The main issue is deciding if you should continue on to a four-year degree to gain the programming skills needed for video game design. Related issues include balancing work, supporting your wife, and planning to start a family soon. A good solution must help you reach your career goals without causing too much financial or personal stress. A simple metaphor is “trying to level up while already in the middle of the game.”

This whole article really got my attention and had me captivated all the way to the last paragraph. I felt like the story was unfinished and she has not gotten any justice yet. This is a very disturbing story, the fact that this man was harassing her by contacting employers and friends of hers and making things up to make her look bad is concerning in itself. What is even more concerning to me is that when she went to law enforcement they didn't do anything and said he didn't commit a crime. I don't understand n how pretending to be her email and messaging people fake stuff could possibly not be a crime. He is fully impacting her ability to make money and stealing her identity. I hope that police do not continue with this way of handling cyberstalking cases.

This article talks about the hate against Megan Markle. It makes me sad, because it seems like there is no real motive for this hate, yet she still receives it on the daily. The journalist writes that maybe the motive is simply racism or a desire to break up the royal family. However, it doesn't seem like Megan has done anything to warrant this kind of hateful response. This is sad. It shows that crowd harassment will continue to happen even without a direct "motive." Even if Megan had done something publicly deemed "wrong," it would still be immoral to harass her.

I find this topic very interesting. On one hand, public images are important and a negative connotation could lead to a large amount of backlash and hate. The way social media works means a constant stream of polarized opinions on controversial topics. On the other hand, some people might say things just to say things. Without the knowledge of most situations, people think that they know everything, especially when they don’t. Most situations or circumstances are not cut and dry and even though people are open to free speech, most people are not informed enough to try to make someone else change their mind.

misleading, since there is no functional parallel to the pipe symbol (|) as known e.g. from Shell commands; in Pandas, | is instead an OR operator

stats of people injured/involved

Two parties views

Yes I believe that crowd harassment can be justified in certain situations. Here it defines that crowd harassment can be riots, mob violence, revolts, revolution. Not all of these will be justified all the time, but there are scenarios that require riots, that require revolution. If a group of people are being mistreated, protests and harassment can become necessary to get justice and stop the mistreatment. A revolution may be necessary to fix an issue, one may be necessary soon in our country. This is why I think that somer crowd harassment can be justified and is not always a negative thing. I notice in the comment above me it says it can never be justified because no violence can be justified. Crowd harassment does not have to include violence, not all riots and revolutions result in violence, harassment is not a term that only covers violence. A crowd can harass with their words too.

fire quote

interesting how they repeat this example. The two pieces are related so they comparison is valid.

this makes me want to uninstall google

"Computational exploitation of a natural human desire" is a crazy quote

this is interesting

These are leftist conspiracies?

The point made in this is interesting, as well as new to me; the idea that changing these platforms is not up to the companies. I feel this has been the goal of a lot of the discussion, that the companies and platforms need to change. It is true though that the tradeoffs make that an undesirable decision for shareholders. However, I don't know how involved we should push for the government to be in this process. Right now that seems like a recipe for disaster.

I wish the author had a source cited or linked

This is really interesting

The idea of things being 'experienced simultaneously but separately' is so interesting. It reminds me of discussions I have heard or seen that debate whether or not social media has made us more connected or more isolated/lonely.

very 1984

easy to understand yet powerful analogy

what about social media causes the public sphere we're in today, phantom?

the platforms as a whole? (trump)

the changing landscape of journalism is a continuous topic in my journalism classes, however it raises the questions of is the original foundations of journalism ARE obsolete?

The article explains how a child might see a harmless situation such as a parent lying about eating all of their Halloween candy as dire. The understanding to a toddler would show distrust towards a parental figure because of the effort they went through in order to retrieve the candy. Personally, I think it’s really weird how people laugh at kids for expressing emotions such as crying or anger. It might seem innocent for anyone who understands that Halloween candy isn’t that big of a deal but ultimately, this can affect a child’s developing mind to hide their efforts away from people. The worst part about this is the world-wide display of a child crying and the laughter from it. This would be it’s own thing that might affect a child but the fact that a child crying is being seen by millions of people across the globe is slightly dystopian.

The Amazon forest which should be immune to forest fires and large deforestation rates naturally, is suffering due to climate change and human activities. This affects the tropical forest by reducing resistance at the same time it is becoming more vulnerable.

The forest became a hotspot for those who chose to participate in an illegal act of deforestation. This was because of how dry the forests became, making them very vulnerable and flammable. Most blazes during this time were predicted to have been the result of acts of arson.

The El Nino phenomenon helped set forth the amazon drought to be one of the most severe in recent history. This phenomenon caused lower rainfall and the water levels in the Amazon's main rivers dropped to their lowest in more than 120 years. This had a huge impact on the amount of water present in the Amazon Rainforest.

This is why it is important to catch these issues sooner

Brazil had the percentage of carbon emissions, weighing in at 61 %, with the second largest being Bolivia at 32 %, almost half of Brazil.

In two years, 2022-2024, the carbon dioxide released from forest fire season showed a sevenfold increase. Which indicates the rates have rose to be 7 times what they were two years ago.

The interesting difference is the level of how this might affect a person. Even though they are quite similar in their feeling, they are quite different in execution. While guilt is the feeling of certain actions that they regret, shame is an overarching feeling of self. While most shame is felt as a result of many guilty actions, it can truly impact how someone carries themselves. People can hide how they truly feel about things by masking themselves or just shutting the world out in fear of messing up.

Crowd harassment is bullying. Therefore, it is hurtful and it is wrong. Even if the target is rich, famous, or powerful, words can be hurtful, and we should not use them to harass anyone. Crowd harassment can seem excusable because we think that if everyone is speaking hatefully about someone it must be excusable. However, we cannot succumb to this form of peer pressure. It is never okay to harass someone, even if they have opinions you do not agree with and even if others say it is okay to harass them.

While the level of convenience of social media has made it easy to positively communicate with others, it also makes it easier to harass people. Because of anonymity on the internet, it makes it easy for someone to send hurtful comments or damaging posts and get away with it easier.

Spectrum could add value to this data

Patreon is a platform that is mainly used to support/give funding to creators, usually either in the form of paid products or a subscription service. It also provides certain rewards or perks to its users.

I love that scene from Crazy Rich Asians where multiple people on social media work together to figure out who Nick is dating. I think this is a great example of how quickly crowdsourcing can work. I can think of multiple cases where people on social media sites, Twitter, reddit, etc. Have solved questions, crimes, and even found missing people through each other's collaborations. In the end I think this goes to show that the efforts of many often work more quickly and efficiently than just one.

I think this is the best example of crowdsourcing. Everyone has access and when people need help this platform gives them a space to ask for it. The number pone thing I think it is helpful for is paying medical bills. Medical bills can be insane in the united states and people often do not deserve to be put in the spots they are put in to have to deal with an injury and pay these bills. I do wonder about any fraud that occurs on gofundme. Are there any cases pop people faking an issue that they need money for and just take peoples money for nothing.

I think websites like Patreon, KickStarter, GoFundMe, etc. are great examples of real world crowdsourcing. Crowdsouring at it's core is the collaboration of multiple people. Unlike social media websites that arguably focus on an individual's profile, these websites often rely on the donations and support of many, weather it be to fund their creative idea, finical needs, etc. It is the group collaboration from others that allow for these ideas to happen.

I feel like I vaguely remember hearing about this and the disaster that the internet detectives on Reddit caused. Oftentimes especially with high profile cases, people post false information that they heard from other comments and other people with no verification of the information they are providing. For example, recently, with the d4vd case, people would post wrong information a lot of the time on comment sections and automatically assuming there was a lot of evidence to convict him.

When a wiki or knowledge website is edited by anyone, the information could be wrong or influenced by personal bias. The consequences are catastrophic since everyone is reading it, might citie it to twist the truth.

This source discusses the timeline of crowdsourcing, starting from as early as the year 614. It also discusses how crowdsourcing has had impact on the different fields.

This bibliography gives a clear overview of what crowdsourcing is to me, how it works, and why it has become so common on digital platforms. I find it helpful that it explains both the advantages, such as like lower cost and faster results, and the many different forms crowdsourcing can take.

This article is about how a couple’s proposal moment was captured by an unknown photographer. The photographer then posted the pictures without permission to find the couple. The twitte went viral and people found that couple. This is a very heartwarming cause of crowdsourcing. The couple got a lot of blessing by strangers online.

The often times free nature of crowd sourcing can be suspectable to abuse, commonly seen in voting systems. This results in voting systems being a target of trolling by large communities, such as 4chan abusing events that allows the wider community to vote for certain things, such as naming of a location or promotional event at a location. The anonymous and purposefully assessable design of crowd sourcing makes it difficult for companies and organizations to filter bad actors.

Metoo movement is a social movement against sexual abuse, and it encouraged people to share their experiences about it. The campaign led to increased media attention, workplace consequences for perpetrators, and international expansion, becoming a broader movement for justice for marginalized people.

This WIRED video is actually quite interesting. It reminds us from a somewhat funny yet realistic perspective that when robots really start working alongside us, we humans might end up being the ones who are the least adaptable. Although the video is light-hearted, the awkward moments it highlights - such as not knowing whether to greet the robot, standing too close, or mistaking the robot for "understanding" your gestures - are actually very close to the real confusion we experience when interacting with new technologies in our daily lives. I think the most valuable aspect of this video is that it makes us realize that human-robot interaction is not only a technical issue, but also a social and psychological one. As robots become increasingly intelligent, we need to learn how to coexist with them emotionally and habitually.

The Wikipedia page on the MeToo movement explains how a single hashtag turned into a massive crowdsourced effort to call out sexual harassment and assault. What stood out to me is how the movement showed the power of collective voices online. Once people saw others sharing their experiences, it encouraged even more people to come forward. It connects to this chapter’s idea of crowdsourcing because the impact came from large amount of individuals contributing their own stories, creating a larger cultural shift that wouldn’t have been possible alone.

After the Boston Marathon Bombings a subreddit was made to try to use crowdsourcing to find the bombers. The creator admits that it would have never worked. This place was for people to sift through photos to try to find the identity of the bombers by linking photos of them taken on the day to other photos on the internet. They did actually find one photo that the FBI had not found yet but besides that the whole project as pretty much a bust.

This is a wonderful example of when using social media to find people can be good. Unlike the reddit used to try to identify one of the Boston bombers this Twitter search was a positive example of how online communities can come together to help people.

The study "The Effects of AI-based Credibility Indicators on the Detection and Spread of Misinformation under Social Influence" claims that "We conclude by providing implications for better utilizing AI to fight misinformation." However this seems a bit contradictory since AI spreads a lot of misinformation itself, especially about topics its not heavily trained on.

This is interesting because it makes me think about how these forms of communication may have evolved throughout history, or remained the same. For example, the action of passing a note in secrecy has been mainly replaced by texting.

I think this section gives a clear explanation of what crowdsourcing is and how it differs from crowdfunding, using examples that are easy to understand. It also helps me see how digital tools make collaboration easier by removing limits of location and time. I like how it points out that online communication doesn’t fully replace in-person interaction, but can still offer unique advantages.

In my opinion, I think it is great to have all these methods of communicating online. These ways makes online communication so much more interesting and secured. In different scenarios, different methods can maximize the efficiency of the communication and create a better place for all the internet users.

I completely agree with this statement because it points out a core contradiction of technology in communication: the more we try to "simulate" reality, the more we realize that we can't achieve an exact replica. No matter how clear the video chat is, it cannot replace the eye contact, spatial sense, and body language in a real-life interaction; delays, image quality, and environmental noise all make communication different from reality. However, this statement also implies an important point: Instead of insisting on replicating face-to-face interactions, we should consider the unique advantages of digital communication - such as asynchronous communication, cross-regional collaboration, record-keeping, and simultaneous multi-person editing. In other words, the value of technology is not just to imitate reality, but to create new communication methods that do not exist in reality.

The main reason that users feel different when they chat with robots online is robots work based on the program, and they do not change so fast and flexible. The programmer cannot add human minds to the robots, and there will be a problem if people cannot tell the difference between a human and a robot.

phenomena

Phenomena

I have always been interested in wikipedia since I was younger. I never really understood how they can filter and edit the edits that are made by people to wikipedia sites. It seems like it would be impossible to filter it but they must do it somehow. When I was younger I would try to edit wikipedia sites to say funny things but I don't think that these edits were ever really on the site because when I would go on my dad's phone and look up the site I wouldn't see my edits. I would love to know how wikipedia deals with filtering good and bad edits by the public.

I feel like Wikipedia is a perfect example of crowdsourcing on the internet, because it is an online database that relies on volunteer editors to make articles on an infinite amount of topics. I was unaware of the scandal where a US congressional staff edited Wikipedia pages, but that's interesting because it raises questions on who can edit Wikipedia articles and how the website can enforce editors are not editing sources with a lot of bias.

There are a lot of platforms out there that are not tropically designed for crowdsourcing but are really good for it. The ones that come to mind for me are venmo and zelle. These are both personal digital payment methods that offer almost identical services. I have seen many times people put out a mutual aid ask through their instagram story and have a venmo/zelle link or qr code so that people can scan it and support whatever cause. Though, I would be interested to hear either company's argument for why they are better than the other. As I see it they are the same.

I like this section because it captures how essential tension is to storytelling. It’s what turns plain information into something people actually care about. I agree that without some sense of conflict or uncertainty, even well-written pieces feel flat. It reminded me that design and communication work the same way, you need a spark of tension or curiosity to hold people’s attention.

I agree that tension was the missing element. I believe that if stories did not have tension and contained a mere collection of facts, the audience would be bored. This aligns with my understanding of the traditional story-telling structure, also known as freytag's pyramid. I think most stories follow this structure, as they have exposition, an incident, rising action, climax, falling action, and then finally a resolution. If a story did not have any bumps, or problems or tension on the way, the flow of the story would be somewhat linear and uninteresting.

What I really like about this graph is how it shows that tension rises across the three-act structure—the idea that tension doesn’t appear right away, but is “introduced at the end of the first act,” then keeps climbing until it peaks in Act II. I agree with this way of mapping stories because it makes the relationship between time and emotional intensity really clear; seeing it graphed like this helped me understand why the middle of a story always feels the most chaotic and full of movement. It also made me realize that the release of tension in Act III isn’t just a wrap-up, but an intentional structural payoff that depends entirely on how well the earlier acts were built.

I really like how this three-part diagram connects the structure of tension to the flow of time because it makes the shape of a story feel almost mathematical. The idea that tension is introduced right at the transition into the second act feels accurate to most stories I enjoy—there’s always that moment where things shift from setup to real conflict. I agree that the gradual rise through Act Two is what keeps audiences engaged, because it mirrors how stakes build in real life. What stood out to me most is the idea that the third act isn’t just a resolution, but a space to examine the consequences of the climax, which makes the story feel more meaningful instead of just abruptly ending. Overall, this model helped me visualize why the “And, But, Therefore” structure works so well in narrative writing.

To notice this is very important. People may feel anxious when they are on social media, watching others showcase their assets, beauty, or grades. However, most normal people are not posting things on social media, which makes users think, "Am I worse than others?" Moreover, sometimes we see numerous complaints about a single product online, which creates the impression that this product or thing is particularly bad. However, people who are satisfied with it often won't post their praise unless it exceeds their expectations.

This would make sense for most of the other social media sites as well. Most people don't post all the time, meanwhile there is a smaller amount of people that are posting almost every single day or are posting every single day. Meanwhile, most people are posting things to their social media maybe once a month or even less than that. This would mean that a smaller percentage makes up a significant portion of the posts.

Upon further, thinking, I find this phenomenon to be very true. If you really look into it, even things like the food we eat all originate from very few variety of "mother" brands such as Coca-Cola, PepsiCo, Kellogg's, etc. I watched a video recently that revealed most restaurant foods originate from Sysco. Applying this to my own experiences, I can even count multiple times where group projects I've been assigned to end up just being 2 people mainly working on it, and the rest simply adding pictures to the slides.

How a person reacts at a conflict affects how well the child resilience and conflict resolution skills are when they're older

First the definition of good/bad crowd sourcing need to be clearly defined. There are many different types of 'good' crowd sourcing, one objective metric of good would be honest and correct factual information. A method some websites use is using a user voting system, where good and factual information is 'upvoted' and promoted more then information that is deemed less objective then others. Such websites include Wikipedia, and twitter community notes.

I've definitely taken part in crowdsourcing without even realizing it - like helping tag videos, report spam, or add info to online maps. I think social media companies should take some responsibility for what their users do, especially when harmful content spreads because of their design. Platforms could do more to guide people toward helpful actions, like fact-checking or supporting good causes, instead of just chasing clicks and treads.

I feel like social media companies should take some responsibility, especially when crowd actions cause harm, like harassment, misinformation, or targeted attacks. They created the environment, so they should make sure it doesn’t goes farther to harmful behavior. At the same time, they can’t control every individual, but they can control them by rules, the design, and the tools that possible shape a behavior.

This article is part of the special JITC series: SITC 40th Anniversary: I-O Progress and Potential

It really has little to no impact on my studies and academic performance. If anything, most of the time it pushes me to do better.

How novel/different is this compared to published CAST technologies to deserve it's own name?

Interesting. I wonder how you can reach such high resolution of the source to single line / paragraph level unless using tiny sized chunks in a RAG like platform?

Skip Stream

This is a great example of harm that can be done by the internet. It may have been unintended but there was harm nonetheless. When people have the ability to use the internet to find people it can be a great tool, however when there is a tragic event emotions run high and it is easy for that panic to translate into unintentional harm. This case is a good example of the snowball effect that can happen if one person gets something wrong and everyone assumes they are right out of fear or pride.

I think this is really important. As music educators it is really important for us to allow students to understand the way our classes function can also be carried over into the world outside of class epesically when dealing with topics like inclusivity and respect. Music class in itself can be vulnerable especially at a young age and it’s really important to create an understanding of yourself at this age.

I think this is a really important point because if you put the time in before the students arrive or even take the time to do it in the beginning ig of the school year it will all be worth it to make it the best environment for all of your students to feel like they can be the most successful and fully be themselves.

I find these couple sentences really important because it is important to understand that these behaviors may be caused by something outside of the classroom and could be caused by an expression of internal emotions so that must be taken into account when teaching students of varying abilities. It is important to keep intent in mind and make sure you’re checking in with students before immediately assuming they’re exhibiting this behavior to be disruptive.

I’ve observed this recently in the district that I’m in for this semester and I find that the relationship between the educator and the paraprofessionals is very important because both groups can observe any new behaviors or things that do and don’t work with the students and I find that the relationship between both parties is really important and must be developed.

I think this is a really effective way to helping students understand the rules more. Especially if a student is really struggling with following all the rules maybe assigning them one to work on will help them continue to understand and remember them and when one rule is mastered move onto another. I never really though of this so I think it’s really interesting and could be helpful in the future.

what he's going to argue/offer while taking all that has been said thus far into consideration (considering the ARPANET and digital networks, etc.

eLife Assessment

This study demonstrates the cartilage-protective effects of osteoactivin in inflammatory experimental models. The work offers valuable insights advancing current knowledge regarding regulation of joint inflammation and tissue degeneration. The evidence provided is compelling and suggests that osteoactivin may serve as a promising therapeutic target for inflammatory joint diseases.

Reviewer #1 (Public review):

Summary:

While previous studies by this group and others have demonstrated the anti-inflammatory properties of osteoactivin, its specific role in cartilage homeostasis and disease pathogenesis remains unknown.

Strengths:

Strengths of the study include its clinical relevance, given the lack of curative treatments for osteoarthritis, as well as the clarity of the narrative and the quality of most results."

Weaknesses:

A limitation of the study is the reliance on standard techniques; however, this is a minor concern that does not diminish the overall impact or significance of the work.

Comments on revisions:

The authors have satisfactorily addressed my concerns.

Reviewer #2 (Public review):

Summary:

This manuscript presents compelling evidence for a novel anti-inflammatory function of glycoprotein non-metastatic melanoma protein B (GPNMB) in chondrocyte biology and osteoarthritis (OA) pathology. Through a combination of in vitro, ex vivo, and in vivo models, including the destabilization of the medial meniscus (DMM) surgery in mice, the authors demonstrate that GPNMB expression is upregulated in OA-affected cartilage and that recombinant GPNMB treatment reduces the expression of key catabolic markers (MMPs, Adamts-4, and IL-6) without impairing anabolic gene expression. Notably, DBA/2J mice lacking functional GPNMB exhibit exacerbated cartilage degradation post-injury. Mechanistically, GPNMB appears to mitigate inflammation via the MAPK/ERK pathway. Overall, the work is thorough, methodologically sound, and significantly advances our understanding of GPNMB as a protective modulator in osteoarthritic joint disease. The findings could open pathways for therapeutic development.

Strengths:

(1) Clear hypothesis addressing a well-defined knowledge gap.

(2) Robust and multi-modal experimental design: includes human, mouse, cell-line, explant, and surgical OA models.

(3) Elegant use of DBA/2J GPNMB-deficient mice to mimic endogenous loss-of-function.

(4) Mechanistic insight provided through MAPK signaling analysis.

(5) Statistical analysis appears rigorous and the figures are informative.

Weaknesses:

(1) Clarify the strain background of the DBA/2J GPNMB+ mice: While DBA/2J GPNMB+ is described as a control, it would help to explicitly state whether these are transgenically rescued mice or another background strain. Are they littermates, congenic, or a separate colony?

(2) Provide exact sample sizes and variance in all figure legends: Some figures (e.g., Figure 2 panels) do not consistently mention how many replicates were used (biological vs. technical) for each experimental group. Standardizing this across all panels would improve reproducibility.

(3) Expand on potential sex differences: The DMM model is applied only in male mice, which is noted in the methods. It would be helpful if the authors added 1-2 lines in the discussion acknowledging potential sex-based differences in OA progression and GPNMB function.

(4) Visual clarity in schematic (Figure 7): The proposed mechanism is helpful but the text within the schematic is somewhat dense and could be made more readable with spacing or enlarged font. Also, label the MAPK/ERK pathway explicitly in panel B.

Comments on revisions:

The authors have addressed all the concerns raised in the initial review.

Author response:

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

Reviewer #1 (Public Reviews):

Weaknesses:

A limitation of the study is the reliance on standard techniques; however, this is a minor concern that does not diminish the overall impact or significance of the work.

We agree that standard techniques were utilized. We believe this approach enhances the reliability and reproducibility of our findings. These methods are well-validated in the field and allow for robust interpretation of the results presented.

Reviewer #2 (Public Reviews):

Weaknesses: 

(1) Clarify the strain background of the DBA/2J GPNMB+ mice: While DBA/2J GPNMB+ is described as a control, it would help to explicitly state whether these are transgenically rescued mice or another background strain. Are they littermates, congenic, or a separate colony?

The following language was added to the manuscript, “The DBA/2J GPNMB+ mice are a coisogenic strain purchased from Jackson Laboratories. Jackon Laboratories generated these mice by knocking in the wild-type allele of Gpnmb into the DBA/2J background. By doing so, they rescued the phenotype of the DBA/2J mice. This description has been highlighted in our previous publications (Abdelmagid et al., 2014; Abdelmagid et al., 2015).”

(2) Provide exact sample sizes and variance in all figure legends: Some figures (e.g., Figure 2 panels) do not consistently mention how many replicates were used (biological vs. technical) for each experimental group. Standardizing this across all panels would improve reproducibility.

The manuscript has been updated to include replicates in each figure legend.

(3) Expand on potential sex differences: The DMM model is applied only in male mice, which is noted in the methods. It would be helpful if the authors added 1-2 lines in the discussion acknowledging potential sex-based differences in OA progression and GPNMB function. 

To our knowledge there are no sexbased differences in OA progression and GPNMB function in the literature. It was initially reported that only male C57BL/6J mice (Jackson Laboratories) develop OA following DMM however, recent literature has shown that both male and female mice develop the disease (Hwang et al., 2021; Ma et al., 2007). For the purpose of this manuscript, only male mice were used to provide preliminary results, however, we plan to repeat the included studies in female mice in the near future.  

(4) Visual clarity in schematic (Figure 7): The proposed mechanism is helpful, but the text within the schematic is somewhat dense and could be made more readable with spacing or enlarged font. Also, label the MAPK/ERK pathway explicitly in panel B.

We updated the schematic diagram in figure 7 and the figure legend.

Reviewer #1 (Recommendations for the Authors):

Several concerns must be addressed to improve the clarity and scientific rigor of the manuscript: 

(1) Abstract: Specify which MMPs and MAPKs are modulated by osteoactivin.

We specified the MMPs and clarified that GPNMB plays a role in pERK inhibition following inflammation induced by IL-1β stimulation. 

(2) Human explant validation: The regulation of MMP-9, MMP-13, and IL-6 should be validated in the human cartilage explant model to support the claim that "GPNMB has an anti-inflammatory role in human primary chondrocytes" (line 123). Additionally, the anatomical origin of the explants must be stated.

Thank you very much for the recommendation. We agree that validating the explant culture for MMP-9, MMP-13, and IL-6 would strengthen our data. Unfortunately, this experiment has been terminated and we no longer have access to the tissue. Human explants were obtained from discarded knee articular cartilage following arthroplasty. The manuscript has been updated to include this information.

(3) DBA/2J GPNMB expression: GPNMB is known to be produced as a truncated protein in DBA/2J cells. The manuscript should address why its expression is reduced. Does this involve mRNA instability? Also, the nomenclature "DBA/2J GPNMB+" versus "DBA/2J" is confusing, especially since both mRNA and protein are still detectable, albeit at reduced levels. Figure 2C is not convincing; therefore, Figures 2C and 2D can be omitted.

The following language was added to the manuscript, “Our results are consistent with the literature which shows that that the GPNMB gene in DBA/2J mice carries a nonsense mutation that leads to reduced RNA stability (Anderson et al., 2008).” We can appreciate that the nomenclature "DBA/2J GPNMB+" versus "DBA/2J" could be confusing. However, this is the standard language used in multiple publications, and we want to remain consistent with the literature. Based on your recommendation we have removed Figure 2 C and D and updated the methods and results sections accordingly.   

(4) Figures 2J-L: The claim that gene expression changes are "significantly higher in DBA/2J animals compared to fold changes seen in chondrocytes from DBA/2J GPNMB+ controls" is not supported by the current presentation. The data should be plotted on the same graphs, and appropriate statistical analysis (e.g., two-way ANOVA) must be performed.

Graphs for figure 2 have been updated and the appropriate analyses have been performed. 

(5) Figure 6: The GPNMB expression data in the presence and absence of IL-1β at 0 and 10 minutes are missing.

We apologize for the confusion. We corrected the mistake and removed the mention of the timepoints 0 and 10 minutes.  

Reviewer #2 (Recommendations for the Authors):

Consider unifying terminology around "GPNMB" and "osteoactivin": The term "osteoactivin" is used in some contexts and "GPNMB" in others. Since the focus is GPNMB's role in cartilage, suggest using a single term throughout to prevent confusion.

Thank you for your comment. We include osteoactivin for clarification purposes once in the abstract, introduction and discussion. 

In summary, we believe we have addressed all comments/concerns raised by the reviewers. We appreciate the opportunity to improve the quality of our manuscript.

References

Abdelmagid, S. M., Belcher, J. Y., Moussa, F. M., Lababidi, S. L., Sondag, G. R., Novak, K. M., Sanyurah, A. S., Frara, N. A., Razmpour, R., & Del Carpio-Cano, F. E. (2014). Mutation in osteoactivin decreases bone formation in vivo and osteoblast differentiation in vitro. The American journal of pathology, 184(3), 697-713. 

Abdelmagid, S. M., Sondag, G. R., Moussa, F. M., Belcher, J. Y., Yu, B., Stinnett, H., Novak, K., Mbimba, T., Khol, M., Hankenson, K. D., Malcuit, C., & Safadi, F. F. (2015). Mutation in Osteoactivin Promotes Receptor Activator of NFκB Ligand (RANKL)-mediated Osteoclast Differentiation and Survival but Inhibits Osteoclast Function. J Biol Chem, 290(33), 2012820146. https://doi.org/10.1074/jbc.M114.624270  

Anderson, M. G., Nair, K. S., Amonoo, L. A., Mehalow, A., Trantow, C. M., Masli, S., & John, S. W. (2008). GpnmbR 150Xallele must be present in bone marrow derived cells to mediate DBA/2J glaucoma. BMC genetics, 9(1), 1-14. 

Hwang, H., Park, I., Hong, J., Kim, J., & Kim, H. (2021). Comparison of joint degeneration and pain in male and female mice in DMM model of osteoarthritis. Osteoarthritis and Cartilage, 29(5), 728738. 

Ma, H.-L., Blanchet, T., Peluso, D., Hopkins, B., Morris, E., & Glasson, S. (2007). Osteoarthritis severity is sex dependent in a surgical mouse model. Osteoarthritis and Cartilage, 15(6), 695-700.

Use bold and yellow highlight / underlining.

This is repeating what we already say below the little chart with the 6/26 numbers. Replace with this: Most of the 20 newly affected districts share two features: they lie in the commuter belts of major cities or in attractive coastal regions, and their rent burdens have climbed from the low-to-mid 20s to over 30% within just a decade. In other words, not only have Germany’s classic boom regions become more expensive, the pressure has spilled over into the very areas that many people once saw as an affordable alternative.

Directly remove this entire box.

Begin the sentence with "however, despite...."

replace with:

The following chart tracks both the nominal raises and the inflation-adjusted reality for a set of professions that show some of the strongest upward or downward trends since 2016.

After this sentence insert the following paragraph:

By contrast, many high-skilled technical professions, including IT, and mechanical and electrical engineering, saw only moderate increases despite booming demand for skilled labor.

Before this sentence insert the following paragraph: Traditionally lower-paid roles such as elder care, cleaning, and hospitality recorded the strongest nominal wage gains since 2016, driven by higher minimum wages, stronger collective bargaining agreements, and political attention directed at essential workers during the pandemic.

get rid of this paragraph and replace with this:

A clear pattern emerges across these low-burden regions. Many of them are former industrial centres such as Gelsenkirchen, Hagen, Salzgitter, or Wolfsburg, or rural and semi-rural East German districts like Chemnitz, Zwickau, Vogtlandkreis, and Salzlandkreis. These are not classic commuter belts of major cities, nor places experiencing strong population inflows. Instead, they tend to have slow or negative population growth, limited rental pressure, and only moderate increases in housing demand. As a result, rents have remained comparatively stable, and even with lower average incomes, households in these districts can maintain a comfortably low rent-to-income ratio, a rare form of financial breathing room in today’s market.

this is good quote

If the temporal lobe is damaged does it mean that all of the function of the temporal lobe is finished, or is still possible that some of the function still retains?

The diencephalon consist of the hypothalamus, thalamus, and epithalamus, which are important for memory, sleep, and hormone homeostasis.

1/ 1. Openness=Content creator, fashion designer 2. Conscientiousness=Nurse, Social worker, Teacher 3. Extraversion=Sales, Motivational speaker 4. Agreeableness=Counselor, Customer service 5. Neuroticism=Researcher, Delivery, work alone

Conscientiousness seems a desired trait across all jobs. 2/The unique challenges for low self-esteem: Managing employees with low self-esteem may be challenging at times because negative feedback given with the intention of improving performance may be viewed as a negative judgment on their worth as an employee. Therefore, effectively managing employees with relatively low self-esteem requires tact and providing lots of positive feedback when discussing performance incidents.

The unique challenge for low self-efficacy: People with low self-efficacy tend to procrastinate. training people to increase their self-efficacy may be effective. Some people may also respond well to verbal encouragement. By showing that you believe they can be successful and effectively playing the role of cheerleader, a manager may be able to increase self-efficacy beliefs. Empowering people—giving them opportunities to test their skills so that they can see what they are capable of—is also a good way of increasing self-efficacy

3/ Personality testing, Testing of cognitive abilities(mental intelligence), Interviews 4/ I had to face many dishonest people who were like scammers and I had to lie but I hate dishonesty. I could not fake myself well. I eventually quit the job. 5/ Openness can help find opportunities in businesses as the traits are creative and open to new ideas. It can help find creative solutions. Conscientiousness helps pay attention to details that would serve an accurate judgement of people.

Author Response:

Reviewer #1 (Public Review):

This ms targets an interesting question, whether changes of feedforward inhibition at the DG-CA3 synapses regulate the representational capabilities of contextual fear memory at CA1 and the anterior cingulate cortex (ACC). The paper exploits a recent tool developed by the group (viral-mediated shRNA interference of Ablim3 in DG), to enhance PV+ mediated inhibition of CA3 pyramidal cells by increasing both their recruitment by DG cells and their number of contacts over postsynaptic cells. Using micro-endoscopic imaging of mice experiencing contextual fear conditioning, the authors nicely evaluate the effect of feedforward inhibitory control of CA3 outputs in the formation, stabilization and specificity of contextual fear memory representations in the CA1 and ACC. Data is relevant to understand how specific microcircuit motifs can influence representational dynamics in downstream regions. I have some methodological comments and recommendations for authors to improve their presentation and to exclude potential confounding factors.

1- Since imaging is performed in CA1 and ACC separately, the study design entails 4 groups: shNT vs shRNA which is the main experimental manipulation, plus CA1 vs ACC. While data is in general carefully presented, some analysis may require additional validation to discard whether some regional effects caused by manipulation may actually reflect group differences. This is important because there may be some differences between ACC and CA1 groups in some behavioral readout (e.g. Fig.2c; Fig.S2b) which may actually explains different effect of manipulation. Formal comparisons of behavior in ACC and CA1 shNT groups may be required to discard this effect.

We compared behavior data in the control groups across brain region to test if our calcium imaging findings are driven by differences in groups rather than virus manipulation. We did not find a significant difference for any of the data sets (see figure legend Rebuttal Figure 1 a-d for details). In general, we tried to avoid presenting the same (or part of the same) dataset in multiple figures. An alternative would be to plot all 4 groups in 1 graph and test as such but that would decrease readability in our opinion. Therefore, we are happy to provide the additional graphs and analysis but prefer not to include them in the main manuscript. (Rebuttal Figure 1a-d).

2- Differences of activity level (calcium rate) are examined using bins of 5 seconds for a total of 360 sec of exploratory activity. To discard motility effects an analysis is implemented using 1 sec bins. Thus, the two data samples are not commensurate. Also, an ANOVA on calcium rate is applied over uneven multiple comparisons to account for statistical effects of region x time or context x time. This is relevant for fig.1g vs 1i and Fig.S2j,l and may require correction.

We assume you mean “1 minute” and not “1 sec” here. We presented the two datasets (calcium event rate) and moving index indeed using different time bins (5 sec and 1 minute respectively). It is true that a difference in binning and therefore different sample size in one factor (time) could affect the result of the ANOVA. Rebuttal Figure 1 e-f shows the behavior comparison made in Suppl.Figure 2b in the original manuscript with a 5 second bin. A 2-Way ANOVA with repeated measurements reveals no main virus effect [Two-way repeated measures ANOVA, ACC (e): virus x time effect 0.0113; virus main effect N.S., time main effect N.S., n=5 per group; CA1 (f): virus x time effect N.S.; virus main effect N.S., time main effect N.S., n=5 shNT, n=6 shRNA]. In ACC, we find a significant interaction effect but a posthoc Sidak test did not reveal a difference between virus groups at any time point. This confirms our previous findings that differences in movement do not seem to drive the differences between virus groups.

3- Fig.3 nicely show accurate context classification based on calcium activity from A&C contexts neurons using support-vector machine. The authors report very interesting representational effects for shNT vs shRNA manipulations. Is prediction accuracy of the SVM classifier correlated with behavioral discrimination? That would reinforce conclusions.

Thank you for raising this very interesting point and indeed, we found a positive correlation between the discrimination ratio and the accuracy of the SVM classifier (Pearson’s r, shNT: R2 = 0.5794, p= 0.0282, n=4; shRNA: R2= 0.5771, p= 0.0288 , n=4. We added these data in Figure 4 (Figure 4c) and in Rebuttal Figure 1g.

Regarding conclusions and physiological relevance, the authors may need to discuss why enhanced feedforward inhibition at DG-CA3 synapses is not naturally established given the beneficial effect in context discrimination.

We apologize that we did not make that aspect of our manipulation clearer in our discussion. We edited the introduction and discussion (LL 65, LL 365) to clearly convey that FFI in DG-CA3 is naturally temporarily increased following learning (Ruediger 2011, Ruediger 2012, Guo et al 2018).

Reviewer #3 (Public Review):

In this study, Twarkowski et al. aim to understand the role of a specific circuit motif, dentate gyrus (DG) to CA3 feed-forward inhibition (FFI), for memory encoding and consolidation. FFI is a ubiquitous circuit motif in the brain. As a result, providing insights on its function is an interesting and a potentially very impactful contribution to neuroscience.

To tackle this issue, the authors describe how increasing DG-CA3 FFI impacts the ensemble activity in hippocampal area CA1 and the anterior cingulate cortex (ACC) in mice undergoing a contextual fear conditioning paradigm. To selectively increase FFI onto CA3 neurons, the study uses a molecular tool (downregulation of Ablim3 using virally mediated expression of shRNA), which has been developed by the same group (Guo et al, 2018, Nature Medicine). The impact of this manipulation is assessed via chronic in vivo one-photon Ca2+ imaging of dorsal CA1 and ACC neurons on the day of fear conditioning, one day after (recent recall), and 16 days after (remote recall) the fear conditioning. During and after fear conditioning, the results show in both experimental groups (shRNA and control) various population activity changes in both CA1 and ACC. Furthermore, the study finds improved context discrimination in the shRNA group only at the remote recall timepoint. The authors' conclusion is that increasing FFI enhances the formation of learning-specific ensembles, first in CA1 and later in ACC, which is associated with an improved memory recall. The experiments presented here were very technically challenging and produced a comprehensive and valuable dataset describing the parallel ensemble activity changes in CA1 and ACC after fear conditioning, with or without increasing DG-CA3 FFI. However, a causal relationship between the manipulation of DG-CA3 FFI, the network activity changes in CA1 and ACC, and the behavioral improvement is, in my opinion, not fully demonstrated. This is for a couple of reasons:

1) The magnitude of the effect of the shRNA manipulation on the immediate downstream area CA3 remains unclear. Therefore, the findings in the downstream areas CA1 or even ACC (which is at least three synapses removed from CA3) are, in my opinion, difficult to interpret. This uncertainty includes (1) the extent of the virus injection in the dentate gyrus and the extent of subsequent changes in CA3, and (2) the effect of the manipulation on CA3 pyramidal cell activity in vivo. The original paper (Guo et al, 2018) uses in vitro voltage-clamp recordings to record EPSCs/IPSCs in CA3, but does not exclude possible compensatory changes in vivo, e.g., in the excitability of CA3 neurons, which could result from increasing FFI chronically over a few weeks. The data in Figures 1f and g seems to suggest that there are baseline activity changes in CA1, which might be caused by changes in the upstream CA3 network activity. Along the same lines, I am unsure how to interpret the comparisons between CA1 and ACC in Figure 1; within brain region comparisons are more relevant and should be shown instead.

This is a great point and was raised by all reviewers. We acknowledge the weakness of this comparison, apologize for this misstep in our analysis and have accordingly, removed this dataset from our manuscript. Instead, we performed new experiments using in vivo electrophysiology to allow for cross-region comparison of LFPs in CA1 and ACC within the same animal. We removed data from Figure 1 e-i and added new, simultaneous electrophysiological LFP recordings (Figure 5 and supplementary Figure 4 in revised manuscript).

We found an increased number of CA1 ripples that are coupled with ACC spindles (“coupled ripples”) in shRNA mice compared to control mice prior to a learning event (Figure 5c, two-tailed unpaired student’s t-test with Welch’s correction, p=0.0499, n=5) with no difference in time spend in slow-wave sleep (SWS) (supplementary Figure 4a) or total numbers of spindles or ripples (supplementary Figure 4b-c). Control mice show a learning-dependent increase in coupled ripples (Figure 5f, two-tailed paired student’s t-test, p=0.019, n=5) to a similar level as seen in shRNA mice prior to learning. No further increase is seen in shRNA mice indicating a saturation of circuit changes that cannot be further amplified following learning.

2) Several parameters are used in this study to describe the network activity in CA1 and ACC. These include the number of correlated neuron pairs, the number of neurons active in both the training context and a neutral context (so-called A-C neurons), or the event rate observed in these A-C neurons. Most of the activity changes observed do not appear specific to the shRNA group and occur also under control condition, suggesting that they are not caused by an increase in DG-CA3 FFI. It would be helpful to clarify the sequence, how increasing FFI onto CA3 is hypothesized to cause the changes in CA1 or even ACC.

We apologize for failing to make this clearer. Prior work has shown that learning increases FFI in DG-CA3 and downregulates Ablim3 in DG (Ruediger 2011, 2012, Guo et al 2018). Therefore, it is not surprising that we observe similar changes in the control (shNT) group as shRNA group.

From previous work we know that shNT mice show increased DG-CA3 FFI following learning (training day) for approximately 24 hours (Guo et al, 2018). Thus, our manipulation allows us to mimic and boost a naturally occurring learning-induced synaptic modification in an inhibitory microcircuit in DGCA3 and examine the impact on network mechanisms underlying systems consolidation. Importantly, enhanced feedforward inhibition at the DG-CA3 synapses is naturally established for several hours following a spatial learning event (see Ruediger et al, 2011, Guo et al, 2018). Leveraging a molecular tool to enhance FFI prior to learning, we were able to reveal that DG-CA3 FFI plays a role in tuning the circuit towards cross-regional long-term storage of precise neuronal representations. (see also edits in text, LL 365).

Author Response:

Reviewer #1 (Public Review):

[...]

1. A notable shortcoming of the authors' interpretation is the generalization of their findings to preterm premature rupture of membranes (PPROM). As noted by the authors, term labor is considered a "sterile" process, which is particularly important in terms of the authors' findings since TLR4 in the fetal membranes may be responding to endogenous signals such as danger signals. However, a large proportion of PPROM cases are associated with microbial invasion of the amniotic cavity, and thus in this context TLR4 would be responding to bacterial products.

To bring in some new elements and address this reviewer’s concern, along with the potential extrapolation between physiological rupture and pathological rupture in the case of PPROM, we decided first to remove Figure 3C (expression of TLR4 in the presence of LPS from bacterial origin) from the revised version of the manuscript. To address this comment, it is well known that the percentage of PPROM associated with microbial invasion are variable based on the weeks of gestation. In fact, early gestational ages are clearly linked to high-microbial-associated intra-amniotic inflammation prevalence (64.3% when <25 WGA) whereas this percentage subsequently decreases throughout gestation (Romero et al., 2015), reaching one-third at term, which better links with the gestational stage of the current study. Such observations support the fact that the TLR4 model in physiological rupture could be transposed—at least in part—to sterile PPROM and initiated by the presence of alarmins (i.e., HMGB1) and their binding to such type of receptors. Indeed, TLR4 is now well described as being stimulated by ligands other than LPS, such as HMGB1, a member of the DAMPs (Robertson et al., 2020). Furthermore, the quantification of TLR4 mRNA expression and protein in the case of PPROM without chorioamnionitis compared with term no labor without chorioamnionitis was already carried out (Kim et al., 2004), indicating an absence of clear link between the chorioamnionitis and TLR4 expression. Finally, in an animal model of PPROM, an article underlined the importance of TLR4 in preterm labor by using TLR4 mice mutants in a sterile context (Wahid et al., 2015).

1. It is a well-known concept that TLR4 is expressed by the fetal membranes and is responsive to LPS stimulation, and thus the confirmatory set of experiments performed by the authors do not seem to be as novel. Indeed, given that this study was focused on the "sterile" process of term labor, perhaps the utilization of danger signals that can interact with TLR4 would be more appropriate.

The choice to use LPS (Figure 3C) was only to confirm that TLR4 leads to a proinflammation activation in the amnion and choriodecidua, demonstrating the functional pathway after TLR4 activation in the fetal membranes environment. We completely agree these are not novel data; this is why we decided to remove this part of results in the revised version of the manuscript. Furthermore, we decided to not repeat the use of DAMPs (such as HMGB1) to stimulate the TLR4 pathway in this work because it was already published in the fetal membranes context (Bredeson et al., 2014). To be in accordance with your comments, we have modified the end of the results paragraph entitled ‘Combination of transcriptomic and methylomic results in the ZAM zone demonstrate that genes more expressed in the choriodecidua are linked to pregnancy pathologies’ to better justify the choice to focus on TLR4 global transcriptional regulation.

1. The distinction between the ZAM and ZIM seems to have been lost among the TLR4-focused experiments, and thus it is unclear how these fetal membrane zones fit into the conceptual model proposed by the authors in the final figure.

The reviewer is correct here, so to avoid confusion between the ZIM and ZAM used, we decided to do the following: - Read carefully all the successive paragraphs of the results to check for the presence of ‘ZAM specification’ - Add ‘ZAM’ in the legend of Figure 4. This information was present in the related text of the article. - Update Figure 7 and its legend (model of regulation). We had ‘ZAM zone’ in the discussion part regarding Figure 7.

1. The study is largely descriptive and would benefit from the addition of fetal membrane tissues from pregnancy complications such as PPROM and/or animal models in which premature rupture of the membranes has been induced.

We agree that animal models are available. Nevertheless, we considered that such models are far from the human reality. In fact, animal models are often used for fetal membrane studies, but they are different regarding pregnancy physiology, structure and uterine environment, which hamper their use. We used ‘term’ fetal membrane to decipher the physiological rupture of membrane and demonstrate the importance of the TLR4 actor. To bring some elements regarding this comment and the possible extrapolation between physiological rupture and pathological rupture in the case of PPROM, we decided to remove Figure 3C (expression of TLR4 in the presence of LPS from bacterial origin) to focus more on the physiological rupture of fetal membranes without the involvement of bacterial presence. Previous bibliographic data answer the reviewer’s question: Kim et al. (2004) well demonstrated that TLR4 mRNA levels are higher in PPROM (31.2 weeks of gestation) fetal membranes without chorioamnionitis than in term (39.1 week of gestation) ones without chorioamnionitis.

1. The study focuses on the mechanisms of rupture of membranes, but does not provide an explanation as to how the regulation of TLR4 mediates the process of membrane rupture.

We agree with your comment; however, ‘how the regulation of TLR4 mediates the process of membrane rupture’ is not the topic of the manuscript. In addition, this has already been well established in previous publications. Nevertheless, we added a sentence in the introduction part between the lines 97-100 : ‘The mechanisms implying TLR4 in the physiological or pathological rupture of membrane in case of PPROM are well known. Triggering TLR4 will lead to NFκB activation, leading to an increase of the release of proinflammatory cytokine, concentration of matrix metalloprotease and prostaglandin, which are well established actors of fetal membrane rupture (Robertson et al., 2020).

Reviewer #2 (Public Review):

This is a well-conceived and executed paper that adds novel data to improve our understanding of rupture of the human fetal membranes. The new information presented not only addresses gaps in our understanding of normal parturition mechanisms but also the significant issue of preterm birth. The authors highlight the need to understand the understudied human fetal membranes to be able to understand its role in normal parturition but also to lower the rates of preterm birth. They not only establish the need to study this tissue but also to improve our appreciation for regional differences within it, using a comprehensive genetic approach. The authors provide data from a genome wide methylation study and cross reference this with transcriptome data. Using this new knowledge, they then zero in on a specific gene of interest TLR4. This receptor is already established as an extremely important receptor for preterm birth but little is known about its role in normal parturition. Strengths of this paper stem from the comprehensive data set provided, answering both the questions pertaining to the specific aims of this paper but also potentially future questions and providing potential focused targets of study. One example of this may be the common methylated genes that are found in both the ZIM and ZAM, illustrating not regional changes but gestational programming of this tissue.

