure the stability of the test performance across folds. In each outer-fold CV loop, one of the outer folds was treated as an outer-fold test set, and the rest was treated as an outer-fold training set. Ultimately, looping through the nested CV resulted in a) prediction models from each of the 18 sets of features as well as b) prediction models that drew information across different combinations of the 18 separate sets, known as “stacked models.” We specified eight stacked models: “All” (i.e., including all 18 sets of features),  “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, there were 26 prediction models in total for both Brain Age and Brain Cognition.

To create these 26 prediction models, we applied three steps for each outer-fold loop. The first step aimed at tuning prediction models for each of 18 sets of features. This step only involved the outer-fold training set and did not involve the outer-fold test set. Here, we divided the outer-fold training set into five inner folds and applied inner-fold CV to tune hyperparameters with grid search. Specifically, in each inner-fold CV, one of the inner folds was treated as an inner-fold validation set, and the rest was treated as an inner-fold training set. Within each inner-fold CV loop, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters and applied the estimated model to the inner-fold validation set. Acer looping through the inner-fold CV, we, then, chose the prediction models that led to the highest performance, reflected by coefficient of determination (R2), on average across the inner-fold validation sets. This led to 18 tuned models, one for each of the 18 sets of features, for each outer fold.

The second step aimed at tuning stacked models. Same as the first step, the second step only involved the outer-fold training set and did not involve the outer-fold test set. Here, using the same outer-fold training set as the first step, we applied tuned models, created from the first step, one from each of the 18 sets of features, resulting in 18 predicted values for each participant. We, then, re-divided this outer-fold training set into new five inner folds. In each inner fold, we treated different combinations of the 18 predicted values from separate sets of features as features to predict the targets in separate “stacked” models. Same as the first step, in each inner-fold CV loop, we treated one out of five inner folds as an inner-fold validation set, and the rest as an inner-fold training set. Also as in the first step, we used the inner-fold training set to estimate parameters of the prediction model with a particular set of hyperparameters from our grid. We tuned the hyperparameters of stacked models using grid search by selecting the models with the highest R2 on average across the inner-fold validation sets. This led to eight tuned stacked models.

The third step aimed at testing the predictive performance of the 18 tuned prediction models from each of the set of features, built from the first step, and eight tuned stacked models, built from the second step. Unlike the first two steps, here we applied the already tuned models to the outer-fold test set. We started by applying the 18 tuned prediction models from each of the sets of features to each observation in the outer-fold test set, resulting in 18 predicted values. We then applied the tuned stacked models to these predicted values from separate sets of features, resulting in eight predicted values. 

To demonstrate the predictive performance, we assessed the similarity between the observed values and the predicted values of each model across outer-fold test sets, using Pearson’s r, coefficient of determination (R2) and mean absolute error (MAE). Note that for R2, we used the sum of squares definition (i.e., R2 \= 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020). We considered the predicted values from the outer-fold test sets of models predicting age or fluid cognition, as Brain Age and Brain Cognition, respectively.”

Author response image 1.

Diagram of the nested cross-validation used for creating predictions for models of each set of features as well as predictions for stacked models. 

Note some previous research, including ours (Tetereva et al., 2022), splits the observations in the outer-fold training set into layer 1 and layer 2 and applies the first and second steps to layers 1 and 2, respectively. Here we decided against this approach and used the same outer-fold training set for both first and second steps in order to avoid potential bias toward the stacked models. This is because, when the data are split into two layers, predictive models built for each separate set of features only use the data from layer 1, while the stacked models use the data from both layers 1 and 2. In practice with large enough data, these two approaches might not differ much, as we demonstrated previously (Tetereva et al., 2022).