We thank the reviewer for the positive and constructive comments regarding the article. Following all the reviewers’ comments, we now have an improved version.

Reviewer #3 (Public Review):

Manuscript by Belville et al describes the significance of epigenetic and transcription associated changes to TLR4 as a mechanistic event for sterile inflammation associated with fetal membrane weakening, specifically in the zone of altered morphology. This manuscript is timely in an understudied area of research.

The authors have taken an extensive set of experiments to derive their conclusions.

However, it is unclear why the focus is on TLR4. Although LPS is a ligand for TLR4, gram negative infections are rare in PPROM but mostly genital Mycoplasmas. The methylome and transcriptome analysis does not necessarily warrant examination of a single marker. A clear rationale would need to be included.

We would like to thank the reviewer for their comments regarding the article. For the last part of the public review, we would like to underline the following:

-The choice of focusing on TLR4 is explained in the article text between lines 161 and 165 by the following sentences: ‘Of all the genes classified in these processes, TLR4 was the only one represented in all these biological processes and, therefore, seems to play a central role in parturition at term. To validate this in-silico observation and pave the way for describing TLR4’s importance, immunofluorescence experiments were first conducted to confirm the protein’s presence in the amnion and choriodecidua of the ZAM (Figure 3B)’. Furthermore, this choice arises from analysis described in Figure 3A, which underlines that the four GO terms most represented have only one common gene: ‘TLR4’. The combination of two high-scale studies does not permit us to individually characterize how each gene is regulated. Nevertheless, the focus on TLR4 provides an original and interesting hypothesis on how a specific layer regulation between the amnion and choriodecidua could be cellular realised in the ZAM’s weaker zone. Finally, because the high-scale study results are public, this type of analysis could be conducted on other candidate genes.

-Throughout the text, we changed all the ‘E. Coli’ to ‘Gram-negative bacteria’. Furthermore, as found in the literature, genital mycoplasma are considered ‘Gram-negative bacteria’. We focused on the ‘sterile inflammation phenomenon’, and to support the hypothesis concerning the importance of TLR4, we realised a supplementary transcriptome ‘ZAM heatmap’, which confirmed a sur-expression of DAMP in choriodecidua, S100A7, A8 and A9, for example, which are well-known ligands of TLR4 (given below as an image).

Heatmap of genes differentially expressed in the ZAM zone in relation to the sterile inflammation phenomenon.

Author Response

Reviewer #3 (Public Review):

The authors analyzed several models for predicting the early onset of T2D, where they trained and tested on a UKB based cohort, aged 40 - 69 and suggest two simple logistic regression models: the anthropometric and the five blood tests models in reference to FINDRISC and GDRS models. Their models achieved better auROC, APS, and decile prevalence OR, and better-calibrated predictions.

Strengths:

1.The authors have neatly explained their objectives and performed well-justified analyses.

2.The authors highlight how using both features - HbA1C% measure and reticulocyte count may provide a better indication of the average blood sugar level during the last two-three months than using just the standard HbA1C% measure.

3.Further verification of the proposed anthropometric-based and 5 blood-test results-based modelscan discriminate discriminating within a group of normoglycemic participants and within a group of pre-diabetic participants resulted in outperforming the FINDRISC and the GDRS based models.

Weaknesses:

1. As the authors point out in the manuscript that these models are suited for the UKB cohort or populations with similar characteristics. It limits the extrapolation of these findings onto another cohort from a different background until analyzed on another country/continent-based cohort.

We agree with this comment as we indeed pointed in the paper. We recommend to adjust these models when applying it to populations with distinct characteristics.

1. In the methods section, an additional explanation of how the T2D prevalence bins were formed would be useful to a reader.

We thank the reviewer for this note, we added the following explanation in section 4.11: “We considered several potential risk score limits that separate T2D onset probability in each of the scores groups, and we chose boundaries that showed a separation between the risk groups on the validation datasets. Once we decided on the boundaries of the score, we report the prevalence in each risk group on the test set and we report these results.”

1. The authors have mentioned that the prevalence of diabetes has been rising more rapidly in low and middle-income countries (LMICs) than in high-income countries and the objective of the present research was to develop clinically usable models which are easy to use and highly predictive of T2D onset. As lifestyle is also one of the contributory factors for T2D, additional analysis that includes a comparison of groups between low-income and high-income subjects within UKB-based cohort provided such metadata available would help understand if the prevalence for T2D differs or not between such groups.

We thank the reviewer for this comment, we added below an analysis that we run on our data, showing the deprivation indexes differences between sick and healthy populations. The sick population has a higher deprivation index as expected. When running a Mann-Whitney U Test on the data we get a p value of zero, creating this with a sample of just 1000 participants from each group, we get a p-value of 2.37e-137. This indicates that there is a significant correlation between deprivation index and tendency to develop T2D. We also add this finding to the supplementary material and a reference to it.

You can also find below a SHAP diagram showing tht higher Townsend deprivation index is pushing the prediction for T2D upwards.

Author Response

Reviewer #2 (Public Review):

Summary: This substantial collaborative effort utilized virus-based retrograde tracing from cervical, thoracic and lumbar spinal cord injection sites, tissue clearing and cutting-edge imaging to develop a supraspinal connectome or map of neurons in the brain that project to the spinal cord. The need for such a connectome-atlas resource is nicely described, and the combination of the actual data with the means to probe that data is truly outstanding.

They then compared the connectome from intact mice to those of mice with mild, moderate and severe spinal cord injuries to reveal the neuronal populations that retain axons and synapses below the level of injury. Finally, they look for correlations between the remaining neuronal populations and functional recovery to reveal which are likely contributing to recovery and its variability after injury. Overall, they successfully achieve their primary goals with the following caveats: The injury model chosen is not the most widely employed in the field, and the anatomical assessment of the injuries is incomplete/not ideal.

Concerns/issues:

1) I would like to see additional discussion/rationale for the chosen injury model and how it compares to other more commonly employed animal models and clinical injuries. Please relate how what is being observed with the supraspinal connectome might be different for these other models and for clinical injuries.

We have added text to the Results and Discussion to explain our rationale for selecting the crush injury model, and to acknowledge differences between this model and more clinically relevant contusion models. (Results: line 360-364, Discussion 608-615). We agree wholeheartedly that a critical future direction will be to deploy brain-wide quantification in contusion models, and we are currently seeking funding to obtain the needed equipment.

2) The assessment of the thoracic injuries employed is not ideal because it provides no anatomical description of spared white matter (or numbers of spared axons) at the injury epicenter.

We address this more fully in the related point below. Briefly, we agree with a need to improve the assessment of the lesion but are hampered by tissue availability. We are unable to assess white matter sparing but can offer quantification of the width of residual astrocyte tissue bridges in four spinal sections from each animal (new Figure 5 – figure supplement 3). As discussed below, however, we recognize the limitations of the lesion assessment and agree with the larger point that the current quantification methods do not position us to make claims about the relative efficacy of spinal injury analyses versus whole-brain sparing analyses to stratify severity or predict outcomes. Our approach should be seen as a complement, not a substitute, for existing lesion-based analyses. We have edited language throughout the manuscript to make this position clearer.

3) Related to this, but an issue that requires separate attention is the highly variable appearance of the injury and tracer/virus injection sites, the variability in the spatial relationship with labeled neurons (lumbar) and how these differences could influence labeling, sprouting of axons of passage and interpretation of the data. In particular this is referring to the data shown in Figure 6 (and related data).

It is true that there is some variability in the relative position of the injury and injection, a surgical reality. The degree of variability was perhaps exaggerated in the original Figure 6 (Now Figure 5), in which one image came from one of two animals in the cohort with a notably larger gap between the injury and injection. Nevertheless, this comment raises the important question of how variability in injection-to-injury distance might affect supraspinal label. First, we would emphasize the data in Figure 1 – Figure Supplement 6, in which we showed that the number of retrogradely labeled supraspinal neurons is relatively stable as injection sites are deliberately varied across the lower thoracic and lumbar cord. Indeed, the question raised here is precisely the reason we performed this early test to determine how sensitive the results might be to shifts in segmental targeting. The results indicate that retrograde labeling is fairly insensitive to L1 versus L4 targeting. As an additional check for this specific experiment we also measured the distance between the rostral spread of viral label and the caudal edge of the lesion and plotted it against the total number of retrogradely labeled neurons in the brain. If a smaller injury/injection gap favored more labeling we might expect negative correlation, but none is apparent. We conclude that although the injury/injection distance did vary in the experiment, it likely did not exert a strong influence on retrograde labeling.

Reviewer #3 (Public Review):

In this manuscript, Wang et al describe a series of experiments aimed at optimizing the experimental and computational approach to the detection of projection-specific neurons across the entire mouse brain. This work builds on a large body of work that has developed nuclear-fused viral labelling, next-generation fluorophores, tissue clearing, image registration, and automated cell segmentation. They apply their techniques to understand projection-specific patterns of supraspinal neurons to the cervical and lumbar spinal cord, and to reveal brain and brainstem connections that are preferentially spared or lost after spinal cord injury.

Strengths:

Although this work does not put forward any fundamentally new methodologies, their careful optimization of the experimental and quantification process will be appreciated by other laboratories attempting to use these types of methods. Moreover, the observations of topological arrangement of various supraspinal centres are important and I believe will be interesting to others in the field.

The web app provided by the authors provides a nice interface for users to explore these data. I think this will be appreciated by people in the field interested in what happens to their brain or brainstem region of interest.

Weaknesses:

Overall the work is well done; however, some of the novelty claims should be better aligned with the experimental findings. Moreover, the statistical approaches put forward to understand the relationship between spinal cord injury severity and cell counts across the mouse brain needs to be more carefully considered.

The authors state that they provide an experimental platform for these types of analysis to be done. My apologies if I missed it but I could not find anywhere the information on viral construct availability or code availability to reproduce the results. Certainly both of these aspects would be required for people to replicate the pipeline. Moreover, the described methodology for imaging and processing is quite sparse. While I appreciate that this information is widely provided in papers that have developed these methods, I do not think it is appropriate to claim to have provided a platform for people to enable these types of analyses without a more in-depth description of the methods. Alternatively, the authors could instead focus on how they optimized current methodologies and avoid the overstatement that this work provides a tool for users. The exception to this is of course the viral constructs, the plasmids of which should be deposited.

We agree that we have not provided a tool per se, more of an example that could be followed. We have revised language in the abstract, introduction, and discussion to make it clear that we optimized existing methods and provide an example of how this can be done, but are not offering a “plug and play” solution to the problem of registration that would, for example, allow upload of external data. For example, in the abstract we replaced “We now provide an experimental platform” with “Here we assemble an experimental workflow.” (Line 28). The term “platform” no longer appears in the manuscript and has been replaced throughout by “example.” We how this matches the intention of the comment and are happy to revise further as needed. Note that the plasmids have been deposited to Addgene.

It was not completely to me clear why or when the authors switch back and forth between different resolutions throughout the manuscript. In the abstract it states that 60 regions were examined, but elsewhere the number is as many as 500. My understanding is that current versions of the Allen Brain Annotation include more than 2000 regions. I think it would make things clear for the readers if a single resolution was used throughout, or at least justified narratively throughout the text to avoid confusion.

Thank you for pointing this out. The Cellfinder application recognizes 645 discrete regions in the brain, and across all experiments we detected supraspinal nuclei in 69 of these. This number, however, includes some very fine distinctions, for example three separate subregions of vestibular nuclei, three subregions of the superior olivary complex, etc. True experts may desire this level of information, but with the goal of accessibility we find it useful to collapse closely related / adjacent regions to an umbrella term. Doing so generates a list of 25 grouped or summary regions. In the revised version we move the 69-region data completely to the supplemental data (there for the experts who wish to parse), and use the consistent 25-region system (plus cervical spinal cord in later sections) to present data in the main figures. We have added text to the Results section (lines 157-162) to clarify this grouping system.

The others provide an interesting analysis of the difference between cervical and lumbar projections. I think this might be one of the more interesting aspects of the paper - yet I found myself a bit confused by the analysis, and whether any of the differences observed were robust. Just prior to this experiment the authors provide a comparison of the mScarlet vs. the mGL, and demonstrate that mGL may label more cells. Yet, in the cervical vs. lumbar analysis it appears they are being treated 1 to 1. Moreover, I could not find any actual statistical analysis of this data? My impression would be that given the potential difference in labelling efficiency between the mScarlet and mGL this should be done using some kind of count analysis that takes into account the overall number of neurons labelled, such as a Chi-sq test or perhaps something more sophisticated. Then, with this kind of statistical analysis in place, do any of the discussed differences hold up? If not, I do not think this would detract from the interesting topological observations - but would call on the authors to be a bit more conservative about their statements and discussion regarding differences in the proportions of neurons projecting to certain supraspinal centers.

This is an important point. In response to this input and related comments from other reviewers we performed new experiments to assess co-localization. The new data address the point above by including quantification of the degree of colocalization that results from titer-matched co-injection of the two fluorophores, providing baseline data. The results of this can be found in Figure 3 – figure supplement 3 and form the basis for statistical comparisons to experimental animals shown in Figure 3.

Finally, I do have some concerns about the author's use of linear regression in their analysis of brain regions after varying severities of SCI. First of all, the BMS score is notoriously non-linear. Despite wide use of linear regressions in the field to attempt to associate various outcomes to these kinds of ordinal measures, this is not appropriate. Some have suggested a rank conversion of the BMS prior to linear analyses, but even this comes with its own problems. Ultimately, the authors have here 2-3 clear cohorts of behavioral scores and drawing a linear regression between these is unlikely to be robustly informative. Moreover, it is unclear whether the authors properly adjusted their p-values from running these regressions on 60 (600?) regions. Finally, the statement in the abstract and discussion that the authors "explain more variability" compared to typical lesion severity analysis is also unsupported. My suggestion would be the following:

Remove the linear regression analyses associated with BMS. I do not think these add value to the paper, and if anything provide a large window of false interpretation due to a violation of the assumptions of this test.

Consider adding a more appropriate statistical analysis of the brain regions, such as a non-parametric group analysis. Knowing which brain regions are severity dependent, and which ones are not, would already be an interesting finding. This finding would not be confounded by any attempt to link it to crude measures of behavior.

We agree that the linear regression approach was flawed and appreciate the opportunity to correct it. After consultation with two groups of statisticians we were forced to conclude that the data are simply underpowered for mixed model and ranking approaches. We therefore adopted a much simpler strategy. As you point out (and as noted by the statisticians), the behavioral data are bimodal; one group of animals regained plantar stepping ability, albeit with varying degrees of coordination (BMS 6-8), while the others showed at most rare plantar steps (BMS 0-3.5). We therefore asked whether the number of spared neurons in each brain region differed between the two groups and also examined the degree of “overlap” in the sparing values between the two groups. The data are now presented in Figure 6.

If the authors would like to state anything about 'explaining more variability' then the proper statistical analysis should be used, which in this case would be to compare the models using a LRT or equivalent. However, as I mentioned it does not seem to be appropriate to be doing this with linear models so the authors should consider a non-linear equivalent if they choose to proceed with this.

We thank the reviewer for the excellent suggestion. However as we explained above after consultation with two groups of statisticians we were forced to conclude that the data are underpowered and could not apply some of the methods suggested. Especially in light of our simplified analysis, we think it is better to remove any claims of the relative success of the sparing in different regions to explain more or less variability. Instead we can simply report that sparing in some regions, but not others, is significantly different between “low-performing” and “high-performing” groups.

Author Response:

Reviewer #1 (Public Review):

This paper focuses on the role of historical evolutionary patterns that lead to genetic adaptation in cytokine production and immune mediated diseases including infectious, inflammatory, and autoimmune diseases. The overall goal of this research was to track the evolutionary trajectories of cytokine production capacity over time in a number of patients with different exposure to infectious organisms, infectious disease, autoimmune and inflammatory diseases using the 500 Functional Genomics cohort of the Human Functional Genomics Project. The identified cohort is made up of 534 individuals of Western European ancestry. Much of this focus is on the impact and limitations of certain datasets that they have chosen to use such as the "average genotyped dosage" to be substituted for missing variants and data interpretation.

We fully agree with the reviewer, we replace missing variants in a sample with its average dosage in the entire dataset. This makes it so missing variants in a sample do not bias the trends over time we observe. If we were to correct it using only samples from within their own era we would be inflating differences between the different era's. Whereas only using shared variants would increase the noise for older samples due to higher error rates associated with DNA degradation.

Moreover, some data pairings in the data set are not complete or had varying time points .

The stimulation periods were chosen based on extensive studies that showed that the timepoints used were best suited for assessing monocyte-derived and lymphocyte-derived cytokines per stimulus. Not all the stimuli induce the production of all cytokines, so the selection of the cytokine-stimulus pairs was performed for those pairs in which a cytokine production could be measured (PMID: 1385767; PMID: 19380112; PMID: 27814509; PMID: 27814508; PMID: 27814507). The differences in the cytokine availability and time points are adjusted to the optimal time of production per stimuli. Monocyte-derived cytokines (IL-1b, IL-6 and TNFa) are early response cytokines, produced by innate immune cells shortly after stimulation. IFNg, IL-17 and IL-22 are lymphocyte-derived cytokines, produced by adaptive immune cells, in this case T helper cells. These cells need to differentiate for several days before they start to produce these cytokines, this is the reason why the time point of the measurements of these cytokines is 7 days. In the case of IFNg, it can also be produced by NK cells, so it was measured after 48h after stimulation in whole blood samples. We have included these considerations in the new version of the text (lines 82 to 87).

Similarly, a split was done to look at before and after the Neolithic era and the linear regression correspond to those two eras. However, the authors do not comment or show the data to demonstrate why they choose that specific breakpoint as opposed to looking at every historical era transition, i.e., from early upper paleolithic to late upper paleolithic to Mesolithic to Neolithic to post-Neolithic to modern.

We thank the reviewer for this remark and acknowledge that we do not address the rationale behind our choice to look at this split specifically sufficiently. We hypothesized that the start of the Neolithic with its increase in population density and contact with animals would also be a turning point for many immune responses and immune related traits. We added various analyses to better highlight this and also show differences between different adjacent time periods.

-The original figures showed only models using two separate linear regression lines and the different thresholds for missing genotype rates showed consistent results. In the new figures we depict LOESS regression models to better show the difference in mean PRS at every point in time and we additionally show boxplots with the different major age periods pooling the paleolithic and mesolithic samples together as pre-neolithic samples in order to account for the lower sample number in the earlier historical periods. To highlight this we have added a new section in lines 123 to 129 and new versions of the figures 1, 2, 3 and 4.

-In the new figure 2 we add LOESS regression models for which we do not bias our analysis into defining a break at a certain time period. We furthermore show boxplots with pairwise comparisons (student’s T-test) for broader time periods highlighting the changes in PRS that would correspond with major changes in human lifestyle such as the shift from a hunter-gatherer to a neolithic lifestyle or the rapid urbanization of human society.

-In the new Figure 3 we confirm that the various traits showing a clear change in PRS start at the advent of the Neolithic or post-Neolithic era using both the LOESS regression and pairwise comparisons (student T-test).

-Similarly the heatmap in our original figure 4 has also been revised to only show the large sample set.

Lastly, the authors should highlight additional limitations of this current study in terms of the generalizability to other populations or to clearly state that this is limited to the European population at the specified latitude and longitudes used.

We thank the reviewer for his feedback and agree we should put more emphasis on this. In our study we focus on summary statistics obtained from European populations and only employ European aDNA samples, so our results should not be extrapolated to other populations from other geographical areas. We have included this in the Discussion of the new version of the manuscript (lines 289 to 292). However, our findings are mostly in agreement with previous studies in other populations, which adds robustness to the results of our study.

Reviewer #2 (Public Review):

In "Evolution of cytokine production capacity in ancient and modern European populations", Dominguez-Andrés et al. collect a large amount of trait association data from various studies on immune-mediated disorders and cytokine production, and use this data to create polygenic scores in ancient genomes. They then use the scores to attempt to test whether the Neolithic transition was characterized by strong changes in the adaptive response to pathogens. The impact of pathogens in human prehistory and the evolutionary response to them is an intriguing line of inquiry that is now beginning to be approachable with the rapidly increasing availability of ancient genomes.

While the study shows a commendable collection of association data, great expertise in immune biology and an interesting study question, the manuscript suffers from severe statistical issues, which makes me doubt the validity and robustness of their conclusions. I list my concerns below, in rough order of how important I believe they are to the claims of the paper:

—In addition to the magnitude of an effect away from the null, P-values are a function of the amount of data one has to fit a model or test a hypothesis. In this case, the authors have vastly more data after the Neolithic Revolution than before, and so have much higher power to reject the null hypothesis of "no relationship to time" after the revolution than before. One can see this in the plots the authors provided, which show vastly more data after the Neolithic, and consequently a greater ability to fit a significant linear model (in any direction) afterwards as well.

We thank the reviewer for raising this very important point. In order to account for this difference in sample size for the different historical periods we pooled all samples prior to the neolithic era together to test for differences in mean PRS between neighbouring historical periods. This way we lose some strength in terms of the carbon-dated age of each sample but we gain the ability to compare more different pairings than just pre- and post-neolithic samples. We added various analyses to better highlight this and also show differences between different adjacent time periods:

-The original figures showed only models using two separate linear regression lines and the different thresholds for missing genotype rates showed consistent results. In the new figures we depict LOESS regression models to better show the difference in mean PRS at every point in time and we additionally show boxplots with the different major age periods pooling the paleolithic and mesolithic samples together as pre-neolithic samples in order to account for the lower sample number in the earlier historical periods. To highlight this we have added a new section in lines 123 to 129 and new versions of the Figures 1, 2, 3 and 4.

-In the new figure 2 we add LOESS regression models for which we do not bias our analysis into defining a break at a certain time period. We furthermore show boxplots with pairwise comparisons (student’s T-test) for broader time periods highlighting the changes in PRS that would correspond with major changes in human lifestyle such as the shift from a hunter-gatherer to a neolithic lifestyle or the rapid urbanization of human society.

-In the new figure 3 we confirm that the various traits showing a clear change in PRS start at the advent of the Neolithic or post-Neolithic era using both the LOESS regression and pairwise comparisons (student T-test).

-Similarly the heatmap in our original figure 4 has also been revised to only show the large sample set.

—The authors argue that Figure S2 makes their results robust to sample size differences, but showing a consistency in direction before and after downsampling in the post-neolithic samples is not enough, because:

1) you still lack power to detect changes in direction before the Neolithic.

2) even for the post-Neolithic, the relationship may be in the same direction but no longer significant after downsampling. How much the significance of the linear model fit is affected by the downsampling is not shown.

We thank the reviewer for pointing this out. The low sample count dating back to before the Neolithic era makes it indeed hard to accurately detect changes in PRS significantly correlated with time. Instead, we now aim to pool these samples together and compare the distribution of their PRS with those of Neolithic samples to better be able to detect significant differences in PRS between these historical time periods.

In order to show the significance of each linear model as well we now show the -Log10 of the P value multiplied by the sign of the correlation coefficient. This way we can better highlight the consistency in direction as well as significance and show that downsampling affects the order of significance. Please see the new Figure 4-figure supplement 1. We have also discussed this more in depth on lines 267-272 of the new version of the text.

—The authors chose to test "relationship between PRS with time" before and after the Neolithic as a way to demonstrate that "the advent of the Neolithic was a turning point for immune-mediated traits in Europeans". A more appropriate way to test this would be creating a model that incorporates both sets of scores together, accounts for both sample size and genetic drift in the change of polygenic scores, and shows a significant shift occurs particularly in the Neolithic, rather in any other time period, instead of choosing the Neolithic as an "a priori" partition of the data. My guess is that one could have partitioned the data into pre- and post-Mesolithic and gotten similar results, largely due to imbalances in data availability.

We agree with the reviewer that the exact pairing of the groups might influence the conclusions, showing the importance of remaining unbiased in our a priori partitioning of the data like the reviewer accurately pointed out. We aim to account for sample imbalances by pooling the paleolithic and mesolithic samples together and instead of just testing pre- versus post- Neolithic samples we perform a pairwise comparison between neighbouring historical periods using a T test thereby taking into account the sample size of each group.

—The authors only talk about partitions before and after the Neolithic, but plots are colored by multiple other periods. Why is the pre- and post-Neolithic the only transition that is mentioned?

Our initial hypothesis was that the pre-versus post-Neolithic shift was a turning point for immune responses. However, based on the suggestions of the reviewers, we have decided to perform the analysis in a more unbiased way, so we show the comparison of different individual era's. The new analyses and the new Figures provided address these issues.

—Extrapolating polygenic scores to the distant past is especially problematic given recent findings about the poor portability of scores across populations (Martin et al. 2017, 2019) and the sensitivity of tests of polygenic adaptation to the choice of GWAS reference used to derive effect size estimates (Berg et al. 2019, Sohail et al. 2019). In addition to being more heavily under-represented, paleolithic hunter-gatherers are the most differentiated populations in the time series relative to the GWAS reference data, and so presumably they are also the genomes for which PGS estimates built using such a reference would have higher error (see, e.g. Rosenberg et al. 2019). Some analyses showing how believable these scores are is warranted (perhaps by comparing to phenotypes in distant present-day populations with equivalent amounts of differentiation to the GWAS panel).

A similar study regarding standing height in ancient populations (PMID: 31594846) validated this approach when comparing polygenic scores based on modern populations with skeletal remains from ancient individuals. We do acknowledge the absolute results of the polygenic scores are less accurate for aDNA samples compared to a modern European cohort. The effect size estimates gained using a modern cohort are less accurate for aDNA samples than unrelated modern samples, and this is certainly an unavoidable limitation of the study.This is the reason why we focus on the direction of change of the trends and not on the absolute polygenic scores since such subtle differences do not affect the conclusions of our study.

—In multiple parts of the paper, the authors mention "adaptation" as equivalent to the patterns they claim to have found, but alternative hypotheses like genetic drift are not tested (see e.g. Guo et al. 2018 for a review of methods that could be used for this).

We thank the reviewer for this feedback. Based on this, we have added an Fst based test for selection to determine whether the changes we see in PRS over time are due to selection or due to genetic drift. This test shows that changes between the pre-Neolithic to Neolithic are not significantly different from drift whereas after the onset of the Neolithic we do see significant amount of selection. We have explained this further in the manuscript on lines 130-135 and included the new Table S2.

New Table S2 : Tests for selection as opposed to genetic drift were performed between populations from adjacent time periods. A two tailed test was used to determine whether mean trait Fst between pre-Neolithic - Neolithic, Neolithic - post-Neolithic, and post-Neolithic - Modern samples was significantly different compared to 10000 random LD and MAF matched mean Fst’s calculated using a same amount of SNP’s.

—250 kb window is too short a physical distance for ensuring associated loci that are included in the score are not in LD, and much shorter than standard approaches for building polygenic scores in a population genomic context (e.g. see Berg et al. 2019, Berisa et al. 2016). Is this a robust correction for LD?

We thank the reviewer for this remark, we tested multiple thresholds for window sizes, increasing the window size from 250 kb to 500 kb and 1000 kb (please see below new Figure 1-figure supplement 2) Although the level of significance changes for a few traits, the direction of the change remains stable across the three thresholds, demonstrating the robustness of our results. We have chosen this approach because the aDNA samples present a too high error rate and contain a relatively high amount of missing data to accurately determine LD, and determining LD using a modern reference cohort would bias our analysis by assuming the aDNA samples have a similar LD structure as modern samples.

New Figure 1-figure supplement 2: PRS correlation pre- and post-Neolithic revolution using polygenic scores calculated at varying window sizes.

We have edited the manuscript accordingly to show the consistency between these varying window sizes on lines 111-113.

—If one substitutes dosage with the average genotyped dosage for a variant from the entire dataset, then one is biasing towards the partitions of the dataset that are over-represented, in this case, post-Neolithic samples.

We fully agree with the reviewer, however the substitution of missing dosages with average dosages prevents the introduction of the bias in our models caused by varying amounts of missing SNPs in the older samples. Although our average scores on an absolute level are largely influenced by the more abundant post-Neolithic samples, this reduces the odds of wrongfully observing significant trends caused by the sparsity of the data. While the absolute scores might be biased towards a certain value, the differences and thus the direction of the change in PRS is affected by the non-missing variants in each sample.

—It seems from Figure 2, that some scores are indeed very sensitive to the choice of P-value cutoff (e.g., Malaria, Tuberculosis) and to the amount of missing data (e.g. HIV). This should be highlighted in the main text.

The reviewer is right, and this is largely due to the fewer number of SNPs that are included in the model at stricter p-value cutoffs, which is in part a limitation of the available GWAS summary statistics. Using fewer SNPs in our PRS calculations reduces the variability between different samples which weakens our ability to accurately model changes in these specific complex traits and detect statistical significance. We have highlighted this in the main text on lines 193-196.

—Some of the score distributions look a bit strange, like the Tuberculosis ones in Figure 2, which appear concentrated into particular values. Could this be because some of the scores are made with very few component SNPs?

We thank the reviewer for pointing this out and this is indeed correct. At stricter thresholds fewer significant QTLs will be included in the polygenic score model. We chose to still show these plots to point out those results might more easily differ if more variants could be included. At more lenient thresholds more variants can be included increasing the power of the model but the score might be less informative for the trait that way.

Author Response

Reviewer #3 (Public Review):

Myelodysplastic syndrome (MDS) is a heterogenous, clonal hematopoietic stem cell disorder characterized by morphological dysplasia in one or more hematopoietic lineages, cytopenias (most frequently anemia), and ineffective hematopoiesis. In patients with MDS, transfusion therapy treatment causes clinical iron overload; however it has been unclear if treatment with iron chelation yields clinical benefits. In the present study, the authors use a transgenic mouse model of MDS, NUP98-HOXD13 (referred to here as "MDS mice") to investigate this area. Starting at 5 months of age (before MDS mice progress to acute leukemia), the authors administered DFP in the drinking water for 4 weeks, and compared parameters to untreated MDS mice and WT controls.

The authors first show that MDS mice exhibit systemic iron overload and macrocytic anemia that is improved by treatment with the iron chelator deferiprone (DFP). They then perform a detailed characterization the effects of DFP treatment on erythroid differentiation and various parameters related to iron transport and trafficking in MDS erythroblasts. Strengths of the work are the use of a well-characterized mouse model of MDS with appropriate animal group sizes and detailed analyses of systemic iron parameters and erythroid subpopulations. A remediable weakness is that in certain areas of the Results and Discussion, the authors overinterpret their findings by inferring causation when they have only shown a correlation. Additionally, when drawing conclusions based on changes in erythroblast mRNA expression levels between groups, the authors should consider that translation efficiency may be altered in MDS and that the NUP98 fusion protein itself, by acting as a chimeric transcription factor, may also impact gene expression profiles. Given that the application of chelators for treatment of MDS remains controversial, this work will be of interest to scientists focused on erythroid maturation and iron dysregulation in MDS, as well as clinicians caring for patients with this disorder.

Major Comments

1) The authors define the stages of erythroblast differentiation using the CD44-FSC method, which assumes that CD44 expression levels during the stages of erythroid differentiation are not altered by MDS itself. Are morphologically abnormal erythroblasts, such as bi-nucleate forms, captured in this analysis, and if so, are they classified in the appropriate subset? The percentage of erythroblasts in the bone marrow of MDS mice in this current study is lower than that reported by Suragani et al (Nat Med 2014), who employed a different strategy to define erythroid precursors. While representative erythroblast gating is presented as Supplemental Figure 17, it would be important to present representative gating from all 3 animal groups: WT, MDS, and MDS+DFP mice.

We appreciate this comment and have added representative gating for all 3 groups to Supplemental Figure 17 (new Figure 3 – figure supplement 6 in the revised manuscript).

2) Methods, "Statistical analysis." The authors state that all comparisons were done with 2-tailed student paired t test, which would not be appropriate for comparisons being made between independent animals groups (i.e. when groups are not "paired").

We appreciate this comment and have reanalyzed all revised mouse data using one-way ANOVA with multiple comparisons and Tukey post-test analyses when more than 2 groups were compared. This has been edited in the Methods section in the revised manuscript.

3) The Results (p.7) indicates that both sexes showed similar responses to DFP; however, the figure legends do not indicate sex. Given that systemic iron metabolism in mice shows sex-related differences, sex should be specified.

We appreciate this comment and present here the gender-specific data for the reviewers’ evaluation (Author respone image 1). Similarly elevated transferrin saturation (a) (n = 3-4 male mice/group and n = 4-6 female mice/group) and hemoglobin (b) (n = 4-6 male mice/group and n = 4-9 female mice/group) are observed in male and female DFP-treated MDS mice. (c) Bone marrow erythroblasts are decreased to a greater degree in male relative to female DFP-treated MDS mice (n = 4-7 male mice/group and n = 8-9 female mice/group). We have added the data on gender-specific measures to new Figure 1 - figure supplement 3, Figure 2 – figure supplement 1, and Figure 3 – figure supplement 1 in the revised manuscript.

Author respone image 1.

Author Response

Reviewer #1 (Public Review):

The manuscript by Xu et. al. does a very thorough characterization and molecular dissection of the role of SSH2 in spermatogenesis. Loss of SSh2 in germ cells results in germ cell arrest In step2-3 spermatids and eventually leads to germ cell loss by apoptosis. Molecular characterization of the mutant mice shows that the loss of SSH2 prevents the fusion of proacrosomal vesicles leading to the formation of a fragmented acrosome. The fragmentation of the acrosome is due to the impaired actin bundling and dephosphorylation of COFILIN. In short, this is a comprehensive body of work.

We thank the referee for these insightful comments.

Reviewer #2 (Public Review):

The acrosome is a unique sperm-specific subcellular organelle required for the fertilization process, and it is also an organelle undergoing extensive morphological and structural transformation during sperm development. The mechanism underlying the extensive acrosome morphogenesis and biogenesis remains incompletely understood. Xu et al in their manuscript entitled "The Slingshot phosphatase 2 is required for acrosome biogenesis during spermatogenesis in mice" reported that the Slingshot Phosphatase 2 is essential for acrosome biogenesis and male fertility through their characterization of spermatogenic and acrosomal defects in Ssh2 knockout mice they generated. Specifically, the authors provided molecular, genetic, and subcellular evidence supporting that Ssh2 mutation impaired the phosphorylation of an acting-binding protein, COFILIN during spermiogenesis and accordingly actin cytoskeleton remodeling, crucial for proacrosomal vesicle trafficking and acrosome biogenesis. The manuscript by Xu et. al. does a very thorough characterization and molecular dissection of the role of SSH2 in spermatogenesis. Loss of SSh2 in germ cells results in germ cell arrest In step2-3 spermatids and eventually leads to germ cell loss by apoptosis. Molecular characterization of the mutant mice shows that the loss of SSH2 prevents the fusion of proacrosomal vesicles leading to the formation of a fragmented acrosome. The fragmentation of the acrosome is due to the impaired actin bundling and dephosphorylation of COFILIN. In short, this is a comprehensive body of work.

We appreciate and thank Referee #2 for the positive feedback and insightful comments.

Strengths:

Nicely written manuscript, addresses an important mechanistic question of the roles of cytoskeleton remodeling in acrosome biogenesis and provided genetic, subcellular, and molecular evidence to build up their support for their hypothesis that Ssh2 regulates actin cytoskeleton remodeling, a process essential for proacrosomal vesicle trafficking and acrosome biogenesis, through dephosphorylation actin-binding protein during spermiogenesis.

We again thank to the Referee #2 for appreciating and encouraging us regarding our current research work.

Weaknesses:

For body weight, and testis weight of the mutants, the authors concluded that there is no significant difference between the mutant and wildtype (Fig 1E -1G), but they appear to use mice between 6-8 wk old, both the testis and body weight of males at 6-8 wks is still growing, with the number of mice analyzed being six, you could easily miss the significant difference of the testis size and or body weight with such a varied age and a small sample size.

We thank the referee for their prompting of this important discussion point, which we now cover in our revised manuscript. In our originally submitted manuscript, we only presented the data for body weight, testis weight, and T/B ratio for mice between the age of 6–8 weeks, however, we have added the additional data of mice with age more than 8 weeks in the revised manuscript in a new Figure 1E-1G with the sample size of 12 for each genotype. We have also updated the relevant content in the figure caption. The revised figure caption for Figure 1 panels E–G reads as follows: “(E-G) Body weights (26.3609 ± 0.4914 for WT; 25.1741 ± 0.5189 for Ssh2 KO), weights of the testes (0.0862 ± 0.0036 for WT; 0.0788 ± 0.0023 for Ssh2 KO), and the testis-to-body weight ratio (0.3281 ± 0.0153 for WT; 0.3154 ± 0.0135 for Ssh2 KO) of adult WT and Ssh2 KO males (n = 12). Data are presented as the mean ± SEM; p > 0.05 calculated by Student’s t-test. Bars indicate the range of the data.”

Other points:

Comments: 1) Could the uniform cytoplasmic distribution of diminutive actin filaments in the wild type and disrupted actin filament remodeling be examined at the EM level on the round spermatids?

We apologize for the confusion. Previously, we conducted a transmission electron microscopy (TEM) analysis on the testes samples to discover the distribution and ultrastructural organization of F-actin in WT and Ssh2 KO round spermatids. Unfortunately, even at high magnification (30,000x, right panel of Figure R1-Response Figure 1) by TEM of testicular section no diminutive actin filament was observed in the cytoplasm of round spermatids except for the acroplaxome-an actin-rich specialized structure anchors the acrosome-in WT spermatids as well as some thick bundle-like structures located at the acrosomal region of Ssh2 KO spermatids (Fig. R1). According to their unique characteristic of appearance, we interpreted these electron-dense bundles as the aberrantly aggregated actin filaments whose lengths are in accordance with the lengths of COFILIN-saturated F-actin fragments (Bamburg et al., 2021), suggesting the disrupted actin filament remodeling during acrosome biogenesis resulted from Ssh2 KO. However, due to the technological limitations of TEM and the complexity of intracellular environment of round spermatids, we only recognized few aggregated actin bundles with the loss of filamentous appearance in Ssh2 KO spermatids and no typical diminutive actin filament was detected which had been imaged under high-resolution cryo-TEM (Haviv et al., 2008) or live-cell total internal reflection fluorescence microscopy (Johnson et al., 2015) on the purified actin bundles and cultured cells. Given the lack of effective approaches to culture murine round spermatids in vitro, confocal microscopy of flourescence-labelled F-actin (e.g., IF staining by FITC-phalloidin) is a more accessible method for visualizing the disruption of actin remodeling than EM in murine spermatids as the actin-related findings that several other studies demonstrated (Djuzenova et al., 2015; Meenderink et al., 2019).

Comments: 2) Any other defects are seen besides acrosome in the mutant testis given the important roles of actin cytoskeleton network and high expression of Ssh2 in spermatocytes, were chromatoid bodies or mitochondria affected in any way? Any other defects in the mice overall including female fertility and other organs, given the previously reported roles in the nervous system. It could be helpful information for others interested in Ssh 2 protein and actin cytoskeleton's roles in general.

The referee has here raised an interesting point. Firstly, besides the acrosome-related defects in Ssh2 KO spermatids, we identified increased germ cell apoptosis and aberrant activation of apoptotic Bcl-2/Caspase-3 pathway in the testes of Ssh2 KO mice which were speculated to be triggered by the disordered COFILIN-mediated F-actin remodeling and have attracted our attention to further elucidate the underlying mechanisms in the future. Secondly, given the high expression of SSH2 in spermatocytes demonstrated by IF staining shown in figure 4B and 4C,we thus performed the surface chromosome spreading on spermatocytes to observe whether the morphology of chromatid bodies and the meiotic progression was affected by Ssh2 KO and no obvious defects were observed as shown in supplementary Figure S3 in originally submitted manuscript. Thirdly, no obvious morphological abnormality in chromatin or mitochondrial structure was detected in Ssh2 KO germ cells such as spermatocytes and round spermatids under TEM which prevents us to pursue it further. Fourthly, we have observed the potential effect(s) of Ssh2 KO on female fertility using Ssh2 KO female mice and did not find any obvious infertility defect in Ssh2 KO females compared to their WT littermates as demonstrated by the data of the body weight, ovary weight, ovary-to-body weight ratio, size of ovaries and fertility test as well as the images of ovarian HE staining (Fig. R1). Moreover, given that during our investigation period, Ssh2 KO males and females did not manifest any defective physical development, aberrant physiological status or mental disorder notwithstanding the roles of SSH2 in neurite extension had been reported (Endo, Ohashi, & Mizuno, 2007), we did not conduct the experiments to observe the effect(s) of SSH2 in other organs except for the female fertility.

Fig. R1 No reproductive defects were found in Ssh2 KO females. (A-C) Body weights, weights of the ovaries, and the ovary-to-body weight ratio of adult WT and Ssh2 KO females aged 8-10 weeks (n = 5); p > 0.05 calculated by Student’s t-test. Bars indicate the range of data. (D) The size of ovaries from Ssh2 KO were indistinguishable from ovaries of WT mice age 8 weeks, n = 4. (E) Histology of the ovaries from WT and Ssh2 KO mice. Sections were stained with hematoxylin and eosin. Scale bars: 200 μm. Images are representative of ovaries extracted from 8-week-old adult female mice per genotype. (F) Number of pups per litter from WT and Ssh2 KO male mice (8 weeks old) after crossing with WT adult male mice (n =3); p > 0.05 calculated by Student’s t-test. Bars indicate the range of the data.

Comments: 3) Providing detailed information on the number of animals used and cells analyzed in the legend is nice, but it might be even better for the readers to include sample size and the number of cells examined in the figure/graph if possible.

We appreciate the suggestions from the reviewer. We have integrated some information of sample size in the figures where appropriate. Firstly, we integrated sample size in the figure 1C, 1E, 1F, 1G and 1I. Secondly, we included sample size and the number of seminiferous tubule/epididymal duct we evaluated for TUNEL (+) cell counting in figure 2C and figure 2D. Thirdly, we included sample size and the number of spermatids for co-localization in figure 6B and figure 6D.

Comments: 4) Nice discussion and comparison with GOPC and GM130, how about comparison and discussion with other acrosome defective mutants like PICK1, and ATG to provide some insights into acrosome biogenesis and proacrosomal vesicle trafficking?

We greatly appreciate the referee for positive appraisal of our work with constructive suggestions, unfortunately, we are unable to address these defective mutants with certainty due to the lack of proper sample accessibility (only 3 of 16-month-old Ssh2 KO mice are accessible now). We compared the cytological staining of GM130 and GOPC in WT and Ssh2 KO spermatids using tubule squash sections as the description in the originally submitted manuscript which are prepared from fresh testes originated from 8-week-old mice and we now have several aged Ssh2 KO mice which prevent us to achieve the staining of PICK1 and ATG. PICK1 was previously reported to facilitate vesicle trafficking from the Golgi apparatus to the acrosome which co-localizes with GOPC in the proacrosomal granules (Xiao et al., 2009) and the phenotypes of Pick1 KO mice share a lot of similar characteristics with that of Ssh2 KO mice such as the fragmentation of the acrosome and increased germ cell apoptosis. Both autophagy-related ATG5 (Huang et al., 2021) and ATG7 (Wang et al., 2014) were reported to participate in the process of acrosome biogenesis and ATG7 is required for proacrosomal vesicle transportation/fusion by conjugating LC3 to the membrane of proacrosomal vesicles. Although the spermatids evaluated in these KO mice models could still be developed into spermatozoa with defective acrosome that is different from the situation in Ssh2 KO mice, it would be meaningful to discover the affects by Ssh2 KO on the localization of these regulators of acrosome biogenesis in spermatids and their potential interactions with SSH2. Indeed, in future work, we plan to pursue these issues and the content related to PICK1 has been added to the discussion in the revised manuscript as follows: “Moreover, it is intriguing to note that the phenotypes of Ssh2 KO mice share a lot of similarities with that of Pick1 KO model (Xiao et al., 2009) such as acrosome fragmentation and enhanced germ cell apoptosis, suggesting the possibility that SSH2 and PICK1 work together in a same trafficking machinery functioning in acrosome biogenesis which needs to be clarified further.”

Comments: 5) Given the literature on Cofilin's requirement for male fertility and the increased p-Cofilin in Ssh2 mutant testis by Western and IF, the authors have a strong case for their hypothesis. But given the general role of phosphatase, it might be prudent to discuss alternative possibilities.

We thank the reviewer for these valuable suggestions. Given that p-COFILIN is the only known substrate of SSH2 based on previous reports, we focused principally on this cascade to conduct our investigation. As a phosphatase, SSH2 is very likely to interact with many other proteins functioning in various cellular processes other than the actin-binding proteins which remain elusive. As directed, we now have added some content related to the regarding above concern in the discussion section of the revised manuscript as follows: “Given the diverse physiological roles reported for Slingshot family proteins, the possibility of the alternative mechanism underlying involvement of SSH2 in cellular events beyond the COFILIN-mediated actin remodeling should be noted. According to some publicly accessible databases as the indicators of potential protein–protein interactions such as BioGRID (Oughtred et al., 2019) and IntAct (Del Toro et al., 2022), SSH2 might interact with a set of actin-based molecular motors covering MYH9, MYO19 and MYO18A, which have been implicated in the maintenance of Golgi morphology and Golgi anterograde vesicular trafficking via the PI4P/GOLPH3/MYO18A/F-actin pathway (Rahajeng et al., 2019).”

Author Response

Reviewer #2 (Public Review):

Zylbertal and Bianco propose a new model of trial-to-trial neuronal variability that incorporates the spatial distance between neurons. The 7-parameter model is attractive because of its simplicity: A neuron's activity is a function of stimulus drive, neighboring neurons, and global inhibition. A neuroscientist studying almost any brain area in any model organism could make use of this model, provided that they have access to 1) simultaneously-recorded neurons and 2) the spatial locations of those neurons. I could foresee this model being the de-facto model to compare to all future models, as it is easy to code up and interpret. The paper explores the effectiveness of this distance model by modeling neural activity in the zebrafish optic tectum. They find that this distance-based model can capture 1) bursting found in spontaneous activity, 2) ongoing co-fluctuations during stimulus-evoked activity, and 3) adaptation effects during prey-catching behavior.

Strengths:

The main strength of the paper is the interpretability of the distance-based model. This model is agnostic to the brain area from which the population of neurons is recorded, making the model broadly applicable to many neuroscientists. I would certainly use this model for any baseline comparisons of trial-to-trial variability.

The model is assessed in three different contexts, including spontaneous activity and behavior. That the model provides some prediction in all three contexts is a strong indicator that this model will be useful in other contexts, including other model organisms. The model could reasonably be extended to other cognitive states (e.g., spatial attention) or accounting for other neuron properties (such as feature tuning, as mentioned in the manuscript).

The analyses and intuition to show how the distance-based model explains adaptation were insightful and concise.

We thank the reviewer for these supportive comments.

Weaknesses:

Model evaluation and comparison: The paper does not fully evaluate the model or its assumptions; here, I note details in which evaluation is needed. A key assumption of the model - that correlations fall off in a gaussian manner (Fig. 1C-E - is not supported by Fig. 1C, which appears to have an exponential fall-off. Functions other than gaussian may provide better fits.

A key feature of our model is that connection strengths smoothly decrease with distance. However, we did not intend to make strong claims about the exact function parametrizing this distance relationship. In light of the reviewer’s comment, we have additionally tested an exponential function and find that it too can describe activity correlations in OT with a negligible decrease in r2 (Figure 1 – figure supplement 1A-C). The main purpose of the analysis was to show that the correlation is maximal around the seed and decays uniformly with distance from it (i.e. no sub-networks or cliques are detected). We have emphasized this in a revised conclusion paragraph and note that while multiple functions can be used to parameterize the relationship, they are nonetheless certainly simplifications. Secondly, we also ran a version of the network simulation where the connections decay in space according to an exponential rather than Gaussian function and show that, as expected, tectal bursting is robust to this change.

Furthermore, it is not clear whether the r^2s in Fig. 1E are computed in a held-out manner (more details about what goes into computing r^2 are needed).

These values are computed by fitting the 2-d Gaussian (or exponential function) to all neurons excluding the seed itself (added a short clarification in the Methods).

Assessing the model based on peak location alone (Fig. 1E) is not sufficient, as other smooth monotonically-decreasing functions may perform similarly.

As discussed above, an exponential function indeed performs similarly to a Gaussian. However, goodness of fit is secondary to the main aim of Fig 1E, which is to show that the correlation peak tends to fall near the seed cell.

Simulating from the model greatly improves the reader's understanding (Fig. 2D), but no explanation is given for why the simulations (Fig. 2D) have almost no background spikes and much fewer, non-co-occurring bursts than those of real data (Fig. 2E).

In part this is because the simulation results depicted in Fig 2D were derived from the ‘baseline model’, prior to optimizing to match biological bursting statistics. It is thus expected that activity will differ from experimental observation and was our main motive to tune the model parameters (now emphasized in the text). However, the model will certainly not account for all aspects of tectal activity; rather, it was designed to reproduce bursting as a prominent feature of ongoing activity and in the second part of the paper we explore the extent to which it can account for other phenomena. As noted above, in the revised abstract, introduction and discussion we have tried to clarify the motivation for developing the model and how it was used to gain insight into activity-dependent changes in network excitability.

A key assumption of the distance model (Fig. 2A) is that each neuron has the same gaussian fall-off (i.e., sigma_excitation and sigma_inhibition), but it is unclear if the data support this assumption.

We intentionally opted for a simple model (i.e. described by few parameters), in part due to the lack of connectivity data and additionally to set a lower bound on the extent to which multiple features of tectal activity could be accounted for. More complex models with additional degrees of freedom (such as cell-specific connectivity) may well describe the data better, but likely at the cost of interpretability. We consider such extensions are beyond the scope of the present study but might be fruitful avenues for future research.

Although an excitatory and inhibitory gain is assumed (Fig. 2A), it is not clear from the data (Fig. 1C) that an inhibitory gain is needed (no negative correlations are observed in Fig. 1C-D).

This is now explored in the revised Figure 3A which includes the condition of zero inhibition gain. See also response to reviewer 1.

After optimization (Fig. 3), the model is evaluated on predicting burst properties but not evaluated on predicting held-out responses (R^2s or likelihoods), and no other model (e.g., fitting a GLM or a model with only an excitatory gain) is considered. In particular, one may consider a model in which "assemblies" do exist - does such an assembly model lead to better held-out prediction performance?

The model we developed is a mechanistic, generative model. In contrast to Pillow et al 2008, we did not fit the model to data but rather we used it to simulate network activity and tuned the seven parameters (using EMOO) to best match biological observations. Thus, rather than assessing goodness-of-fit using cross-validation, our approach involved comparison of summary statistics related to the target emergent phenomenon (tectal bursting). This was necessary as bursting appears highly stochastic. Further to the comments above, we have expanded the parameter space to include instances with only an excitatory gain (where bursting failed) and no distance-dependence (again, busting failed). Introducing assemblies into the model will inevitably support bursting (and introduce many more free parameters), but one of our key observations is that such assemblies are not required for this aspect of spontaneous activity. Again, our aim was not to produce a detailed picture of tectal connectivity, but rather to develop a minimal model and estimate the extent to which it can account for observed features of activity. Note that the second half of the paper (Figure 4 onwards) shows the model can explain phenomena that were not considered during parameter tuning.

It is unclear why a genetic algorithm (Fig. 1A-C) is necessary versus a grid search; it appears that solutions in Generation 2 (Fig. 3C, leftmost plot, points close to the origin) are as good as solutions in Generation 30 and that the spreads of points across generations do not shrink (as one would expect from better mutations). Given the small number of parameters (7), a grid search is reasonable, computationally tractable, and easier to understand for all readers (Fig. 3A).

Perhaps in hindsight a grid search would have worked, but at increased computational cost (each instantiation of the model is computationally expansive). At the time we chose EMOO, and since it produced satisfactory results, we kept it. As often happens with multi-objective optimization, an improvement in one objective usually happens at the expense of other objectives, so the spread of the points does not shrink much but they move closer to the axes (i.e. reduced error). The final parameter combination is closer to the origin than any point in generation 2, though admittedly not by much. Importantly, however, optimizing the model using the training features generalized to other burst-related statistics.

It is unclear why the excitatory and inhibitory gains of the temporal profiles (Fig. 3I) appear to be gaussian but are formulated as exponential (formula for I_ij^X in Methods).

The interactions indeed have exponential decay in time. These might appear Gaussian because the axis scale is logarithmic.

Overall, comparing this model to other possible (similar) models and reporting held-out prediction performance will support the claim that the distance model is a good explanation for trial-to-trial variability.

See comments above. A key point we want to stress is that we intentionally explored a minimal network model and found that, despite obvious simplifications of the biology, it was nonetheless able to explain multiple aspects of tectal physiology and behaviour. We hope that it inspires future studies and can be extended, in parallel to experimental findings, to more accurately represent the cell-type diversity and cell-specific connectivity of the tectal network.

Data results: Data results were clear and straightforward. However, the explanation was not given for certain results. For example, the relationship between pre-stimulus linear drive and delta R was weak; the examples in Fig. 4C do not appear to be representative of the other sessions. The example sessions in Fig. 4C have R^2=0.17 and 0.19, the two outliers in the R^2 histogram (Fig. 4D).

The revised figure 4 is based on new data and new analysis (see below), and the presented examples no longer represent the extreme tail of the distribution (they still, however, represent strong examples, as is now explicitly indicated in the figure legend).

The black trace in Fig. 4D has large variations (e.g., a linear drive of 25 and 30 have a change in delta R of ~0.1 - greater than the overall change of the dashed line at both ends, ~0.08) but the SEMs are very tight. This suggests that either this last fluctuation is real and a major effect of the data (although not present in Fig. 4C) or the SEM is not conservative enough. No null distribution or statistics were computed on the R^2 distribution (Fig. 4C, blue distribution) to confirm the R^2s are statistically significant and not due to random fluctuations.

We agree that this was not sufficiently robust and in response to this comment we undertook a significant revision to figure 4 and the associated text:

i) The revised figure is based on an entirely new dataset, allowing us to verify the results on independent data. We used 5 min ISI for all stimulus presentations, regardless of stimulus type (high or low elevation), thus ensuring that we are only examining differences in state brought about by previous ongoing activity, without risk of ‘contamination’ by evoked activity.

ii) As per the reviewer’s suggestion, we compared model-estimated pre-stimulus state to a null estimate using randomly sampled time-points. We additionally compared the optimised model with the baseline model. Whereas the null (random times) estimates had no predictive power, both models using pre-stimulus activity were able to explain a fraction of the response residuals with the optimised model performing better.

iii) We refined the binning process by first computing, for each response, the mean of response residuals across neurons for each bin of estimated linear drive, and then averaging across responses. This prevents the relationship being skewed by rare instances involving unusually large numbers of neurons for a particular linear drive bin, and thereby eliminates the fluctuations the reviewer was referring to.

The absence of any background activity in Fig. 6B (e.g., during the rest blocks) is confusing, given that in spontaneous activity many bursts and background activity are present (Fig. 2E).

The raster only presents evoked responses and no background activity is shown. This has been clarified in the revised figure and legend.

Finally, it appears that the anterior optic tectum contributes to convergent saccades (CS) (Fig. 7E) but no post-saccadic activity is shown to assess how activity changes after the saccade (e.g., plotting activity from 0 to 60).

Activity before and after the saccade is shown in Fig 7A. Fig 7E shows the ‘linear drive’ (or ‘excitability’), and how it changes leading up to the saccade. Since we were interested in the association between pre-saccade state and saccade-associated activity, we did not plot post-saccadic linear drive. However, as can be seen in the below figure for the reviewer, linear drive is strongly suppressed by the saccade, as expected due to CS-associated activity.

No explanation is given why activity drops ~30 seconds before a convergent saccade (Fig. 7E).

This is no longer shown after we trimmed the history data in Fig 7E in accordance with a comment from reviewer 1. We speculate, however, that the mean linear drive of a compact population of neurons would be somewhat periodical, since a high linear drive leads to a burst which results in a prolonged inhibition (low linear drive) with a slow recovery and so on.

No statistical test is performed on the R^2 distribution (Fig. 7H) to confirm the R^2s (with a mean close to R^2=0.01) are meaningful and not due to random fluctuations.

We revised the analysis in Fig 7 along the same lines as the revision of Fig 4. Model-estimated linear drive predicts CS-associated activity whereas a null estimate (random times) shows no such relationship.

Presentation: A disjointed part of the paper is that for the first part (Figs. 1-3), the focus is on capturing burst activity, but for the second part (Figs. 4-7), the focus is on trial-to-trial variability with no mention of bursts. It is unclear how the reader should relate the two and if bursts serve a purpose for stimulus-evoked activity.

In the first part of the paper (Figs. 1-3), we use ongoing activity to develop an understanding (formulated as a network model) of how activity modulates the network state. In the second part, we test this understanding in the context of evoked responses and show that model-estimated network state explains a fraction of visual response variability and experience-dependent changes in activity and behaviour. In the revised MS we further emphasize this idea and have edited the results text to strengthen the connections between these parts of the study. See also comments above.

Citations: The manuscript may cite other relevant studies in electrophysiology that have investigated noise correlations, such as:

• Luczak et al., Neuron 2009 (comparing spontaneous and evoked activity).

• Cohen and Kohn, Nat Neuro 2011 (review on noise correlations).

• Smith and Kohn, JNeurosci 2008 (looking at correlations over distance).

• Lin et al., Neuron 2015 (modeling shared variability).

• Goris et al., Nat Neuro 2014 (check out Fig. 4).

• Umakantha et al., Neuron 2021 (links noise correlation and dim reduction; includes other recent references to noise correlations).

We agree that the manuscript could benefit from citing some of these suggested studies and have added citations accordingly.

Author Response

Reviewer #1 (Public Review):

In this manuscript, the authors find CpGs within 500Kb of a gene that associate with transcript abundance (cis-eQTMs) in children from the HELIX study. There is much to admire about this work. With two notable exceptions, their work is solid and builds/improves on the work that came before it. Their catalogue of eQTMs could be useful to many other researchers that utilize methylation data from whole blood samples in children. Their annotation of eQTMs is well thought out and exhaustive. As this portion of the work is descriptive, most of their methods are appropriate.

Unfortunately, their use of results from a model that does not account for cell-type proportions across samples diminishes the utility and impact of their findings. I believe that their catalog of eQTMs contains a great deal of spurious results that primarily represent the differences in cell-type proportions across samples.

Lastly, the authors postulate that the eQTM gene associations found uniquely in their unadjusted model (in comparison to results from a model that does account for cell type proportion) represent cell-specific associations that are lost when a fully-adjusted model is assumed. To test this hypothesis, the authors appear to repurpose methods that were not intended for the purposes used in this manuscript. The manuscript lacks adequate statistical validation to support their repurposing of the method, as well as the methodological detail needed to peer review it. This section is a distraction from an otherwise worthy manuscript. But provide evidences that enriched for cell sp CpGs.

Major points

1. Line 414-475: In this section, the authors are suggesting that CpGs that are significant without adjusting for cell type are due to methylation-expression associations that are found only in one cell type, while association found in the fully adjusted model are associations that are shared across the cell types. I do not agree with this hypothesis, as I do not agree that the confounding that occurs when cell-type proportions are not accounted for would behave in this way. Although restricting their search for eQTMs to only those CpGs proximal to a gene will reduce the number of spurious associations, a great deal of the findings in the authors' unadjusted model likely reflect differences in cell-type proportions across samples alone. The Reinius manuscript, cited in this paper, indicates that geneproximal CpGs can have methylation patterns that vary across cell types.

Following reviewers’ recommendations, we have reconsidered our initial hypothesis about the role of cellular composition in the association between methylation and gene expression. Although we still think that some of the eQTMs only found in the model unadjusted for cellular composition could represent cell specific effects, we acknowledge that the majority might be confounded by the extensive gene expression and DNA methylation differences between cell types. Also, we recognize that more sophisticated statistical tests should be applied to prove our hypothesis. Because of this, we have decided to report the eQTMs of the model adjusted for cellular composition in the main manuscript and keep the results of the model unadjusted for cellular composition only in the online catalogue.

1. Line 476-488: Their evidence due to F-statistics is tenuous. The authors do not give enough methodological detail to explain how they're assessing their hypothesis in the results or methods (lines 932-946) sections. The methods they give are difficult to follow. The results in figure S19A are not compelling. The citation in the methods (by Reinius) do not make sense, because Reinius et al did not use F-statistics as a proxy for cell type specificity. The citation that the authors give for this method in the results does not appear to be appropriate for this analysis, either. Jaffe and Irizarry state that a CpG with a high Fstatistic indicates that the methylation at that CpG varies across cell type. They suggest removing these CpGs from significant results, or estimating and correcting for cell type proportions, as their presence would be evidence of statistical confounding. The authors of this manuscript indicate that they find higher F-statistics among the eQTMs uniquely found in the unadjusted model, which seems to only strengthen the idea that the unadjusted model is suffering from statistical confounding.

We recognize the miss-interpretation of the F-statistic in relation to cellular composition. We have deleted all this part from the updated version of the manuscript.

1. The methods used to generate adjusted p-values in this manuscript are not appropriate as they are written. Further, they are nothing like the methods used in the paper cited by the authors. The Bonder paper used permutations to estimate an empirical FDR and cites a publication by Westra et al for their method (below). The Westra paper is a better one to cite, because the methods are more clear. Neither the Bonder nor the Westra paper uses the BH procedure for FDR.

Westra, H.-J. et al. Systematic identification of trans eQTLs as putative drivers of known disease associations. Nat. Genet. 45, 1238-1243 (2013).

We apologize for this misleading citation. Although Bonder et al applied a permutation approach to adjust for multiple testing, our approach was inspired by the method applied in the GTEx project (GTEx consortium, 2020), using CpGs instead of SNPs. The citation has been corrected in the manuscript. Moreover, we have explained in more detail the whole multiple-testing processes in the Material and Methods section (page 14, line 316):

“To ensure that CpGs paired to a higher number of Genes do not have higher chances of being part of an eQTM, multiple-testing was controlled at the CpG level, following a procedure previously applied in the Genotype-Tissue Expression (GTEx) project (Gamazon et al., 2018). Briefly, our statistic used to test the hypothesis that a pair CpGGene is significantly associated is based on considering the lowest p-value observed for a given CpG and all its pairs Gene (e.g. those in the 1 Mb window centered at the TSS). As we do not know the distribution of this statistic under the null, we used a permutation test. We generated 100 permuted gene expression datasets and ran our previous linear regression models obtaining 100 permuted p-values for each CpG-Gene pair. Then, for each CpG, we selected among all CpG-Gene pairs the minimum p-value in each permutation and fitted a beta distribution that is the distribution we obtain when dealing with extreme values (e.g. minimum) (Dudbridge and Gusnanto, 2008). Next, for each CpG, we took the minimum p-value observed in the real data and used the beta distribution to compute the probability of observing a lower p-value. We defined this probability as the empirical p-value of the CpG. Then, we considered as significant those CpGs with empirical p-values to be significant at 5% false discovery rate using BenjaminiHochberg method. Finally, we applied a last step to identify all significant CpG-Gene pairs for all eCpGs. To do so, we defined a genome-wide empirical p-value threshold as the empirical p-value of the eCpG closest to the 5% false discovery rate threshold. We used this empirical p-value to calculate a nominal p-value threshold for each eCpG, based on the beta distribution obtained from the minimum permuted p-values. This nominal p-value threshold was defined as the value for which the inverse cumulative distribution of the beta distribution was equal to the empirical p-value. Then, for each eCpG, we considered as significant all eCpG-Gene variants with a p-value smaller than nominal p-value.”

References:<br /> GTEx consortium, The GTEx Consortium atlas of genetic regulatory effects across human tissues, Science (2020) Sep 11;369(6509):1318-1330. doi: 10.1126/science.aaz1776.

Reviewer #2 (Public Review):

Strength:

Comprehensive analysis Considering genetic factors such as meQTL and comparing results with adult data are interesting.

We thank the reviewer for his/her positive feedback on the manuscript. We agree that the analysis of genetic data and the comparison with eQTMs described in adults are two important points of the study.

Weakness:

• Manuscript is not summarized well. Please send less important findings to supplementary materials. The manuscript is not well written, which includes every little detail in the text, resulting in 86 pages of the manuscript.

Following reviewers’ comments, we have simplified the manuscript. Now only the eQTMs identified in the model adjusted for cellular composition are reported. In addition, functional enrichment analyses have been simplified without reporting all odds ratios (OR) and p-values, which can be seen in the Figures.

• Any possible reason that the eQTM methylation probes are enriched in weak transcription regions? This is surprising.

Bonder et al also found that blood eQTMs were slightly enriched for weak transcription regions (TxWk). Weak transcription regions are highly constitutive and found across many different cell types (Roadmap Epigenetics Consortium, 2015). However, hematopoietic stem cells and immune cells have lower representation of TxWk and other active states, which may be related to their capacity to generate sub-lineages and enter quiescence.

Given that we analyzed whole blood and that ROADMAP chromatin states are only available for blood specific cell types, each CpG in the array was annotated to one or several chromatin states by taking a state as present in that locus if it was described in at least 1 of the 27 bloodrelated cell types. By applying this strategy we may be “over-representing” TxWk chromatin states, in the case TxWk are cell-type specific. As a result, even if each blood cell type might have few TxWk, many positions can be TxWk in at least one cell type, inflating the CpGs considered as TxWk. This might have affected some of the enrichments.

On the other hand, CpG probe reliability depends on methylation levels and variance. TxWk regions show high methylation levels, which tend to be measured with more error. This also might have impacted the results, however the analysis considering only reliable probes (ICC >0.4) showed similar enrichment for TxWk.

Besides these, we do not have a clear answer for the question raised by the reviewer.

References:

Bonder MJ, Luijk R, Zhernakova D V, Moed M, Deelen P, Vermaat M, et al. Disease variants alter transcription factor levels and methylation of their binding sites. Nat Genet [Internet]. 2017 [cited 2017 Nov 2];49:131–8. Available from: http://www.ncbi.nlm.nih.gov/pubmed/27918535

Roadmap Epigenomics Consortium, Kundaje A, Meuleman W, Ernst J, Bilenky M, Yen A, Heravi-Moussavi A, Kheradpour P, Zhang Z, Wang J, Ziller MJ, Amin V, Whitaker JW, Schultz MD, Ward LD, Sarkar A, Quon G, Sandstrom RS, Eaton ML, Wu YC, Pfenning AR, Wang X, Claussnitzer M, Liu Y, Coarfa C, Harris RA, Shoresh N, Epstein CB, Gjoneska E, Leung D, Xie W, Hawkins RD, Lister R, Hong C, Gascard P, Mungall AJ, Moore R, Chuah E, Tam A, Canfield TK, Hansen RS, Kaul R, Sabo PJ, Bansal MS, Carles A, Dixon JR, Farh KH, Feizi S, Karlic R, Kim AR, Kulkarni A, Li D, Lowdon R, Elliott G, Mercer TR, Neph SJ, Onuchic V, Polak P, Rajagopal N, Ray P, Sallari RC, Siebenthall KT, Sinnott-Armstrong NA, Stevens M, Thurman RE, Wu J, Zhang B, Zhou X, Beaudet AE, Boyer LA, De Jager PL, Farnham PJ, Fisher SJ, Haussler D, Jones SJ, Li W, Marra MA, McManus MT, Sunyaev S, Thomson JA, Tlsty TD, Tsai LH, Wang W, Waterland RA, Zhang MQ, Chadwick LH, Bernstein BE, Costello JF, Ecker JR, Hirst M, Meissner A, Milosavljevic A, Ren B, Stamatoyannopoulos JA, Wang T, Kellis M. Integrative analysis of 111 reference human epigenomes. Nature. 2015 Feb 19;518(7539):317-30. doi: 10.1038/nature14248. PMID: 25693563; PMCID: PMC4530010.

• The result that the magnitude of the effect was independent of the distance between the CpG and the TC TSS is surprising. Could you draw a figure where x-axis is the distance between the CpG site and TC TSS and y-axis is p-value?

As suggested by the reviewer, we have taken a more detailed look at the relationship between the effect size and the distance between the CpG and the TC’s TSS. First, we confirmed that the relative orientation (upstream or downstream) did not affect the strength of the association (p-value=0.68). Second, we applied a linear regression between the absolute log2 fold change and the log10 of the distance (in absolute value), finding that they were inversely related. We have updated the manuscript with this information (page 22, line 504):

“We observed an inverse linear association between the eCpG-eGene’s TSS distance and the effect size (p-value = 7.75e-9, Figure 2B); while we did not observe significant differences in effect size due to the relative orientation of the eCpG (upstream or downstream) with respect to the eGene’s TSS (p-value = 0.68).”

Results are shown in Figure 2B. Of note, we winsorized effect size values in order to improve the visualization. The winsorizing process is also explained in Figure 2 legend. Moreover, we have done the plot suggested by the reviewer (see below). It shows that associations with smallest p-values are found close to the TC’s TSS. Nonetheless, as this pattern is also observed for the effect sizes, we have decided to not include it in the manuscript.

• Concerned about too many significant eQTMs. Almost half of genes are associated with methylation. I wonder if false positives are well controlled using the empirical p-values. Using empirical p-value with permutation may mislead since especially you only use 100 permutations. I wonder the result would be similar if they compare their result with the traditional way, either adjusting p-values using p-values from entire TCs or adjusting pvalues using a gene-based method as commonly used in GWAS. Compare your previous result with my suggestion for the first analysis.

Despite the number of genes (TCs) whose expression is associated with DNA methylation is quite high, we do not think this is due to not correctly controlling false positives. Our approach is based on the method used by GTEx (GTEx consortium) and implemented in the FastQTL package (Ongen et al. 2016), to control for positives in the eQTLs discovery. As in GTEx, we run 100 permutations to estimate the parameters of a beta distribution, which we used to model the distribution of p-values for each CpG. Then, to correct for the number of TCs among significant CpGs, we applied False Discovery Rate (FDR) at a threshold < 0.05. Finally, we defined the final set of significant eQTMs using the beta distribution defined in a previous step.

For illustration, we compared the number of eQTMs with our approach to what we would obtain by uniquely applying the FDR method (adjusted p-value <0.05), getting fewer associations with our approach: eQTMs (45,203 with FDR vs 39,749 with our approach), eCpGs (24,611 vs 21,966) and eGenes (9,937 vs 8,886). Among the 8,886 significant eGenes, 6,288 of them are annotated to coding genes, thus representing 27% of the 23,054 eGenes coding for a gene included in the array.

References:

GTEx consortium, The GTEx Consortium atlas of genetic regulatory effects across human tissues, Science (2020) Sep 11;369(6509):1318-1330. doi: 10.1126/science.aaz1776.

Ongen et al. Fast and efficient QTL mapper for thousands of molecular phenotypes, Bioinformatics (2016) May 15;32(10):1479-85. doi: 10.1093/bioinformatics/btv722. Epub 2015 Dec 26.

• I recommend starting with cell type specific results. Without adjusting cell type, the result doesn't make sense.

As suggested by other reviewers, we have withdrawn the model unadjusted for cellular composition.

Reviewer #3 (Public Review):

Although several DNA methylation-gene expression studies have been carried out in adults, this is the first in children. The importance of this is underlined by the finding that surprisingly few associations are observed in both adults and children. This is a timely study and certain to be important for the interpretation of future omic studies in blood samples obtained from children.

We agree with the reviewer that eQTMs in children are important for interpreting EWAS findings conducted in child cohorts such as those of the Pregnancy And Childhood Epigenetics (PACE) consortium.

It is unfortunate that the authors chose to base their reporting on associations unadjusted for cell count heterogeneity. They incorrectly claim that associations linked to cell count variation are likely to be cell-type-specific. While possible, it is probably more likely that the association exists entirely due to cell type differences (which tend to be large) with little or no association within any of the cell types (which tend to be much smaller). In the interests of interpretability, it would be better to report only associations obtained after adjusting for cell count variation.

Following reviewers’ recommendations, we have reconsidered our initial hypothesis about the role of cellular composition in the association between methylation and gene expression. Although we still think that some of the eQTMs only found in the model unadjusted for cellular composition could represent cell specific effects, we acknowledge that the majority might be confounded by the extensive gene expression and DNA methylation differences between cell types. Also, we recognize that more sophisticated statistical tests should be applied to prove our hypothesis. Because of this we have decided to report the eQTMs of the model adjusted for cellular composition in the main manuscript and keep the results of the model unadjusted for cellular composition only in the online catalogue.

Several enrichments could be related to variation in probe quality across the DNA methylation arrays.

For example, enrichment for eQTM CpG sites among those that change with age could simply be due to the fact age and eQTM effects are more likely to be observed for CpG sites with high quality probes than low quality probes. It is more informative to instead ask if eQTM CpG sites are more likely to have increasing rather than decreasing methylation with age. This avoids the probe quality bias since probes with positive associations with age would be expected to have roughly the same quality as those with negative associations with age. There are several other analyses prone to the probe quality bias.

See answer to question 2, below.

Author Response:

Reviewer #1:

This work provides insight into the effects of tetraplegia on the cortical representation of the body in S1. By using fMRI and an attempted finger movement task, the researchers were able to show preserved fine-grained digit maps - even in patients without sensory and motor hand function as well as no spared spinal tissue bridges. The authors also explored whether certain clinical and behavioral determinates may contribute to preserving S1 somatotopy after spinal cord injury.

Overall I found the manuscript to be well-written, the study to be interesting, and the analysis reasonable. I do, however, think the manuscript would benefit by considering and addressing two main suggestions.

1) Provide additional context / rationale for some of the methods. Specific examples below:

a) The rationale behind using the RSA analysis seemed to be predicated on the notion that the signals elicited via a phase-encoded design can only yield information about each voxel's preferred digit and little-to-no information about the degree of digit overlap (see lines 163-166 and 571-575). While this is the case for conventional analyses of these signals, there are more recently developed approaches that are now capable of estimating the degree of somatotopic overlap from phase-encoded data (see: Da Rocha Amaral et al., 2020; Puckett et al., 2020). Although I personally would be interested in seeing one of these types of analyses run on this data, I do not think it is necessary given the RSA data / analysis. Rather, I merely think it is important to add some context so that the reader is not misled into believing that there is no way to estimate this type of information from phase-encoded signals. - Da Rocha Amaral S, Sanchez Panchuelo RM, Francis S (2020) A Data-Driven Multi-scale Technique for fMRI Mapping of the Human Somatosensory Cortex. Brain Topogr 33 (1):22-36. doi:10.1007/s10548-019-00728-6 - Puckett AM, Bollmann S, Junday K, Barth M, Cunnington R (2020) Bayesian population receptive field modeling in human somatosensory cortex. Neuroimage 208:116465. doi:10.1016/j.neuroimage.2019.116465

We did not intend to give the impression that inter-finger overlap can only be estimated using RSA. To clarify this, we included a sentence in our methods section stating that inter-finger overlap cannot be estimated using the traditional travelling wave approach, but new methods have estimated somatotopic overlap from travelling wave data. Since our RSA approach lends itself for estimating inter-finger overlap and is currently the gold standard in characterizing these representational patterns, we opt –in accordance with the reviewer’s comment– not to include this additional analysis.

Revised text Methods:

“While the traditional traveling wave approach is powerful to uncover the somatotopic finger arrangement, a fuller description of hand representation can be obtained by taking into account the entire fine-grained activity pattern of all fingers. RSA-based inter-finger overlap patterns have been shown to depict the invariant representational structure of fingers better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). RSA-based measures are furthermore not prone to some of the problems of measurements of finger selectivity (e.g., dependence on map thresholds). The most common approach for investigating inter-finger overlap is RSA, as used here, though note that somatotopic overlap has recently been estimated from travelling wave data using an iterated Multigrid Priors (iMGP) method and population receptive field modelling (Da Rocha Amaral et al., 2020; Puckett et al., 2020).”

b. The rationale for using minimally thresholded (Z>2) data for the Dice overlap analysis as opposed to the threshold used in data visualization (q<0.05) was unclear. Providing the minimally thresholded maps (in Supplementary) would also aid interpretation of the Dice overlap results.

We followed previously published procedures for calculating the Dice overlap between the two split-halves of the data (Kikkert et al., 2016; J. Kolasinski et al., 2016; Sanders et al., 2019). We used minimally thresholded data to calculate the dice overlap to ensure that our analysis was sensitive to overlaps that would be missed when using high thresholds. We clarified this in the revised manuscript. We thank the reviewer for their suggestion to add a Figure displaying the minimally thresholded split-half hard-edged finger maps - we have added this to the revised manuscript as Figure 2-Figure supplement 1.

To ensure that our thresholding procedure did not change the results of the dice overlap analysis, we repeated this analysis using split-half maps that were thresholded using a q < 0.05 FDR criterion (as was used to create the travelling wave maps in Figures 2A-B). We found the same results as when using the Z >2 thresholding criterion: Overall, split-half consistency was not significantly different between patients and controls, as tested using a robust mixed ANOVA (F(1,17.69) = 0.08, p = 0.79). There was a significant difference in split- half consistency between pairs of same, neighbouring, and non-neighbouring fingers (F(2,14.77) = 38.80, p < 0.001). This neighbourhood relationship was not significantly different between the control and patient groups (i.e., there was no significant interaction; F(2,14.77) = 0.12, p = 0.89). We have included this analysis and the relating figure as Figure 2- Figure supplement 2 in the revised manuscript.

Revised text Methods:

“We followed previously described procedures for calculating the DOC between two halves of the travelling wave data (Kikkert et al., 2016; Kolasinski et al., 2016; Sanders et al., 2019). The averaged finger-specific maps of the first forward and backward runs formed the first data half. The averaged finger-specific maps of the second forward and backward runs formed the second data half. The finger-specific clusters were minimally thresholded (Z>2) on the cortical surface and masked using an S1 ROI, created based on Brodmann area parcellation using Freesurfer (see Figure 2– figure supplement 1 for a visualisation of the minimally thresholded split-half hard-edged finger maps used to calculate the DOC). We used minimally thresholded finger-specific clusters for the DOC analysis to ensure we were sensitive to overlaps that would be missed when using high thresholds. Note that results were unchanged when thresholding the finger-specific clusters using an FDR q < 0.05 criterion (see Figure 2 – figure supplement 2).”

2) Provide a more thorough discussion - particularly with respect to the possible role of top-down processes (e.g., attention).

a) The authors discuss a few potential signal sources that may contribute to the maintenance of (and ability to measure) the somatotopic maps; however, the overall interpretation seems a bit "motor efferent heavy". That is, it seems the authors favor an explanation that the activity patterns measured in S1 were elicited by efference copies from the motor system and that occasional corollary discharges or attempted motor movements play a role in their maintenance over time. The authors consider other explanations, noting - for example - the potential role of attention in preserving the somatotopic representations given that attention has been shown to be able to activate S1 hand representations. The mention of this was, however, rather brief - and I believe the issue deserves a bit more of a balanced consideration.

When the authors consider the possible role of attention in maintaining the somatotopic representations (lines 329-333), they mention that observing others' fingers being touched or attending to others' finger movements may contribute. But there is no mention of attending to one's own fingers (which has been shown to elicit activity as cited). I realize that the patients lack sensorimotor function (and hence may find it difficult to "attend" to their fingers); however, they have all had prior experience with their fingers and therefore might still be able to attend to them (or at least the idea of their digits) such that activity is elicited. For example, it is not clear to me that it would be any more difficult for the patients to be asked to attend to their digits compared to being asked to attempt to move their digits. I would even suggest that attempting to move a digit (regardless of whether you can or not) requires that one attends to the digit before attempting to initiate the movement as well as throughout the attempted motor movement. Because of this, it seems possible that attention-related processes could be playing a role in or even driving the signals measured during the attempted movement task - as well as those involved in the ongoing maintenance of the maps after injury. I don't think this possibility can be dismissed given the data in hand, but perhaps the issue could be addressed by a bit more thorough of a discussion on the process of "attempting to move" a digit (even one that does not move) - and the various top-down processes that might be involved.

We thank the reviewer for their consideration and insights into the potential mechanisms underlying our results. We have now elaborated further on the possibility that attention- related processes might have contributed to the reported effects, also in consideration of comment 3.4.

Revised text Discussion:

“Spared spinal cord tissue bridges can be found in most patients with a clinically incomplete injury, their width being predictive of electrophysiological information flow, recovery of sensorimotor function, and neuropathic pain (Huber et al., 2017; Pfyffer et al., 2021, 2019; Vallotton et al., 2019). However, in this study, spared midsagittal spinal tissue bridges at the lesion level, motor function, and sensory function did not seem necessary to maintain and activate a somatotopic hand representation in S1. We found a highly typical hand representation in two patients (S01 and S03) who did not have any spared spinal tissue bridges at the lesion level, a complete (S01) or near complete (S03) hand paralysis, and a complete (S01) or near complete loss (S03) of hand sensory function. Our predictive modelling results were in line with this notion and showed that these behavioural and structural spinal cord determinants were not predictive of hand representation typicality. Note however that our sample size was limited, and it is challenging to draw definite conclusions from non-significant predictive modelling results.”

“How may these representations be preserved over time and activated through attempted movements in the absence of peripheral information? S1 is reciprocally connected with various brain areas, e.g., M1, lateral parietal cortex, poster parietal area 5, secondary somatosensory cortex, and supplementary motor cortex (Delhaye et al., 2019). After loss of sensory inputs and paralysis through SCI, S1 representations may be activated and preserved through its interconnections with these areas. Firstly, it is possible that cortico-cortical efference copies may keep a representation ‘alive’ through occasional corollary discharge (London and Miller, 2013). While motor and sensory signals no longer pass through the spinal cord in the absence of spinal tissue bridges, S1 and M1 remain intact. When a motor command is initiated (e.g., in the form of an attempted hand movement) an efference copy is thought to be sent to S1 in the form of corollary discharge. This corollary discharge resembles the expected somatosensory feedback activity pattern and may drive somatotopic S1 activity even in the absence of ascending afferent signals from the hand (Adams et al., 2013; London and Miller, 2013). It is possible that our patients occasionally performed attempted movements which would result in corollary discharge in S1. Second, it is likely that attempting individual finger movements poses high attentional demands on tetraplegic patients. Accordingly, attentional processes might have contributed to eliciting somatotopic S1 activity. Evidence for this account comes from studies showing that it is possible to activate somatotopic S1 hand representations through attending to individual fingers (Puckett et al., 2017) or through touch observation (Kuehn et al., 2018). Attending to fingers during our attempted finger movement task may have been sufficient to elicit somatotopic S1 activity through top-down processes in the tetraplegic patients who lacked hand motor and sensory function. Furthermore, one might speculate that observing others’ or one’s own fingers being touched or directing attention to others’ hand movements or one’s own fingers may help preserve somatotopic representations. Third, it is possible that these somatotopic maps are relatively hardwired and while they deteriorate over time, they never fully disappear. Indeed, somatotopic mapping of a sensory deprived body part has been shown to be resilient after dystonia (Ejaz et al., 2016; though see Burman et al., (2009) and Taub et al., (1998)) and arm amputation (Bruurmijn et al., 2017; Kikkert et al., 2016; Wesselink et al., 2019). Fourth, it is possible that even though a patient is clinically assessed to be complete and is unable to perceive sensory stimuli on the deprived body part, there is still some ascending information flow that contributes to preserving somatotopy (Wrigley et al., 2018). A recent study found that although complete paraplegic SCI patients were unable to perceive a brushing stimulus on their toe, 48% of patients activated the location appropriate S1 area (Wrigley et al., 2018). However, the authors of this study defined the completeness of patients’ injuries via behavioural testing, while we additionally assessed the retained connections passing through the SCI directly via quantification of spared spinal tissue bridges through structural MRI. It is unlikely that spinal tissue carrying somatotopically organised information would be missed by our assessment (Huber et al., 2017; Pfyffer et al., 2019). Our experiment did not allow us to tease apart these potential processes and it is likely that various processes simultaneously influence the preservation of S1 somatotopy and elicited the observed somatotopic S1 activity.”

Reviewer #2:

The authors investigate SCI patients and characterize the topographic representation of the hand in sensorimotor cortex when asked to move their hand (which controls could do but patients could not). The authors compare some parameters of topographic map organization and conclude that they do not differ between patients and controls, whereas they find changes in the typicality of the maps that decrease with years since disease onset in patients. Whereas these initial analyses are interesting, they are not clearly related to a mechanistic model of the disorder and the underlying pathophysiology that is expected in the patients. Furthermore, additional analyses on more fine-grained map changes are needed to support the authors' claims. Finally, the major result of changed typicality in the patients is in my view not valid.

• Concept 1. At present, there is no clear hypotheses about the (expected or hypothesized) mechanistic changes of the sensorimotor maps in the patients. The authors refer to "altered" maps and repeatedly say that "results are mixed" (3 times in the introduction).

We thank the reviewer for highlighting to us that our introduction and hypotheses were unclear and/or incomplete to them. We have restructured our Introduction to better highlight competing hypotheses on how SCI may change S1 hand representations, the reasons for our analytical approach, and elaborate on our hypotheses.

Revised text Introduction:

“Research in non-human primate models of chronic and complete cervical SCI has shown that the S1 hand area becomes largely unresponsive to tactile hand stimulation after the injury (Jain et al., 2008; Kambi et al., 2014; Liao et al., 2021). The surviving finger-related activity became disorganised such that a few somatotopically appropriate sites but also other somatotopically nonmatched sites were activated (Liao et al., 2021). Seminal nonhuman primate research has further demonstrated that SCI leads to extensive cortical reorganisation in S1, such that tactile stimulation of cortically adjacent body parts (e.g., of the face) activated the deprived brain territory (e.g., of the hand; Halder et al., 2018; Jain et al., 2008; Kambi et al., 2014). Although the physiological hand representation appears to largely be altered following a chronic cervical SCI in non-human primates, the anatomical isomorphs of individual fingers are unchanged (Jain et al., 1998). This suggests that while a hand representation can no longer be activated through tactile stimulation after the loss of afferent spinal pathways, a latent and somatotopic hand representation could be preserved regardless of large-scale physiological reorganisation.

A similar pattern of results has been reported for human SCI patients. Transcranial magnetic stimulation (TMS) studies induced current in localised areas of SCI patient’s M1 to induce a peripheral muscle response. They found that representations of more impaired muscles retract or are absent while representations of less impaired muscles shift and expand (Fassett et al., 2018; Freund et al., 2011a; Levy et al., 1990; Streletz et al., 1995; Topka et al., 1991; Urbin et al., 2019). Similarly, human fMRI studies have shown that cortically neighbouring body part representations can shift towards, though do not invade, the deprived M1 and S1 cortex (Freund et al., 2011b; Henderson et al., 2011; Jutzeler et al., 2015; Wrigley et al., 2018, 2009). Other human fMRI studies hint at the possibility of latent somatotopic hand representations following SCI by showing that attempted movements with the paralysed and sensory deprived body part can still evoke signals in the sensorimotor system (Cramer et al., 2005; Freund et al., 2011b; Kokotilo et al., 2009; Solstrand Dahlberg et al., 2018). This attempted ‘net’ movement activity was, however, shown to substantially differ from healthy controls: Activity levels have been shown to be increased (Freund et al., 2011b; Kokotilo et al., 2009; Solstrand Dahlberg et al., 2018) or decreased (Hotz- Boendermaker et al., 2008), volumes of activation have been shown to be reduced (Cramer et al., 2005; Hotz-Boendermaker et al., 2008), activation was found in somatotopically nonmatched cortical sites (Freund et al., 2011b), and activation was poorly modulated when patients switched from attempted to imagined movements (Cramer et al., 2005). These observations have therefore mostly been attributed to abnormal and/or disorganised processing induced by the SCI. It remains possible though that, despite certain aspects of sensorimotor activity being altered after SCI, somatotopically typical representations of the paralysed and sensory deprived body parts can be preserved (e.g., finger somatotopy of affected hand). Such preserved representations have the potential to be exploited in a functionally meaningful manner (e.g., via neuroprosthetics).

Case studies using intracortical stimulation in the S1 hand area to elicit finger sensations in SCI patients hint at such preserved somatotopic representations (Fifer et al., 2020; Flesher et al., 2016), with one exception (Armenta Salas et al., 2018). Negative results were suggested to be due to a loss of hand somatotopy and/or reorganisation in S1 of the implanted SCI patient or due to potential misplacement of the implant (Armenta Salas et al., 2018). Whether fine-grained somatotopy is generally preserved in the tetraplegic patient population remains unknown. It is also unclear what clinical, behavioural, and structural spinal cord determinants may influence such representations to be maintained. Here we used functional MRI (fMRI) and a visually cued (attempted) finger movement task in tetraplegic patients to examine whether hand somatotopy is preserved following a disconnection between the brain and the periphery. We instructed patients to perform the fMRI tasks with their most impaired upper limb and matched controls’ tested hands to patients’ tested hands. If a patient was unable to make overt finger movements due to their injury, then we carefully instructed them to make attempted (i.e., not imagined) finger movements. To see whether patient’s maps exhibited characteristics of somatotopy, we visualised finger selectivity in S1 using a travelling wave approach. To investigate whether fine-grained hand somatotopy was preserved and could be activated in S1 following SCI, we assessed inter-finger representational distance patterns using representational similarity analysis (RSA). These inter-finger distance patterns are thought to be shaped by daily life experience such that fingers used more frequently together in daily life have lower representational distances (Ejaz et al., 2015). RSA-based inter-finger distance patterns have been shown to depict the invariant representational structure of fingers in S1 and M1 better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). Over the past years RSA has therefore regularly been used to investigate somatotopy of finger representations both in healthy (e.g., Akselrod et al., 2017; Ariani et al., 2020; Ejaz et al., 2015; Gooijers et al., 2021; Kieliba et al., 2021; Kolasinski et al., 2016; Liu et al., 2021; Sanders et al., 2019) and patient populations (e.g., Dempsey-Jones et al., 2019; Ejaz et al., 2016; Kikkert et al., 2016; Wesselink et al., 2019). We closely followed procedures that have previously been used to map preserved and typical somatotopic finger selectivity and inter-finger representational distance patterns of amputees’ missing hands in S1 using volitional phantom finger movements (Kikkert et al., 2016; Wesselink et al., 2019). However, in amputees, these movements generally recruit the residual arm muscles that used to control the missing limb via intact connections between the brain and spinal cord. Whether similar preserved somatotopic mapping can be observed in SCI patients with diminished or no connections between the brain and the periphery is unclear. If finger somatotopy is preserved in tetraplegic patients, then we should find typical inter-finger representational distance patterns in the S1 hand area of these patients. By measuring a group of fourteen chronic tetraplegic patients with varying amounts of spared spinal cord tissue at the lesion level (quantified by means of midsagittal tissue bridges based on sagittal T2w scans), we uniquely assessed whether preserved connections between the brain and periphery are necessary to preserve fine somatotopic mapping in S1 (Huber et al., 2017; Pfyffer et al., 2019). If spared connections between the periphery and the brain are not necessary for preserving hand somatotopy, then we would find typical inter-finger representational distance patterns even in patients without spared spinal tissue bridges. We also investigated what clinical and behavioural determinants may contribute to preserving S1 hand somatotopy after chronic SCI. If spared sensorimotor hand function is not necessary for preserving hand somatotopy, then we would find typical inter-finger representational distance patterns even in patients who suffer from full sensory loss and paralysis of the hand(s).”

They do not in detail report which results actually have been reported before, which is a major problem, because those prior results should have motivated the analyses the authors conducted. For instance, two of the cited studies found that in SCI patients, only ONE FINGER shifted towards the malfunctioning area (i.e., the small finger) whereas all other fingers were the same. However, the authors do NOT perform single finger analyses but always average their results ACROSS fingers. This is even true in spite of some patients indeed showing MISSING FINGERS as is clearly evident in the figure, and in spite of the clearly reduced distance of the thumb in the patients as is also visible in another figure. Nothing of this is seen in the results, because the ANOVA and analyses never have the factor of "finger". Instead, the authors always average the analyses across finger. The conclusion that the maps do not differ is therefore not justified at present. This severely reduces any conclusions that an be drawn from the data at present.

We apologise for the lack of clarity. We now added additional detail regarding studies showing altered sensorimotor processing following SCI. We also clarified that we based our analysis steps on previous studies investigating hand somatotopy following deafferentation (i.e., following arm amputation; Kikkert et al., 2016; Wesselink et al., 2019) and somatotopic reorganisation RSA- based inter-finger distance patterns have been shown to depict the invariant representational structure of fingers in S1 and M1 better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). Over the past years RSA has therefore regularly been used to investigate somatotopy of finger representations both in healthy (e.g., Akselrod et al., 2017; Ariani et al., 2020; Ejaz et al., 2015; Gooijers et al., 2021; Kieliba et al., 2021; Kolasinski et al., 2016; Liu et al., 2021; Sanders et al., 2019) and patient populations (e.g. Dempsey-Jones et al., 2019; Ejaz et al., 2016; Kikkert et al., 2016; Wesselink et al., 2019). It is believed to be the most appropriate measure to reliably detect subtle changes in somatotopy. We adjusted the text in our revised Introduction section to better highlight this.

Please note that we do not average across fingers in our RSA typicality procedure. Instead, RSA considers how the (attempted) movement with one finger changes the activity pattern across the whole hand representation. Note that somatotopic reorganisation will change the inter-finger distance measured with this method as previously shown (Kieliba et al., 2021; Kolasinski et al., 2016; Wesselink et al., 2019).

Still, as per the reviewer’s suggestion, we conducted a robust mixed ANOVA on the RSA distance measures with a within-subjects factor for finger pair (10 levels) and a between- subjects factor for group (2 levels: controls and SCI patients). We did not find a significant group effect (F(1,21.66) = 1.50, p = 0.23). There was a significant difference in distance between finger pairs (F(9,15.38) = 27.22, p < 0.001), but this was not significantly different between groups (i.e., no significant finger pair by group interaction; F(9,15.38) = 1.05, p = 0.45). When testing for group differences per finger pair, the BF only revealed inconclusive evidence (BF > 0.37 and < 1.11; note that we could not run a Bayesian ANOVA due to normality violations). We have added this analysis to the revised manuscript.

Lastly, we would like to highlight that our argument is that the finger maps can be preserved in the absence of sensory and motor function, but over time they deteriorate and become less somatotopic. As such, we do not aim to state that they are unchanged overall – but rather that they can be unchanged even despite loss of sensory and motor function. We have clarified this in our abstract and manuscript to avoid confusion.

Revised abstract:

“Previous studies showed reorganised and/or altered activity in the primary sensorimotor cortex after a spinal cord injury (SCI), suggested to reflect abnormal processing. However,little is knownaboutwhether somatotopically-specific representations can be preserved despite alterations in net activity. In this observational study we used functional MRI and an (attempted) finger movement task in tetraplegic patients to characterise the somatotopic hand layout in primary somatosensory cortex. We further used structural MRI to assess spared spinal tissue bridges. We found that somatotopic hand representations can be preserved in absence of sensory and motor hand functioning, and no spared spinal tissue bridges. Such preserved hand somatotopy could be exploited by rehabilitation approaches that aim to establish new hand-brain functional connections after SCI (e.g., neuroprosthetics). However, over years since SCI the hand representation somatotopy deteriorated, suggesting that somatotopic hand representations are more easily targeted within the first years after SCI.”

Revised text Methods:

“Second, we tested whether the inter-finger distances were different between controls and patients using a robust mixed ANOVA with a within-participants factor for finger pair (10 levels) and a between-participants factor for group (2 levels: controls and patients).”

Revised text Results:

“We then tested whether the inter-finger distances were different across finger pairs between controls and SCI patients using a robust mixed ANOVA with a within-participants factor for finger pair (10 levels) and a between-participants factor for group (2 levels: controls and patients). We did not find a significant difference in inter-finger distances between patients and controls (F(1,21.66) = 1.50, p = 0.23). The inter-finger distances were significantly different across finger pairs, as would be expected based on somatotopic mapping (F(9,15.38) = 27.22, p < 0.001). This pattern of inter-finger distances was not significantly different between groups (i.e., no significant finger pair by group interaction; F(9,15.38) = 1.05, p = 0.45). When testing for group differences per finger pair, the BF only revealed inconclusive evidence (BF > 0.37 and < 1.11; note that we could not run a Bayesian ANOVA due to normality violations).”

Revised text Discussion:

“In this study we investigated whether hand somatotopy is preserved and can be activated through attempted movements following tetraplegia. We tested a heterogenous group of SCI patients to examine what clinical, behavioural, and structural spinal cord determinants contribute to preserving S1 somatotopy. Our results revealed that detailed hand somatotopy can be preserved following tetraplegia, even in the absence of sensory and motor function and a lack of spared spinal tissue bridges. However, over time since SCI these finger maps deteriorated such that the hand somatotopy became less typical.”

• Concept 2: This also relates to the fact that the most prominent and consistent finding of prior studies was to show changes in map AMPLITUDE in the maps of patients. It is not clear to me how amplitude was measured here, because the text says "average BOLD activity". What should be reported are standard measures of signal amplitude both across the map area and for individual fingers.

We apologise for the lack of clarity, “average BOLD activity” represented the average z- standardised activity within the S1 hand ROI. To comply with the reviewer’s comment, we adjusted this to the percent signal change underneath the S1 hand ROI and report this instead in our revised manuscript and in revised Figure 3A and revised Figure 3- Figure supplement 1. Note that results were unchanged.

As per the reviewer’s suggestion, we further extracted the activity levels for individual fingers under finger-specific ROIs. To create finger-specific ROIs, probability finger maps were created based on the travelling wave data of the control group, thresholded at 25% (i.e., meaning that at least 5 out of 18 control participants needed to significantly activate a vertex for this vertex to be included in the ROI), and binarised. We then used the separately acquired blocked design data to extract the corresponding finger movement activity levels underlying these finger-specific ROIs per participant. Per ROI, we then compared the activity level between groups. After correction for multiple comparisons, there was no significant difference between groups for the thumb (U = 93, p = 0.37), index (t(30) = -0.003, p = 0.99), middle (t(30) = 1.11, p = 0.35), ring (t(30) = 2.02, p = 0.13), or little finger (t(30) = 2.14, p = 0.20). We have added this analysis to Appendix 1.

Note that lower or higher BOLD amplitude levels do not influence our typicality scores per se. Indeed, typical inter-finger representational patterns have been shown to persist even in ipsilateral M1 that exhibited a negative BOLD response during finger movements (Berlot et al., 2019). As long as the typical inter-finger relationships are preserved, brain areas that have low amplitudes of activity can have a typical somatotopic representation.

Revised text in Methods:

"The percent signal change for overall task-related activity was then extracted for voxels underlying this S1 hand ROI per participant. A similar analysis was used to investigate overall task-related activity in an M1 hand ROI (see Figure 3- Figure supplement 1). We further compared activity levels in finger-specific ROIs in S1 between groups and conducted a geodesic distance analysis to assess whether the finger representations of the SCI patients were aligned differently and/or shifted compared to the control participants (see Appendix 1)."

Revised text in Results:

“Task-related activity was quantified by extracting the percent signal change for finger movement (across all fingers) versus baseline across within the contralateral S1 hand ROI (see Figure 3A). Overall, all patients were able to engage their S1 hand area by moving individual fingers (t(13)=7.46, p < 0.001; BF10=4.28e +3), as did controls (t(17)=9.92, p < 0.001; BF10=7.40e +5). Furthermore, patients’ task-related activity was not significantly different from controls (t(30)=-0.82, p=0.42; BF10=0.44), with the BF showing anecdotal evidence in favour of the null hypothesis.”

Revised Appendix 1:

“Percent signal change in finger-specific clusters To assess whether finger movement activity levels were different between patients and controls, we created finger-specific ROIs and extracted the activity level of the corresponding finger movement for each participant. To create the finger-specific ROIs, the probability finger surface maps that were created from the travelling wave data of the control group (see main manuscript) were thresholded at 25% (i.e., meaning that at least 5 out of 18 control participants needed to significantly activate a vertex for this vertex to be included in the ROI), and binarised. We then used the separately acquired blocked design data to extract the finger movement activity levels underlying these finger-specific ROIs. We first flipped the contrast images resulting from each participant’s fixed effects analysis (i.e., that was ran to average across the 4 blocked design runs) along the x-axis for the left-hand tested participants. Each participant’s contrast maps were then resampled to the Freesurfer 2D average atlas and the averaged z-standardised activity level was extracted for each finger movement vs rest contrast underlying the finger-specific ROIs. We compared the activity levels for each finger movement in the corresponding finger ROI (i.e., thumb movement activity in the thumb ROI, index finger movement activity in the index finger ROI, etc.) between groups. After correction for multiple comparisons, there was no significant difference between groups for the thumb (U = 93, p = 0.37), index (t(30) = -0.003, p = 0.99), middle (t(30) = 1.11, p = 0.35), ring (t(30) = 2.02, p = 0.13), or little finger (t(30) = 2.14, p = 0.20).”

Appendix 1- Figure 1: Finger-specific activity levels in finger-specific regions of interest. A) Finger- specific ROIs were based on the control group’s binarised 25% probability travelling wave finger selectivity maps. B) Finger movement activity levels in the corresponding finger-specific ROIs. There were no significant differences in activity levels between the SCI patient and control groups. Controls are projected in grey; SCI patients are projected in orange. Error bars show the standard error of the mean. White arrows indicate the central sulcus. A = anterior; P = posterior.

• Concept 3: The authors present a hypothesis on the underlying mechanisms of SCI that does not seem to reflect prior data. The argument is that changes in map alignment relate to maladaptive changes and pain. However, the literature that the authors cite does not support this claim. In fact, Freund 2011 promotes the importance of map amplitude but not alignment, whereas other studies either show no relation of activation to pain, or they even show that map shift relates to LESS pain, i.e., the reverse argument than what the authors say. My impression is that the model that the authors present is mainly a model that is used for phantom pain but not for SCI. Taking this into consideration, the findings the authors present are not surprising anymore, because in fact none of these studies claimed that the affected area should be absent in SCI patients; these papers only say that the other body parts change in location or amplitude, which is something the authors did not measure. It is important to make this clear in the text.

As the reviewer states, the literature is debated regarding the relationship between reorganisation and pain in SCI patients. We did not highlight this clearly enough. To improve clarity and focus our message we have therefore removed the sentence regarding reorganisation and pain from the Introduction of our revised manuscript. Also taking comment 2.1 and 2.2 into consideration, we have restructured our Introduction.

We respectfully disagree with the reviewer that our results are not novel or surprising. Whether the full fine-grained hand somatotopy is preserved following a complete motor and sensory loss through tetraplegia has not been considered before. Furthermore, to our knowledge, there is no paper that has inspected the full somatotopic layout in a heterogenous sample of SCI patients and shown that over time since injury, hand somatotopy deteriorates. We indeed cannot make claims regarding the reorganization in S1 with regards to neighbouring cortical areas activating the hand area, as we have now clarified further in the revised Discussion. We now also clarify in our discussion that our result does not exclude the possibility of reorganisation occurring simultaneously and that this is topic for further investigation. As described in the Discussion, it is very possible that reorganisation and preserved somatotopy could co-occur.

Revised text Discussion:

“We did not probe body parts other than the hand and could therefore not investigate whether any remapping of other (neighbouring and/or intact) body part representations towards or into the deprived S1 hand cortex may have taken place. Whether reorganisation and preservation of the original function can simultaneously take place within the same cortical area therefore remains a topic for further investigation. It is possible that reorganisation and preservation of the original function could co-occur within cortical areas. Indeed, non-human primate studies demonstrated that remapping observed in S1 actually reflects reorganisation in subcortical areas of the somatosensory pathway, principally the brainstem (Chand and Jain, 2015; Kambi et al., 2014). As such, the deprived S1 area receives reorganised somatosensory inputs upon tactile stimulation of neighbouring intact body parts. This would simultaneously allow the original S1 representation of the deprived body part to be preserved, as observed in our results when we directly probed the deprived S1 hand area through attempted finger movements.”

• Concept 4: There is yet another more general point on the concept and related hypotheses: Why do the authors assume that immediately after SCI the finger map should disappear? This seems to me the more unlikely hypotheses compared to what the data seem to suggest: preservation and detoriation over time. In my view, there is no biological model that would suggest that a finger map suddenly disappears after input loss. How should this deterioration be mediated? By cellular loss? As already stated above, the finding is therefore much less surprising as the authors argue.

We did not expect that finger maps would disappear, especially given the case studies using S1 intracortical stimulation studies in SCI patients and the result of preserved somatotopy of the missing hand in amputees. We are not sure which part of the manuscript might have caused this misunderstanding.

With regards to the reviewer’s comment that there are no models to suggest that fingers maps would disappear: there is competing research on this as we now explain in our revised Introduction. Non-human primate research has shown that the S1 hand area becomes largely unresponsive to tactile hand stimulation after an SCI (Jain et al., 2008; Kambi et al., 2014; Liao et al., 2021). The surviving finger-related activity was shown to be disorganised such that a few somatotopically appropriate sites but also other somatotopically nonmatched sites were activated (Liao et al., 2021). These fingers areas in S1 became responsive to touch on the face. Furthermore, TMS studies that induce current in localised areas of M1 to induce a peripheral muscle response in SCI patients have shown that representations of more impaired muscles retract or are absent (Fassett et al., 2018; Freund et al., 2011a; Levy et al., 1990; Streletz et al., 1995; Topka et al., 1991; Urbin et al., 2019). We do not believe that this indicates that the S1 hand somatotopy is lost, but rather that tactile inputs and motor outputs no longer pass the level of injury. Indeed, non-human primate work showing immutable myelin borders between finger representations in S1 post SCI suggests that a latent hand representation may be preserved. Further hints for such preserved somatotopy comes from fMRI studies showing net sensorimotor activity during attempted movements with the paralysed body part, intracortical stimulation studies in SCI patients, and preserved somatotopic maps of the missing hand in amputees. We have restructured our Introduction accordingly, also taking into consideration comments 2.1, 2.2, and 2.4.

• Methods & Results. The authors refer to an analyses that they call "typicality" where they say that they assess how "typical" a finger map is. Given this is not a standard measure, I was wondering how the authors decided what a "typical" finger map is. In fact, there are a few papers published on this issue where the average location of each finger in a large number of subjects is detailed. Rather than referring to this literature, the authors use another dataset from another study of themselves that was conduced on n=8 individuals and using 7T MRI (note that in the present study, 3T MRI was used) to define what "typical" is. This approach is not valid. First, this "typical" dataset is not validated for being typical (i.e., it is not compared with standard atlases on hand and finger location), second, it was assessed using a different MRI field strength, third, it was too little subjects to say that this should be a typical dataset, forth, the group differed from the patients in terms of age and gender (i.e., non-matched group), and fifth, the authors even say that the design was different ("was defined similarly", i.e., not the same). This approach is therefore in my view not valid, particularly given the authors measured age- and gender-matched controls that should be used to compare the maps with the patients. This is a critical point because changes in typicality is the main result of the paper.

We respectfully disagree with the reviewer that the typicality measure is not standard, invalid, and inaccurate. RSA-based inter-finger overlap patterns have been shown to depict the invariant representational structure of fingers better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). RSA-based inter- finger representation measures have been shown to have more within-subject stability (both within the same session and between sessions that were 6 months apart) and less inter-subject variability (Ejaz et al., 2015) than these other measures of somatotopy. RSA-based measures are furthermore not prone to some of the problems of measurements of finger selectivity (e.g., dependence on map thresholds). Indeed, over the past years RSA has become the golden standard to investigate somatotopy of finger representations both in healthy (e.g., Akselrod et al., 2017; Ariani et al., 2020; Ejaz et al., 2015; Gooijers et al., 2021; Kieliba et al., 2021; Kolasinski et al., 2016; Liu et al., 2021; Sanders et al., 2019) and patient populations (e.g. Dempsey-Jones et al., 2019; Ejaz et al., 2016; Kikkert et al., 2016; Wesselink et al., 2019). Moreover, various papers have been published in eLife and elsewhere that used the same RSA-based typicality criteria to assess plasticity in finger representations (Dempsey-Jones et al., 2019; Ejaz et al., 2015; Kieliba et al., 2021; Wesselink et al., 2019). We now highlight this in the revised Introduction.

The canonical RDM used in our study has previously been used as a canonical RDM in a 3T study exploring finger somatotopy in amputees (Wesselink et al., 2019) and was made available to us (note that we did not collect this data ourselves). We aimed to use similar measures as in Wesselink et al (2019) and therefore felt it was most appropriate to use the same canonical RDM. One of the strengths of RSA is it can be used to quantitatively relate brain activity measures obtained using different modalities, across different species, brain areas, brain and behavioural measures etc. (Kriegeskorte et al., 2008). As such, the fact that this canonical RDM was constructed based on data collected using 7T fMRI using a digit tapping task should not influence our results. We however agree with the reviewer it is good to demonstrate that our results would not change when using a canonical RDM based on the average RDM of our age-, sex- and handedness matched control group. We therefore recalculated the typicality of all participants using the controls’ average RDM as the canonical RDM. We found a strong and highly significant correlation in typicality scores calculated using the canonical RDM from the independent dataset and the controls’ average RDM (see figure below). This was true for both the patient (rs = 0.92, p < 0.001; red dots) and control groups (rs = 0.78, p < 0.001; grey dots).

We then repeated all analysis using these newly calculated typicality scores. As expected, we found the same results as when using a canonical RDM based on the independent dataset (see below for details). This analysis has been added to the revised Appendix 1 and is referred to in the main manuscript.

Revised text Introduction:

“To investigate whether fine-grained hand somatotopy was preserved and could be activated in S1 following SCI, we assessed inter-finger representational distance patterns using representational similarity analysis (RSA). These inter-finger distance patterns are thought to be shaped by daily life experience such that fingers used more frequently together in daily life have lower representational distances (Ejaz et al., 2015). RSA-based inter-finger distance patterns have been shown to depict the invariant representational structure of fingers in S1 and M1 better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). Over the past years RSA has therefore regularly been used to investigate somatotopy of finger representations both in healthy (e.g., Akselrod et al., 2017; Ariani et al., 2020; Ejaz et al., 2015; Gooijers et al., 2021; Kieliba et al., 2021; Kolasinski et al., 2016; Liu et al., 2021; Sanders et al., 2019) and patient populations (e.g., Dempsey- Jones et al., 2019; Ejaz et al., 2016; Kikkert et al., 2016; Wesselink et al., 2019). We closely followed procedures that have previously been used to map preserved and typical somatotopic finger selectivity and inter-finger representational distance patterns of amputees’ missing hands in S1 using volitional phantom finger movements (Kikkert et al., 2016; Wesselink et al., 2019).”

Revised text Results:

“This canonical RDM was based on 7T finger movement fMRI data in an independently acquired cohort of healthy controls (n = 8). The S1 hand ROI used to calculated this canonical RDM was defined similarly as in the current study (see Wesselink and Maimon- Mor, (2017b) for details). Note that results were unchanged when calculating typicality scores using a canonical RDM based on the averaged RDM of the age-, sex-, and handedness-matched control group tested in this study (see Appendix 1).”

Revised text Methods:

“While the traditional traveling wave approach is powerful to uncover the somatotopic finger arrangement, a fuller description of hand representation can be obtained by taking into account the entire fine-grained activity pattern of all fingers. RSA-based inter-finger overlap patterns have been shown to depict the invariant representational structure of fingers better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). RSA-based measures are furthermore not prone to some of the problems of measurements of finger selectivity (e.g., dependence on map thresholds).”

“Third, we estimated the somatotopic typicality (or normality) of each participant’s RDM by calculating a Spearman correlation with a canonical RDM. We followed previously described procedures for calculating the typicality score (Dempsey-Jones et al., 2019; Ejaz et al., 2015; Kieliba et al., 2021; Wesselink et al., 2019). The canonical RDM was based on 7T finger movement fMRI data in an independently acquired cohort of healthy controls (n = 8). The S1 hand ROI used to calculated this canonical RDM was defined similarly as in the current study (see Wesselink and Maimon-Mor, (2017b) for details). Note that results were unchanged when calculating typicality scores using a canonical RDM based on the averaged RDM of the sex-, handedness-, and age matched control group tested in this study (see Appendix 1).”

Revised text Appendix 1:

“Typicality analysis using a canonical RDM based on the controls’ average RDM

To ensure that our typicality results did not change when using a canonical inter-finger RDM based on the age-, sex-, and handedness matched subjects tested in this study, we recalculated the typicality scores of all participants using the averaged inter-finger RDM of our control sample as the canonical RDM. We found a strong and highly significant correlation between the typicality scores calculated using the canonical inter-finger RDM from the independent dataset (reported in the main manuscript) and the typicality scores calculated using our controls’ average RDM. This was true for both the SCI patient (rs = 0.92, p < 0.001) and control groups (rs = 0.78, p < 0.001).

We then repeated all typicality analysis reported in the main manuscript. As expected, using the typicality scores calculated using our controls’ average RDM we found the same results as when using the canonical inter-finger RDM from the independent dataset: There was a significant difference in typicality between SCI patients, healthy controls, and congenital one-handers (H(2)=27.61, p < 0.001). We further found significantly higher typicality in controls compared to congenital one-handers (U=0, p < 0.001; BF10=76.11). Importantly, the typicality scores of the SCI patients were significantly higher than the congenital one-handers (U=2, p < 0.001; BF10=50.98), but not significantly different from the controls (U=94, p=0.24; BF10=0.55). Number of years since SCI significantly correlated with hand representation typicality (rs=-0.54, p=0.05) and patients with more retained GRASSP motor function of the tested upper limb had more typical hand representations in S1 (rs=0.58, p=0.03). There was no significant correlation between S1 hand representation typicality and GRASSP sensory function of the tested upper limb, spared midsagittal spinal tissue bridges at the lesion level, or cross-sectional spinal cord area (rs=0.40, p=0.15, rs=0.50, p=0.10, and rs=0.48, p=0.08, respectively). An exploratory stepwise linear regression analysis revealed that years since SCI significantly predicted hand representation typicality in S1 with R2=0.33 (F(1,10)=4.98, p=0.05). Motor function, sensory function, spared midsagittal spinal tissue bridges at the lesion level, and spinal cord area did not significantly add to the prediction (t=1.31, p=0.22, t=1.62, p=0.14, t=1.70, p=0.12, and t=1.09, p=0.30, respectively).”

• Methods & Results: The authors make a few unproven claims, such as saying "generally, the position, order of finger preference, and extent of the hand maps were qualitatively similar between patients and control". There are no data to support these claims.

As indicated in this sentence, this claim substantiated a qualitative inspection of the finger maps in Figure 2 and we indeed do not support this claim with quantitative analysis. We have therefore removed this sentence from the revised manuscript and instead say, as per the suggestion of reviewer 1, that overall, there were aspects of somatotopic finger selectivity in the SCI patients’ hand maps,

Revised text Results:

“Overall, we found aspects of somatotopic finger selectivity in the maps of SCI patients’ hands, in which neighbouring clusters showed selectivity for neighbouring fingers in contralateral S1, similar to those observed in eighteen age-, sex-, and handedness matched healthy controls (see Figure 2A&B). A characteristic hand map shows a gradient of finger preference, progressing from the thumb (red, laterally) to the little finger (pink, medially). Notably, a characteristic hand map was even found in a patient who suffered complete paralysis and sensory deprivation of the hands (Figure 2. patient map 1; patient S01). Despite most maps (Figure 2, except patient map 3) displaying aspects of characteristic finger selectivity, some finger representations were not visible in the thresholded patient and control maps.”

• Methods & Results: The authors argue that the map architecture is topographic as soon as the dissimilarity between two different fingers is above 0. First, what I am really wondering about is why the authors do not provide the exact dissimilarity values in the text but only give the stats for the difference to 0 (t-value, p-value, Bayes factor). Were the dissimilarity values perhaps very low? The values should be reported. Also, when this argument that maps are topographic as long as the value of two different fingers is above 0 should hold, then the authors have to show that the value for mapping the SAME finger is indeed 0. Otherwise, this argument is not convincing.

We would like to clarify that a representation is not per se topographic when the RSA dissimilarity is > 0. The dissimilarity value provided by RSA indicates the extent to which a pair of conditions is distinguished – it can be viewed as encapsulating the information content carried by the region (Kriegeskorte et al., 2008). Due to cross-validation across runs, the expected distance value would be zero (but can go below 0) if two conditions’ activity patterns are not statistically different from each other, and larger than zero if there is differentiation between the conditions (fingers’ activity patterns in the S1 hand area in our case; Kriegeskorte et al., 2008; Nili et al., 2014). The diagonal of the RDM reflect comparisons between the same fingers and therefore reflect distances between the exact same activity pattern in the same run and are thus 0 by definition (Kriegeskorte et al., 2008; Nili et al., 2014). This was also the case in our individual participant RDMs. Since this is not a meaningful value (a distance between 2 identical activity patterns will always be 0) we chose not to report this. We have clarified the meaning of the separability measure in the revised Methods section.

To investigate whether a representation is somatotopic, we have to take into account the full fine-grained inter-finger distance pattern. The full fine-grained inter-finger distance pattern is related to everyday use of our hand and has been shown to depict the invariant representational structure of fingers better than the size, shape, and exact location of the areas activated by finger movements (Ejaz et al., 2015). To determine whether a participant’s inter-finger distance pattern is somatotopic one should associate it to a canonical RDM – which is done in the typicality analysis (see also our response to comment 2.6).

What can be done to demonstrate the validity of an ROI, is to run RSA on a control ROI where one would not expect to find activity that is distinguishable between finger conditions. Rather than comparing your separability measure against 0, one can then compare the separability of your ROI that is expected to contain this information to that of your control ROI. We created a cerebral spinal fluid (CSF) ROI, repeated our RSA analysis in this ROI, and then compared the separability of the CSF and S1 hand area ROIs. As expected, there was a significant difference between separability (or representation strength) in the S1 hand area and CSF ROIs for both controls (W=171, p < 0.001; BF10=4059) and patients (W=105, p < 0.00; BF10=279). This analysis has been added to the revised manuscript.

Individual participant separability values (i.e., distances averaged across fingers) are visualised in Figure 3D. Following the reviewer’s suggestion, we have included individual participant inter-finger distance plots for both the controls and SCI patients as Figure 3- Figure supplement 2 and Figure 3- figure supplement 3, respectively. The inter-finger distances for each finger pair and subject can be extracted from this. We feel this is more readily readable and interpretable than a table containing the 10 inter-finger distance scores for all 32 participants. These values have instead been made available online, together with our other data, on https://osf.io/e8u95/.

Revised text Methods:

“If there is no information in the ROI that can statistically distinguish between the finger conditions, then due to cross-validation the expected distance measure would be 0. If there is differentiation between the finger conditions, the separability would be larger than 0 (Nili et al., 2014). Note that this does not directly indicate that this region contains topographic information, but rather that this ROI contains information that can distinguish between the finger conditions. To further ensure that our S1 hand ROI was activated distinctly for different fingers, we created a cerebral spinal fluid (CSF) ROI that would not contain finger specific information. We then repeated our RSA analysis in this ROI and statistically compared the separability of the CSF and S1 hand area ROIs.”

Revised text Results:

“We found that inter-finger separability in the S1 hand area was greater than 0 for patients (t(13) = 9.83, p < 0.001; BF10 = 6.77e +4) and controls (t(17) = 11.70, p < 0.001; BF10 = 6.92e +6), indicating that the S1 hand area in both groups contained information about individuated finger representations. Furthermore, for both controls (W = 171, p < 0.001; BF10 = 4059) and patients (W = 105, p < 0.001; BF10 = 279) there was significant greater separability (or representation strength) in the S1 hand area than in a control cerebral spinal fluid ROI that would not be expected to contain finger specific information. We did not find a significant group difference in inter-finger separability of the S1 hand area (t(30) = 1.52, p = 0.14; BF10 = 0.81), with the BF showing anecdotal evidence in favour of the null hypothesis.”

• Discussion. The authors argue that spared midsagittal spinal tissue bridges are not necessary because they were not predictive of hand representation typicality. First, the measure of typicality is questionable and should not be used to make general claims about the importance of structural differences. Second, given there were only n=14 patients included, one may question generally whether predictive modelling can be done with these data. This statement should therefore be removed.

We would like to clarify that, like the reviewer, we do not believe that spared midsagittal spinal tissue bridges are unimportant. Indeed, a large body of our own research focuses on the importance of spared spinal tissue bridges in recovery of sensorimotor function and pain (Huber et al., 2017; Pfyffer et al., 2021, 2019; Vallotton et al., 2019). We have added a clarification sentence regarding the importance of tissue bridges with regards to recovery of function. We agree with the reviewer that given our limited sample size, it is difficult to make conclusive claims based on non-significant predictive modelling and correlational results. In the revised manuscript we therefore focus this statement (i.e., that sensory and motor hand function and tissue bridges are not necessary to preserve hand somatotopy) on our finding that two patients without spared tissue bridges at the lesion level and with complete or near complete loss of sensory and motor hand function had a highly typical hand representation. We present our predictive modelling results as being in line with this notion and added a word of caution that it is challenging to draw definite conclusions from non-significant predictive modelling and correlation results in such a limited sample size.

With regards to the reviewer’s concern about the validity of the typicality measure – please see our detailed response to comment 2.6.

Revised text Discussion:

“Spared spinal cord tissue bridges can be found in most patients with a clinically incomplete injury, their width being predictive of electrophysiological information flow, recovery of sensorimotor function, and neuropathic pain (Huber et al., 2017; Pfyffer et al., 2021, 2019; Vallotton et al., 2019). However, in this study, spared midsagittal spinal tissue bridges at the lesion level and sensorimotor hand function did not seem necessary to maintain and activate a somatotopic hand representation in S1. We found a highly typical hand representation in two patients (S01 and S03) who did not have any spared spinal tissue bridges at the lesion level, a complete (S01) or near complete (S03) hand paralysis, and a complete (S01) or near complete loss (S03) of hand sensory function. Our predictive modelling results were in line with this notion and showed that these behavioural and structural spinal cord determinants were not predictive of hand representation typicality. Note however that our sample size was limited, and it is challenging to draw definite conclusions from non-significant predictive modelling results.”

• Discussion. The authors say that hand representation is "preserved" in SCI patients. Perhaps it is better to be precise and to say that they active during movement planning.

We thank the reviewer for their suggestion and revised the Discussion accordingly.

Revised text Discussion:

"In this study we investigated whether hand somatotopy is preserved and can be activated through attempted movements following tetraplegia."

"How may these representations be preserved over time and activated through attempted movements in the absence of peripheral information?"

"Together, our findings indicate that in the first years after a tetraplegia, the somatotopic S1 hand representation is preserved and can be activated through attempted movements even in the absence of retained sensory function, motor function, and spared spinal tissue bridges."

Reviewer #3:

The demonstration that cortex associated with an amputated limb can be activated by other body parts after amputation has been interpreted as evidence that the deafferented cortex "reorganizes" and assumes a new function. However, other studies suggest that the somatotopic organization of somatosensory cortex in amputees is relatively spared, even when probed long after amputation. One possibility is that the stability is due to residual peripheral input. In this study, Kikkert et al. examine the somatotopic organization of somatosensory cortex in patients whose spinal cord injury has led to tetraplegia. They find that the somatotopic organization of the hand representation of somatosensory cortex is relatively spared in these patients. Surprisingly, the amount of spared sensorimotor function is a poor predictor of the stability of the patients' hand somatotopy. Nonethless, the hand representation deteriorates over decades after the injury. These findings contribute to a developing story on how sensory representations are formed and maintained and provide a counterpoint to extreme interpretations of the "reorganization" hypothesis mentioned above. Furthermore, the stability of body maps in somatosensory cortex after spinal cord injury has implications for the development of brain-machine interfaces.

I have only minor comments:

1) Given the controversy in the field, the use of the phrase "take over the deprived territory" (line 45) is muddled. Perhaps a more nuanced exposition of this phenomenon is in order?

We agree a more nuanced expression would be more appropriate. We have changed this sentence accordingly in the revised manuscript.

Revised text Introduction:

“Seminal research in nonhuman primate models of SCI has shown that this leads to extensive cortical reorganisation, such that tactile stimulation of cortically adjacent body parts (e.g. of the face) activated the deprived brain territory (e.g. of the hand; Halder et al., 2018; Jain et al., 2008; Kambi et al., 2014).”

2) The statement that "results are mixed" regarding intracortical microstimulation of S1 is dubious. In only one case has the hand representation been mislocalized, out of many cases (several at CalTech, 3 at the University of Pittsburgh, one at Case Western, one at Hopkins/APL, and one at UChicago). Perhaps rephrase to "with one exception?"

We agree that this sentence may give a wrong outlook on the literature and have changed the text per the reviewer’s suggestion.

Revised text Introduction:

“Case studies using intracortical stimulation in the S1 hand area to elicit finger sensations in SCI patients hint at such preserved somatotopic representations (Fifer et al., 2020; Flesher et al., 2016), with one exception (Armenta Salas et al., 2018).”

3) The phrase "tetraplegic sinal cord injury" seems awkward.

Thank you for highlighting this to us. We have corrected these instances in our revised manuscript to “tetraplegia”.

4) The stability of the representation is attributed to efference copy from M1. While this is a fine speculation, somatosensory cortex is part of a circuit and is interconnected with many other brain areas, M1 being one. Perhaps the stability is maintained due to the position of somatosensory cortex within this circuit, and not solely by its relationship with M1? There seems to be an overemphasis of this hypothesis at the exclusion of others.

Thank you for this comment. We agree we overemphasized the efference copy theory. We have adjusted this and now provide a more balanced description of potential circuits and interconnections that could maintain somatotopic representations after tetraplegia.

Author Response:

Reviewer #1 (Public Review):

In this report, Shekhar et al, have profiled developing retinal ganglion cells from embryonic and postnatal mouse retina to explore the diversification of this class of neurons into specific subtypes. In mature retina, scRNAseq and other methods have defined approximately 45 different subtypes of RGCs, and the authors ask whether these arise from a common postmitotic precursor, or many ditinct subtypes of precursors. The overall message, is that subtype diversification arises as a "gradual, asynchronus fate restriction of postmitotic multipotential precursors. The authors find that over time, clusters of cells become "decoupled" as they split into subclusters. This process of fate decoupling is associated with changes in the expression of specific transcription factors. This allows them to both predict lineage relationships among RGC subtypes and the time during development when these specification events occur. Although this conclusion based almost entirely on a computational analysis of the relationships among cells sampled at discrete times, the evidence presented supports the overall conclusion. Future experimental validation of the proposed lineage relationships of RGC subtypes will be needed, but this report clearly outlines the overall pattern of diversification in this cell class.

We thank the reviewer for their thoughtful assessment of our study.

Reviewer #2 (Public Review):

The manuscript "Diversification of multipotential postmitotic mouse retinal ganglion cell precursors into discrete types" by Shekhar and colleagues represents an in-depth analysis of an additional transcriptomic datasets of retinal single-cells. It explores the progression of retinal ganglion cells diversity during development and describes some of aspects of fate acquisition in these postmitotic neurons. Altogether the findings provide another resource on which the neural development community will be able to generate new hypotheses in the field of retinal ganglion cell differentiation. A key point that is made by the authors regards the progression of the number of ganglion cell types in the mouse retina, i.e., how, and when neuronal "classes diversify into subclasses and types" (also p. 125). In particular, the authors would like to address whether postmitotic neurons follow either a predetermination or a stepwise progression (Fig. 2a). This is indeed a fascinating question, and the analysis, including the one based on the Waddington-OT method is conceptually interesting.

Comments and questions:

Is the transcriptomic diversity, based on highly variable genes (the number of which is not detailed in the study) a robust proxy to assess cell types? One could argue that early on predetermined cell types are specified by a small set of determinants, both at the proteomic and transcriptomic level, and that it takes several days or week to generate the cascade that allows the detection of transcriptional diversity at the level of >100 gene expression levels.

We had tested the dependence of our results on the number of highly variable genes (HVGs) used. This analysis, shown in Figure 2h, demonstrates that results are robust over the range tested – 1244-3003 total HVGs. Since the analysis in the paper employs 2800 HVGs (~800- 1500 at each stage), we are confident that we are in comfortable excess of the number at which we would need to worry. We have expanded the discussion to avoid confusion on this point. We also address the possibility that a small set of determinants are sufficient to define cell state in a transcriptomic study. This is a common argument, but we believe it is a tenuous one. We believe that the only way a small number of genes can truly define cell state is if they are expressed at very high levels. If these are expressed at high levels, they should be detected in our data and should drive the clustering. If they are expressed at extremely low levels, then given the nature of molecular fluctuations in cells, they cannot be expected to serve as a stable scaffold for differentiation. Indeed, a small set of determinants (usually transcription factors) may be necessary to specify a cell type. However, sufficiency of specification requires the expression of a usually much larger of number downstream regulators.

Since there are many RGC subsets (45) that share a great number of their gene expression, is it possible that a given RGC could transition from one subset to another between P5 and P56? Or even responding to a state linked to sustained activity? Was this possibility tested in the model?

We cannot address the possibility that cells swap types postnatally so that the cells comprising type X at P5 are not the same ones that comprise type X at P56. It does seem pretty unlikely, as the cell types are well-separated in transcriptional space (~250 DE genes on average). Regarding activity, we have made some initial tests by preventing visually evoked activity from birth to P56 in three different ways (dark-rearing and two mutant lines). We find no statistically significant effect on diversification. These results are currently being prepared for publication.

The authors state that early during development there is less diversity than later. This statement seems obvious but how much. Can this be due to differential differentiation stage? At E16 RGC are a mix of cells born from E11 to E16, with the latter barely located in the GCL. Does this tend to show a continuum that is may be probably lost when the analysis is performed on cells isolated a long time after they were born (postnatal stages)? Alternatively, would it be possible to compare RGC that have been label with birth dating methods?

Regarding the amount of diversification, we quantified this using the Rao diversity index (Figure 2h), which suggests an overall increase in 2-fold transcriptional diversity at P56 compared to the early stages. The continuum is likely because cells at early stage are close to the precursor stage and not very differentiated. Regarding combining RNA-seq with birthdating, although elegant methods now make this combination possible, it falls beyond the scope of this study.

Comparing data produced by different methods can be challenging. Here the authors compared transcriptomic diversity between embryonic dataset produced with 10X genomics (E13 to P0) and, on the other hand, postnatal P5 that were produced using a different drop-seq procedure). Is it possible to control that the differences observed are not due to the different methods?

It is correct that most of the P5 data was produced using Drop-seq, but that dataset also includes transcriptomes obtained by the 10X method. The relative frequency of RGC clusters and the average gene expression values obtained using either method was highly correlated (Reviewer Fig. 1). This is now pointed out in the “Methods.”

Reviewer Fig. 1. Comparison between the relative frequency of types (left) and the average gene expression levels (right) at P5 between 10X data (y-axis) and Drop-seq data (x-axis). R corresponds to the Pearson correlation coefficient. The axes are plotted in the logarithmic scale.

It might be important to control the conclusion that diversity is lower at E13 vs P5 when we see that thrice less cells (5900 vs 180000) were analyzed at early stage (BrdU, EdU, CFSE...)? A simple downsampling prior to the analysis may help.

Although we collected different numbers of cells at different ages, we noted in the text that they do not influence the number of clusters. Regarding P5 specifically, Rheaume et al. (who we now discuss) obtained very similar results to ours with only 6000 cells (3x lower).

Ipsilateral RGC: It is striking that the DEG between C-RGC and I-RGC reflect a strong bias with cells scored as" ipsi" are immature RGC while the other ("contra") are much more mature. This bias comes from the way ipsilateral RGC were "inferred" using non-specific markers. Can the author try again the analysis by identifying RGC using more robust markers? (eg. EphB1). Would it be possible to select I-RGC and C-RGC that share same level of differentiation? Previous studies already identified I-RGC signature using more specific set-up (Wang et al., 2016 from retrogradely labelled RGC; Lo Giudice et al., 2019 with I-RGC specific transgenic mouse).

We are not sure how the reviewer concludes that the putative I-RGCs are more immature than the putative C-RGCs. As discussed earlier, insofar as expression levels of pan-RGC markers are indicative of maturational stage, we found no evidence that clustering is driven by maturation gradients. Thus, we expect our putative I-RGCs and C-RGCs to not differ in differentiation state. Following the reviewer’s suggestion, we now include EphB1(Ephb1) in our I-RGC signature. The impact of replacing Igfbp5 with Ephb1 on the inferred proportion of I-RGCs within each terminal type was minimal (Reviewer Fig. 2). We would like to note that to assemble our IRGC/C-RGC signatures we relied on data presented Wang et al. (2016). Outside of wellestablished markers (e.g. Zic2, and Isl2), we chose the RNA-seq hits in Wang et al. that had been validated histologically in the same paper or that are correlated with Zic2 expression in our data. This nominated Igfbp5, Zic1, Fgf12, and Igf1.

Reviewer Fig. 2. Comparison of inferred I-RGC frequency within each terminal type (points) using two I-RGC signature reported in the paper. For the y-axis we used Zic2 and EphB1.

It would be important to discuss how their findings differs from the others (including Rheaume et al., 2018). To make a strong point, I-RGC shall be isolated at a stage of final maturation (P5?) and using retrograde labelling, which is a robust method to ensure the ipsilateral identity of postnatal RGCs.

We cite Rheaume et al. in several places. In fact, there is good transcriptional correspondence between our dataset and theirs (Figure S1i), despite the differences in the number of cells profiled (~6000 vs ~18000) and technologies (10X vs. Drop-seq/10X). We now mention this is the text. Note also that we had compared our P56 data with Rheaume et al.’s, P5 data in an earlier publication (Tran et al., 2019) and observed a similar tight correspondence between clusters. Zic1 is expressed in I-RGCs (Wang et al., 2016) at early stages, and in our dataset its expression at E13 and E14 is similar to that of Zic2 (Supplementary Fig. 8); Postnatally, however, it marks W3B RGCs (Tran et al., 2019), many of which project contralaterally (Kim et al., J. Neurosci. 2010). Regarding retrograde labeling, as noted above, additional experiments would take a prohibitively long time (up to a year) to complete.

It is unclear how good Zic1 and Igf1 can be used as I-RGC marker. Can the author specify how specific to I-RGC they are? Have they been confirmed as marker using retrograde labelling experiments?

We have relied on previous work, primarily from the Mason lab, to choose I-RGC and C-RGC markers. Igf1 is a C-RGC marker that is expressed in a complementary fashion with Igfbp5, an I-RGC marker as noted in Wang et al, 2016. They also perform ISH to show that Igf1 is not expressed in the VT crescent, while Igfbp5 is (see Fig. 5 in Wang et al., 2016). Similarly, Zic1 is also cited in Wang et al. as an RNA-seq hit for I-RGCs. Although Zic1 was not validated using ISH, we found its expression pattern to be highly correlated with Zic2 at E13 (Supplementary Fig. 8c).

The enrichment procedure may deplete the RGC subpopulation that express low levels of Thy1 or L1CAM. A comparison on that point could be done with the other datasets analysed in the study.

We presume the reviewer is referring to the data of Lo Guidice and Clark/Blackshaw, which we show in comparison to ours in Figure S1. In both of those studies, all retinal cells were analyzed, whereas we enriched RGCs. As noted in the text, RGCs comprise a very small fraction of all retinal cells, so Lo Giudice and Clark/Blackshaw lacked the resolution to resolve RGC diversity at later time points. Indeed, there is no whole retina dataset available in which RGCs are numerous enough for comprehensive subtyping. Our approach to this issue was to collect RGCs with both Thy1 and L1 at E13, E14, E16 and P0, with the idea that the markers might have complementary strengths and weaknesses. In fact, at each age, all clusters are present in both collection types, although frequencies vary. This concordance supports the idea that neither marker excludes particular types. We now stress this point in results and in the Supplementary Fig. 2 legend.

In supplemental Fig. S1e: why are cells embedded from "Clark" datasets only clusters on the right side of the UMAP while the others are more evenly distributed?

Actually, both the Clark et al. and Lo Giudice et al. datasets are predominantly clustered on the right side of the UMAP. This reflects the methodological difference noted above: they profiled the whole retina, whereas we isolated RGCs. Thus, their datasets contain a much higher abundance of RPCs and non-neurogenic precursors compared to ours. The right clusters represent RPCs due to their expression of Fgf15 and other markers, while the left clusters represent RGCs based on their expression of Nefl. Indeed, a main reason for including these plots was to illustrate the relative abundance of RGCs in our data (also see Supplementary Fig. S1h).

What could explain that CD90 and L1CAM population are intermingled at E14, distinct at E16, and then more mixed at P0?

We believe the reviewer is referring to Supplementary Figs. S2a-c. Given the temporal expression level changes in Thy1 and L1cam (Supplementary Fig. S1c) in RGCs, a likely possibility is that they enrich RGC precursor subsets at different relative frequencies. We now note this in the Supplementary Fig. 2 legend.

On Fig. 6: the E13 RGC seems to be segregated in early born RGC expressing Eomes and later born expressing neurod2. Thus, fare coupling with P5 seems to suggest that Eomes population at P5 may have been generated first, and Neurod2 generated later. Is that possible?

That the Eomes RGCs are specified before Neurod2 RGCs is one of our conclusions from the fate decoupling analysis (Figures 6f-h). Whether this is because the former arise from early born cells and the latter arise from later born cells is not clear. There is disagreement in the literature on whether ipRGCs are born at a different time than other RGCs, so we prefer not to make a comment.

Methods: The Methods section is extensive, and yet it is presented in a rather complex manner so that it is difficult to understand for a broad audience. It would be valuable if the authors could simplify or better explain some parts (the WOT section in particular).

We believe that the sections on animals, molecular biology and histology are quite straightforward, but agree that the sections describing the computational analysis are hard going. We have modified them in several places as requested. As regards better explanation of the WOT, we now precede that section with an “overview” as a way of making it easier to follow. (We had already included an overview of the clustering procedures.) We have also provided further detail on some of the reviewer’s subsequent questions on this section, including the use of HVGs, the Classifier, and the strategy for inferring I-RGCs (see below). Perhaps most important, we have worked to make the “Results” and “Discussion” sections accessible to a broad audience.

*Highly variable genes (HVG) used for clustering and dimensionality reduction: how many of them and what are they? Are they the same used for each stage?

Since clustering was performed at each stage independently, we determined HVGs at each stage separately using a statistical method introduced in one of our previous studies (Pandey et al., Current Biology, 2018). The total number of HVGs at each stage were as follows: E13: N=1094 E14: N=834 E16: N=822 P0: N=881 P5: N=1105 P56: N=1510

We note that these are not necessarily the same at each stage due to the temporal variation in gene expression. Together these correspond to 2854 unique genes (union of all HVGs). The WOT analysis was done using this full set.

*In the methods p9: "The common features G = GR ∩ GT are used to train a third classifier ClassR on the reference atlas AR. This ensures that inferred transcriptomic correspondences are based on "core" gene expression programs that underlie cell type identity rather than maturation-associated genes." Could the authors explain the relevance of using a third model and, more importantly, is there any genes that eliminated through the procedure that could be important to drive the diversification process? If so, would it be possible to estimate their number and the relative impact?

The rationale for this was as follows. Our goal is to map cells from one time point to a type at another time point. The naïve way to do this would be to use a classifier trained entirely at either of the time point. However, the features of such a classifier is likely to contain genes that are not expressed at the earlier time point, and likely to generate spurious mappings (since the set of cluster specific genes are not identical). Therefore, we sought to train a classifier that is trained using genes that are part of conserved transcriptional signatures at both time points, which corresponds to the third model.

When this filtering was not performed, the temporal correspondences in the supervised classification model were less specific than those reported. In particular, ARI values dropped by about 15% on average. The simple reason for this is that a cluster specific gene at E13 (for e.g.) may no longer be expressed at E14, and vice-versa. Thus, by restricting the features to a common set of cluster specific genes, we obtained the “best possible” transcriptomic correspondences between clusters at consecutive time points. We note that the correspondences obtained in this way (Figure 3) were recovered through WOT when the results of the latter were collapsed at the cluster level (Supplementary Fig. 5).

*Methods page 15: Inference of ipsilaterally-projecting RGC types. Wouldn't it be more valuable to consider more markers to distinguish RGC precursors?

As indicated before, we used I-RGC genes and C-RGC genes reported in Wang et al., 2016 (Table 2), in addition to the well-known markers Zic2 and Isl2. Here, we prioritized genes that had been histologically validated (Figs. 4 and 5), which were expressed in our data (Sema3e and Tbx20 were not considered as these undetectable at E13 in our data). Following the reviewer’s earlier suggestion, we also noted that including Ephb1 in our signature minimally impacts the results.

Discussion: *Is there somewhat a plasticity that allow the RGC subgroups to switch over time? (IF we were to record the transcriptome of the same cell over time, will one observe that the cell belong to another cluster / subgroup?

One can only speculate. Other than long-term in vivo imaging combined with vital type-specific markers we know of no way to experimentally address the possibility that cells swap types postnatally so that the cells comprising type x at P5 are not the same ones that comprise type x at P56. It does seem pretty unlikely though.

*While the data appears technically rigorous, and the number of cells sequenced very high, the results seem redundant with several prior studies and the discrepancies are not sufficiently discussed.

We are confused by this point, since the reviewer does not cite the papers to which s/he refers. To our knowledge there is no study at present that has described RGC diversification, so it is not clear what would be discrepant.

Author Response

Reviewer #1 (Public Review):

It is well established that valuation and value-based decision-making is context-dependent. This manuscript presents the results of six behavioral experiments specifically designed to disentangle two prominent functional forms of value normalization during reward learning: divisive normalization and range normalization. The behavioral and modeling results are clear and convincing, showing that key features of choice behavior in the current setting are incompatible with divisive normalization but are well predicted by a non-linear transformation of range-normalized values.

Overall, this is an excellent study with important implications for reinforcement learning and decision-making research. The manuscript could be strengthened by examining individual variability in value normalization, as outlined below.

We thank the Reviewer for the positive appreciation of our work and for the very relevant suggestions. Please find our point-by-point answer below.

There is a lot of individual variation in the choice data that may potentially be explained by individual differences in normalization strategies. It would be important to examine whether there are any subgroups of subjects whose behavior is better explained by a divisive vs. range normalization process. Alternatively, it may be possible to compute an index that captures how much a given subject displays behavior compatible with divisive vs. range normalization. Seeing the distribution of such an index could provide insights into individual differences in normalization strategies.

Thank you for pointing this out, it is indeed true that there is some variability. To address this, and in line with the Reviewer’s suggestion, we extracted model attributions per participant on the individual out-of-sample log-likelihood, using the VBA_toolbox in Matlab (Daunizeau et al., 2014). In experiment 1 (presented in the main text), we found that the RANGE model accounted for 79% of the participants, while the DIVISIVE model accounted for 12%. The relative difference was even higher when including the RANGEω model in the model space: the RANGE and RANGEω models account for a total of 85% of the participants, while the DIVISIVE model accounted only for 5%.

In experiment 2 (presented in the supplementary materials), the results were comparable (see Figure 3-figure supplement 3: 73% vs 10%, 83% vs 2%).

To provide further insights into the behavioral signatures behind inter-individual differences, we plotted the transfer choice rates for each group of participants (best explained by the RANGE, DIVISIVE, or UNBIASED models), and the results are similar to our model predictions from Figure 1C:

Author Response Image 1. Behavioral data in the transfer phase, split over participants best explained by the RANGE (left), DIVISIVE (middle) or UNBIASED (right) model in experiment 1 (A) and experiment 2 (B) (versions a, b and c were pooled together).

To keep things concise, we did not include this last figure in the revised manuscript, but it will be available for the interested readers in the Rebuttal letter.

One possibility currently not considered by the authors is that both forms of value normalization are at work at the same time. It would be interesting to see the results from a hybrid model. R1.2 Thank you for the suggestion, we fitted and simulated a hybrid model as a weighted sum between both forms of normalization:

First, the HYBRID model quantitatively wins over the DIVISIVE model (oosLLHYB vs oosLLDIV : t(149)=10.19, p<.0001, d=0.41) but not over the RANGE model, which produced a marginally higher log-likelihood (oosLLHYB vs oosLLRAN : t(149)=-1.82, p=.07, d=-0.008). Second, model simulations also suggest that the model would predict a very similar (if not worse) behavior compared to the RANGE model (see figure below). This is supported by the distribution of the weight parameter over our participants: it appears that, consistently with the model attributions presented above, most participants are best explained by a range-normalization rule (weight > 0.5, 87% of the participants, see figure below). Together, these results favor the RANGE model over the DIVISIVE model in our task.

Out of curiosity, we also implemented a hybrid model as a weighted sum between absolute (UNBIASED model) and relative (RANGE model) valuations:

Model fitting, simulations and comparisons slightly favored this hybrid model over the UNBIASED model (oosLLHYB vs oosLLUNB: t(149)=2.63, p=.0094, d=0.15), but also drastically favored the range normalization account (oosLLHYB vs oosLLRAN : t(149)=-3.80, p=.00021, d=-0.40, see Author Response Image 2).

Author Response Image 2. Model simulations in the transfer phase for the RANGE model (left) and the HYBRID model (middle) defined as a weighted sum between divisive and range forms of normalization (top) and between unbiased (no normalization) and range normalization (bottom). The HYBRID model features an additional weight parameter, whose distribution favors the range normalization rule (right).

To keep things concise, we did not include this last figure in the revised manuscript, but it will be available for the interested readers in the Rebuttal letter.

Reviewer #2 (Public Review):

This paper studies how relative values are encoded in a learning task, and how they are subsequently used to make a decision. This is a topic that integrates multiple disciplines (psych, neuro, economics) and has generated significant interest. The experimental setting is based on previous work from this research team that has advanced the field's understanding of value coding in learning tasks. These experiments are well-designed to distinguish some predictions of different accounts for value encoding. However there is an additional treatment that would provide an additional (strong) test of these theories: RN would make an equivalent set of predictions if the range were equivalently adjusted downward instead (for example by adding a "68" option to "50" and "86", and then comparing to WB and WT). The predictions of DN would differ however because adding a low-value alternative to the normalization would not change it much. Would the behaviour of subjects be symmetric for equivalent ranges, as RN predicts? If so this would be a compelling result, because symmetry is a very strong theoretical assumption in this setting.

We thank the Reviewer for the overall positive appraisal concerning our work, but also for the stimulating and constructive remarks that we have addressed below. At this stage, we just wanted to mention that we also agree with the Reviewer concerning the fact that a design where we add "68" option to "50" and "86" would represent also an important test of our hypotheses. This is why we had, in fact, run this experiment. Unfortunately, their results were somehow buried in the Supplementary Materials of our original submission and not correctly highlighted in the main text. We modified the manuscript in order to make them more visible:

Behavioral results in three experiments (N=50 each) featuring a slightly different design, where we added a mid value option (NT68) between NT50 and NT87 converge to the same broad conclusion: the behavioral pattern in the transfer phase is largely incompatible with that predicted by outcome divisive normalization during the learning phase (Figure 2-figure supplement 2).

Reviewer #3 (Public Review):

Bavard & Palminteri extend their research program by devising a task that enables them to disassociate two types of normalisation: range normalisation (by which outcomes are normalised by the min and max of the options) and divisive normalisation (in which outcomes are normalised by the average of the options in ones context). By providing 4 different training contexts in which the range of outcomes and number of options vary, they successfully show using 'ex ante' simulations that different learning approaches during training (unbiased, divisive, range) should lead to different patterns of choice in a subsequent probe phase during which all options from the training are paired with one another generating novel choice pairings. These patterns are somewhat subtle but are elegantly unpacked. They then fit participants' training choices to different learning models and test how well these models predict probe phase choices. They find evidence - both in terms of quantitive (i.e. comparing out-of-sample log-likelihood scores) and qualitative (comparing the pattern of choices observed to the pattern that would be observed under each mode) fit - for the range model. This fit is further improved by adding a power parameter which suggests that alongside being relativised via range normalisation, outcomes were also transformed non-linearly.

I thought this approach to address their research question was really successful and the methods and results were strong, credible, and robust (owing to the number of experiments conducted, the design used and combination of approaches used). I do not think the paper has any major weaknesses. The paper is very clear and well-written which aids interpretability.

This is an important topic for understanding, predicting, and improving behaviour in a range of domains potentially. The findings will be of interest to researchers in interdisciplinary fields such as neuroeconomics and behavioural economics as well as reinforcement learning and cognitive psychology.

We thank Prof. Garrett for his positive evaluation and supportive attitude.

Author Response

Reviewer #1 (Public Review):

In this paper, Fernandes et al. take advantage of synthetic constructs to test how Bicoid (Bcd) activates its downstream target Hunchback (Hb). They explore synthetic constructs containing only Bcd, Bcd and Hb, and Bcd and Zelda binding sites. They use these to develop theoretical models for how Bcd drives Hb in the early embryo. They show that Hb sites alone are insufficient to drive further Hb expression.

The paper's first half focuses on how well the synthetic constructs replicate the in vivo expression of hb. This approach is generally convincing, and the results are interesting. Consistent with previous work, they show that Bcd alone is sufficient to drive an expression profile that is similar to wild‐type, but the addition of Hb and Zelda are needed to generate precise and rapid formation of the boundaries. The experimental results are supported by modelling. The model does a nice job of encapsulating the key conclusions and clearly adds value to the analysis.

In the second part of the paper, the authors use their synthetic approach to look at how the Hb boundary alters depending on Bcd dosage. This part asks whether the observed Bcd gradient is the same as the activity gradient of Bcd (i.e. the "active" part of Bcd is not a priori the same as the protein gradient). This is a very interesting problem and good the authors have tried to tackle this. However, the strength of their conclusions needs to be substantially tempered as they rely on an overestimation of the Bcd gradient decay length.

Comments:

‐ My major concern regards the conclusions for the final section on the activity gradient. In the Introduction it is stated: "[the Bcd gradient has] an exponential AP gradient with a decay length of L ~ 20% egg‐length (EL)". While this was the initial estimate (Houchmandzadeh et al., Nature 2002), later measurements by the Gregor lab (see Supplementary Material of Liu et al., PNAS 2013) found that "The mean length constant was reduced to 16.5 ± 0.7%EL after corrections for EGFP maturation". The original measurements by Houchmandzadeh et al. had issues with background control, that also led to the longer measured decay length. In later work, Durrieu et al., Mol Sys Biol 2018, found a similar scale for the decay length to Liu et al. Looking at Figure 5, a value of 16.5%EL for the decay length is fully consistent with the activity and protein gradients for Bcd being similar. In short, the strength of the conclusions clearly does not match the known gradient and should be substantially toned down.

The reviewer is right: several studies aiming to quantitatively measure the Bicoid protein gradient ended‐up with quite different decay lengths.

A summary of the various decay lengths measured, and the method used for these measurements is given below:

As indicated, these measurements are quite variable among the different studies and the differences can potentially be attributed to different methods of detection (antibody staining on fixed samples vs fluorescent measurements on live sample) or to the type of protein detected (endogenous Bicoid vs fluorescently tagged).

We agree with the reviewer that given these discrepancies, the exact value of the Bcd protein gradient decay length is not known and that we only have measurements that put it in between 16 and 25 % EL (see the Table above). Therefore, we agree that we should tone down the difference between the protein vs activity gradient and focus on the measurements of the effective activity gradient decay length allowed by our synthetic reporters. This allows us to revisit the measurement of the Hill coefficient of the transcription step‐like response, which is based on the decay‐length for the Bcd protein gradient, and assumed in previous published work to be of 20% EL (Gregor et al., Cell, 2007a; Estrada et al., 2016; Tran et al., PLoS CB, 2018). Importantly, the new Hill coefficient allows us to set the Bcd system within the limits of an equilibrium model.

As mentioned by the reviewer, it is possible that the decay length of the protein gradient measured using antibody staining (Houchmandzadeh et al,, Nature, 2002) was not correct due to background controls. Such measurements were also performed in Xu et al. (2015) which agree with the original measurements (Houchmandzadeh et al., Nature 2002). As indicated in the table above, all the other measurements of the Bcd protein gradient decay length were done using fluorescently tagged Bcd proteins and we cannot exclude the possibility the wt vs tagged protein might have different decay lengths due to potentially different diffusion coefficients or half‐lives. Before drawing any conclusion on the exact value of the endogenous Bcd protein gradient decay length, it is essential to measure it again in conditions that correct for the background issues for immuno‐staining as it was done in Liu et al., PNAS, 2013 for the Bcd‐eGFP protein. In this study, the authors only measured the decay length of the Bcd fusion protein using immuno‐staining for the Bcd protein. Unfortunately, in this study, the authors did not measure again the decay length of the endogenous Bcd protein gradient using immuno‐staining and the same procedure for background control. Therefore, they do not firmly exclude the possibility that the endogenous vs tagged Bcd proteins might have different decay length.

We thank the reviewer for his comment which helped us to clarify the message. In addition, as there is clearly an issue for the measurements of the Bcd protein gradient, we added a section in the SI (Section E) and a Table (Table S4) describing the various decay length measured for the Bcd or the Bcd‐fluorescently tagged protein gradients from previous studies. In the discussion, together with the possibility that there might be a protein vs activity gradient (as we originally proposed and believe is still a valid possibility), we also discuss the alternative possibility proposed by the reviewer which is that the protein vs activity gradients have the same decay lengths but that the decay length of the Bcd protein gradient was potentially not correctly evaluated.

‐ All of the experiments are performed in a background with the hb gene present. Does this impact on the readout, as the synthetic lines are essentially competing with the wild‐type genes? What controls were done to account for this?

We agree with the reviewer that this concern might be particularly relevant at the hb boundary where a nucleus has been shown to only contain ~ 700 Bicoid molecules (Gregor et al., Cell, 2007b). However, ~1000 Bicoid binding regions have been identified by ChIP seq experiments in nc14 embryos (Hannon et al., Elife, 2017) and given that several Bcd binding sites are generally clustered together in a Bcd region, the number of Bcd binding sites in the fly genome is likely larger than 1000. It is much greater than the number of Bicoid binding sites in our synthetic reporters. Therefore, we think that it is unlikely that adding the synthetic reporters (which in the case of B12 only represents at most 1/100 of the Bcd binding sites in the genome) will severely alter the competition for Bcd binding between the other Bcd binding sites in the genome. Additionally, the insertion of a BAC spanning the endogenous hb locus with all its Bcd‐dependent enhancers did not affect (as far as we can tell) the regulation of the wildtype gene (Lucas, Tran et al., 2018).

We have added a sentence concerning this point in the main text (lines 108 to 111).

‐ Further, the activity of the synthetic reporters depends on the location of insertion. Erceg et al. PLoS Genetics 2014 showed that the same synthetic enhancer can have different readout depending on its genomic location. I'm aware that the authors use a landing site that appears to replicate similar hb kinetics, but did they try random insertion or other landing site? In short, how robust are their results to the specific local genome site? This should have been tested, especially given the boldly written conclusions from the work.

This concern of the reviewer has been tested and is addressed Fig S1 where we compare two random insertions of the hb‐P2 transgene (on chromosome II and III; Lucas, Tran et al., 2018) and the insertion at the VK33 landing site that was used for the whole study. As shown Fig. S1, the dynamics of transcription (kymographs) are very similar. In the main text, the reference Fig. S1 is found in the Materials and Methods section (bottom of the 1st paragraph concerning the Drosophila stocks, lines 518).

‐ Related to the above, it's also not obvious that readout is linear ‐ i.e. as more binding sites are added, there could be cooperativity between binding domains. This may have been accounted for in the model but it is not clear to me how.

The reviewer is totally correct. It is clear from our data that readout is not linear: comparing (increase of 1.5 X in the number of BS) B6 with B9 leads to a 4.5 X greater activation rate and this argues against independent activation of transcription by individual bound Bcd TF. There is almost no impact of adding 3 more sites when comparing B9 to B12 (even though it corresponds to an increase of 1.33 X in the number of BS). This issue has been rephrased in the main text (lines 200 to 203) and further developed for the modeling aspects in the SI section C and Figure S3. It is also discussed in the second paragraph of the discussion (lines 380 to 383).

‐ It would be good in the Introduction/Discussion to give a broader perspective on the advantages and disadvantages of the synthetic approach to study gene regulation. The intro only discusses Tran et al. Yet, there is a strong history of using this approach, which has also helped to reveal some of the approaches shortcoming. E.g. Gertz et al. Nature 2009 and Sharon et al. Nature Biotechnology 2012. Again, I may have missed, but from my reading I cannot see any critical analysis of the pros/cons of the synthetic approach in development. This is necessary to give readers a clearer context.

One sentence was added in the introduction concerning this point (lines 79 to 82).

A short review concerning the synthetic approach in development has also been added at the beginning of the discussion (lines 347 to 359).

Reviewer #2 (Public Review):

It is known that Bicoid increases in concentration across the syncytial division cycles, the gradient length scale for Bicoid does not change, and hunchback also increases in concentration during the syncytial cycles but the sharp boundary of the hunchback gradient is constantly seen despite the change in concentration of Bicoid. This manuscript shows that by increasing the Bicoid concentration or by adding Zelda binding sites, the expression of hunchback can be recapitulated to that of a previously studied promoter for hunchback.

I have the following comments to understand the implications of the study in the context of increasing concentrations of Bicoid during the syncytial division cycles:

‐ Bicoid itself is also increasing over the syncytial division cycles, how does this change in concentration of Bicoid affect the activation of the hunchback promoter given the cooperative binding of Bicoid and Bicoid and Zelda as documented by the study?

We thank the reviewer for this remark about the dynamics of the Bcd gradient, which we may have taken for granted. A seminal work on the dynamics of the Bcd gradient using fluorescent‐tagged Bcd (Gregor et al, Cell, 2007a) has shown that the gradient of Bcd nuclear concentration (this nuclear concentration is the one that matter for transcription) remains stable over nuclear cycles, despite a global increase of Bcd amount in the embryo. This can be explained by the fact that Bcd molecules are imported in the nuclei and that the number of nuclei double at every cycle, such that both processes compensate each other. Thus, we assumed that the gradient of Bcd nuclear concentration was stable over nc11 to nc13.

We have clarified this assumption in the model section in the manuscript (lines 165‐168).

Supporting our assumption, when looking at the transcription dynamics regulated by Bcd, in Lucas et al, PLoS Gen, 2018, we observed very reproducible expression pattern dynamics of the hb‐P2 reporter at each cycle nc11 to nc13. Such reproducibility in the pattern dynamics were also observed in this current work for hb‐P2, B6, B9, B12 and H6B6 reporters (Fig. S6A). Also, in Lucas et al, PLoS Gen, 2018, the shift in the established boundary positions of hb‐P2 reporter between nc11 to nc13 is ~2%EL (approximately a nucleus length ~10μm) and it is thus marginal.

In addition, as mentioned in the text (lines 105 to 107), we only focused our analysis on nc13 data which are statistically stronger given the higher number of nuclei analyzed. Thus, any change of Bcd nuclear concentration that would happen over nuclear cycles will not matter.

Concerning Zelda: Zelda’s transcriptional activity when measured on a reporter with only 6 Zld binding sites changes drastically over the nuclear cycles, with strong activity at nc11 and much weaker activity at nc13 (Fig S4A). This indicates that the changes in expression pattern dynamics of Z2B6 from nc11 to nc13 are caused predominantly by decreasing Zelda activity: the effect of Zld on the Z2B6 promoter is very strong during nc11 and nc12. It is also very strong at the beginning of nc13 (even though the Z6 reporter is almost silent) and became a bit weaker in the second part of nc13 (Fig S4B‐D).

‐ Does the change in concentration of Bicoid across the nuclear cycles shift the gradient similar to the change in numbers of Bicoid binding sites?

In both Lucas et al, PLoS Gen, 2018 and in this work (Fig. 1, Fig. 3 and Fig. S6A), we found that the positions of the expression boundary are very reproducible and stable in time for hb‐P2, B6, B9, B12, H6B6 during the interphase of nc12 to 13. For hb‐P2, the averaged shift of the established boundary position in nc11, 12 and 13 is within 2 %EL. This averaged shift between the cycles is of similar magnitude to the difference caused by embryo‐to‐embryo variability within nc13 (~2 %EL) (Gregor et al, Cell, 2007b, Lucas et al, PloS Gen, 2018). This shift is much smaller than the difference between the expression boundary positions of B6 and B9 (~ 8 % EL) and between B6 and Z2B6 (~17.5 %EL) in nc13.

For these reasons, we conclude that the difference between the expression patterns of B6, B9 and Z2B6 are caused predominantly by changing the TF binding site configurations of the reporters, rather than variability in the Bcd gradient.

The assumption of gradient stability has been clarified in the previous answer and in the manuscript (lines 165‐168).

‐ The intensity is a little higher for B9 and B12 at the anterior in 2B? Is this statistically different? is this likely to change the amount of Bicoid expression at the locus and lead to more robust activation?

We performed statistical tests to distinguish the spot intensities at the anterior pole for every pair of reporters in Fig. 2B (hb‐P2, B6, B9 and B12). All p‐values from pair‐wise KS tests are greater than 0.067, suggesting that the spot intensities at the anterior pole are not distinguishable between these reporters.

We have clarified this in the manuscript (line 157).

‐Are the fraction of active loci not changing across the syncytial cycles when the concentration of Bicoid also changes and consistent with the synthetic promoters?

To measure the reproducibility of the expression pattern dynamics in different nuclear cycles, we compared the boundary position of the fraction of active loci pattern as a function of time for all hbP2 and synthetic reporters (Fig. S6A). In this figure panel, for all reporters except Z2B6, the curves in nc12 and nc13 largely overlap, suggesting high reproducibility in the pattern dynamics between cycles and consequently low sensitivity to the subtle variation in the Bcd nuclear concentration gradient between the cycles.

For Z2B6, we attributed the difference in pattern dynamics between nc12 and nc13 to the changes in Zelda activity, as validated independently with a synthetic reporter with only 6 Zld binding sites (Fig. S4A).

‐How do the numbers of Hb BS change the expression of Hb? H6B6 has 6 Hb BS whereas the Hb‐P2 has 1? Are more controls needed to compare these 2 contexts?

As our goal was to determine to which mechanistic step of our model each TF (Bcd, Hb, Zld) contributed, we added BS numbers that are much higher than in the hb‐P2 promoter. The added number of Hb BS remains very low when compared to total number of Hb binding sites in the entire genome (Karplan et al, PLOS Gen, 2011), therefore, it is very unlikely to affect the endogenous expression of Hb protein.

We clarified this in the manuscript (lines 211 to 212).

Does Zelda concentration change across the syncytial division cycles? How does the change in concentration in the natural context affect the promoter activation of Hb?

Zelda concentration is stable over the nuclear cycles, as observed with the fluorescently‐tagged Zld protein (Dufourt et al., Nat Com, 2018). However, Zelda’s transcriptional activity when measured on a reporter with only 6 Zld binding sites changes drastically over the nuclear cycles, with strong activity at nc11 and much weaker activity at nc13 (Fig S4A, this work).

The impact of this change in Zld activity can be observed with the Z2B6 promoter, with the expression boundary moving from the posterior region toward the anterior region over the nuclear cycles (Fig. S4B‐D). However, we don’t detect any changes in the expression pattern dynamics of hb‐P2 over the nuclear cycles (Fig. S6A and in Lucas et al., PLoS Gen, 2018).

We have clarified this in lines 250‐251 of the main manuscript.

‐Changing the dose of Bicoid shifts the boundary of hunchback expression. It would be nice to model or test this in the context of varing doses of zelda or even reason this with respect to varying doses of zelda across the syncytial division cycles.

We thank the reviewer for this insight. Concerning Zelda, we did not perform any experiment reducing the amount of Zelda in the embryo. However, in a previous study (Lucas et al., PLoS Genetics, 2018), we observed that the boundary of hb was shifted towards the anterior when decreasing the amount of Zelda consistent to the fact that the dose of Zelda is critical to set the boundary position and the threshold of Bcd concentration required for activation. However, as Zelda is distributed homogeneously along the AP axis, it cannot bring per se positional information to the system.

Reviewer #3 (Public Review):

I think the framing could be improved to better reflect the contribution of the work. From the abstract, for example, it's unclear to me what the authors think is the most meaningful conclusion. Is it the observations about the finer details of TF regulation (bursting dynamics), the fact that Bcd is probably the sole source of "positional information" for hb‐p2, that Bcd exists in active/inactive form, or the fact that an equilibrium model probably suffices to explain what we observe? The first sentence itself seems to suggest this paper will discuss "dynamic positional information", in which case it's somewhat misleading to say this kind of work is "largely unexplored"; Johannes Jaeger in particular has been a strong proponent of this view since at least 2004. On that note some particularly relevant recent papers in the Drosophila early embryo include:

1) Jaeger and Verd (2020) Curr Topics Dev Biol

2) Verd et al. (2017) PLoS Comp Biol

3) Huang, Amourda, et al. and Saunders (2017) eLife

4) Yang, Zhu, et al. (2020) eLife [see also the second half of Perkins (2021) PLoS Comp Biol for further discussion of that model]

‐Some reviews from James Briscoe also discuss this perspective.

We agree with the reviewer that the phrasing of the abstract was not clear enough to emphasize the contribution of the work and we are also sorry if it suggested that the dynamic positional information is largely unexplored because this was not at all our intention.

We rephrased the abstract aiming to better highlight the most meaningful conclusions.

‐I would also recommend modifying the title to reflect the biology found in the new results.

We modified the title to better reflect the new results:<br /> “Synthetic reconstruction of the hunchback promoter specifies the role of Bicoid, Zelda and Hunchback in the dynamics of its transcription”

‐A major point that the authors should address is the design of the synthetic constructs. From table S1, the sites are often very closely linked (4‐7 base pairs). From the footprint of these proteins, we know they can cover DNA across this size (see, https://pubmed.ncbi.nlm.nih.gov/8620846/). As such, there may be direct competition/steric hindrance (see https://pubmed.ncbi.nlm.nih.gov/28052257/). What impact does this have on their interpretations? Note also that the native enhancer has spaced sites with variable identities.

We completely agree with the reviewer comment in the sense that we named our reporters according to the number (N) of Bcd binding sites sequences that they contain, even though we cannot prove definitively that they can effectively be bound simultaneously by N Bcd molecules. It is thus possible that B9 is not a B9 but an effective B6 (i.e. B9 can only be bound simultaneously by 6 molecules) if, for instance, the binding of a Bcd molecule to one site would prevent by the binding of another Bcd molecule to a nearby site (as proposed by the reviewer in the case of direct competition or steric hindrance).

Even though we cannot exclude this possibility, we think that our use of B6, B9, B12, in reference to the 6 Bcd BS of hb‐P2 promoter, is relevant for several reasons : i) some of the Bcd BS in the hb‐P2 promoter are also very close from each other (see Table S1); ii) the design of the synthetic construct was made by multimerizing a series of 3 strong Bcd binding sites with a similar spacing as found for the closest sites in the hb‐P2 promoter (as shown in Figure 1A and Table S1); iii) the binding of the Bicoid protein has been shown in foot printing experiments in vitro to be more efficient on sites of the hb‐P2 promoter that are close from each other, and this has even been interpreted as binding cooperativity (Ma et al., 1996); iv) even though these experiments were not performed with full‐length proteins, two molecules of the paired homeodomain (from the same family of DNA binding domain as Bcd) are able to simultaneously bind to two binding sites separated by only 2 base pairs. This binding to very close sites is even cooperative while when the two sites are distant by 5 base pairs or more, the simultaneous binding to the two sites occurs without cooperativity (Wilson et al., 1993).

Conversely, as it is very difficult to demonstrate that 9 Bcd molecules can effectively bind to our B9 promoter, it is very difficult to know exactly how many binding sites for Bcd the hb‐P2 contains, and a large debate concerning not only the number but also the identity of the Bcd sites in the hb promoter is still ongoing (Park et al., 2019; Ling et al., 2019).

As we cannot exclude the possibility that B9 is an effective B6, it remains possible that B9 and hb‐P2 (which is supposed to only contains 6 sites) have the same number of effective Bcd binding site and this could explain why the two reporters have very similar transcription dynamics and features.

Regarding other interpretations in the manuscript, we identified two other aspects that will be affected if our synthetic reporters have fewer effective sites than the number of sites they carry. The first one concerns the synergy, as the increase in the number of sites of 1.5 from B6 to B9 might be over‐estimated but this would even increase the synergistic effect given the 4.5 difference in activity of the two reporters (Fig. S3). The second one concerns the discussion on the Hill coefficient and the decay length where the effective number of binding sites (N) is required to determine the limit of concentration sensing (Fig. 5). This would particularly be important for the hb‐P2 promoter.

Except for these specific points, we don’t think that the possibility that reporters do not exactly contain as many as effective binding sites than proposed, has a huge impact on our interpretations and the general message conveyed in this manuscript. Most importantly, it is very clear that our B6 and B9 reporters differ only by three Bcd binding sites and have yet very distinct expression dynamics: while B9 recapitulates almost all transcription features of hb‐P2, B6 is far from achieving it. Similarly, H6B6 and Z2B6 have very different transcription features than B6 and these differences have been key for understanding the mechanistic functions of the three TF we studied.

This discussion has been added to the discussion (lines 400 to 414)

Author Response:

Reviewer #3 (Public Review):

This paper reports that levodopa administration to healthy volunteers enhances the guidance of model-free credit assignment (MFCA) by model-based (MB) inference without altering MF and MB learning per se. The issue addressed is fascinating, timely and clinically relevant, the experimental design and analysis strategy (reported previously) are complex, but sophisticated and clever and the results are tantalizing. They suggest that ldopa boosts model-based instruction about what (unobserved or inferred) state the model-free system might learn about. As such, the paper substantiates the hypothesis that dopamine plays a role specifically in the interaction between distinct model-based and model-free systems. This is really a very valuable contribution, one that my lab and I expect many other labs had already picked up immediately after it appeared as a preprint.

Major strengths include the combination of pharmacology with a substantial sample size, clever theory-driven experimental design and application of advanced computational modeling. The key effect of ldopa on retroactive MF inference is not large, but substantiated by both model-agnostic and model-informed analyses and therefore the primary conclusion is supported by the results.

The paper raises the following questions.

What putative neural mechanism led the authors to predict this selective modulation of the interaction? The introduction states that "Given DA's contribution to both MF and MB systems, we set out to examine whether this aspect of MB-MF cooperation is subject to DA influence." This is vague. For the hypothesis to be plausible, it would need to be grounded in some idea about how the effect would be implemented. Where exactly does dopamine act to elicit an effect on retroactive MB inference, but not MB learning per se? If the mechanism is a modulation of working memory and/or replay itself, then shouldn't that lead to boosting of both MB learning as well as MB influences on MF learning? Addressing this involves specification of the mechanistic basis of the hypothesis in the introduction, but the question also pertains to the discussion section. Hippocampal replay is invoked, but can the authors clarify why a prefrontal working memory (retrieval) mechanism invoked in the preceding paragraph would not suffice. In any case, it seems that an effect of dopamine on replay would also alter MB choice/planning?

In sum, we agree with this criticism and have now revised the relevant intro paragraph (p. 3/4).

We now discuss DAergic manipulation of replay in particular (p. 24). We infer that a component of a MB influence over choice comes from the way it trains a putative MF system (something explicitly modelled in Mattar & Daw, 2018, and a new preprint from Antonov et al., 2021, referencing data from Eldar et al., 2020) – and consider what happens if this is boosted by DA manipulations. The difference between the standard two-step task and the present task is that in our task there is extra work for the MB system in order to perform inference so as to resolve uncertainty for MFCA. We later suggest that the anticorrelation we found between the effect of DA on MB influence over choice and MB guidance of MFCA arises from this extra work.

The broader questions raised about (prefrontal) working memory and (hippocampal) replay pertains to recent and ongoing work, and we feel this should be part of the discussion, which we have re-written this to detail more clearly different possible mechanistic explanations, pointing to how they might be tested in the future (p. 23/24).

A second issue is that the critical drug effects seems somewhat marginally significant and the key plots (e.g. Fig3b and Fig 44b,c, but also other plots) do not visualize relevant variability in the drug effect. I would recommend plotting differences between LDopa and placebo, allowing readers to appreciate the relevant individual variability in the drug effects.

We have now replotted the data in the new Figures 4 and 5 to reflect drug-related variability.

Third, I do wonder how to reconcile the lack of a drug x common reward effect (the lack of a dopamine effect on MF learning) as well as the lack of a drug effect on choice generalization with the long literature on dopamine and MF reinforcement and newer literature on dopamine effects on MB learning and inference. The authors mention this in the discussion, but do not provide an account. Can they elaborate on what makes these pure MB and MF metrics here less sensitive than in various other studies, and/or what are the implications of the lack of these effects for our understanding of dopamine's contributions to learning?

Regarding a lack of a drug effect on MF learning or control, we now elaborate on this on p. 22/23:

“With respect to our current task, and an established two-step task designed to dissociate MF and MB influences (Daw et al., 2011), there is as yet no compelling evidence for an direct impact of DA on MF learning or control (Deserno et al., 2015a; Kroemer et al., 2019; Sharp et al., 2016; Wunderlich et al., 2012, Kroemer et al., 2019). A commonality of our novel and the two-step task is dynamically changing reward contingencies. As MF learning is by definition incremental, slowly accumulating reward value over extended time-periods, it follows that dynamic reward schedules may lessen a sensitivity to detect changes in MF processes (see Doll et al., 2016 for discussion). In line with this, experiments in humans indicate that value-based choices performed without feedback-based learning (for reviews see, Maia & Frank, 2011; Collins and Frank, 2014), as well as learning in stable environments (Pessiglione et al., 2006), are susceptible to DA drug influences (or genetic proxies thereof) as expected under an MF RL account. Thus, the impact of DA boosting agents may vary as a function of contextual task demands. This resonates with features of our pharmacological manipulation using levodopa, which impacts primarily on presynaptic synthesis. Thus, instead of necessarily directly altering phasic DA release, levodopa impacts on baseline storage (Kumakura and Cumming, 2009), likely reflected in overall DA tone. DA tone is proposed to encode average environmental reward rate (Mohebi et al., 2019; Niv et al., 2007), a putative environmental summary statistic that might in turn impact an arbitration between behavioural control strategies according to environmental demands (Cools, 2019).”

As pointed out by the reviewer as well, in the present task we did not find an effect of levodopa on MB influences per se and now discuss this on p. 22:

“In this context, a primary drug effect on prefrontal DA might result in a boosting of purely MB influences. However, we found no such influence at a group level – unlike that seen previously in tasks that used only a single measure of MB influences (Sharpe et al., 2017; Wunderlich et al., 2012). Our novel task systematically separates two MB processes: a guidance of MFCA by MB inference and pure MB control. While we found that only one of these, namely guidance of MFCA by MB inference, was sensitive to enhancement of DA levels at a group level, we did detect a negative correlation between the DA drug effects on MB guidance of MFCA and on pure MBCA. One explanation is that a DA-dependent enhancement in pure MB influences was masked by this boosting in the guidance of MFCA by MB inference. In this regard, our data is suggestive of between-subject heterogeneity in the effects of boosting DA on distinct aspects of MB influences.”

Another open question remains as to why different task conditions (guidance of MFCA by MB vs. pure MB control) apparently differ in their sensitivity to the drug manipulation. We discuss this (p. 22) by proposing that a cost-benefit trade-off might play an important role (Westbrook et al., 2020).

Fourth, the correlation with WM and drug effect on preferential MBCA for non-informative but not informative destination is really quite small, and while I understand that WM should be associated with preferential MBCA under placebo, it does not become clear what makes the authors predict specifically that WM predicts a dopa effect on this metric, rather than the metric taken under placebo, for example.

Our initial reasoning was that MFCA based on reward at the non-informative destination should be particularly sensitive to WM, on the basis that the reward is no longer perceptually available once state uncertainty can be resolved by the MB system. However, we agree with the reviewer that this reasoning does not indicate why it should specifically effect the drug-induced change. In light of this critique, we have removed this part from the abstract, introduction and the main results but still report this relation to WM in Appendix 1 (p. 44/45, subheading “Drug effect on guidance of MFCA and working memory”, Appendix 1 - Figure 11) as an exploratory analysis as suggested in the editor’s summary.

A fifth issue is that I am not quite convinced about the negative link between dopamine's effects on MBCA and on PMFCA. The rationale for including WM, informativeness as well as DA effects on MBCA in the model of DA effects on PMFCA wasn't clear to me. The reported correlation is statistically quite marginal, and given that it was probably not the first one tested and given the multiple factors involved, I am somewhat concerned about the degree to which this reflects overfitting. I also find the pattern of effects rather difficult to make sense of: in high WM individuals, the drug-effects on PMFCA and MBCA are negatively related for informative and non-informative destinations. In low WM individuals, the drug-effects on PMFCA and MBCA are negatively related for informative, but not non-informative destinations. It is unclear to me how this pattern leads to the conclusion that there is a tradeoff between PMFCA and MBCA. And even if so, why would this be the case? It would be relevant to report the simple effects, that is the pattern of correlations under placebo separately from those under ldopa.

The reviewer’s critique is well taken. In connection to the working memory finding reported in the previous section of the initial manuscript, we reasoned that it would be necessary to include WM in the model as well. We still consider this analysis on inter-individual differences in drug effects from different task conditions is important because it connects our current work to previous work linking DA to MB control. However, we now perform a simplified analysis on this where we leave out WM and instead average PMFCA across informative and non-informative destinations (since we had no prior hypothesis that these conditions should differ, p. 19/20). This results in a significant negative correlation of drug-related change in average PMFCA and MB control (Figure 6A, r=-.31,p=.02 Pearson r=-.30, p=.017, Spearman r=-.33, p=.009). In addition, we also ran extended simulations to verify that this negative correlation does not result from correlations among model parameters (see Appendix 1 - Figure 10 for control analysis verifying that this negative correlation survives control for parameter-tradeoff).

Figure 6. Inter-individual differences in drug effects in MBCA and in preferential MFCA, averaged across informative and non-informative destinations (aPMFCA). A) Scatter plot of the drug effects (levodopa minus placebo; ∆ aPMFCA, ∆ MBCA). Dashed regression line and r Pearson correlation coefficient. B) Drug effects in credit assignment (∆ CA) based on a median on ∆ MBCA. Error bars correspond to SEM reflecting variability between participants.

As suggested by the reviewer, we unpack this correlation further (p. 19/20) by taking the median on Δ MBCA (-0.019) and split the sample in lower/higher median groups. The higher median group showed a positive (M= 0.197, t(30)= 4.934, p<.001) and the lower-median group showed a negative (M= -0.267, t(30)= -7.97, p<.001) drug effect on MBCA, respectively (Figure 6B). In a mixed effects model (see Methods), we regressed aPMFCA against drug and a group indicator of lower/higher median Δ MBCA groups. This revealed a significant drug x Δ MBCA-split interaction (b=-0.17, t(120)=-2.05, p=0.042). In the negative Δ MBCA group (Figure 6B), a significantly positive drug effect on aPMFCA was detected (simple effect: b=.18, F(120,1)=10.35, p=.002) while in the positive Δ MBCA group a drug-dependent change in aPMFCA was not significant (Figure 6B, simple effect: b=.02, F(120,1)=0.10, p=.749).

We have changed the respective section of the results accordingly (p. 19/20). Further, we have motivated this exploratory analysis more clearly in the introduction (p. 3/4) in terms of it providing a link to previous relevant studies (Deserno et al., 2015a; Groman et al., 2019; Sharp et al., 2016; Wunderlich et al., 2012). Lastly, we have endeavoured to improve the discussion on this (p. 21/22).

More generally I would recommend that the authors refrain from putting too much emphasis on these between-subject correlations. Simple power calculation indicates that the sample size one would need to detect a realistically small to medium between-subject effect (that interacts with all kinds of within-subject factors) is in any case much larger than the sample size in this study.

We agree with this and have, as mentioned above, substantially adjusted the section on inter-individual differences. We have moved the WM analysis to Appendix 1 (p. 44/45, subheading “Drug effect on guidance of MFCA and working memory”, Appendix 1 - Figure 11) and greatly simplified the analysis of inter-individual differences in drug effects (see previous paragraph). We also mention the overall small to moderate effects in the limitations section (p. 25/26).

Another question is how worried should we be that the critical MB guidance of MFCA effect was not observed under placebo (Figure 3b)? I realize that the computational model-based analyses do speak to this issue, but here I had some questions too. Are the results from the model-informed and model-agnostic analyses otherwise consistent? Model-agnostic analyses reveal a greater effect of LDopa on informative destination for the ghost-nominated than the ghost-rejected trials and no effect for noninformative destination. Conversely model-informed analyses reveal a nomination effect of ldopa across informative and noninformative trials. This was not addressed, or am I missing something? In fact, regarding the modeling, I am not the best person to evaluate the details of the model comparison, fitting and recovery procedures, but the question that does rise is, and I would make explicit in the current paper how does this model space, the winning model and the modeling exercise differ (or not) from that in the previous paper by Moran et al without LDopa administration.

A detailed response to this was provided in replay to point 6 as summarized by the editor. And we provide a summary here as well.

Firstly, we clearly indicate discrepancies between our model-agnostic and computational modelling analyse and acknowledge that discrepancies may be expected when effects of interest are weak to moderate, which we acknowledge (p. 25/26, limitations).

Secondly, the results from the computational model are generally statistically stronger, which is not surprising given that they are based on influences from far more trials. We now include a discussion of this in more detail in the section on limitations (p. 25/26).

Thirdly, although the computational model uses a slightly different parameterization from that reported in Moran et al. (2019), it is a formal extension of that model, allowing the strength of effects for informative and uninformative destinations to differ. We now include a reference to this change in parameterization in the limitation section (p. 25/26), and include a more detailed description in Appendix 1 (p. 45-47).

Finally, to test if the current models support our main conclusion from Moran et al. (2019) that retrospective MB inference guides MFCA for both the informative and non-informative destinations, we reanalysed the Moran et al. (2019) data using the current novel models and found converging support, as we now report (Appendix 1 – Figure 8).

Finally, the general story that dopamine boosts model-based instruction about what the model-free system should learn is reminiscent of the previous work showing that prefrontal dopamine alters instruction biasing of reinforcement learning (Doll and Frank) and I would have thought this might deserve a little more attention, earlier on in the intro.

The reviewer is indeed correct and we now reference this line of work (Doll et al., 2009, 2011) in the intro (p. 4).

Author Response

Reviewer #1 (Public Review):

While the mechanism about arm-races between plant and specialist herbivores has been studied, such as detoxification of specific secondary metabolites, the mechanism of the wider diet breadth, so-called generalist herbivores have been less studied. Since the heterogeneity of host plant species, the experimental validation of phylogenetic generalism of herbivores seemed as hard to be conducted. The authors declared the two major hypotheses about the large diet breadth ("metabolic generalism" and "multi-host metabolic specialism"), and carefully designed the experiment using Drosophila suzukii as a model herbivore species.

By an untargeted metabolomics approach using UHPLC-MS, authors attempted to falsify the hypotheses both in qualitative- and quantitative metabolomic profiles. Intersections of four fruit (puree) samples and each diet-based fly individual samples from the qualitative data revealed that there were few ions that occur as the specific metabolite in each diet-based fly group, which could reject the "multi-host metabolic specialism" hypothesis. Quantitative data also showed results that could support the "metabolic generalism" hypothesis. Therefore, the wide diet breadth of D. suzukii seemed to be derived from the general metabolism rather than the adaptive traits of the diverse host plant species. On the other hand, the reduction of the metabolites (ions) set using GLM seemed logical and 2-D clustering from the reduced ions set showed that quantitative aspects of diet-associated ions could classify "what the flies ate". These interesting results could enhance the understanding of the diet breadth (niche) of herbivorous insects.

The authors' approach seemed clear to falsify the hypotheses based on the appropriate data processing. The intersection of shared ions from the qualitative dataset could distinguish the diet-specific metabolites in flies and commonly occurring metabolites among flies and/or fruits. Also, filtering on the diet-specific ions seemed to be a logical and appropriate way. Meanwhile, the discussion about the results seemed to be focused on different points regarding the research hypotheses which were raised in the introduction part. Discussion about the results mainly focused on the metabolism of D. suzukii itself, rather than the research hypotheses and questions that were raised from the evolution of the wide diet breadth of generalist herbivores. In particular, the conclusion seems to be far from the main context of the authors' research; e.g. frugivory. It makes the implication of the study weaker.

We wish to thank Reviewer #1 for their appreciation of our study. As recommended, we now focus our discussion more on the general aspect of our findings (relevant to insects, herbivores, or frugivores), and less on the peculiarities of the metabolism of D. suzukii itself. Specifically, we now only mention D. suzukii in one section (two sentences) of our Discussion, to serve as an example (l.387-396). Thanks to this comment, the Discussion may interest a broader readership, on the evolution of diet breadth in generalist herbivorous species and offers a better understanding of the general implications of our findings.

Reviewer #2 (Public Review):

The manuscript: "Metabolic consequences of various fruit-based diets in a generalist insect species" by Olazcuaga et al., addresses an interesting question. Using an untargeted metabolomics approach, the authors study how diet generalism may have evolved versus diet specialization which is generally more commonly observed, at least in drosophila species. Using the phytophagous species Drosophila suzukii, and by directly comparing the metabolomes of fruit purees and the flies that fed on them, the authors found evidence for "metabolic generalism". Metabolic generalism means that individuals of a generalist species process all types of diet in a similar way, which is in contrast to "multi-host metabolic specialism" which entails the use of specific pathways to metabolize unique compounds of different diets. The authors find strong evidence for the first hypothesis, as they could easily detect the signature of each fruit diet in the flies. The authors then go on to speculate on the evolutionary ramifications of this for how potentially diet specializations may have evolved from diet generalism. Overall, the paper is well written, the experiments well documented, and the conclusions convincing.

We thank Reviewer #2 for their comments and appreciation of our work.

Reviewer #3 (Public Review):

Laure Olazcuaga et al. investigated the metabolomes of four fruit-based diets and corresponding individuals of Drosophila suzukii that reared on them using comparative metabolomics analysis. They observed that the four fruit-based diets are metabolically dissimilar. On the contrary, flies that fed on them are mostly similar in their metabolic response. From a quantitative point of view, they find that part of the fly metabolomes correlates well with that of the corresponding diet metabolomes, which is indicative of insect ingestive history. By further focusing on 71 metabolites derived from diet-specific fly ions and highly abundant fruit ions, the authors show that D. suzukii differentially accumulates diet metabolism in a compound-specific manner. The authors claim that the data support the metabolic generalism hypothesis while rejecting the multi-host metabolic specialism hypothesis. This study provides a valuable global chemical comparison of how diverse diet metabolites are processed by a generalist insect species.

Strengths:

The rapid advances in high-resolution mass spectrometry have recently accelerated the discovery of many novel post-ingestive compounds through comparative metabolomics analysis of insect/frass and plant samples. Untargeted metabolomics is thus a very powerful approach for the systematic comparison of global chemical shifts when diverse plant-derived specialized metabolites are further modified or quantitatively metabolized after ingestion by insects. The technique can be readily extended to a larger micro- or macro-evolutionary context for both generalist and specialist insects to systematically investigate how plant chemical diversity contributes to dietary generalism and specialism.

We would like to thank Reviewer #3 for their insightful comments on the power of untargeted metabolomics to evaluate the fate of plant metabolites and their use by herbivores. We also agree that these techniques can be used to tackle eco-evolutionary issues, such as the origin and maintenance of dietary generalism and specialism here. We hope that our study will inspire other researchers to explore such techniques and experiments to gain a global overview of biochemistry fluxes and their evolution. We now mention it in the conclusion (L454-459).

Weaknesses:

The authors claim that their data support the hypothesis of metabolic generalism, however, a total analysis of insect metabolism may not generate a clean dataset for direct comparison of fruit-derived metabolites with those metabolized by D. suzukii, given that much of these metabolites would be "diluted" proportionally by insect-derived metabolites. If the insect-derived metabolites predominate, then, as the authors observed, a tight clustering of D. suzukii metabolomes in the PCA plot would be expected. It is therefore very difficult to interpret these patterns.

We agree with Reviewer #3 that a careful examination of the different possible origins of metabolites should take place to distinguish between our two competing hypotheses.

The only source of metabolites for insects in our experimental setup is a mixture of (i) a large proportion of fruit purees and (ii) a minor proportion of artificial medium consisting mainly of yeast. Our goal is thus to understand the fate of (i) “fruit-derived” metabolites (transformed and untransformed), while controlling for (ii) “artificial media-derived” metabolites, that constitute a nuisance signal but are necessary for a complete development in our system.

By “fruit-derived” and “insect-derived” metabolites, it is our understanding that Reviewer #3 means “fruit” metabolites (when in insects, untransformed “fruit-derived” metabolites) and “artificial medium-derived” metabolites. It is true that we do wish to avoid a predominance of “artificial medium-derived” metabolites and focus on “fruit-derived” metabolites in insects. We also want to note that it is of primary importance in our study to distinguish between “fruit” metabolites that are carried as is (“fruit” metabolites present in insects, ie untransformed “fruit-derived” metabolites), and “fruit” metabolites that are used after transformation by the insect (i.e., transformed “fruit-derived” metabolites).

We agree with Reviewer #3 that the presence of “artificial medium-derived” metabolites could be problematic in direct comparisons of fruits and insects (and not among fruits or among insects’ comparisons).

However, we took some steps to avoid such problems:

1. We included control fly samples in our experiment: at each experimental generation, flies developed only on artificial medium (without fruit puree) were collected and processed simultaneously with flies that developed on fruit media. Results using these artificial medium-reared flies as controls (by subtracting their ions levels and removing ions that were similar, respective of their generation) were similar to results using raw data and conclusions were identical (see below).

2. We lowered the proportion of artificial medium in our fruit media so that it was kept to a minimum, compatible with larval development and adult survival.

Consistent with the low impact of this “artificial medium” component on our conclusions, we also wish to point out the presence pattern of metabolites found only in flies and never in fruits when using raw data (Figure 3, yellow stack). Even in the most conservative hypothesis of 100% of these metabolites originating from our artificial medium (which is probably not the case), we observe that it constitutes only a minor proportion of metabolites common to all flies (15.7%).

For your consideration, we include below the main Figures, using both raw data and artificial medium-controlled:

Figure 2, left = raw data; right = artificial-media controlled:

Figure 3, left = raw data; right = artificial-media controlled:

Figure 3S1, left = raw data; right = artificial-media controlled:

Figure 4, above = raw data; below = artificial-media controlled:

We hope that we convinced the Editor/Reviewers that raw data and artificial-medium controlled data provide a single and same answer to all our analyses. We chose to present only raw data, to simplify the Materials & Methods section.

We however modified the current version of the manuscript to inform the reader that proper controls were done and that their inclusion do not modify any of our conclusions (l.110-113 and l.583-589).

We also wish to point out two additional comments:

• As Reviewer #1 also recommended, we modified the expectations drawn in Fig1G to better consider the general comment of “insect derived” metabolites being fundamentally different from plant metabolites (even if we do show in our study that only approx. 9% of metabolites are private to flies).

• The main part of our care in the use of this global PCA analysis is that it follows two other analyses (global intersection and comparison of intersections among fruits and among flies) and precedes another one (fly-focused PCA). We hope that all these analyses help the readers get a comprehensive overview of the dataset and associated results, avoiding reliance on a single analysis.

• We also help readers to explore and visualize all analyses presented in our manuscript by setting up a shiny application (in addition to our available dataset and R code), at https://fruitfliesmetabo.shinyapps.io/shiny/. This is now mentioned in the main text (l.588-589).

We thank the Reviewer for their comment that greatly improved the manuscript.

The authors generated a qualitative dataset using the peak list produced by XCMS which contains quantitative peak areas, it is unclear how the threshold was selected to determine if a peak is present or absent in a given sample. The qualitative dataset would influence the output of their data analysis.

The referee is right in pointing out that the threshold used to determine if a peak is present or absent in a given sample was not clearly specified. This has now been corrected in the “Host use” section of the Materials & Methods (l.513-516). Briefly, a given replicate of a compound was considered present if the corresponding peak area following XCMS quantification was > 1000. This threshold was selected to be close to the practical quantification threshold of the Thermo Exactive mass spectrometer used in this study. This threshold was selected in order to allow the quantification of low-abundance compounds, as many plant-derived diet compounds were expected to be present in trace amounts in flies. We additionally applied a stringent rule for presence of any given compound (presence in at least 3 biological replicates).

The authors reply on in-source fragmentation for peak annotation when authentic standards are not available. The accuracy of the annotation thus requires further validation.

The Supplementary Table 1 was unfortunately omitted in the first submission of the manuscript. This oversight has been now corrected and the Supplementary Table 1 details all information used for metabolite annotation. In particular, MS/MS data comparison with mass spectral databases as well as with published literature have been added to substantiate metabolite identifications. This MS/MS data was produced thanks to the comment of the Reviewer. We also provide four more annotations from standards to attain 30 / 71 identifications validated through chemical standards.

Author Response:

Reviewer #1 (Public Review):

This manuscript elegantly demonstrates that the degradation of PTPN14 by human papillomavirus (HPV) 16 and 18 E7 proteins previously reported by the authors is essential for E7-mediated YAP1 activation. This is important for E7-mediated maintenance of basal cell state and presumably persistence of HPV infection. The authors use a series of innovative tissue models combined with validation in clinical samples to demonstrate the importance of YAP1 activation in high-risk HPV pathogenesis.

The data are of high quality with excellent controls. The manuscript is well-written and the rationale of each experiment easy to follow. In general the results support the authors conclusions. I have the following suggestion to improve the manuscript: The enhanced nuclear expression of YAP in the basal cells of epithelia expressing HPV16/18 E7 is difficult to see in the low resolution IF images shown. The magnified images do show enhanced expression compared to HFK cultures, but to remove any bias in selection of enhanced areas, could the authors include quantification of the distribution of IF signal in the basal cells, compared to the suprabasal cells, of the epithelia shown with statistical analysis? Figure 2 would also benefit from quantification as described above.

We appreciate the positive feedback and constructive suggestions from Reviewer #1. We used widefield images with the goal of presenting as many cells in organotypic cultures as possible, but at low magnification. We have further analyzed the imaging data and updated the manuscript as follows:

1) We assessed YAP1 intensity in basal and suprabasal layers as suggested by the reviewer. Consistent with literature reports, YAP1 is expressed predominantly in basal cells in each of our organotypic cultures, independent of E7 status (see figure below).

2) Because YAP1 is always more highly expressed in basal cells than in suprabasal cells and YAP1 is regulated at the level of nuclear/cytoplasmic localization, we anticipated that quantification of YAP1 nuclear localization in our organotypic cultures may be more useful to readers than basal/suprabasal quantification.

Consequently, we conducted classification-based analyses to quantify YAP1 nuclear localization (a surrogate for YAP1 activity) in the cultures. Each image to be analyzed was deidentified and assigned a coded name. Each cell in the basal layer was then classified as having either predominantly nuclear YAP1 staining, predominantly cytoplasmic YAP1 staining, or YAP1 staining that is comparably distributed between the nucleus and cytoplasm. At least three fields were analyzed per raft. We assessed YAP1 localization in 8,323 cells (average 378.3 cells/culture shown in the text for almost all cultures). The quantifications are now included in Figure 1-figure supplement 2C-E, Figure 1-Figure supplement 5A-C, and Figure 2-figure supplement 1D-F.

The new quantifications do not change our interpretations of the results nor our conclusion that HPV E7 degrades PTPN14 to activate YAP1 in basal cells. We noted that HPV E6 may promote YAP1 nuclear localization to some degree and have updated the text accordingly.

Reviewer #2 (Public Review):

Strengths: A major strength of this report is the use of several different technical approaches, the results from which converge to provide several types of data supporting their conclusions. These various techniques include genetic knockdown/overexpression in primary keratinocytes, organotypic raft cultures, laser-capture microdissection, cell fate monitoring assays, and analysis of publicly available datasets. The manuscript is well-written and the figures are well-made. Weaknesses: Overall, there are only a few minor weaknesses related to figure quality and presentation (which will be conveyed in the private recommendations to the authors).

We appreciate the positive feedback and these thoughtful comments from reviewer #2.

Are claims/conclusions justified by data? Overall, the authors' conclusions are adequately justified by the data. However, there were a few interpretations I felt were somewhat overstated given the experiments performed and data provided. 1. The first issue relates to the interpretation/conclusion of the results from experiments analyzing basal cell number. In Figure 2, the basal cell number was indeed reduced in R84S compared to WT E7. However, it was not reduced to parental HFK levels, suggesting other E7 activities are involved in increasing basal cell number. A similar observation is presented in Figure 7 (E-F), where the R84S E7 mutant still had significantly higher basal cell retention than the empty vector control, albeit lower than WT E7. While their data certainly indicates that the binding and subsequent degradation of PTPN14 is an E7 function important to increasing basal cell number and retention, there are clearly other E7 functions involved. While the authors don't necessarily overinterpret these findings, the possibility that other E7 functions are involved is not explicitly acknowledged or explored in the Discussion.

Indeed, cells expressing HPV18 E7 R84S retain some capacity to increase basal cell number (Figure 2) and promote basal cell retention (Figure 7). It is possible that an activity of HPV E7 in addition to PTPN14 degradation influences these phenotypes. HPV18 E7 R84S retains the capacity to bind and degrade RB1 (Hatterschide et al., 2020). The basal cells in the HPV18 E7 R84S cell fate experiment were predominantly found in clusters indicative of possible clonal expansion. We hypothesize that such clusters reflect proliferation induced by RB1 inactivation and cause the ratio of basal to suprabasal cells to remain high even in the R84S mutant condition. Our hypothesis is now described in further detail in the text.

1. The second issue pertains to the findings related to the effect on differentiation upon modulation of key Hippo pathway components (Figure 4). It does not appear that the authors performed these studies in the presence of any well-known stimuli that induce the differentiation process in keratinocytes grown in 2D culture (high calcium, high serum, etc) nor did they use these cells in organotypic rafts wherein differentiation occurs during the raft stratification process. This is particularly true in the studies exploring PTPN14 plus LATS1/2 silencing and the effect on repression of keratinocyte differentiation. Whereas it seems PTPN14 itself was serving as the differentiation stimuli in earlier experiments (Figure 4C/D), it does not appear any differentiation stimuli were provided in the experiments shown in Figures 4E-I. For these reasons, the interpretation drawn by the authors that "...inactivation of three different YAP1 inhibitors dampens differentiation gene expression" (Line 220-221) and "inactivation of LATS1 or LATS2...also repressed differentiation genes" (Lines 349-350) seems specific to endogenous levels of differentiation genes. It seems difficult to conclude that inactivation of the Hippo pathway is actively repressing the induction of differentiation if the cells are not being treated with stimuli to induce differentiation.

Indeed, no differentiation stimuli were used in these experiments. We previously observed that PTPN14 knockout or E7 expression reduced differentiation gene expression both in undifferentiated cells and in cells stimulated to differentiate (Hatterschide et al., 2019, 2020). We anticipate that gene expression in unstimulated cells is reflective of gene expression in cells stimulated to differentiate. We altered the results and discussion text to emphasize that the experiment measures differentiation gene expression in unstimulated cells.

Author Response:

Reviewer #1 (Public Review):

This paper provides experimental and modeling analysis of the inter-brain coupling of socially interacting bats, and reports that coordinated brain activity evolves at a slower time scale than the activity describing the differences. Specifically, the paper finds that there is an attracting submanifold corresponding to the mean (or "common mode") of neural activity, and that the dynamics in the orthogonal eigenmode, corresponding to the difference in brain activity, decays rapidly. These rapid decays in the difference mode are referred to as "catch up" activity.

There are two main findings:

1) Neural activity (especially higher frequency LFP activity in the 30-150Hz range) is modulated by social context. Specifically, the ratio of the averaged, moment-to-moment MEAN:DIFF ratio is much higher when the bats are in a single chamber, clearly indicating that the animals are coordinating their neural activity. This change also seems to hold -- although not as striking -- in lower-frequency LFP and spiking activity.

2) The time scales of the mean vs. difference dynamics are segregated: the "difference dynamics" evolve at a faster time scale than "similarity dynamics", seems to be well supported.

The basic finding is presented in Figure 1. The rest of the paper is focused on a modeling study to garner further insight into the dynamics.

Weaknesses:

This is an entirely phenomenological paper, and while it claims to garner "mechanistic insight", it is unclear what that means.

We regret not clarifying sufficiently what we meant by “mechanistic insight.” The insight is the following: functional across-brain coupling acts as positive feedback to the mean component of neural activity, which amplifies it and slows it down; at the same time, it acts as negative feedback to the difference component, which suppresses it and speeds it up. Thus, findings (1) and (2) in the reviewer’s summary above can be explained by the same model mechanism. As the reviewer pointed out below, the details of the model are complex, which could have made the simple mechanism above opaque. Thus, we analyzed two simplified versions of the model to make the mechanistic insight clear. This is detailed below in our response to the reviewer’s comment on model complexity.

The basic idea of the model is simple and somewhat interesting, but the details are extremely complex. There are many examples of this, but the method used to "regress out" the behavior was very hard to interpret.

The method for regressing out behavior was described in Materials and Methods section 3.10, and we regret having neglected to reference it in the main text. We now reference it at the first instance in the main text where this is relevant.

On the face of it, the model is extremely simple: a two-state linear dynamical system. However, this simplistic description buries extreme complexity. The model is extremely complex as involves a large number of parameters (e.g., time switching 'b' values, the values of which are completely unclear), the switching over time of these parameters based on hand-scored animal behavioral state, and the complex mix of markovian and linear dynamical systems theoretic results.

As the reviewer pointed out, the core of the model is very simple: a linear dynamical system that models neural activity coupling. The model mechanism of positive and negative feedback, which is responsible for reproducing the two experimental results summarized by the reviewer above, is contained in this core (see Materials and Methods section 3.7 for details). On top of this, the model has a layer of complexity, involving a Markov chain model of behavior and a large number of behavioral parameters. This layer of complexity is independent from the feedback mechanism of the core of the model. Thus, while it makes the model more biologically realistic, it is not required to reproduce the two main experimental results. To explicitly show this, and to better understand the dependence of model behavior on its parameters, we analyzed two reduced versions of the model. The first reduced model replaces the behavioral inputs with white noise. The original model is , where a is neural activity, , is the coupling matrix, b is behavioral modulation, and τ is a time constant. b is where the complexity lies, as it is simulated using a Markov chain and involves many parameters. To strip away this layer of complexity, we replaced b with noise having a simple structure, namely, the mean and difference components of b having identical, flat power spectra. Importantly, this noise input does not induce correlation between bats, and it amounts to inputs of the same magnitude and same timescales to the mean and difference components of a. The resulting reduced model has only two parameters, the functional self-coupling C_S and functional across-brain coupling C_I (for simplicity, τ can be absorbed into the other parameters). We are interested in the two results the reviewer summarized above: (1) the mean component of neural activity having a larger variance than the difference component; (2) the mean component having a slow timescale than the difference component. In the manuscript, these are respectively quantified using the variance ratio and the power spectral centroid ratio of the mean and difference components. The reduced model allowed us to derive analytical expressions for these two quantities (see Materials and Methods section 3.8 for details). We found that they have very simple dependence on the functional coupling parameters: the variance ratio (mean variance divided by difference variance) is approximately , and the centroid ratio (mean centroid divided by difference centroid) is approximately .

This parameter dependence is visualized below (note that the color maps are in log scale, and the white spaces are regions where the model is unstable).

In the experimental data, the mean component had larger variance and lower power spectral centroid than the difference component. This corresponds to the parameter regime of (enclosed by dashed lines). Thus, a positive C_I acts as positive feedback to the mean component and negative feedback to the difference component, modulating their variance and timescales in opposite directions. This is consistent with the analysis of the original model in Materials and Methods section 3.7. In the revised manuscript, we’ve now added analysis of this reduced model to the Results section, and the above figure has been added as Figure 3I-J.

The reviewer has stated a concern regarding the large number of parameters that set the input level according to behavioral state (b_resting, b_(social grooming), b_fighting, etc.). These parameters are important for ensuring that the model outputs realistic levels of behaviorally modulated neural activity (discussed below in our reply regarding model fit), but they are not important for the main results on variance and timescales. To demonstrate this, we studied a second reduced model. This model is identical to our original model except that, for each simulation, each of the behavior parameters (b_fighting, etc.) was independently drawn from the uniform distribution from 0 to 1. Despite the completely random behavioral parameters, this reduced model reproduces the variance and timescales results just like the original model, as shown in the figure below (compare with Figure 3E-F).

To summarize, the reduced models allowed us to identify the simple parameter dependence of the modeling results, and showed that the simple linear dynamical system at the core of the original model is sufficient to reproduce the two main experimental observations.

Indeed, a fundamental weakness of the model is that the Markov chain is taken as an "input" to the 2-state linear systems model, as if somehow the neural state does not affect the state transitions.

Yes, this is a limitation of our model. We’ve added a discussion of this limitation, as well as future directions for overcoming it, in the Discussion section. The reason we did not model neural control of behavioral transitions is that it is under-constrained by existing data. While the brain obviously controls behaviors, not every part of the brain controls every behavior. Of the 11 behaviors observed in this study, we do not know which of them is controlled by the bat frontal cortex, and we do not know how they might be controlled (i.e., what specific spatiotemporal activity patterns affects behaviors in what ways). Without this knowledge, it’s unclear how to implement neural control of behavior in the model. This knowledge requires perturbation studies (lesion, inactivation, or activity manipulation) to establish casual relationships from neural activity to specific behaviors in the bat, which will be an important future direction.

On the other hand, as the reviewer stated, our model included behavioral modulation of neural activity. It is well known that in mammals, arousal and movement modulate neural activity globally across cortex (McGinley et al., 2015, Neuron). Thus, given that different behaviors in general involve different levels of arousal and movement, our model included behavior-dependent modulation of frontal cortical neural activity. Finally, for the reviewer’s convenience, we also quote below the paragraph addressing this issue in the revised Discussion. “Another limitation of our model is the “open-loop” nature of the relationship between behavior and neural activity. Specifically, we modeled neural activity as being modulated by behavior, but behavior was modeled using a Markov chain that is independent from the neural activity. In reality, neural activity and behavior form a closed-loop, with different social behaviors being controlled by the neural activity of specific neural populations in specific brain regions. Thus, an important future direction is to close the loop by incorporating neural control of social behaviors into models of the inter-brain relationship in bats. This will require future experimental studies to identify which frontal cortical regions and populations in bats are necessary or sufficient to control social behaviors, as well as the detailed causal relationship from neural activity to social behavior. Furthermore, as social interactions can occur at multiple timescales, it will be interesting to investigate how these are controlled by neural activity at different timescales, and how those timescales are shaped by functional across-brain coupling. In summary, such a closed-loop model will shed light on how inter-brain activity patterns and dynamic social interactions co-evolve and feedback onto each other.”

Further, the Markov assumption is not rigorously tested.

We have now tested the Markov assumption, using the following methods. We compared three models of bat behaviors: (1) the independent model, where the behavioral state at a given time point is independent from the state at other time points; (2) the 1st-order dependency model, where the behavioral state at a given time point depends on the state at the previous time point only; (3) the 2nd-order dependency model, where the behavioral state at a given time point depends on the states at the two previous time points. The Markov assumption corresponds to model (2), which is used as a part of the main model of the paper. Note that models with longer time-dependencies (≥3) were not tested because the number of parameters grows exponentially with model order and our dataset is not large enough to fit them.

To compare the three models, we split the behavioral data into a training set and a test set, fitted each model on the training set (Laplace smoothing was used to avoid assigning zero probability to unobserved events), and calculated the log-likelihood of the test set under each model. The figure below shows the cross-validated likelihoods for the behavioral data of one-chamber (A) and two-chambers (B) sessions, which were fitted separately; circles and error bars are means and standard deviations across 100 random splits of the data into training and test sets.

As the figure above shows, the 1st-order model had the highest likelihood on average. This does not necessarily prove that bat behavior obeys the Markov assumption (if we had a lot more data, we might be able to fit better 2nd-order and higher-order models). But this does mean that, given the amount of data we have, the best model that we can fit is the 1st-order Markov chain. Thus, this result supports our usage of the Markov chain in the main model of the paper. In the revised manuscript, the above figure is included as Figure 3—figure supplement 2A-B, and the analysis is described in Materials and Methods section 3.5.

No model selecting or other model validation appears to be done.

To evaluate model fit, we simulated our model using experimentally observed behaviors (rather than simulating behaviors using a Markov chain), and compared the simulated neural activity with the experimentally observed activity (see Materials and Methods section 3.6 for detailed procedures). The comparison for an example experimental session is shown below, where we’ve plotted the experimentally observed neural activity and behaviors for bat 1 (A) and bat 2 (B), along with the simulated neural activity. The correlation coefficient between data and model are indicated above each plot. These are representative examples, as the average correlation over all sessions and bats is 0.72 (standard deviation is 0.10). This figure was added to the revised manuscript as Figure 3—figure supplement 1.

In evaluating model fit, we realized that the model in the original manuscript produced outputs with a DC offset different from that of the data. Thus, in the revised manuscript (including the figure above), we added one more behavioral parameter (b_constant) that adjusts the DC offset, which is a parameter that reflects the effect of a baseline arousal level on neural activity (Materials and Methods section 3.4). Note that, since the only effect of this parameter is to adjust the DC offset of neural activity, it does not change any of the results in the paper.

In short, the model, while very interesting, is so complex that it is literally impossible to evaluate. The authors report literally no shortcomings of their model. They do not report parameter estimation methods. They do not report fitting errors or other model validation metrics. The only evaluation is whether it can produce certain outputs that are similar to biological data. While the latter is certainly important, all models are wrong, and it essential to have a model simple enough to understand, both in terms of how it works and how it fails.

The comments on the complexity of the model and on fitting errors have been addressed above. Regarding parameter estimation methods, they were described in Materials and Methods section 3.14, and we regret having neglected to directly reference it in the original manuscript. We now reference the section in the legend of Figure 3A which is the first place to introduce the parameters. Briefly, the behavioral parameters (b_resting, b_fighting, etc.) were simply chosen to be the average neural activity during the respective behaviors from the data; the other parameters were chosen by hand to roughly match the levels of activity from the data, keeping within the parameter regime of identified from the analyses. As we showed above, these parameters provide a reasonable fit to the data.

The reason we chose the parameters heuristically in this way, rather than by minimizing some error objective, is the following. Our goal was to build a model that could qualitatively reproduce the experimental findings in a robust manner, that is, without fine-tuning of parameters. Thus, we analyzed the model to understand how model behaviors depend on the parameters, and to identify the parameter regime that reproduces the qualitative trends seen in the data (Figure 3I-J; Materials and Methods sections 3.7 and 3.8). Guided by these analyses, we chose parameters heuristically without algorithmic fine-tuning.

Finally, following suggestions from reviewer 1 and reviewer 3, we have added discussions of shortcomings of the models (the last two paragraphs of the Discussion). With these discussions of model limitations, along with the presentation of simple insights into model mechanism from the reduced models above, we believe we have now presented a model that is “simple enough to understand, both in terms of how it works and how it fails.”

In general, while the basic finding is fairly interesting, and the experiments and their findings are highly relevant to the field, the modeling and its explication fall short.

It is not that it is wrong or bad; however, it is not clear that such a complex model increases our understanding beyond the experimental findings in Figure 1, and if it does, there has to be a major caveat that the model itself is not carefully vetted.

Based on the reviewer’s comments on the model’s complexity, we have analyzed reduced versions of the model to understand its simple underlying mechanisms, as described above. This goes beyond the experimental findings in Figure 1, as it provides a computational mechanism that could give rise to those experimental findings. Moreover, based on the reviewer’s comments, we have more carefully vetted the model, by evaluating model fit and testing different behavioral models that assume or doesn’t assume the Markov property. Finally, we now discuss caveats of the model in the Discussion section, including the open-loop nature of the model as pointed out by the reviewer.

Author Response

Reviewer #1 (Public Review):

Overall, the science is sound and interesting, and the results are clearly presented. However, the paper falls in-between describing a novel method and studying biology. As a consequence, it is a bit difficult to grasp the general flow, central story and focus point. The study does uncover several interesting phenomena, but none are really studied in much detail and the novel biological insight is therefore a bit limited and lost in the abundance of observations. Several interesting novel interactions are uncovered, in particular for the SPS sensor and GAPDH paralogs, but these are not followed up on in much detail. The same can be said for the more general observations, eg the fact that different types of mutations (missense vs nonsense) in different types of genes (essential vs non-essential, housekeeping vs. stress-regulated...) cause different effects.

This is not to say that the paper has no merit - far from it even. But, in its current form, it is a bit chaotic. Maybe there is simply too much in the paper? To me, it would already help if the authors would explicitly state that the paper is a "methods" paper that describes a novel technique for studying the effects of mutations on protein abundance, and then goes on to demonstrate the possibilities of the technology by giving a few examples of the phenomena that can be studied. The discussion section ends in this way, but it may be helpful if this was moved to the end of the introduction.

We modified the manuscript as suggested.

Reviewer #2 (Public Review):

Schubert et al. describe a new pooled screening strategy that combines protein abundance measurements of 11 proteins determined via FACS with genome-wide mutagenesis of stop codons and missense mutations (achieved via a base editor) in yeast. The method allows to identify genetic perturbations that affect steady state protein levels (vs transcript abundance), and in this way define regulators of protein abundance. The authors find that perturbation of essential genes more often alters protein abundance than of nonessential genes and proteins with core cellular functions more often decrease in abundance in response to genetic perturbations than stress proteins. Genes whose knockouts affected the level of several of the 11 proteins were enriched in protein biosynthetic processes while genes whose knockouts affected specific proteins were enriched for functions in transcriptional regulation. The authors also leverage the dataset to confirm known and identify new regulatory relationships, such as a link between the SDS amino acid sensor and the stress response gene Yhb1 or between Ras/PKA signalling and GAPDH isoenzymes Tdh1, 2, and 3. In addition, the paper contains a section on benchmarking of the base editor in yeast, where it has not been used before.

Strengths and weaknesses of the paper

The authors establish the BE3 base editor as a screening tool in S. cerevisiae and very thoroughly benchmark its functionality for single edits and in different screening formats (fitness and FACS screening). This will be very beneficial for the yeast community.

The strategy established here allows measuring the effect of genetic perturbations on protein abundances in highly complex libraries. This complements capabilities for measuring effects of genetic perturbations on transcript levels, which is important as for some proteins mRNA and protein levels do not correlate well. The ability to measure proteins directly therefore promises to close an important gap in determining all their regulatory inputs. The strategy is furthermore broadly applicable beyond the current study. All experimental procedures are very well described and plasmids and scripts are openly shared, maximizing utility for the community.

There is a good balance between global analyses aimed at characterizing properties of the regulatory network and more detailed analyses of interesting new regulatory relationships. Some of the key conclusions are further supported by additional experimental evidence, which includes re-making specific mutations and confirming their effects on protein levels by mass spectrometry.

The conclusions of the paper are mostly well supported, but I am missing some analyses on reproducibility and potential confounders and some of the data analysis steps should be clarified.

The paper starts on the premise that measuring protein levels will identify regulators and regulatory principles that would not be found by measuring transcripts, but since the findings are not discussed in light of studies looking at mRNA levels it is unclear how the current study extends knowledge regarding the regulatory inputs of each protein.

See response to Comment #10.

Specific comments regarding data analysis, reproducibility, confounders

1) The authors use the number of unique barcodes per guide RNA rather than barcode counts to determine fold-changes. For reliable fold changes the number of unique barcodes per gRNA should then ideally be in the 100s for each guide, is that the case? It would also be important to show the distribution of the number of barcodes per gRNA and their abundances determined from read counts. I could imagine that if the distribution of barcodes per gRNA or the abundance of these barcodes is highly skewed (particularly if there are many barcodes with only few reads) that could lead to spurious differences in unique barcode number between the high and low fluorescence pool. I imagine some skew is present as is normal in pooled library experiments. The fold-changes in the control pools could show whether spurious differences are a problem, but it is not clear to me if and how these controls are used in the protein screen.

Because of the large number of screens performed in this study (11 proteins, with 8 replicates for each) we had to trade off sequencing depth and power against cell sorting time and sequencing cost, resulting in lower read and barcode numbers than what might be ideally aimed for. As described further in the response to Comment #5, we added a new figure to the manuscript that shows that the correlation of fold-changes between replicates is high (Figure 3–S1A). The second figure below shows that the correlation between the number of unique barcodes and the number of reads per gRNA is highly significant (p < 2.2e-16).

2) I like the idea of using an additional barcode (plasmid barcode) to distinguish between different cells with the same gRNA - this would directly allow to assess variability and serve as a sort of replicate within replicate. However, this information is not leveraged in the analysis. It would be nice to see an analysis of how well the different plasmid barcodes tagging the same gRNA agree (for fitness and protein abundance), to show how reproducible and reliable the findings are.

We agree with the reviewer that this would be nice to do in principle, but our sequencing depth for the sorted cell populations was not high enough to compare the same barcode across the low/unsorted/high samples. See also our response to Comment #5 for the replicate analyses.

3) From Fig 1 and previous research on base editors it is clear that mutation outcomes are often heterogeneous for the same gRNA and comprise a substantial fraction of wild-type alleles, alleles where only part of the Cs in the target window or where Cs outside the target window are edited, and non C-to-T edits. How does this reflect on the variability of phenotypic measurements, given that any barcode represents a genetically heterogeneous population of cells rather than a specific genotype? This would be important information for anyone planning to use the base editor in future.

We agree with the reviewer that the heterogeneity of editing outcomes is an important point to keep in mind when working with base editors. In genetic screens, like the ones described here, often the individual edit is less important, and the overall effects of the base editor are specific/localized enough to obtain insights into the effects of mutations in the area where the gRNA targets the genome. For example, in our test screens for Canavanine resistance and fitness effects, in which we used gRNAs predicted to introduce stop codons into the CAN1 gene and into essential genes, respectively, we see the expected loss-of-function effect for a majority of the gRNAs (canavanine screen: expected effect for 67% of all gRNAs introducing stop codons into CAN1; fitness screen: expected effect for 59% of all gRNAs introducing stop codons into essential genes) (Figure 2). In the canavanine screen, we also see that gRNAs predicted to introduce missense mutations at highly conserved residues are more likely to lead to a loss-of-function effect than gRNAs predicted to introduce missense mutations at less conserved residues, further highlighting the differentiated results that can be obtained with the base editor despite the heterogeneity in editing outcomes overall. We would certainly advise anyone to confirm by sequencing the base edits in individual mutants whenever a precise mutation is desired, as we did in this study when following up on selected findings with individual mutants.

4) How common are additional mutations in the genome of these cells and could they confound the measured effects? I can think of several sources of additional mutations, such as off-target editing, edits outside the target window, or when 2 gRNA plasmids are present in the same cell (both target windows obtain edits). Could some of these events explain the discrepancy in phenotype for two gRNAs that should make the same mutation (Fig S4)? Even though BE3 has been described in mammalian cells, an off-target analysis would be desirable as there can be substantial differences in off-target behavior between cell types and organisms.

Generally, we are not very concerned about random off-target activity of the base editor because we would not expect this to cause a consistent signal that would be picked up in our screen as a significant effect of a particular gRNA. Reproducible off-target editing with a specific gRNA at a site other than the intended target site would be problematic, though. We limited the chance of this happening by not using gRNAs that may target similar sequences to the intended target site in the genome. Specifically, we excluded gRNAs that have more than one target in the genome when the 12 nucleotides in the seed region (directly upstream of the PAM site) are considered (DiCarlo et al., Nucleic Acids Research, 2013).

We do observe some off-target editing right outside the target window, but generally at much lower frequency than the on-target editing in the target window (Figure 1B and Figure 1–S2). Since for most of our analyses we grouped perturbations per gene, such off-target edits should not affect our findings. In addition, we validated key findings with independent experiments. For our study, we used the Base Editor v3 (Komor et al., Nature, 2016); more recently, additional base editors have been developed that show improved accuracy and efficiency, and we would recommend these base editors when starting a new study (see, e.g., Anzalone et al., Nature Biotechnology, 2020).

We are not concerned about cases in which one cell gets two gRNAs, since the chance that the same two gRNAs end up in one cell repeatedly is low, and such events would therefore not result in a significant signal in our screens.

We don’t think that off-target mutations can explain the discrepancy between pairs of gRNAs that should introduce the same mutation (Figure 3–S1. The effect of the two gRNAs is actually well-correlated, but, often, one of the two gRNAs doesn’t pass our significance cut-off or simply doesn’t edit efficiently (i.e., most discrepancies arise from false negatives rather than false positives). We may therefore miss the effects of some mutations, but we are unlikely to draw erroneous conclusions from significant signals.

5) In the protein screen normalization uses the total unique barcode counts. Does this efficiently correct for differences from sequencing (rather than total read counts or other methods)? It would be nice to see some replicate plots for the analysis of the fitness as well as the protein screen to be able to judge that.

We made a new figure that shows a replicate comparison for the protein screen (see below; in the manuscript it is Figure 3–S1A) and commented on it in the manuscript. For this analysis, the eight replicates for each protein were split into two groups of four replicates each and analyzed the same way as the eight replicates. The correlation between the two groups of replicates is highly significant (p < 2.2e-16). The second figure shows that the total number of reads and the total number of unique barcodes are well correlated.

For the fitness screen, we used read counts rather than barcode counts for the analysis since read counts better reflect the dropout of cells due to reduced fitness. The figure below shows a replicate comparison for the fitness screen. For this analysis, the four replicates were split into two groups of two replicates each and analyzed the same way as the four replicates. The correlation between the two groups of replicates is highly significant (p < 2.2e-16).

6) In the main text the authors mention very high agreement between gRNAs introducing the same mutation but this is only based on 20 or so gRNA pairs; for many more pairs that introduce the same mutation only one reaches significance, and the correlation in their effects is lower (Fig S4). It would be better to reflect this in the text directly rather than exclusively in the supplementary information.

We clarified this in the manuscript main text: “For 78 of these gRNA pairs, at least one gRNA had a significant effect (FDR < 0.05) on at least one of the eleven proteins; their effects were highly correlated (Pearson’s R2 = 0.43, p < 2.2E-16) (Figure 3–S1B). For the 20 gRNA pairs for which both gRNAs had a significant effect, the correlation was even higher (Pearson’s R2 = 0.819, p = 8.8e-13) (Figure 3–S1C). These findings show that the significant gRNA effects that we identify have a low false positive rate, but they also suggest that many real gRNA effects are not detected in the screen due to limitations in statistical power.”

7) When the different gRNAs for a targeted gene are combined, instead of using an averaged measure of their effects the authors use the largest fold-change. This seems not ideal to me as it is sensitive to outliers (experimental error or background mutations present in that strain).

We agree that the method we used is more sensitive to outliers than averaging per gene. However, because many gRNAs have no effect either because they are not editing efficiently or because the edit doesn’t have a phenotypic consequence, an averaging method across all gRNAs targeting the same gene would be too conservative and not properly capture the effect of a perturbation of that gene.

8) Phenotyping is performed directly after editing, when the base editor is still present in the cells and could still interact with target sites. I could imagine this could lead to reduced levels of the proteins targeted for mutagenesis as it could act like a CRISPRi transcriptional roadblock. Could this enhance some of the effects or alter them in case of some missense mutations?

To reduce potential “CRISPRi-like” effects of the base editor on gene expression, we placed the base editor under a galactose-inducible promoter. For both the fitness and protein screens we grew the cultures in media without galactose for another 24 hours (fitness screen) or 8-9 hours (protein screens) before sampling. In the latter case, this recovery time corresponded to more than three cell divisions, after which we assume base editor levels to have strongly decreased, and therefore to no longer interfere with transcription. This is also supported by our ability to detect discordant effects of gRNAs targeting the same gene (e.g., the two mutations leading to loss-of-function and gain-of-function of RAS2), which would otherwise be overshadowed by a CRISPRi effect.

9) I feel that the main text does not reflect the actual editing efficiency very well (the main numbers I noticed were 95% C to T conversion and 89% of these occurring in a specific window). More informative for interpreting the results would be to know what fraction of the alleles show an edit (vs wild-type) and how many show the 'complete' edit (as the authors assume 100% of the genotypes generated by a gRNA to be conversion of all Cs to Ts in the target window). It would be important to state in the main text how variable this is for different gRNAs and what the typical purity of editing outcomes is.

We now show the editing efficiency and purity in a new figure (Figure 1B), and discuss it in the main text as follows: “We found that the target window and mutagenesis pattern are very similar to those described in human cells: 95% of edits are C-to-T transitions, and 89% of these occurred in a five-nucleotide window 13 to 17 base pairs upstream of the PAM sequence (Figure 1A; Figure 1–S2) (Komor et al., 2016). Editing efficiency was variable across the eight gRNAs and ranged from 4% to 64% if considering only cases where all Cs in the window are edited; percentages are higher if incomplete edits are considered, too (Figure 1B).”

Comments regarding findings

10) It would be nice to see a comparison of the results to the effects of ~1500 yeast gene knockouts on cellular transcriptomes (https://doi.org/10.1016/j.cell.2014.02.054). This would show where the current study extends established knowledge regarding the regulatory inputs of each protein and highlight the importance of directly measuring protein levels. This would be particularly interesting for proteins whose abundance cannot be predicted well from mRNA abundance.

We agree with the reviewer that it would be very interesting to compare the effect of perturbations on mRNA vs protein levels. We have compared our protein-level data to mRNA-level data from Kemmeren and colleagues (Kemmeren et al., Cell 2014), and we find very good agreement between the effects of gene perturbations on mRNA and protein levels when considering only genes with q < 0.05 and Log2FC > 0.5 in both studies (Pearson’s R = 0.79, p < 5.3e-15).

Gene perturbations with effects detected only on mRNA but not protein levels are enriched in genes with a role in “chromatin organization” (FDR = 0.01; as a background for the analysis, only the 1098 genes covered in both studies were considered). This suggests that perturbations of genes involved in chromatin organization tend to affect mRNA levels but are then buffered and do not lead to altered protein levels. There was no enrichment of functional annotations among gene perturbations with effects on protein levels but not mRNA levels.

We did not include these results in the manuscript because there are some limitations to the conclusions that can be drawn from these comparisons, including that our study has a relatively high number of false negatives, and that the genes perturbed in the Kemmeren et al. study were selected to play a role in gene regulation, meaning that differences in mRNA-vs-protein effects of perturbations are limited to this function, and other gene functions cannot be assessed.

11) The finding that genes that affect only one or two proteins are enriched for roles in transcriptional regulation could be a consequence of 'only' looking at 10 proteins rather than a globally valid conclusion. Particularly as the 10 proteins were selected for diverse functions that are subject to distinct regulatory cascades. ('only' because I appreciate this was a lot of work.)

We agree with this, and we think it is clear in the abstract and the main text of the manuscript that here we studied 11 proteins. We made this point also more explicit in the discussion, so that it is clear for readers that the findings are based on the 11 proteins and may not extrapolate to the entire yeast proteome.

Reviewer #3 (Public Review):

This manuscript presents two main contributions. First, the authors modified a CRISPR base editing system for use in an important model organism: budding yeast. Second, they demonstrate the utility of this system by using it to conduct an extremely high throughput study the effects of mutation on protein abundance. This study confirms known protein regulatory relationships and detects several important new ones. It also reveals trends in the type of mutations that influence protein abundances. Overall, the findings are of high significance and the method appears to be extremely useful. I found the conclusions to be justified by the data.

One potential weakness is that some of the methods are not described in main body of the paper, so the reader has to really dive into the methods section to understand particular aspects of the study, for example, how the fitness competition was conducted.

We expanded the first section for better readability.

Another potential weakness is the comparison of this study (of protein abundances) to previous studies (of transcript abundances) was a little cursory, and left some open questions. For example, is it remarkable that the mutations affecting protein abundance are predominantly in genes involved in translation rather than transcription, or is this an expected result of a study focusing on protein levels?

We thank the reviewer for pointing out that this paragraph requires more explanation. We expanded it as follows: “Of these 29 genes, 21 (72%) have roles in protein translation—more specifically, in ribosome biogenesis and tRNA metabolism (FDR < 8.0e-4, Figure 5C). In contrast, perturbations that affect the abundance of only one or two of the eleven proteins mostly occur in genes with roles in transcription (e.g., GO:0006351, FDR < 1.3e-5). Protein biosynthesis entails both transcription and translation, and these results suggest that perturbations of translational machinery alter protein abundance broadly, while perturbations of transcriptional machinery can tune the abundance of individual proteins. Thus, genes with post-transcriptional functions are more likely to appear as hubs in protein regulatory networks, whereas genes with transcriptional functions are likely to show fewer connections.”

Overall, the strengths of this study far outweigh these weaknesses. This manuscript represents a very large amount of work and demonstrates important new insights into protein regulatory networks.

Author Response

Reviewer #2 (Public Review):

The authors seek to determine how various species combine their effects on the growth of a species of interest when part of the same community.

To this end, the authors carry out an impressive experiment containing what I believe must be one of the largest pairwise + third-order co-culture experiments done to date, using a high-throughput co-culture system they had co-developed in previous work. The unprecedented nature of this data is a major strength of the paper. The authors also discover that species combine their effect through "dominance", i.e. the strongest effect masks the others. This is important as it calls into question the common assumption of additivity that is implicit in the choice of using Lotka-Volterra models.

A stronger claim (i.e. in the abstract) is that joint effect of multiple species on the growth of another can be derived from the effect of individual species. Unless I am misunderstanding something, this statement may have to be qualified a little, as the authors show that a model based on pairwise dominance (i.e. the strongest pairwise) does a somewhat better job (lower RMSD, though granted, not by much, 0.57 vs 0.63) than a model based on single species dominance. This is, the effect of the strongest pair predicts better the effect of a trio than the effect of the larger species.

This issue makes one wonder whether, had the authors included higher-order combinations of species (i.e. five-member consortia or higher), the strongest-effect trio would have predicted better than the strongest-effect pair, which in turn is better predictor than the strongest-effect species. This is important, as it would help one determine to what extent the strongest-effect model would work in more diverse communities, such as those one typically finds in nature. Indeed, the authors find that the predictive ability of the strongest effect species is much stronger for pairs than it is for trios (RMSD of 0.28 vs 0.63). Does the predictive ability of the single species model decline faster and faster as diversity grows beyond 4-member consortia?

Thank you for raising this important point. It is true that in our study we see that single species predict pairs better than trios, and that pairs predict trios better than single species. As we did not perform experiments on more diverse communities (n>4), we are not sure if or how these rules will scale up. We explicitly address these caveats in our revised discussion.

Reviewer #3 (Public Review):

A problem in synthetic ecology is that one can't brute-force complex community design because combinatorics make it basically impossible to screen all possible communities from a bank of possible species. Therefore, we need a way to predict phenomena in complex communities from phenomena in simple communities. This paper aims to improve this predictive ability by comparing a few different simple models applied to a large dataset obtained with the use of the author's "kchip" microfluidics device. The main question they ask is whether the effect of two species on a focal species is predicted from the mean, the sum, or the max of the effect of each single "affecting" species on the focal species. They find that the max effect is often the best predictor, in the sense of minimizing the difference between predicted effect and measured effect. They also measure single-species trait data for their library of strains, including resource niche and antibiotic resistance, and then find that Pearson correlations between distance calculations generated from these metrics and the effect of added species are weak and unpredictive. This work is largely well-done, timely and likely to be of high interest to the field, as predicting ecosystem traits from species traits is a major research aim.

My main criticism is that the main take-home from the paper (fig 3B)-that the strongest effect is the best predictor-is oversold. While it is true that, averaged over their six focal species, the "strongest effect" was the best overall predictor, when one looks at the species-specific data (S9), we see that it is not the best predictor for 1/3 of their focal species, and this fraction grows to 1/2 if one considers a difference in nRMSE of 0.01 to be negligible.

As suggested, we have softened our language regarding the take-home message. This matter is addressed in detail above in response to 'Essential Revisions'. Briefly, we see that the strongest model works best when both single species have qualitatively similar effects, but is slightly less accurate when effects are mixed. We also see overall less accurate predictions for positive effects. In light of these findings, we propose that focal species for which the strongest model is not the most accurate is due to the interaction types, and not specific to the focal species.

We made substantial changes to the manuscript, including the first paragraph of the discussion which more accurately describes these findings and emphasizes the relevant caveats:

"By measuring thousands of simplified microbial communities, we quantified the effects of single species, pairs, and trios on multiple focal species. The most accurate model, overall and specifically when both single species effects were negative, was the strongest effect model. This is in stark contrast to models often used in antibiotic compound combinations, despite most effects being negative, where additivity is often the default model (Bollenbach 2015). The additive model performed well for mixed effects (i.e. one negative and one positive), but only slightly better than the strongest model, and poorly when both species had effects of the same sign. When both single species’ effects were positive, the strongest model was also the best, though the difference was less pronounced and all models performed worse for these interactions. This may be due to the small effect size seen with positive effects, as when we limited negative and mixed effects to a similar range of effects strength, their accuracy dropped to similar values (Figure 3–Figure supplement 5). We posit that the difference in accuracy across species is affected mainly by the effect type dominating different focal species' interactions, rather than by inherent species traits (Figure 3–Figure supplement 6)." (Lines 288-304)

The same criticism applies to the result from figure 2-that pairs of affecting species have more negative effects than single species. Considered across all focal species this is true (though minor in effect size, Fig 2A). But there is only a significant effect within two individual species. Again, this points to the effects being focal-species-specific, and perhaps not as generalizable as is currently being claimed.

Upon more rigorous analysis, and with regard to changes in the dataset after filtering, we see that the more accurate statement is that effects become stronger, not necessarily more negative (in line with the accuracy of the strongest model). The overall trend is towards more negative interactions, due to the majority of interactions being negative, but as stated this is not true for each individual focal. As such the following sentence in the manuscript has been changed:

"The median effect on each focal was more negative by 0.28 on average, though the difference was not significant in all cases; additionally, focals with mostly positive single species interactions showed a small increase in median effect (Fig. 2D)" (Lines 151-154)

As well as the title of this section: "Joint effects of species pairs tend to be stronger than those of individual affecting species" (Lines 127-128)

Another thing that points to a focal-species-specific response is Fig 2D, which shows the distributions of responses of each focal species to pairs. Two of these distributions are unimodal, one appears bimodal, and three appear tri-modal. This suggests to me that the focal species respond in categorically different ways to species addition.

We believe this distribution of pair effects is related to the distribution of single species effects, and not to the way in which different focal species respond to the addition of second species. Though this may be difficult to see from the swarm plots shown in the paper, below is a split violin plot that emphasizes this point.

Fig R1: Distribution of single species and pair effects. Distribution of the effect of single and pairs of affecting species for each focal species individually. Dashed lines represent the median, while dotted lines the interquartile range.

These differences occur even though the focal bacteria are all from the same family. This suggests to me that the generalizability may be even less when a more phylogenetically dispersed set of focal species are used.

We have added the following sentence to the discussion explicitly emphasizing the phylogenetic limitations of our study:

"Lastly, it is important to note that our focal species are all from the same order (Enterobacterales), which may also limit the purview of our findings." (Lines 364-366)

Considering these points together, I argue that the conclusion should be shifted from "strongest effect is the best" to "in 3 of our focal species, strongest effect was the best, but this was not universal, and with only 6 focal species, we can't know if it will always be the best across a set of focal species".

As mentioned above, we have softened our language regarding the take-home message in response to these evaluations.

My second main criticism is that it is hard to understand exactly how the trait data were used to predict effects. It seems like it was just pearson correlation coefficients between interspecies niche distances (or antibiotic distances) and the effect. I'm not very surprised these correlations were unpredictive, because the underlying measurements don't seem to be relevant to the environment tested. What if, rather than using niche data across 20 nutrients, only the growth data on glucose (the carbon source in the experiments) was used? I understand that in a field experiment, for example, one might not know what resources are available, and so measuring niche across 20 resources may be the best thing to do. Here though it seems imperative to test using the most relevant data.

It is true that much of the profiling data is not directly related to the experimental conditions (different carbon sources and antibiotics), but in addition to these we do use measurements from experiments carried out in the same environment as the interactions assays (i.e. growth rate and carrying capacity when growing on glucose), which also showed poor correlation with the effects on focals. Additionally, we believe that these profiles contain relevant information regarding metabolic similarity between species (similar to metabolic models often constructed computationally). To improve clarity, we added the following sentence to the figure legend of Figure 3–Figure supplement 1:

"The growth rate, and maximum OD shown in panel A were measured only in M9 glucose, similar to conditions used in the interaction assays." (Lines 591-592)

Additionally and relatedly, it would be valuable to show the scatterplots leading to the conclusion that trait data were uninformative. Pearson's r only works on an assumption of linearity. But there could be strong relationships between the trait data and effect that are monotonic but not linear, or even that are non-monotonic yet still strong (e.g. U-shaped). For the first case, I recommend switching to Spearman's rho over Pearson's r, because it only assumes monotonicity, not linearity. If there are observable relationships that are not monotonic, a different test should be used.

Per your suggestion, we have changed the measurement of correlation in this analysis from Pearson's r, to Spearman's rho. As we observed similar, and still mostly weak correlations, we did not investigate these relationships further. See Figure 3–Figure supplement 1.

Additionally, we generated heat maps including scatterplots mapping the data leading to these correlations. We found no notable dependency in these plots, and visually they were quite crowded and difficult to interpret. As this is not the central point of our study, we ultimately decided against adding this information to the plots.

In general, I think the analyses using the trait data were too simplistic to conclude that the trait data are not predictive.

We agree that more sophisticated analyses may help connect between species traits and their effects on focal species. In fact, other members of our research group have recently used machine learning to accomplish similar predictions (https://doi.org/10.1101/2022.08.02.502471). As such we have changed the wording in to reflect that this correlation is difficult to find using simple analyses:

"These results indicate that it may be challenging to connect the effects of single and pairs of species on a focal strain to a specific trait of the involved strains, using simple analysis." (Lines 157-159)

Author Response

Reviewer #1 (Public Review):

Slusarczyk et al present a very well written manuscript focused on understanding the mechanisms underlying aging of erythrophagocytic macrophages in the spleen (RPM) and its relationship to iron loading with age. The manuscript is diffuse with a broad swath of data elements. Importantly, the manuscript demonstrates that RPM erythrophagocytic capacity is diminished with age, restored in iron restricted diet fed aged mice. In addition, the mechanism for declining RPM erythrophagocytic capacity appears to be ferroptosis-mediated, insensitive to heme as it is to iron, and occur independently of ROS generation. These are compelling findings. However, some of the data relies on conjecture for conclusion and a clear causal association is not clear. The main conclusion of the manuscript points to the accumulation of unavailable insoluble forms of iron as both causing and resulting from decreased RPM erythrophagocytic capacity.

We are proposing that intracellular iron accumulation progresses first and leads to global proteotoxic damage and increased lipid peroxidation. This eventually triggers the death of a fraction of aging RPMs, thus promoting the formation of extracellular iron-rich protein aggregates. More explanation can be found below. Besides, iron loading suppresses the erythrophagocytic activity of RPMs, hence further contributing to their functional impairment during aging.

In addition, the finding that IR diet leads to increased TF saturation in aged mice is surprising.

We believe that this observation implies better mobilization of splenic iron stores, and corroborates our conclusion that mice that age on an iron-reduced diet benefit from higher iron bioavailability, although these differences are relatively mild. More explanation can be found in our replies to Reviewer #2.

Furthermore, whether the finding in RPMs is intrinsic or related to RBC-related changes with aging is not addressed.

We now addressed this issue and we characterized in more detail both iron and ROS levels in RBCs.

Finally, these findings in a single strain and only female mice is intriguing but warrants tempered conclusions.

We tempered the conclusions and provided a basic characterization of the RPM aging phenotype in Balb/c female mice.

Major points:

1) The main concern is that there is no clear explanation of why iron increases during aging although the authors appear to be saying that iron accumulation is both the cause of and a consequence of decreased RPM erythrophagocytic capacity. This requires more clarification of the main hypothesis on Page 4, line 17-18.

We thank the reviewer for this comment. It was previously reported that iron accumulates substantially in the spleen during aging, especially in female mice (Altamura et al., 2014). Since RPMs are those cells that process most of the iron in the spleen, we aimed to explore what is the relationship between iron accumulation and RPM functions during aging. This investigation led us to uncover that indeed iron accumulation is both the cause and the consequence of RPM dysfunction. Specifically, we propose that intracellular iron loading of RPMs precedes extracellular deposition of iron in a form of protein-rich aggregates, driven by RPMs damage. To support this, we now show that the proteome of RPMs overlaps with those proteins that are present in the age-triggered aggregates (Fig. 3F). Furthermore, corroborating our model, we now demonstrate that transient iron loading of RPMs via iron-dextran injection (new Fig. 3G) leads to the formation of protein-rich aggregates, closely resembling those present in aged spleens (new Fig. 3H). This implies that high iron content in RPMs is indeed a major driving factor that leads to aggregation of their proteome and cell damage. Importantly, we now supported this model with studies using iRPMs. We demonstrated that iron loading and blockage of ferroportin by synthetic mini-hepcidin (PR73)(Stefanova et al., 2018) cause protein aggregation in iRPMs and lead to their decreased viability only in cells that were exposed to heat shock, a well-established trigger of proteotoxicity (new Fig. 5K and L). We propose that these two factors, namely age-triggered decrease in protein homeostasis and exposure to excessive iron levels, act in concert and render RPMs particularly sensitive to damage during aging (see also Discussion, p. 16).

In parallel, our data imply that the increased iron content in aged RPMs drives their decreased erythrophagocytic activity, as we now better documented by more extensive in vitro experiments in iRPMs (new Fig 6E-H). We cannot exclude that some of the senescent splenic RBCs that are retained in the red pulp and evade erythrophagocytosis due to RPM defects in aging, may also contribute to the formation of the aggregates. This is supported by the fact that mice that lack RPMs as well exhibit iron loading in the spleen (Kohyama et al., 2009; Okreglicka et al., 2021), and that the proteome of aggregates overlaps to some extent with the proteome of erythrocytes (new Fig. 3F).

We believe that during aging intracellular iron accumulation is chiefly driven by ferroportin downregulation, as also suggested by Reviewer#3. We now show that ferroportin drops significantly already in mice aged 4 and 5 months (new Fig. 4H), preceding most of the other impairments. This drop coincides with the increase in hepcidin expression, but if this is the sole reason for ferroportin suppression during early aging would require further investigation outside the scope of the present manuscript.

In sum, to address this comment, we now modified the fragment of the introduction that refers to our hypothesis and major findings to be more clear (p. 4), we improved our manuscript by providing new data mentioned above and we added more explanation in the corresponding sections of the Results and Discussion.

2) It is unclear if RPMs are in limited supply. Based on the introduction (page 4, line 13-15), they have limited self-renewal capacity and blood monocytes only partially replenished. Fig 4D suggests that there is a decrease in RPMs from aged mice. The %RPM from CD45+ compartment suggests that there may just be relatively more neutrophils or fewer monocytes recruited. There is not enough clarity on the meaning of this data point.

Thank you for this comment. We fully agree that %RPMs of CD45+ splenocytes, although well-accepted in literature (Kohyama et al., 2009; Okreglicka et al., 2021), is only a relative number. Hence, we now included additional data and explanations regarding the loss of RPMs during aging.

It was reported that the proportion of RPMs derived from bone marrow monocytes increases mildly but progressively during aging (Liu et al., 2019). This implies that due to the loss of the total RPM population, as illustrated by our data, the cells of embryonic origin are likely even more affected. We could confirm this assumption by re-analysis of the data from Liu et al. that we now included in the manuscript as Fig. 5E. These data clearly show that the representation of embryonically-derived RPMs drops more drastically than the percent of total RPMs, whereas the replenishment rate from monocytes is not affected significantly during aging. Consistent with this, we have not observed any robust change in the population of monocytes (F4/80-low, CD11b-high) or pre-RPMs (F4/80-high, CD11b-high) in the spleen at the age of 10 months (Figure 5-figure supplement 2A and B). We also have detected a mild decrease, not an increase, in the number of granulocytes (new Figure 5-figure supplement 2C). Furthermore, we measured in situ apoptosis marker and found a clear sign of apoptosis in the aged spleen (especially in the red pulp area), a phenotype that is less pronounced in mice on an IR diet (new Fig. 5O). This is consistent with the observation that apoptosis markers can be elevated in tissues upon ferroptosis induction (Friedmann Angeli et al., 2014) and that the proteotoxic stress in aged RPMs, which we now emphasized better in our manuscript, may also lead to apoptosis (Brancolini & Iuliano, 2020). Taken together, we strongly believe that the functional defect of embryonically-derived RPMs chiefly contributes to their shortage during aging.

3) Anemia of aging is a complex and poorly understood mechanistically. In general, it is considered similar to anemia of chronic inflammation with increased Epo, mild drop in Hb, and erythroid expansion, similar to ineffective erythropoiesis / low Epo responsiveness. It is not surprising that IR diet did not impact this mild anemia. However, was the MCV or MCH altered in aged and IR aged mice?

We now included the data for hematocrit, RBC counts, MCV, and MCH in Figure 1-figure supplement 5. Hematocrit shows a similar tendency as hemoglobin levels, but the values for RBC counts, MCV, and MCH seem not to be altered. We also show now that the erythropoietic activity in the bone marrow is not affected in aged versus young mice. Taken together, the anemic phenotype in female C57BL/6J mice at this age is very mild, which we emphasized in the main text, and is likely affected by other factors than serum iron levels (p. 6).

4) Page 6, line 23 onward: the conclusion is that KC compensate for the decreased function of RPM in the spleen, based on the expansion of KC fraction in the liver. Is there evidence that KCs are engaged in more erythrophagocytosis in aged mice? Furthermore, iron accumulation in the liver with age does not demonstrate specifically enhanced erythrophagocytosis of KC. Please clarify why liver iron accumulation would not be simply a consequence of increased parenchymal iron similar to increased splenic iron with age, independent of erythrophagocytic activity in resident macrophages in either organ.

Thanks for these questions. For the quantification of the erythrophagocytosis rate in KC, we show, as for the RPMs (Fig. 1K), the % of PKH67-positive macrophages, following transfusion of PKH67-stained stressed RBCs (Fig. 1M). The data implies a mild (not statistically significant) drop (of approx. 30%) in EP activity. We believe that it is overridden by a more pronounced (on average, 2-fold) increase in the representation of KCs (Fig. 1N). The mechanisms of iron accumulation between the spleen and the liver are very different. In the liver, we observed iron deposition in the parenchymal cells (not non-parenchymal, new Fig. 1P) that we currently characterizing in more detail in a parallel manuscript. Our data demonstrate a drop in transferrin saturation in aged mice. Hence, it is highly unlikely that aging would be hallmarked by the presence of circulating non-transferrin-bound iron that would be sequestered by hepatocytes, as shown previously (Jenkitkasemwong et al., 2015). Thus, the iron released locally by KCs is the most likely contributor to progressive hepatocytic iron loading during aging. The mechanism of iron delivery to hepatocytes from erythrophagocytosing KCs was demonstrated by Theurl et al.(Theurl et al., 2016), and we propose that it may be operational, although in a much more prolonged time scale, during aging. We now discussed this part better in our Results sections (p. 7).

5) Unclear whether the effect on RPMs is intrinsic or extrinsic. Would be helpful to evaluate aged iRPMs using young RBC vs. young iRPMs using old RBCs.

We are skeptical if the generation of iRPMs cells from aged mice would be helpful – these cells are a specific type of primary macrophage culture, derived from bone marrow monocytes with MCSF1, and exposed additionally to heme and IL-33 for 4 days. We do not expect that bone marrow monocytes are heavily affected by aging, and would thus recapitulate some aspects of aged RPMs from the spleen, especially after 8-day in vitro culture. However, to address the concerns of the reviewer, we now provide additional data regarding RBC fitness. Consistent with the time life-span experiment (Fig, 2A), we show that oxidative stress in RBCs is only increased in splenic, but not circulating RBCs (new Fig. 2C, replacing the old Fig. 2B and C). In addition, we show no signs of age-triggered iron loading in RBCs, either in the spleen (new Fig. 2F) or in the circulation (new Fig. 2B). Hence, we do not envision a possibility that RPMs become iron-loaded during aging as a result of erythrophagocytosis of iron-loaded RBCs. In support of this, we also have observed that during aging first RPMs’ FPN levels drop, afterward erythrophagocytosis rate decreases, and lastly, RBCs start to exhibit significantly increased oxidative stress (presented now in new Fig. 4H, J and K).

6) Discussion of aggregates in the spleen of aged mice (Fig 2G-2K and Fig 3) is very descriptive and non-specific. For example, if the iron-rich aggregates are hemosiderin, a hemosiderin-specific stain would be helpful. This data specifically is correlatory and difficult to extract value from.

Thanks for these comments. To the best of our knowledge Prussian blue Perls’ staining (Fig. 2J) is considered a hemosiderin staining. Our investigations aimed to better understand the nature and the origin of splenic iron deposits that to some extent are referred to as hemosiderin. Most importantly, as mentioned in our reply R1 Ad. 1. to assign causality to our data, we now demonstrated that iron accumulation in RPMs in response to iron-dextran (Fig. 3G) increases lipid peroxidation (Fig. 5F), tends to provoke RPMs depletion (Fig. 5G) and triggers the formation of protein-rich aggregates (new Fig. 3H). Of note, we assume that the loss of embryonically-derived RPMs in this model may be masked by simultaneous replenishment of the niche from monocytes, a phenomenon that may be addressed by future studies using Ms4a3-driven reporter mice (as shown for aged mice in our new Fig. 5E).

7) The aging phenotype in RPMs appears to be initiated sometime after 2 months of age. However, there is some reversal of the phenotype with increasing age, e.g. Fig 4B with decreased lipid peroxidation in 9 month old relative to 6 month old RPMs. What does this mean? Why is there a partial spontaneous normalization?

Thanks for this comment and questions. Indeed, the degree of lipid peroxidation exhibits some kinetics, suggestive of partial normalization. Of note, such a tendency is not evident for other aging phenotypes of RPMs, hence, we did not emphasize this in the original manuscript. However, in a revised version of the manuscript, we now present the re-analysis of the published data which implies that the number of embryonically-derived RPMs drops substantially between mice at 20 weeks and 36 weeks (new Fig. 5E). We think that the higher proportion of monocyte-derived RPMs in total RPM population later in aging (9 months) might be responsible for the partial alleviation of lipid peroxidation. We now discussed this possibility in the Results sections (p. 12).

8) Does the aging phenotype in RPMs respond to ferristatin? It appears that NAC, which is a glutathione generator and can reverse ferroptosis, does not reverse the decreased RPM erythrophagocytic capacity observed with age yet the authors still propose that ferroptosis is involved. A response to ferristatin is a standard and acceptable approach to evaluating ferroptosis.

We fully agree with the Reviewer that using ferristatin or Liproxstatin-1 would be very helpful to fully characterize a mechanism of RPMs depletion in mice. However, previous in vivo studies involving Liproxstatin-1 administration required daily injections of this ferroptosis inhibitor (Friedmann Angeli et al., 2014). This would be hardly feasible during aging. Regarding the experiments involving iron-dextran injection, using Liproxstatin-1 would require additional permission from the ethical committee which takes time to be processed and received. However, to address this question we now provide data from iRPMs cell cultures (new Fig.5 K-L). In essence, our results imply that both proteotoxic stress and iron overload act in concert to trigger cytotoxicity in RPM in vitro model. Interestingly, this phenomenon does not depend solely on the increased lipid peroxidation, but when we neutralize the latter with Liproxstatin-1, the cytotoxic effect is diminished (please, see also Results on p. 13 and Discussion p. 15/16).

9) The possible central role for HO-1 in the pathophysiology of decreased RPM erythrophagocytic capacity with age is interesting. However, it is not clear how the authors arrived at this hypothesis and would be useful to evaluate in the least whether RBCs in young vs. aged mice have more hemoglobin as these changes may be primary drivers of how much HO-1 is needed during erythrophagocytosis.

Thanks for this comment. We got interested in HO-1 levels based on the RNA sequencing data, which detected lower Hmox-1 expression in aged RPMs (Figure 3-figure supplement 1). We now show that the content of hemoglobin is not significantly altered in aged RBCs (MCH parameter, Figure 1-figure supplement 5E), hence we do not think that this is the major driver for Hmox-1 downregulation. Likewise, the levels of the Bach1 message, a gene encoding Hmox-1 transcriptional repressor, are not significantly altered according to RNAseq data. Hence, the reason for the transcriptional downregulation of Hmox-1 is not clear. Of note, HO-1 protein levels in the total spleen are higher in aged versus young mice, and we also detected a clear appearance of its nuclear truncated and enzymatically-inactive form (see a figure below, we opt not to include this in the manuscript for better clarity). The appearance of truncated HO-1 seems to be partially rescued by the IR diet. It is well established that the nuclear form of HO-1 emerges via proteolytic cleavage and migrates to the nucleus under conditions of oxidative stress (Mascaro et al., 2021). This additionally confirms that the aging spleen is hallmarked by an increased burden of ROS. Moreover, we also detected HO-1 as one of the components of the protein iron-rich aggregates. Thus, we propose that the low levels of the cytoplasmic enzymatically active form of HO-1 in RPMs (that we preferentially detect with our intracellular staining and flow cytometry) may be underlain by its nuclear translocation and sequestration in protein aggregates that evade antibody binding [this is also supported by our observation that the protein aggregates, despite the high content of ferritin (as indicated by MS analysis) are negative for L-ferritin staining. Of note, we also cannot exclude that other cell types in the aging spleen (eg. lymphocytes) express higher levels of HO-1 in response to splenic oxidative stress.

Fig. Total splenic levels of HO-1 in young, aged IR and aged mice.

Reviewer #2 (Public Review):

Slusarczyk et al. investigate the functional impairment of red pulp macrophages (RPMs) during aging. When red blood cells (RBCs) become senescent, they are recycled by RPMs via erythrophagocytosis (EP). This leads to an increase in intracellular heme and iron both of which are cytotoxic. The authors hypothesize that the continuous processing of iron by RPMs could alter their functions in an age-dependent manner. The authors used a wide variety of models: in vivo model using female mice with standard (200ppm) and restricted (25ppm) iron diet, ex vivo model using EP with splenocytes, and in vitro model with EP using iRPMs. The authors found iron accumulation in organs but markers for serum iron deficiency. They show that during aging, RPMs have a higher labile iron pool (LIP), decreased lysosomal activity with a concomitant reduction in EP. Furthermore, aging RPMs undergo ferroptosis resulting in a non-bioavailable iron deposition as intra and extracellular aggregates. Aged mice fed with an iron restricted diet restore most of the iron-recycling capacity of RPMs even though the mild-anemia remains unchanged.

Overall, I find the manuscript to be of significant potential interest. But there are important discrepancies that need to be first resolved. The proposed model is that during aging both EP and HO-1 expression decreases in RPMs but iron and ferroportin levels are elevated. In their model, the authors show intracellular iron-rich proteinaceous aggregates. But if HO-1 levels decrease, intracellular heme levels should increase. If Fpn levels increase, intracellular iron levels should decrease. How does LIP stay high in RPMs under these conditions? I find these to be major conflicting questions in the model.

We thank the Reviewer for her/his valuable feedback. As we mentioned in our replies we can only assume that a small misunderstanding in the interpretation of the presented data underlies this comment. We show that ferroportin levels in RPMs (Fig. 1F) are modulated in a manner that fully reflects the iron status of these cells (both labile and total iron levels, Figs. 1H and I). FPN levels drop in aged RPMs and are rescued when mice are maintained on a reduced iron diet. As pointed out by Reviewer#3, and explained in our replies we believe that ferroportin levels are critical for the observed phenotypes in aging. We now described our data in a more clear way to avoid any potential misinterpretation (p.6).

Reviewer #3 (Public Review):

This is a comprehensive study of the effects of aging of the function of red pulp macrophages (RPM) involved in iron recycling from erythrocytes. The authors document that insoluble iron accumulates in the spleen, that RPM become functionally impaired, and that these effects can be ameliorated by an iron-restricted diet. The study is well written, carefully done, extensively documented, and its conclusions are well supported. It is a useful and important addition for at least three distinct fields: aging, iron and macrophage biology.

The authors do not explain why an iron-restricted diet has such a strong beneficial effect on RPM aging. This is not at all obvious. I assume that the number of erythrocytes that are recycled in the spleen, and are by far the largest source of splenic iron, is not changed much by iron restriction. Is the iron retention time in macrophages changed by the diet, i.e. the recycled iron is retained for a short time when diet is iron-restricted (making hepcidin low and ferroportin high), and long time when iron is sufficient (making hepcidin high and ferroportin low)? Longer iron retention could increase damage and account for the effect. Possibly, macrophages may not empty completely of iron before having to ingest another senescent erythrocyte, and so gradually accumulate iron.

We are very grateful to this Reviewer for emphasizing the importance of the iron export capacity of RPMs as a possible driver of the observed phenotypes. Indeed, as mentioned above, we now show in the revised version of the manuscript that ferroportin drops early during aging (revised Fig. 4). Importantly, we now also observed that iron loading and limitation of iron export from iRPMs via ferroportin aggravate the impact of heat shock (a well-accepted trigger of proteotoxicity) on both protein aggregation and cell viability (new Fig. 5K and L). Physiologically, recent findings show that aging promotes a global decrease in protein solubility [BioRxiv manuscript (Sui X. et al., 2022)], and it is very likely that the constant exposure of RPMs to high iron fluxes renders these specialized cells particularly sensitive to proteome instability. This could be further aggravated by a build-up of iron due to the drop of ferroportin early during aging, ultimately leading to the appearance of the protein aggregates as early as at 5 months of age in C57BL/6J females. Based on the new data, we emphasized this model in the revised version of the manuscript (please, see Discussion on p. 16)

Author Response:

Reviewer #2:

Cai & Padoa-Schioppa recorded from macaque dorsal anterior cingulate cortex (ACCd) while requiring animals to choose between different juice types offered in variable amounts and with different action costs. Authors compared neural activity in ACCd (present study) with previous, directly comparable, findings on this same task when recording in macaque orbitofrontal cortex. The behavioral task is very powerful and the analyses of both the choice behavior and neural data are rigorous. Authors conclude that ACCd is unique in representing more post-decision variables and in its encoding of chosen value and binary outcome in several reference frames (chosen juice, chosen cost, and chosen action), not offer value, like OFC. Indeed, the encoding of choice outcomes in ACCd was skewed toward a cost-based reference frame. Overall, this is important new information about primate ACCd. I have only a few suggestions to enhance clarity. Figures 5 and 7 are maximally informative, but it is not clear that Figure 6 adds much to the reported Results. It is also suggested to abbreviate the comparison with Hosokawa et al. as it presently takes up 3 paragraphs in the Discussion: it is clear the methods and task designs were different enough to not be so easily compared with the present study. An additional suggestion would be to include mention of the comparison with OFC in the abstract and possibly also in the title, since the finding and direct comparison in Figure 7 are some of the most novel and interesting effects of the paper. Other suggestions are minor, and have to do with definition of time windows, variables, and additional papers that authors may cite for a well-rounded Discussion.

Please refer to Essential Revisions point #4. And we added “In contrast to the OFC” in the abstract to highlight the difference between these two regions.

Essential Revisions Point #4 Response:

We shortened the discussion from 3 paragraphs to 1 paragraph as follows.

"In another study, Hosokawa, Kennerley et al. (2013) compared the neuronal coding in ACCd and OFC in a choice task involving cost-benefit tradeoff. Our findings differ in two aspects. First, Hosokawa et. al. (2013) reported contralateral action value coding in ACCd while we did not discover significant offer value coding in either spatial- or action-based reference frames in our ACCd recordings. Second, they reported that there was no action-based value representation in the OFC therefore concluded that OFC does not integrate action cost in economic choice. Two elements may help explain the discrepancies between our findings in ACCd and OFC (Cai and Padoa-Schioppa 2019) and those of Hosokawa et. al. (2013). First, we recall that Hosokawa et. al. (2013) only tested value-related variables such as the benefit, cost and discounted value in action-based reference frame. Most importantly, they did not test the variable that is related to the saccade direction, which is highly correlated with the spatial value signal. As a consequence, contralateral value signal may not be significant if chosen target location was included in their regression analysis. Indeed, in our analysis, saccade direction (or chosen target location) was identified as one of the variables that explained a significant portion of neuronal activity in ACCd (Cai and Padoa-Schioppa 2012, Cai and Padoa-Schioppa 2019).The second and often overlooked aspect is that value may be encoded in schemes other than the action-based reference frame. In their study, each unique combination of reward quantity and cost was presented by a unique picture. Thus, information on good attributes were conveyed to the animal with an “integrated” visual representation. Accordingly, a distinct group of neurons may have been recruited to encode the reward and cost conjunctively represented by a unique fractal, which would result in 16 groups of offer value coding neurons."

Reviewer #3:

Cai and Padoa-Schioppa present a paper titled 'Neuronal Activity in Dorsal Anterior Cingulate Cortex during Economic Choices under Variable Action Costs'. They used a binary choice task where both offers indicated the reward type, reward amount, and the action cost (but not the specific action.) Variable action costs were then operationalized by placing targets on concentric circles of different radius. Here, and in a previous study that included OFC recordings (Cai and Padoa-Schioppa, 2019), monkeys integrated action costs into their decisions. Single-unit recordings in ACCd revealed that neurons predominantly coded for post-decision variables, such as cost of the chosen target and the juice type of the chosen offer, but not pre-decision variables, such as offer values. Given this finding, the authors compared the percentage of neurons in OFC and ACCd that coded for decision variables. In OFC neurons, the activity was mostly restricted to the offer presentation phase, whereas ACCd neurons showed sustained coding of chosen value and costs that lasted until the appearance of the saccade targets. Overall, this is an interesting study that provides evidence that decision-related signals evolve from coding offer values in the OFC to representing chosen costs in the ACC. This finding could highlight the roles of ACC neurons in learning and decision making. We have only a few questions.

1) Do any of the variables used in this study correlate with a conflict? When the authors previously studied ACC, they discarded the conflict monitoring hypothesis - a hypothesis that is well established for ACC hemodynamic responses - for ACC single cell activity based on neural data from 'difficult' decisions (Cai and Padoa-Schioppa, 2012). The definition of difficulty they used, then, was descriptive and based on reaction times (RTs). They defined the most difficult trials as those trials with the longest RTs and discovered that those trials had options with similar offer values. This definition of choice difficulty appears to be contrived from evidence accumulation models/tasks, where normatively harder judgments elicit longer RTs. However, there is no normative economic reason that trials with similar offer values are more difficult or should cause conflict. After all, according to theory, choosing between two options with the same value is as easy as flipping a coin. Here, it seems like the authors could have a more fitting definition of conflict. For example, conflict can be operationalized by considering trials when the animal must choose between a high value/high-cost option and a low-value/low-cost option. In that case, the costs and benefits are in conflict. What do the RTs look like? Do the RTs indicate conflict resolution? If so, is this reflected in neuronal responses?

We thank the reviewer for raising this important point. First, we would like to clarify that both in this study and in our previous study of ACC (Cai and Padoa-Schioppa 2012) we imposed a delay between offer presentation and the go signal. Such delay is critical to disentangle value comparison from action selection. However, the delay effectively dissociates reaction times from the decision difficulty. Normally, we operationalize the decision difficulty (or conflict) with the variable value ratio = chosen value / unchosen value. In an early behavioral study conducted in capuchin monkeys, where no delay was imposed between offer presentation and the go signal, we found that reaction times were strongly correlated with the value ratio, as one would naturally expect (Padoa-Schioppa, Jandolo et al. 2006). In the previous study of ACC (Cai and Padoa-Schioppa 2012) we referenced that earlier result but, again, we did not analyze reaction times.

Coming to the present study, we addressed this question by including in the variable selection analyses the two variables value ratio and cost/benefit conflict = cost of A * sign(offer value A – offer value B) (see also Table 2). The results of the updated analysis are illustrated in the new Figure 4, which we include here below. In essence, including these two variables did not affect the results of the variable selection analysis. That is, both the stepwise and best-subset methods selected the variables chosen value, chosen cost, chosen juice, chosen offer location only and chosen target location only.

Figure 4. Population summary of ANCOVA (all time windows). (A) Explained responses. Row and columns represent, respectively, time windows and variables. In each location, the number indicates the number of responses explained by the corresponding variable in that time window. For example, chosen value (juice) explained 34 responses in the post-offer time window. The same numbers are also represented in gray scale. Note that each response could be explained by more than one variable and thus could contribute to multiple bins in this panel. (B) Best fit. In each location, the number indicates the number of responses for which the corresponding variable provided the best fit (highest R2 in that time window. For example, chosen value (juice) provided the best fit for 40 responses in the late-delay time window. The numerical values are also represented in gray scale. In this plot, each response contributes to at most one bin.

2) The authors claimed that the ACCd neurons integrated juice identity, juice quantity and action costs later in the trial. As they acknowledge, the evidence for this claim is marginal. The conclusion the authors made in line 211, therefore, could be moderated. Given that the model containing cost-related variables is more complex, it is equally valid and more appropriately to write '… we cannot reject the null hypothesis that action cost was not integrated by chosen value responses later in the trial.

We acknowledge the complexity of this claim. However, results from previous studies (Kennerley, Dahmubed et al. 2009, Kennerley and Wallis 2009, Hosokawa, Kennerley et al. 2013) are in favor of establishing a null hypothesis of integration rather than non-integration. Therefore, we feel that it is more appropriate to keep the null hypothesis of cost integration while in the meantime acknowledging that in our study the evidence for cost integration is rather weak.

Author Response

Reviewer #1 (Public Review):

1) It would be helpful to include some sort of comparison in Fig. 4, e.g. the regressions shown in Fig 3, to indicate to what extent the ICCl data corresponds to the "control range" of frequency tuning.

Figure 4 was modified to show the frequency range typically found in the ICCls. This range is based on results from Wagner et al., 2007, which extensively surveyed ICCls responses. This modification shows that our ICCls recordings in the ruff-removed owls cover the normal frequency hearing range of the owl.

2) A central hypothesis of the study is that the frequency preference of the high-frequency neurons is lower in ruff-removed owls because of the lowered reliability caused by a lack of the ruff. Yet, while lower, the frequency range of many neurons in juvenile and ruff-removed owls seems sufficiently high to be still responsive at 7-8 kHz. I think it would be important to know to what extent neurons are still ITD sensitive at the "unreliable high frequencies" even if the CFs are lower since the "optimization" according to reliability depends not on the best frequency of each neuron per se, but whether neurons are less ITD sensitive at the higher, less reliable frequencies.

The concern regarding the frequency range that elicits responsivity was largely addressed above. Specifically, Figure L1 showing frequency tuning of frontally tuned ICx neurons in ruff-removed owls indicates that while there is some variability of tuning across neurons, there is little responsivity above 6 kHz. In contrast, equivalent analysis in juvenile owls (Figure L3), shows there is much more responsiveness and variability across neurons to high and low frequencies. This evidence supports our hypothesis that the juvenile owl brain is still highly plastic, which facilitates learning during development. Although the underlying data was already reported in Figure 7 of our previously submitted manuscript, we can include Figures L1 and L2, potentially as supplemental figures, if considered useful by editors and reviewers. Nevertheless, this argumentation was further expanded in the revised text (Line 229).

Figure L1. Frequency tuning of frontally-tuned ICx neurons in ruff-removed owls. Tuning curves are normalized by the max response. Thick black line indicates the average tuning curve. Dashed black line indicates basal response.

Figure L2. ITD sensitivity across frequencies in ruff-removed owl. Two example neurons shown in a and b. ITD tuning for tones (colored) and broadband (black) plotted by firing rate (non-normalized). Solid colored lines indicate responses to frequencies that are within the neuron’s preferred frequency range (i.e. above the half-height, see Methods), dashed lines indicate frequencies outside of the neuron’s frequency range.

Figure L3. Frequency tuning of frontally-tuned ICx neurons in juvenile owls. Tuning curves are normalized by the max response. Thick black line indicates the average tuning curve. Dashed black line indicates basal response.

3) It would be interesting to have an estimate of the time scale of experience dependency that induces tuning changes. Do the authors have any data on this question? I appreciate the authors' notion that the quantifications in Fig 7 might indicate that juvenile owls are already "beginning to be shaped by ITD reliability" (line 323 in Discussion). How many days after hearing onset would this correspond to? Does this mean that a few days will already induce changes?

While tracking changes induced by ruff-removal over development were outside of the scope of this study, many other studies have assessed experience-dependent plasticity in the barn owl. The recordings in this study were performed approximately 20 days after hearing onset, suggesting that the juveniles had ample time to begin learning. These points were expanded upon in the discussion (Lines 254, 280-283).

Reviewer #2 (Public Review):

1) Why is IPD variability plotted instead of ITD variability (or indeed spatial reliability)? The relationship between these measures is likely to vary across frequency, which makes it difficult to compare ITD variability across frequency when IPDs are plotted. Normalizing data across frequencies also makes it difficult to compare different locations and acoustical conditions. For example, in Fig.1a and Fig.1b, the data shown for 3 kHz at ~160 degrees seems quantitatively and visually quite different, but the difference (in Fig.1c) appears to be negligible.

Justification of why IPD variability is used as an estimate of ITD variability was added to introduction (Lines 55-60), results (Line 100) and methods (Lines 371-374) sections of the manuscript, explaining the fact that because ITD detection is based on phase locking by auditory nerve and ITD detector neurons tuned to narrow frequency bands, responses of ITD detector neurons forwarded to downstream midbrain regions are therefore determined by IPD variability. Additionally, ITD is calculated by dividing IPD by frequency, which makes comparisons of ITD reliability across frequency mathematically uninformative.

2) How well do the measures of ITD reliability used reflect real-world listening? For example, the model used to calculate ITD reliability appears to assume the same (flat) spectral profile for targets and distractors, which are presented simultaneously with the same temporal envelope, and a uniform spatial distribution of sounds across space. It is therefore unclear how robust the study's results are to violations of these assumptions.

While we agree that our analysis cannot completely capture real-world listening for the barn owl, a general analysis using similar flat spectral profiles for targets and concurrent sounds provides a broad assessment of reliability of ITD cues. While a full recapitulation of real-world listening is beyond the scope of this study (i.e. recording natural scenes from the ear canals of wild barn owls), we included additional analyses of ITD reliability in Figure 1-figure supplement 1, described above.

3) Does facial ruff removal produce an isolated effect on ITD variability or does it also produce changes in directional gain, and the relationship between spatial cues and sound location? Although the study considers this issue in some places (e.g. Fig.2, Fig.5), a clearer presentation of the acoustical effects of facial ruff removal and their implications (for all locations, not just those to the front), as well as an attempt to understand how these acoustical changes lead to the observed changes in ITD reliability, would greatly strengthen the study. In addition, Fig.1 shows average ITD reliability across owls, but it would be helpful to know how consistent these measures are across owls, given individual variability in Head-Related Transfer Functions (HRTFs). This potentially has implications for the electrophysiological experiments, if the HRTFs of those animals were not measured. One specific question that is potentially very relevant is whether the facial ruff attenuates sounds presented behind the animal and whether it does so in a frequency-dependent way. In addition, if facial ruff removal enables ILDs to be used for azimuth, then ITDs may also become less necessary at higher frequencies, even if their reliability remains unchanged.

Additional analysis was conducted to generate representation of changes in directional gain induced by ruff removal, added to new figure (Fig 5). This analysis shows that changes in gain following ruff-removal are largely frequency-independent: there is a de-attenuation of peripherally and rearwardly located sounds, but the highest gain remains for high frequencies in frontal space. There is an additional increase in gain for high frequencies from rearward space, these changes would not explain the changes in frequency tuning we report. As mentioned in new additions to the manuscript, the changes at the most rearward-located auditory spatial locations are unlikely to have an effect on the auditory midbrain. No studies in the barn owl have found neurons in the ICx or optic tectum tuned to >120° (Knudsen, 1982; Knudsen, 1984; Cazettes et al., 2014). In addition, variability of IPD reliability across owls was analyzed and reported in the amended Figure 1, which notes very little changes across owls. In this analysis, we did realize that the file of one of the HRTFs obtained from von Campenhausen et al. 2006 was mislabeled, which explains slight differences in revised Fig 1b. Nevertheless, added analysis of IPD reliability across owls indicates that the pattern in ITD reliability is stable across owls (Fig. 1d,e), which supports our decision to not record HRTFs from owls used in this study. Finally, we added to the discussion that clarifies that the use of ILD for azimuth would not provide the same resolution as ITD would (Lines 295-303). We also do not believe that the use of ILD for azimuth would make “ITDs… less necessary at higher frequencies”, given that the ICCls is still computing ITD at these high frequencies (Fig 4), and that ILDs also have higher resolution at higher frequencies, with and without the facial ruff (Olsen et al, 1989; Keller et al., 1998; von Campenhausen et al., 2006).

1) It is unclear why some analyses (Fig.5, Fig.7) are focused on frontal locations and frontally-tuned neurons. It is also unclear why neurons with a best ITDs of 0 are described as frontally tuned since locations behind the animal produce an ITD of 0 also. Related to this, in Fig.1, facial ruff removal appears to reduce IPD variability at low frequencies for locations to the rear (~160 degrees), where the ITD is likely to be close to 0. Neurons with a best ITD of 0 might therefore be expected to adjust their frequency tuning in opposite directions depending on whether they are tuned to frontal or rearward locations.

An extensive explanation was added to the methods detailing why we do not believe the neurons recorded in this study are tuned to the rear. Namely, studies mapping the barn owl’s ICx and optic tectum have not reported neurons tuned to locations >120°, with the number of neurons representing a given spatial location decreasing with eccentricity (Knudsen, 1982; Knudsen, 1984; Cazettes et al., 2014). While we agree that there does seem to be a change in ITD reliability at ~160° following ruff-removal, the result is largely similar to the change that occurs in frontal space (Fig 1b), which is consistent with the ruff-removed head functioning as a sphere. Thus, we wouldn’t expect rearwardly-tuned neurons, if they could be readily found, to adjust their frequency tuning to higher frequencies. Finally, we want to clarify that we focused our analyses on frontally-tuned neurons because frontal space is where we observed the largest change in ITD reliability. Text was added to the Discussion section to clarify this point (Lines 313-321).

2) The study suggests that information about high-frequency ITDs is not passed on to the ICX if the ICX does not contain neurons that have a high best frequency. However, neurons might be sensitive to ITDs at frequencies other than the best frequency, particularly if their frequency tuning is broader. It is also unclear whether the best frequency of a neuron always corresponds to the frequency that provides the most reliable ITD information, which the study implicitly assumes.

The concern about ITD sensitivity at non-preferred frequencies was addressed under the essential revision #3, as well as under Reviewer 1’s concerns.

Author Response

Reviewer #1 (Public Review):

This manuscript reports a systematic study of the cortical propagation patterns of human beta bursts (~13-35Hz) generated around simple finger movements (index and middle finger button presses).

The authors deployed a sophisticated and original methodology to measure the anatomical and dynamical characteristics of the cortical propagation of these transient events. MEG data from another study (visual discrimination task) was repurposed for the present investigation. The data sample is small (8 participants). However, beta bursts were extracted over a +/- 2s time window about each button press, from single trials, yielding the detection and analysis of hundreds of such events of interest. The main finding consists of the demonstration that the cortical activity at the source of movement related beta bursts follows two main propagation patterns: one along an anteroposterior directions (predominantly originating from pre central motor regions), and the other along a medio- lateral (i.e., dorso lateral) direction (predominantly originating from post central sensory regions). Some differences are reported, post-hoc, in terms of amplitude/cortical spread/propagation velocity between pre and post-movement beta bursts. Several control tests are conducted to ascertain the veracity of those findings, accounting for expected variations of signal-to-noise ration across participants and sessions, cortical mesh characteristics and signal leakage expected from MEG source imaging.

One major perceived weakness is the purely descriptive nature of the reported findings: no meaningful difference was found between bursts traveling along the two different principal modes of propagation, and importantly, no relation with behavior (response time) was found. The same stands for pre vs. post motor bursts, except for the expected finding that post-motor bursts are more frequent and tend to be of greater amplitude (yielding the observation of a so-called beta rebound, on average across trials).

Overall, and despite substantial methodological explorations and the description of two modes of propagation, the study falls short of advancing our understanding of the functional role of movement related beta bursts.

For these reasons, the expected impact of the study on the field may be limited. The data is also relatively limited (simple button presses), in terms of behavioral features that could be related to the neurophysiological observations. One missed opportunity to explain the functional role of the distinct propagation patterns reports would have been, for instance, to measure the cortical "destination" of their respective trajectories.

In response to this comment, we would like to highlight two important points.

First, our work constitutes the first non-invasive human confirmation of invasive work in animals (Balasubramanian et al., 2020; Roberts et al., 2019; Rule et al., 2018; (Balasubramanian et al., 2020; Best et al., 2016; Rubino et al., 2006; Takahashi et al., 2011, 2015) and patients (Takahashi et al., 2011). Thus, these results bridges between recordings limited to the size of multielectrode arrays (roughly 0.16 cm2; Balasubramanian et al., 2020; Best et al., 2016; Rubino et al., 2006; Takahashi et al., 2011, 2015) and human EEG recordings spanning across large areas of the cortex and several functionally distinct regions (Alexander et al., 2016; Stolk et al., 2019). The ability to access these neural signatures non- invasively is important for cross-species comparison. This further enables us, to provide an in-depth analysis of the spatiotemporal diversity of human MEG signals and a detailed characterisation of the two propagation directions, which significantly extends previous reports. We note that their functional role remains undetermined also in these animal studies, but being able to identify these signals now in humans can provide a steppingstone for identifying their role.

Second, and related, the reviewers are correct that we did not observe distinct propagation directions between pre- and post-movement bursts, nor a relationship with reaction time. However, such a null result would be relevant, in our view, towards understanding what the functional relevance of these signals, if any, might be. Recent work in macaques indicates that the spatiotemporal patterns of high-gamma activity carry kinematic information about the upcoming movement (Liang et al 2023). The functional role of beta may therefore be more complex and not relate to reaction times or kinematics in a straightforward manner. We believe this is a relevant observation, and in keeping with the continued efforts to identify how sensorimotor beta relates to behaviour. It is increasingly clear that spatiotemporal diversity in animal recordings and human E/MEG and intracranial recordings can constitute a substantial proportion of the measured dynamics. As such, our report is relevant in narrowing down what these signals may reflect.

Together, we think that our work provides new insights into the multidimensional and propagating features of burst activity. This is important for the entire electrophysiology community, as it transforms how we commonly analyse and interpret these important brain signals. We anticipate that our work will guide and inspire future work on the mechanistic underpinnings of these dominant neural signals. We are confident that our article has the scope to reach out to the diverse readership of eLife.

Reviewer #2 (Public Review):

The authors devised novel and interesting experiments using high precision human MEG to demonstrate the propagation of beta oscillation events along two axes in the brain. Using careful analysis, they show different properties of beta events pre- and post movement, including changes in amplitude. Due to beta's prominent role in motor system dynamics, these changes are therefore linked to behavior and offer insights into the mechanisms leading to movement. The linking of wave-like phenomena and transient dynamics in the brain offers new insight into two paradigms about neural dynamics, offering new ways to think about each phenomena on its own.

Although there is a substantial, and recent, body of literature supporting the conclusions that beta and other neural oscillations are transient, care must be taken when analyzing the data and the resulting conclusions about beta properties in both time and space. For example, modifying the threshold at which beta events are detected could alter their reported properties and expression in space and time. The authors should therefore performing parameter sweeps on e.g. the thresholds for detection of oscillation bursts to determine whether their conclusions on beta properties and propagation hold. If this additional analysis does not change their story, it would lend confidence in the results/conclusions.

We thank the reviewing team for this comment. As suggested, we evaluated the effect of different burst thresholds on the burst parameters.

The threshold in the main analysis was determined empirically from the data, as in previous work (Little et al., 2019). Specifically, trial-wise power was correlated with the burst probability across a range of different threshold values (from median to median plus seven standard deviations (std), in steps of 0.25, see Figure 6-figure supplement 1). The threshold value that retained the highest correlation between trial-wise power and burst probability was used to binarize the data.

We repeated our original analysis using four additional thresholds, i.e., original threshold - 0.5 std, -0.25 std, +0.25 std, +0.5 std. As one would expect, burst threshold is negatively related to the number of bursts (i.e., higher thresholds yield fewer bursts, Figure R4a [top]), and positively related to burst amplitude (i.e., higher thresholds yield higher burst amplitudes, Figure R4a [bottom]).

Similarly, the temporal duration of bursts and apparent spatial width are modulated by the burst threshold: lowering the threshold leads to longer temporal duration and larger apparent spatial width while increasing the threshold leads to shorter temporal duration and smaller apparent spatial width Figure R4b. Note that for the temporal and spectral burst characteristics, the difference to the original threshold can be numerically zero, i.e., changing the burst threshold did not lead to changes exceeding the temporal and spectral resolution of the applied time-frequency transformation (i.e., 200ms and 1Hz respectively).

Importantly, across these threshold values, the propagation direction and propagation speed remain comparable.

We now include this result as Figure 6-figure supplement 2and refer to this analysis in the manuscript (page 28 line 717).

“To explore the robustness of the results analyses were repeated using a range of thresholds (Figure 6-figure supplement 2).”

Determining the generators of beta events at different locations is a tricky issue. The authors mentioned a single generator that is responsible for propagating beta along the two axes described. However, it is not clear through what mechanism the beta events could travel along the neural substrate without additional local generators along the way. Previous work on beta events examined how a sequence of synaptic inputs to supra and infragranular layers would contribute to a typical beta event waveform. Although it is possible other mechanisms exist, how might this work as the beta events propagate through space? Some further explanation/investigation on these issues is therefore warranted.

Based on this and other comments (i.e., comments 7 and 8) we re-evaluated the use of the term ‘generator’ in this manuscript.

While the term generator can be used across scales, from micro- to macroscale, ifor the purpose of the present paper, we believe one should differentiate at least two concepts: a) generator of beta bursts, and b) generator of travelling waves.

We realised that in the previous version of the manuscript the term ‘generator’ was at times used without context. We removed the term where no longer necessary.

Further, the previous version of the manuscript discussed putative generators of travelling waves (page 19f.) but not generators of beta bursts. We now address this as follows:

“Studies using biophysical modelling have proposed that beta bursts are generated by a broad infragranular excitatory synaptic drive temporally aligned with a strong supragranular synaptic drive (Law et al., 2022; Neymotin et al., 2020; Sherman et al., 2016; Shin et al., 2017) whereby layer specific inhibition acts to stabilise beta bursts in the temporal domain (West et al., 2023). The supragranular drive is thought to originate in the thalamus (E. G. Jones, 1998, 2001; Mo & Sherman, 2019; Seedat et al., 2020), indicating thalamocortical mechanisms (page 22f).”

Once the mechanisms have been better understood, a question of how much the results generalize to other oscillation frequencies and other brain areas. On the first question of other oscillation frequencies, the authors could easily test whether nearby frequency bands (alpha and low gamma) have similar properties. This would help to determine whether the observations/conclusions are unique to beta, or more generally applicable to transient bursts/waves in the brain. On the second issue of applicability to other brain areas, the authors could relate their work to transient bursts and waves recorded using ECoG and/or iEEG. Some recent work on traveling waves at the brain-wide level would be relevant for such comparisons.

We appreciate the enthusiasm and the suggestions. To comment on the frequency specificity of the observed effects we conducted the same analysis focusing on the gamma frequency range (60-90 Hz). For computational reasons, we limited this analysis to one subject. Figure R1 shows the polar probability histogram for the beta frequency range (left) and the gamma frequency range (right). In contrast to the beta frequency range, no dominant directions were observed for the gamma range and von Mises functions did not converge. These preliminary results suggest some frequency specificity of the spatiotemporal pattern in sensorimotor beta activity. We believe this paves the way for future analysis mapping propagation direction across frequency and space.

Here we did not investigate the spatial specificity of the effects, as the beta frequency range is dominant in sensorimotor areas. Investigating beta bursts in other cortical areas would have likely resulted in very few bursts. We discuss our results across spatial scales in the section: Distinct anatomical propagation axes of sensorimotor beta activity. However, please note that most of the previous literature operates on a different spatial scale (roughly 4mm; Balasubramanian et al., 2020; Best et al., 2016; Rubino et al., 2006; Rule et al., 2018; Takahashi et al., 2011, 2015) and different species (e.g., non-human primates). Non-invasive recordings in humans capture temporospatial patterns of a very different scale, i.e., often across the whole cortex (Alexander et al., 2016; Roberts et al., 2019). Comparing spatiotemporal patterns, across different spatial scales is inherently difficult. Work

investigating different spatial scales simultaneously, such as Sreekumar et al. 2020, is required to fully unpack the relationship between mesoscopic and macroscopic spatiotemporal patterns.

Figure R1: Spatiotemporal organisation for the beta (β, 13-30Hz) and gamma (γ, 60-90) frequency range for one exemplar subject. Same as Figure 4a, but for one exemplar subject.

If the source code could be provided on github along with documentation and a standard "notebook" on use other researchers would benefit greatly.

All analyses are performed using freely available tools in MATLAB. The code carrying out the analysis in this paper can be found here: [link provided upon acceptance]. The 3D burst analyses can be very computationally intensive even on a modern computer system. The analyses in this paper were computed on a MacBook Pro with a 2.6 GHz 6-Core Intel Core i7 and 32 Gb of RAM. Details on the installation and setup of the dependencies can be found in the README.md file in the main study repository.

This information has been added to the paper in the methods section on page 35.

Author Response

Reviewer #1 (Public Review):

This manuscript provides a comprehensive investigation of the effects of the genetic ablation of three different transcription factors (Srf, Mrtfa, and Mrtfb) in the inner ear hair cells. Based on the published data, the authors hypothesized that these transcription factors may be involved in the regulation of the genes essential for building the actin-rich structures at the apex of hair cells, the mechanosensory stereocilia and their mechanical support - the cuticular plate. Indeed, the authors found that two of these transcription factors (Srf and Mrtfb) are essential for the proper formation and/or maintenance of these structures in the auditory hair cells. Surprisingly, Srf- and Mrtfb- deficient hair cells exhibited somewhat similar abnormalities in the stereocilia and in the cuticular plates even though these transcription factors have very different effects on the hair cell transcriptome. Another interesting finding of this study is that the hair cell abnormalities in Srfdeficient mice could be rescued by AAV-mediated delivery of Cnn2, one of the downstream targets of Srf. However, despite a rather comprehensive assessment of the novel mouse models, the authors do not have yet any experimentally testable mechanistic model of how exactly Srf and Mrtfb contribute to the formation of actin cytoskeleton in the hair cells. The lack of any specific working model linking Srf and/or Mrtfb with stereocilia formation decreases the potential impact of this study.

Major comments:

Figures 1 & 3: The conclusion on abnormalities in the actin meshwork of the cuticular plate was based largely on the comparison of the intensities of phalloidin staining in separate samples from different groups. In general, any comparison of the intensity of fluorescence between different samples is unreliable, no matter how carefully one could try matching sample preparation and imaging conditions. In this case, two other techniques would be more convincing: 1) quantification of the volume of the cuticular plates from fluorescent images; and 2) direct examination of the cuticular plates by transmission electron microscopy (TEM).

In fact, the manuscript provides no single TEM image of the F-actin abnormalities either in the cuticular plate or in the stereocilia, even though these abnormalities seem to be the major focus of the study. Overall, it is still unclear what exactly Srf or Mrtfb deficiencies do with F-actin in the hair cells.

Yes, we agree. As suggested by the reviewer, to directly examine the defects in F-actin organization within the cuticular plate of mutant mice, we conducted Transmission Electron Microscopy (TEM) analyses. The results, as presented in the revised Figures 1 and 4 (panels F, G, and E, F, respectively), provide crucial insights into the structural changes in the cuticular plate. Meanwhile, the comparison of the volume of the phalloidin labeled cuticular plate after 3-D reconstruction using Imaris software was conducted and shown in Author response image 1. The results of the cuticular plate (CP) volume were consistent with the relative F-actin intensity change of the cuticular plate in the revised Figures 1B and 4B. For the TEM analysis of the stereocilia, we regret that due to time constraints, we were unable to collect TEM images of stereocilia with sufficient quality for a meaningful comparison. However, we believe that the data we have presented sufficiently addresses the primary concerns, and we appreciate the reviewers’ understanding of these limitations.

Author response image 1.

Figures 2 & 4 represent another example of how deceiving could be a simple comparison of the intensity of fluorescence between the genotypes. It is not clear whether the reduced immunofluorescence of the investigated molecules (ESPN1, EPS8, GNAI3, or FSCN2) results from their mis-localization or represents a simple consequence of the fact that a thinner stereocilium would always have a smaller signal of the protein of interest, even though the ratio of this protein to the number of actin filaments remains unchanged. According to my examination of the representative images of these figures, loss of Srf produces mis-localization of the investigated proteins and irregular labeling in different stereocilia of the same bundle, while loss of Mrtfb does not. Obviously, a simple quantification of the intensity of fluorescence conceals these important differences.

Yes, we agree. In addition to the quantification of tip protein intensity, we have added a few more analyses in the revised Figure 3 and Figure 6, such as the percentage of row 1 tip stereocilia with tip protein staining and the percentage of IHCs with tip protein staining on row 2 tip. Using the results mentioned above, the differences in the expression level, the row-specific distribution and the irregular labeling of tip proteins between the control and the mutants can be analyzed more thoroughly.

Reviewer #2 (Public Review):

The analysis of bundle morphology using both confocal and SEM imaging is a strength of the paper and the authors have some nice images, especially with SEM. Still, the main weakness is that it is unclear how significant their findings are in terms of understanding bundle development; the mouse phenotypes are not distinct enough to make it clear that they serve different functions so the reader is left wondering what the main takeaway is.

Based on the reviewer’s comments, in this revised manuscript, we put more emphasis on describing the effects of SRF and MRTFB on key tip proteins’ localization pattern during stereocilia development, represented by ESPN1, EPS8 and GNAI3, as well as the effects of SRF and MRTFB on the F-actin organization of cuticular plate using TEM. We have made substantial efforts to interpret the mechanistic underpinnings of the roles of SRF and MRTFB in hair cells. This is reflected in the revised Figures 1, 3, 4, 6, and 10, where we provide more comprehensive insights into the mechanisms at play.

We interpret our data in a way that both SRF and MRTF regulate the development and maintenance of the hair cell’s actin cytoskeleton in a complementary manner. Deletion of either gene thus results in somewhat similar phenotypes in hair cell morphology, despite the surprising lack of overlap of SRF and MRTFB downstream targets in the hair cell.

In Figure 1 and 3, changes in bundle morphology clearly don't occur until after P5. Widening still occurs to some extent but lengthening does not and instead the stereocilia appear to shrink in length. EPS8 levels appear to be the most reduced of all the tip proteins (Srf mutants) so I wonder if these mutants are just similar to an EPS8 KO if the loss of EPS8 occurred postnatally (P0-P5).

To address this question, we performed EPS8 staining on the control and Srf cKO hair cells at P4 and P10. We found that the dramatic decrease of the row 1 tip signal for EPS8 started since P4 in Srf cKO IHCs. Although the major hair bundle phenotype of Eps8 KO, including the defects of row 1 stereocilia lengthening and additional rows of short stereocilia also appeared in Srf cKO IHCs, there are still some bundle morphology differences between Eps8 KO and Srf cKO. For example, firstly, both Eps8 KO OHCs and IHCs showed additional rows of short stereocilia, but we only observed additional rows of short stereocilia in Srf cKO IHCs. Secondly, in Valeria Zampini’s study, SEM and TEM images did not show an obvious reduction of row 2 stereocilia widening (P18-P35), while our analysis of SEM images confirmed that the width of row 2 IHC stereocilia was drastically reduced by 40% in Srf cKO (P15). Generally, we think although Srf cKO hair bundles are somewhat similar to Eps8 KO, the Srf cKO hair bundle phenotype might be governed by multiple candidate genes cooperatively.

Reference:

Valeria Zampini, et al. Eps8 regulates hair bundle length and functional maturation of mammalian auditory hair cells. PLoS Biol. 2011 Apr;9(4): e1001048.

A major shortcoming is that there are few details on how the image analyses were done. Were SEM images corrected for shrinkage? How was each of the immunocytochemistry quantitation (e.g., cuticular plates for phalloidin and tip staining for antibodies) done? There are multiple ways of doing this but there are few indications in the manuscript.

We apologize for not making the description of the procedure of images analyses clear enough. As described in Nicolas Grillet group’s study, live and mildly-fixed IHC stereocilia have similar dimensions, while SEM preparation results in a hair bundle at a 2:3 scale compared to the live preparation. In our study, the hair cells selected for SEM imaging and measurements were located in the basal turn (30-32kHz), while the hair cells selected for fluorescence-based imaging and measurements were located in the middle turn (20-24kHz) or the basal turn (32-36kHz). Although our SEM imaging and fluorescence-based imaging of basal turn’s hair bundles were not from the same area exactly, the control hair bundles with SEM imaging have reduced row 1 stereocilia length by 10%-20%, compared to the control hair bundles with fluorescence-based imaging (revised Figure 2 and Figure 5). Generally, our stereocilia dimensions data showed appropriate shrinkage caused by the SEM preparation.

Recognizing the need for clarity, we have provided a detailed description of our image quantification and analysis procedures in the “Materials and Methods” section, specifically under “Immunocytochemistry.” This will aid readers in understanding our methodologies and ensure transparency in our approach.

Reference:

Katharine K Miller, et al. Dimensions of a Living Cochlear Hair Bundle. Front Cell Dev Biol. 2021 Nov 25:9:742529.

The tip protein analysis in Figs 2 and 4 is nice but it would be nice for the authors to show the protein staining separately from the phalloidin so you could see how restricted to the tips it is (each in grayscale). This is especially true for the CNN2 labeling in Fig 7 as it does not look particularly tip specific in the x-y panels. It would be especially important to see the antibody staining in the reslices separate from phalloidin.

Thank you for the suggestions. We have shown tip proteins staining in grayscale separately from the phalloidin in the revised Figure 3 and Figure 6. To clearly show the tip-specific localization of CNN2, we conducted CNN2 staining at different ages during hair bundle development and showed CNN2 labeling in grayscale and in reslices in revised Figure 9-figure supplement 1B.

In Fig 6, why was the transcriptome analysis at P2 given that the phenotype in these mice occurs much later? While redoing the transcriptome analysis is probably not an option, an alternative would be to show more examples of EPS8/GNAI/CNN2 staining in the KO, but at younger ages closer to the time of PCR analysis, such as at P5. Pinpointing when the tip protein intensities start to decrease in the KOs would be useful rather than just showing one age (P10).

We agree with the reviewer. To address this question, we have performed ESPN1, EPS8 and GNAI3 staining on the control and the mutant’s hair cells at P4, P10 and P15 (the revised Figures 3 and 6). According to the new results, we found that the dramatic decreases of the row 1 tip signal for ESPN1 and EPS8 started since P4 in Srf cKO IHCs, is consistent with the appearance of the mild reduction of row 1 stereocilia length in P5 Srf cKO IHCs. For Mrtfb cKO hair cells, the obvious reduction of the row 1 tip signal for ESPN1 was observed until P10. However, a few genes related to cell adhesion and regulation of actin cytoskeleton were significantly down-regulated in P2 Mrtfb deficient hair cell transcriptome. We think that in hair cells the MRTFB may not play a major role in the regulation of stereocilia development, so the morphological defects of stereocilia happened much later in the Mrtfb mutant than in the Srf mutant.

While it is certainly interesting if it turns out CNN2 is indeed at tips in this phase, the experiments do not tell us that much about what role CNN2 may be playing. It is notable that in Fig 7E in the control+GFP panel, CNN2 does not appear to be at the tips. Those images are at P11 whereas the images in panel A are at P6 so perhaps CNN2 decreases after the widening phase. An important missing control is the Anc80L65-Cnn2 AAV in a wild-type cochlea.

We agree with the reviewer. We have conducted more immunostaining experiments to confirm the expression pattern of CNN2 during the stereocilia development, from P0 to P11. The results were included in the revised Figure 9-figure supplement 1B. As the reviewer suggested, CNN2 expression pattern in control cochlea injected with Anc80L65-Cnn2 AAV has also been provided in revised Figure 9E.

Author Response

Reviewer #1 (Public Review):

This is an awesome comprehensive manuscript. Authors start by sorting putative stromal cellcontaining BM non-hematopoietic (CD235a-/CD45-) plus additional CD271+/CD235a/CD45- populations to identify nine individual stromal identities by scRNA-seq. The dual sorting strategy is a clever trick as it enriches for rare stromal (progenitor) cell signals but may suffer a certain bias towards CD271+ stromal progenitors. The lack of readable signatures already among CD45-/CD45- sorts might argue against this fear. This reviewer would appreciate a brief discussion on number & phenotype of putative additional MSSC phenotypes in light of the fact that the majority of 'blood lineage(s)'-negative scRNA-seq signatures identified blood cell progenitor identities (glycophorin A-negative & leukocyte common antigen-negative). The nine stromal cell entities share the CXCL12, VCAN, LEPR main signature. Perhaps the authors could speculate if future studies using VCAN or LEPRbased sort strategies could identify additional stromal progenitor identities?

We would like to thank the reviewer for critically evaluating our work and for the generally positive evaluation of the paper. We apologize for delayed resubmission as it took a long time for a specific antibody to arrive to complete the confocal microscopy analyses.

The reviewer asks for a brief discussion on the cell numbers and phenotypes of MSSC phenotypes. The cell numbers and percentages of MSSC in sorted CD45low/-CD235a- and CD45low/-CD235a-CD271+ cells can be found in Supplementary File 3 and we have added a summary of the phenotypes of MSSC in the new Supplementary File 7.

Due to the extremely low frequency of stromal cells in human bone marrow, we chose a sorting strategy that also included CD45low cells (Fig 1A) to ensure that no stromal cells were excluded from the analysis. Although stromal elements are certainly enriched using this approach, the CD45low population contains several different hematopoietic cell types. These include CD34+ HSPCs which are characterized by low CD45 expression2, as well as the CD45low-expressing fractions of other hematopoietic cell populations such as B cells, T cells, NK cells, megakaryocytes, monocytes, dendritic cells, and granulocytes. Furthermore, CD235a- late-stage erythroid progenitors, which are negative for CD45, are represented as well. Of note, our data are consistent with previously reported murine studies showing the presence of a number of hematopoietic populations in CD45- cells, which accounted for the majority of CD45-Ter119-CD31- murine BM cells3,4. However, despite a certain enrichment of stromal elements in the CD45low cell fraction, frequencies were still too low to allow for a detailed analysis of this important bone marrow compartment. This prompted us to adopt the stromal cell-enrichment strategy as described in the manuscript to achieve a better resolution of the stromal compartment. In fact, sorting based on CD45low/-CD235a-CD271+ allowed us to sufficiently enrich bone marrow stromal cells to be clearly detectable in scRNAseq analysis. According to the reviewer’s suggestion, a brief discussion on this issue is now included in the Discussion (page 28, lines 10-15).

The reviewer also suggested using VCAN or LEPR-based sorting strategy to identify additional stromal identities in future studies.

However, as an extracellular matrix protein, FACS analysis of cellular VCAN expression can only be achieved based on its intracellular expression after fixation and permeabilization5,6. Additionally, while VCAN is highly and ubiquitously expressed by stromal clusters, VCAN is also expressed by monocytes (cluster 36). Therefore, VCAN is not an optimal marker to isolate viable stromal cells.

LEPR is the marker that was reported to identify the majority of colony-forming cells in adult murine bone marrow7. We have previously reported that the majority of human adult bone marrow CFU-Fs is contained in the LEPR+ fraction 8. In our current scRNAseq surface marker profiling analysis, group A cells showed high expression of several canonical stromal markers including VCAM1, PDGFRB, ENG (CD73), as well as LEPR (Fig. 4A). However, the four stromal clusters in Group A could not be separated based on the expression of LEPR. Therefore, we chose not to use LEPR as a marker to prospectively isolate the different stromal cell types.

The authors furthermore localized CD271+, CD81+ and NCAM/CD56+ cells in BM sections in situ. Finally, referring to the strong background of the group in HSC research, in silico prediction by CellPhoneDB identified a wide range of interactions between stromal cells and hematopoietic cells. Evidence for functional interdependence of FCU-F forming cells is completing the novel and more clear bone marrow stromal cell picture.

We thank the reviewer for the positive comments.

An illustrative abstract naming the top9 stromal identities in their top4 clusters by their "top10 markers" + functions would be highly appreciated.

We thank the reviewer for the suggestion. A summary of the characteristics of stromal clusters is now shown in the new Supplementary File 7, which we hope matches the reviewer’s expectations.

Reviewer #2 (Public Review):

Knowledge about composition and function of the different subpopulations of the hematopoietic niche of the BM is limited. Although such knowledge about the mouse BM has been accumulating in recent years, a thorough study of the human BM still needs to be performed. The present manuscript of Li and coworkers fills this gap by performing single cell RNA sequencing (scRNAseq) on control BM as well as CD271+ BM cells enriched for non-hematopoietic niche cells.

We apologize for delayed resubmission as it took a long time for a specific antibody to arrive to complete the confocal microscopy analyses. We thank the reviewer for the critical expert review and overall positive comments.

Based on their scRNAseq, the authors propose 41 different BM cell populations, ten of which represented non-hematopoietic cells, including one endothelial cell cluster. The nine remaining skeletal subpopulations were subdivided into multipotent stromal stem cells (MSSC), four distinct populations of osteoprogenitors, one cluster of osteoblasts and three clusters of pre-fibroblasts. Using bioinformatic tools, the authors then compare their results and divisions of subpopulations to some previously published work from others and attempt to delineate lineage relationships using RNA velocity analyses. From these, they propose different paths from which MSSC enter the progenitor stages, and might differentiate into pre-osteoblasts and -fibroblasts.

It is of interest to note, that apparently adipo-primed cells may also differentiate into osteolineage cells, something that should be further explored or validated. Furthermore, although this analysis yields a large adipo-primed populations, pre-adipocytes and mature adipocytes appear not to be included in the data set the authors used, which should also be explained.

We thank the reviewer for this comment. We chose to annotate Cluster 5 as adipoprimed cluster based on the higher expression of adipogenic differentiation markers as well as a group of stress-related transcription factors (FOS, FOSB, JUNB, EGR1) (Fig. 2B-C, Figure 2-figure supplement 1C) some of which had been shown to mark bone marrow adipogenic progenitors1. Although at considerably lower levels compared to adipogenic genes, osteogenic genes were also expressed in cluster 5 cells (Fig. 2B and D), indicating the multi-potent potential of this cluster. Therefore, our initial annotation of these cells as adipoprimed progenitors was too narrow as it did not include the possible osteogenic differentiation potential. We apologize for the confusion caused by the inappropriate annotation and, in order to avoid any further confusion, cluster 5 has now been re-annotated as ‘highly adipocytic gene-expressing progenitors (HAGEPs), which we believe is a better representation of the cells. We furthermore agree with the reviewer that in-vivo differentiation needs to be performed to address potential differentiation capacities in future studies.

With regard to the lack of adipocytes in our data set, we described in the Materials and Methods section that human bone marrow cells were isolated based on density gradient centrifugation. After centrifugation, the mononuclear cell-containing monolayers were harvested for further analysis. However, the resulting supernatant containing mature adipocytic cells was discarded14. Therefore, adipocyte clusters were not identified in our dataset. We have amended the manuscript accordingly (page 5, line 7).

Regarding the pre-adipocytes, we are not aware of any specific markers for pre-adipocytes in the bone marrow. We examined the only known markers (ICAM1, PPARG, FABP4) that have been shown to mark committed pre-adipocytes in human adipose tissue15. As illustrated in Fig. R1 (below), low expression of all three markers was not restricted to a single distinct cluster but could be found in almost all stromal clusters. These data thus allow us to neither confirm nor exclude the presence of pre-adipocytes in the dataset. Due to the lack of specific markers for pre-adipocytes and the absence of mature adipocytes in the current dataset, it is therefore difficult to identify a well-defined pre-adipocytes cluster.

Figure R1. UMAP illustration of the normalized expression of the markers for pre-adipocytes in stromal clusters.

In addition, based on a separate analysis of surface molecules, the authors propose new markers that could be used to prospectively isolate different human subpopulations of BM niche cells by using CD52, CD81 and NCAM1 (=CD56). Indeed, these analyses yield six different populations with differential abilities to form fibroblast-like colonies and differentiate into adipo-, osteo-, and chondrogenic lineages. To explore how the scRNAseq data may help to understand regulatory processes within the BM, the authors predict possible interactions between hematopoietic and non-hematopoietic subpopulations in the BM. These should be further validated, to support statements as the suggestion in the abstract that separate CXCL12- and SPP1-regulated BM niches might exist.

We agree with the reviewer that functional validation of the CellPhoneDB results using for example in vivo humanized mouse models would be needed to demonstrate the presence of different niches in the bone marrow. At this point of time we only put forward the hypothesis that different niche types exist while we will work on providing experimental proof in our future studies.

The scRNAseq analysis is indeed a strong and important resource, also for later studies meant to increase knowledge about the hematopoietic niche of the BM. Although the analyses using different bioinformatic tools is very helpful, they remain mostly speculative, since validatory experiments, as already mentioned, are missing. As such, I feel the authors did not succeed in achieving their goals of understanding how non-hematopoietic cells of the BM regulate the different hematopoietic processes within the BM. Nevertheless, they have created valuable resources, both in the scRNAseq data they generated, as well as the different predictions about different cell populations, their lineage relationships, and how they might interact with hematopoietic cells.

We thank the reviewer for the appreciation of the value of this dataset. We agree with the reviewer that it is of great importance to validate the contribution of potential driver genes for stromal cell differentiation and verify the in vitro data and in-silico prediction using in-vivo models. As the main goal of the current study was to formulate hypotheses based on the scRNAseq data for future studies, we believe that in vivo validation experiments using engineered human bone marrow models or humanized bone marrow ossicles are out of the scope of the current study, but certainly need to be performed in the future.

The impact of this work is difficult to envision, since validations still need to be performed. Also, it has the born in mind that humans are not mice, which can be studied in neat homogeneous inbred populations. Human populations on the other hand, are quite diverse, so that the data generated in this manuscript and others will probably have to be combined to extrapolate data relevant to the whole of the human population. However, as it is equally difficult to generate reliable scRNAseq data from human BM, it seems likely that the data will indeed an important resource, when more data from different donors become available.

We thank the reviewer for the generally positive evaluation of this study.

Taken at point value, the authors provide evidence that human counterparts exist to several BM populations described in mice. In my opinion, the lineage relationships predicted using the RNA velocity analyses need more substance, as it seems the differentiation-paths may diverge from what is known from mice. If so, this issue should be studied more stringently. Similarly, the paper would have been strengthened considerably if a relevant experimental validation would have been attempted, perhaps by using genetically modified (knockdown) MSSC, similar to Battula et al. (doi: 10.1182/blood-2012-06-437988).

In the study from Welner’s group, stromal differentiation trajectory was inferred based on scRNAseq analysis of murine bone marrow cells using Velocyto16. Velocyto identified MSCs as the ‘source’ cell state with pre-adipocytes, pro-osteoblasts, and prochondrocytes being end states. In our study, the MSSC population was predicted to be at the apex of the trajectory and the pre-osteoblast cluster was placed close to the terminal state of differentiation, which is consistent with the murine study. However, different stromal cell types were identified in mice compared with humans. For example, we have identified prefibroblasts in our dataset which are absent in the murine study, while a well-defined murine pre-adipocyte population was not identified in our human dataset. Therefore, it is not surprising to find some discrepancies between human and murine stromal differentiation trajectories. Of course and as mentioned before, critical in-vivo functional validations need to be carried out to address these important issues in the future.

In summary, this is a very interesting but also descriptive paper with highly important resources. However, to prospectively identify or isolate human non-hematopoietic/nonendothelial niche populations, more stringent validations should have been performed to strengthen the validity of the different analyses that have been performed. As such, it remains an open question which niche subpopulations has the most impact on the different hematopoietic processes important for normal and stress hematopoiesis, as well as malignancies.

Thank you for this comment. We completely agree that more stringent validations are necessary but are outside of the aim of our current hypothesis-generating study. Accordingly, we are planning functional verification studies using genetically manipulated stromal cells in combination with in-vivo humanized ossicles. Furthermore, other groups will hopefully use our database and contribute with functional studies in model systems that are currently not available to us, e.g. iPS-derived bone marrow in-vitro proxies.

Specific remarks

• Since CD45, CD235a, and CD271 are used as distinguishing markers in the sample preparation of the scRNAseq, it would be helpful to highlight these markers in the different analyses (Figures 1D, 2B, 2C-F, and 4A), and restrict the analyses to those cells that also not express CD45, CD235a (why use CD71?) and highly express CD271.

Thank you for this comment. As shown in Fig. R2, we have modified figures Fig. 1D, 2B, and 4A showing now also the expression of PTPRC (CD45), GYPA (CD235a), and NGFR (CD271) on the top (Fig. 1D and 2B) or right (Fig. 4A) panel of the figures. To complement Fig. 2C-F, we have generated new stacked violin plots showing the expression level of three markers by all 9 stromal clusters (Fig. R2B). As we believe that including these three markers in the figures does not provide a better strategy to improve the analyses, we decided to leave the original figures unchanged in this respect.

Figure R2. (A) Modified Fig. 1D, 2B and 4A with PTPRC (CD45), GYPA (CD235a) and NGFR (CD271) expression. (B) Stacked violin plots of PTPRC, GYPA and NGFR expressed by stromal clusters to complement Fig. 2C-F.

With regard to cell exclusion based on CD45, as shown in the modified Figure corresponding to Fig 1A in the manuscript (Fig R2A), CD45 gene expression is observed also in the endothelial cluster, basal cluster, and neuronal cluster (Fig. R2A). These clusters represent non-hematopoietic clusters that we would like to keep in our dataset for further analysis, such as cell-cell interaction. Therefore, we choose to not restrict the analysis to solely CD45 nonexpressing cells.

With regard to CD235a (GYPA), expression of CD235a is not detected in any of the nonhematopoietic clusters. Thus, CD235a-expressing cell exclusion is not necessary.

For CD271, according to our previous results (own unpublished data, belonging to a dataset of which only significantly expressed genes were reported in Li et al.8), protein expression of CD271 is not necessarily reflected by gene expression. In the other words, stromal cells with CD271 protein expression do not always have high mRNA expression. A significant fraction of stromal cells would be excluded if we restrict the analyses only to those cells that show high CD271 gene expression, which would not reflect the real cellular composition of human bone marrow stroma. In order to not risk losing stromal cells, we therefore kept our previous analyses which included stromal cells with various CD271 expression levels.

With regard to using CD71 as an exclusion marker, please see also the comments to reviewer 1. Briefly, according to our data, CD71 (TFRC)-expressing erythroid precursors could still be found after excluding CD45 and CD235a positive cells (Figure 1-figure supplement 1B and R3). As furthermore shown in Figure 1-figure supplement 1G and R2, CD71 expression in the stromal clusters is negligible. Therefore, we believe that this justifies the use of CD71 as an additional marker to exclude erythroid cells. We have amended the discussion to address this issue (page 19, lines 7-8).

Figure R3. FACS plots illustrating the expression of (A) CD71 (TFRC) vs CD271 in CD45- CD235a- cells and (B) FSC-A vs CD81 in CD45-CD235a-CD271+CD71+ cells following exclusion of doublets and dead cells.

• Despite a distinct neuronal cluster (39), there does not seem to be a distinctive marker for these cells. Is this true?

Yes, the reviewer is correct that there is no significantly-expressed distinctive marker for neuronal cells. Multiple markers indicating the presence of different cell types were identified in cluster 39 (Supplementary File 4). Among them, several neuronal markers (NEUROD1, CHGB, ELAVL2, ELAVL3, ELAVL4, STMN2, INSM1, ZIC2, NNAT) were found to be enriched in this cluster (Supplementary File 4 and Fig. 1D) with higher fold changes compared to other identified genes. However, the expression of these genes was not statistically significant, which is mainly due to the heterogeneity of the cluster and thus does not allow us to draw any firm conclusions.

Several genes including MALAT1, HNRNPH1, AC010970.1, and AD000090.1 were identified to be statistically highly expressed by cluster 39 (Supplementary File 4). The expression of these genes is not restricted to any specific cell type. It is therefore impossible to annotate the cluster based on this and our data thus indicated that cluster 39 is a heterogeneous population containing multiple cell types. Based on the expression of neuronal markers, we nevertheless chose to annotate Cluster 39 as “neuronal” as the prominent expression of neuronal markers indicated the presence of neurons in this cluster. To be more accurate, the annotation of cluster 39 has been changed to ‘neuronal cell-containing cluster’ to correctly reflect the presence of non-neuronal gene expressing cells as well (page 29, lines 3-8).

• Since based on 2C and 2D, the authors are unable to distinguish adipo- from osteogenic cells, would the authors use the same molecules to distinguish different populations of 2C-D, or would they use other markers, if so which and why.

We agree with the reviewer that at the first glance adipo-primed (cluster 5, now annotated as “highly adipocytic gene-expressing progenitors”, HAGEPs), balanced progenitors (cluster 16), and pre-osteoblasts (cluster 38) shared a similar expression pattern according to the violin plots in Fig. 2C and 2D. However, as illustrated in the heatmap (Fig. 2B), the expression patterns of adipo-primed (HAGEP) and balanced progenitors were quite different in terms of their expression of adipogenic and osteogenic markers. Both adipogenic and osteogenic marker expression was detected in HAGEPs, balanced progenitors, and preosteoblasts. Thus, as violin plots are summarizing the overall expression levels of a certain marker in a certain cluster, these plots tend to make it more difficult to detect differential expression patterns between different clusters. In this case, the heatmap shown in Fig. 2B is a good complement to the violin plots as it is demonstrating the different expression patterns of every cell in the different stromal clusters.

Additionally, cluster 5 showed the expression of a group of stress-related transcription factors (FOS, FOSB, JUNB, EGR1) (Fig. 2B and Figure 2-figure supplement 1C), some of which had been shown to mark bone marrow adipogenic progenitors1. The expression of the abovementioned stress-related transcription factors (putative adipogenic progenitor markers) was generally lower in cluster 38 compared to cluster 5, further demonstrating that clusters were different.

Furthermore, there was a gradual upregulation of more mature osteogenic markers such as RUNX1, CDH11, EBF1, and EBF3 from cluster 5 to cluster 16 and finally cluster 38. As shown in Fig. 2D, the expression of these markers was higher in cluster 38 compared to cluster 5. Therefore, cluster 38 was annotated as pre-osteoblasts.

Most of the stromal clusters form a continuum (Fig. 2A), which correlates very well with the gradual transition of different cellular states during stromal cell development. It is highly unlikely that abrupt and dramatic gene expression changes would occur during the cellular state transition of cells of the same lineage. Therefore, it is not surprising to find the differences in gene expression profiles between stromal clusters share a certain level of similarities.

In summary, we rely on several factors to distinguish different stromal clusters, which include canonical adipo-, osteo- and chondrogenic markers, stress markers, heatmap, violin plots, and the gradual up-regulation of certain lineage-specific markers.

To directly answer the reviewer’s question, we believe that we are able to distinguish different stromal clusters based on our data.

• In de Jong et al., an inflammatory MSC population (iMSC) is defined. Since the Schneider group showed that inflammatory S100A8 and A9 are expressed by inflamed MSC, is it possible that the some of the designated pre-fibroblasts actually correspond to these S100A8/A9-expressing iMSC?

We thank the reviewer for raising this interesting question.

First of all, we would like to point out that scRNAseq was performed using viably frozen bone marrow aspirates in de Jong’s study while freshly isolated bone marrows were used in our study. There might be discrepancies between frozen and fresh bone marrow samples in terms of cellular composition including stromal composition and, importantly, processinginduced stress-related gene expression profiles.

To investigate if designated pre-fibroblasts actually correspond to iMSCs as suggested by the reviewer, we have re-examined the expression of some of the key iMSC genes as reported by de Jong et al 17. As shown in Fig. R6, the markers that can distinguish iMSC from other MSC clusters in de Jong et al. study were not exclusively expressed by pre-fibroblasts, but also by other stromal cell types including HAGEPs, balanced progenitors, and pre-osteoblasts.

In the study by R. Schneider’s group18, significant upregulation of S100A8/S100A9 was observed in stromal cells from patients with myelofibrosis. Furthermore, base-line expression of S100A8/A9 was also observed in the fibroblast clusters in the control group, which correlates very well with our data of S100A8/9 expression in pre-fibroblasts in normal donors (Fig. 2F). Our data thus indicate – in line with Schneider’s findings - that there is a baseline level expression of S100A8/9 in fibroblasts in hematologically normal samples and that the expression of S100A8/9 is not restricted to inflamed MSC.

In summary, the gene expression profiles observed in our study do not indicate the presence of iMSC in the healthy bone marrow.

• Figure 3A: Do human adipo-primed cells (cluster 5) indeed differentiate into osteogenic cells (clusters 6, 38, and 39). This would be highly unexpected. Can the authors substantiate this "reliable outcome of the RNA velocity analysis"?

Please refer to our previous responses regarding this topic. Briefly, as shown in Fig. 2B and D, both osteogenic and adipogenic genes are expressed in cluster 5, indicating the multi-potent potentials of this cluster. Although the cluster was initially annotated as adipo-primed progenitors, this was not intended to exclude the osteogenic differentiation potential of these progenitors. Nevertheless, this annotation did not correctly reflect the differentiation potential and might thus have caused confusion, for which we apologize. In order to more correctly describe the characteristics of these cells, cluster 5 has now been reannotated as ‘highly adipocytic gene-expressing progenitors (HAGEPs)’.

In general, the outcome of the RNA velocity analysis needs to be corroborated by in-vivo differentiation experiments. But we believe that functional verification, which would be extensive, is out of the scope of the current study and we will address these questions in future studies.

• How statistically certain are the authors, that the populations in Figure 4B as defined by flow cytometry, correspond to MSSC, adipo-primed cells, osteoprogenitors, etc., as defined by scRNAseq?

To address this question, we sorted the A1-A4 populations and performed RT- PCR to examine the CD81 expression level in each cluster. As shown in Figure 4-figure supplement 1B, CD81 expression levels were higher in A1 and A2 compared with A3 and A4, which is consistent with the scRNAseq data that showed the highest CD81 expression in MSSCs compared to other clusters (Supplementary File 4).

The phenotypes defined in this study allowed us to isolate different stromal cell types which demonstrated significant functional differences as described in the manuscript (page 19, lines 17-25; page 20, lines 1-11). These results, in combination with the quantitative real-time PCR results (Figure 4-figure supplement 1B), demonstrated that the A1-A4 subsets in FACS are functionally distinct populations and are likely to be – at least in large parts – identical or equivalent to the transcriptionally identified clusters in group A stromal cells. However, at this point, we do not have performed the required experiments (scRNAseq of sorted cells) that would provide sufficient proof to confirm this statement statistically.

• The immunohistochemistry results shown do not allow distinct conclusions as the colors give unequivocal mix-colors, and surface expression cannot be distinguished from intracellular expression. Please use a 3D (confocal) method for such statements.

We thank the reviewer for the suggestion and we have performed additional confocal microscopy analysis of human bone marrow biopsies as suggested by the reviewer. Representative confocal images are now presented in the middle and right panel of Fig. 6E. We also include a separate file (Supplemental confocal image file). Here, confocal scans of all maker combinations are shown as ortho views in addition to detailed intensity profile analyses of the cells of interest clearly distinguishing surface staining from intracellular staining.

Confocal analysis of bone marrow biopsies confirmed our findings presented in the manuscript. As observed in the scanning images, CD271-expressing cells were negative for CD45 and were located in perivascular, endosteal, and peri-adipocytic regions. CD271/CD81double positive cells could be found either in the peri-adipocytic regions or perivascular regions while CD271/NCAM1 double-positive cells were exclusively situated at the bone-lining endosteal regions. The results of the confocal analysis have been added to the revised manuscript (page 21, lines 15-17).

• Figure 5A: as all cells seem to interact with all other cells, this figure does not convey relevant information about BM regions using for instance CXCL12 or SPP1. Please reanalyze to show specificity of the interactions of the single clusters. Also, since it is unlikely the CellPhoneDB2-predicted interactions are restricted to hematopoietic responders, please also describe the possible interactions between non-hematopoietic cells.

Fig. 5A was used to demonstrate the complexity of the interactions between hematopoietic cells and stromal cells.

To gain a more detailed understanding of the interactions, we also performed an analysis with the top-listed ligand-receptor pairs as shown in Fig. 5B-C and Figure 5-figure supplement 1B. Here, each dot represents the interaction of a specific ligand-receptor pair listed on the x-axis between the two individual clusters indicated in the y-axis, which we believe shows what the reviewer is asking for.

The specificity of the interactions between single clusters were shown in Fig. 5B-C and Figure 5-figure supplement 1B. The CXCL12- and SPP1-mediated interactions between MSSC/OC and hematopoietic clusters clearly suggested stromal cell type-specific interactions.

Regarding non-hematopoietic cells, both inter- and intra-stromal interactions were identified to be operative between different stromal subsets as well as within the same stromal cell population as shown in Figure 5-figure supplement 3B. In addition, we have also analyzed the interaction pattern between endothelial cells and hematopoietic cells as shown in Fig. 7A, and thus we believe that we have sufficiently described these interactions as requested by the reviewer.

Author Response

Reviewer #2 (Public Review):

Point 1: The transcriptomic analysis of E12.5 endocardial cushion cells in the various mouse models is informative in the extraction of Igf2- and H19-specific gene functions. In Fig. 6D, a huge sex effect is obvious with many more DEGs in female embryos compared to males. How can this be explained given that Igf2/H19 reside on Chr7 and do not primarily affect gene expression on the X chromosome? Is any chromosomal bias observed in the genomic distribution of DEGs?

We examined chromosomal distribution of DEGs between WT and +/hIC1 (Supplemental Figure 6D) and did not see any bias on X chromosome. We described this result on lines 278-280: “Although the number of +/hIC1-specific DEGs largely differed between males and females, there was no sex-specific bias on the X chromosome (Supplemental Figure 6D).” Additionally, we agree with the reviewer that it is noteworthy that the dysregulated H19/Igf2 expression affected transcriptome in a sex-specific manner, especially when the mutation is located on a somatic chromosome. Although investigating the role of hormones versus sex chromosome in these effects would be quite interesting, it is beyond the scope of current study.

Point 2: A separate issue is raised by Fig. 6E that shows a most dramatic dysregulation of a single gene in the delta3.8/hIC1 "rescue" model. Interestingly, this gene is Shh. Hence, these embryos should exhibit some dramatic skeletal abnormalities or other defects linked to sonic hedgehog function.

The reason why Shh appeared to be differentially expressed between wild-type and d3.8/hIC1 samples was that Shh expression was 0 across all the samples except for two wild-type samples. In order to detect all the DEGs that might be lowly expressed, we did not want to filter DEGs based on the level of total expression. As a result, Shh was represented as significantly differently expressed in d3.8/hIC1 samples, although its expression in our samples appears to be too low to have any significant effect on development. This explanation was added to lines 310-312. To confirm that this was an exceptional case, we analyzed the expression of DEGs obtained from other pairwise comparisons. In the volcano plots below, genes of which expression is not statistically different between two groups are marked grey. Genes of which expression is statistically different and detected in both groups are marked red. Genes with statistically different but not detected in one group at all, such as Shh, are marked blue (Figure G). It is clear that that almost all of our DEGs are expressed consistently across the groups, and genes with no expression detected in one group are very rare.

Point 3: The placental analysis needs to be strengthened. Placentas should be consistently positioned with the decidua facing up, and the chorionic plate down. The placentas in Fig. 3F are sectioned at an angle and the chorionic plate is missing. These images must be replaced with better histological sections.

As requested, we have replaced placental images with better representative sections (Figure 3F and 4E). In addition, we have improved alignment of placental histology figures.

Point 4: The CD34 staining has not worked and does not show any fetal vasculature, in particular not in the WT sample.

As requested, we have replaced the CD34 vascular stained images with those that better represent fetal vasculature (Figure 3G).

Point 5: The "thrombi" highlighted in Fig. 4E are well within the normal range, to make the point that these are persistent abnormalities more thorough measurements would need to be performed (number, size, etc).

As requested, we measured the number and relative size of the thrombi that are found in dH19/hIC1 placentas with lesions. No thrombi were found in wild-type placentas whereas an average of 1.3 thrombi were found in six dH19/hIC1 placentas. The size of the thrombi widely varied, but occupied average of 2.58% of the labyrinth zone where these lesions were found (Supplemental Figure 4D). Additionally, we replaced the image in Figure 4E into the section that better represents the lesion.

Point 6: The statement that H19 is disproportionately contributing to the labyrinth phenotype (lines 154/155) is not warranted as Igf2 expression is reduced to virtually nothing in these mice. Even though there is more H19 in the labyrinth than in the junctional zone, the phenotype may still be driven by a loss of Igf2. Given the quasi Igf2-null situation in +/hIC1 mice, is the glycogen cell type phenotype recapitulated in these mice, and how do glycogen numbers compare in the other mouse models?

The sentence was edited in line 157. We performed Periodic acid Schiff (PAS) staining on +/hIC1 placentas to address if glycogen cells are affected by abnormal H19/Igf2 expression (Supplemental Figure 1E). In contrary to previous reports where Igf2-null mice had lower placental glycogen concentration (Lopez et al., 1996) and H19 deletion led to increased placental glycogen storage (Esquiliano et al., 2009), our quantification on PAS-stained images showed that the glycogen content is not significantly different between wild-type and +/hIC1 placentas. We have described this result in lines 166-168.

Point 7: How do delta3.8/+ and delta3.8/hIC1 mice with a VSD survive? Is it resolved some time after birth such that heart function is compatible with postnatal viability? And more importantly, do H19 expression levels correlate with phenotype severity on an individual basis?

Our study was limited to phenotypes prior to birth, thus postnatal/adult phenotypes were not examined. Because the VSD showed only partial penetrance in these mice, we cannot state that the d3.8/+ or d3.8/hlC1 mice with VSDs survive. It has also been previously reported in another mouse model with incomplete penetrance of a VSD that the mice which survived to adulthood did not have the VSDs (Sakata et al., 2002). We find it highly unlikely that either mouse model would survive significantly past the postnatal timepoint with a VSD. We have examined two PN0 d3.8/hIC1 neonates, and both did not have VSD.

Regarding the second point, the only way to quantitatively address this question would be to do qPCR or RNA-seq on individual hearts, which then makes it impossible for those hearts to be examined for histology to confirm the VSD. Thus, hearts used to identify VSDs via histology could not also be used for quantitative H19 measurements. One thing to note is that the H19/Igf2 expression in independent replicates of d3.8/hIC1 cardiac ECs used in our RNA-seq experiment is quite variable, not clustering together in contrast to other mouse models used in this study (Fig. 6A). Such wide range of variability in the extent of H19/Igf2 dysregulation suggests that H19/Igf2 levels could have an impact on the penetrance or the severity of the VSD phenotype in d3.8/hIC1 embryos.

Author Response

Reviewer #2 (Public Review):

Weaknesses:

1) The relevance of the LPS-induced calvarial osteolysis model is not clear. Calvaria is mostly composed of cortical bone-like structures lacking marrow space, though small marrow space exists near the suture. Osteolysis appears to occur in areas apart from where marrow is located. The authors did not show in the manuscript which cells Adipoq-Cre marks in the calvaria.

We have shown in a recent publication that MALPs exist in the calvarial bone marrow (2). As shown in Fig. R1A, Td+ cells are layer of cortical bone (Fig. R1B, blue arrows). In WT mice, after LPS injection, the normal bone structure, including suture and cortical bone, were mostly eroded, and filled with inflammatory cells (green arrows). Thus, osteolysis does occur at the area where bone marrow is originally located. On the contrary, calvarial bone structure was preserved in the CKO mice, demonstrating that Csf1 deficiency in MALPs suppresses LPS-induced osteolysis. We included the H&E staining data in the revised manuscript:

"H&E staining showed that calvarial bone marrow is surrounded by a thin layer of cortical bone (Fig. 5C). After the LPS injection, normal calvarial structure, including suture and cortical bone, were mostly eroded and filled with inflammatory cells in WT mice, but unaltered in CKO mice."

Figure R1. Calvarial bone marrow structure. (A) Representative coronal section of 1.5-month-old Adipoq/Td mouse calvaria. Bone surfaces are outlined by dashed lines. Boxed areas in the low magnification image (top) are enlarged to show periosteum (bottom left), suture (bottom middle), and bone marrow (BM, bottom right) regions. Red: Td; Blue: DAPI. Adopted from our previous publication (2). (B) H&E staining of coronal sections of WT and Csf1 CKOAdipoq mice after LPS injection. Blue arrows point to bone marrow space close to suture (indicated by *). Green arrows point to the osteolytic lesion where cortical bone was eroded, and the space were filled with inflammatory cells.

2) Although the contrast between the two Csf1 conditional deletion models (Adipoq-Cre and Prx1-Cre) is very interesting, the relationship between these two cell populations are not well described. The authors did not clarify if MALPs are also targeted by Prx1-Cre, or these two cell types are from different cell lineages. "Other mesenchymal lineage cells" in the subtitle is not extremely helpful to place this finding in context.

We thank the Reviewer for this comment. The original article constructing Prx1-Cre mouse line demonstrates that Prx1-Cre targets all mesenchymal cells in the limb bud at early as 10.5 dpc (10). This early expression pattern ensures that all bone marrow mesenchymal lineage cells, including MALPs, are targeted by Prx1-Cre. In addition, based on our scRNA-seq data (1), Adipoq is mainly expressed in MALPs, while Prrx1 (Prx1) is highly expressed not only in MALPs but also in EMPs, IMPs, LMPs, LCPs, and OBs (Fig. R2). Thus, the fact that Prx1-Cre driven CKO mice have much more severer bone phenotypes than AdipoqCre driven CKO mice indicates that mesenchymal lineage cells other than MALPs also contribute Csf1 to regulate bone resorption. To avoid confusion, we changed the title and the first sentence in the Result session about Prx1 mice to the following:

"Csf1 from mesenchymal lineage cells other than MALPs regulate bone structure.

To explore whether Csf1 from MALPs plays a dominant role in regulating bone structure, we generated Prx1-Cre Csf1flox/flox (Csf1 CKOPrx1) mice to knockout Csf1 in all mesenchymal lineage cells in bone (10), including MALPs."

Figure R2. Dotplot of Prrx1 and Adipoq expression in bone marrow mesenchymal lineage cells based on our scRNA-seq analysis of 1-month-old mice.

3) The data supporting defective bone marrow hematopoiesis in Csf1 CKO mice are not particularly strong. They observed a reduction in bone marrow cellularity, but this was only associated with an expected reduction in macrophages and a mild reduction in overall HSPC populations. More in-depth analyses might be required to define mechanisms underlying reduced bone marrow cellularity in CKO mice.

We thank the Reviewer for this constructive comment. Accordingly, we performed a thorough analysis of bone marrow hematopoietic compartments and observed significant decreases of monocytes and erythroid progenitors in CKO mice compared to WT mice. These results are now included as Fig. 6E.

4) Some of the phenotypic analyses are still incomplete. The authors did not report whether CHet (Adipoq-Cre Csf1(flox/+)) showed any bone phenotype. Further, the authors did not report whether Csf1 mRNA or M-Csf protein is indeed expressed by MALPs, with current evidence solely reliant on scRNAseq and qPCR data of bulk-isolated cells. More specific histological methods will be helpful to support the premise of the study.

A pilot microCT study revealed the same femoral trabecular bone structure in WT and Adipoq-Cre Csf1flox/+ (Csf1 Het) mice at 3 months of age (Fig. R3). While the sample number for Het is low, we are confident about this conclusion.

Figure R3. MicroCT measurement of trabecular bone structural parameters from WT and Csf1 Het mice. BV/TV: bone volume fraction; BMD: bone mineral density; Tb.N: trabecular number; Tb.Th: trabecular thickness; Tb.Sp: trabecular separation; SMI: structural model index. n=3-8 mice/group.

Author response:

Reviewer #1 (Public Review):

In this paper, Tompary & Davachi present work looking at how memories become integrated over time in the brain, and relating those mechanisms to responses on a priming task as a behavioral measure of memory linkage. They find that remotely but not recently formed memories are behaviorally linked and that this is associated with a change in the neural representation in mPFC. They also find that the same behavioral outcomes are associated with the increased coupling of the posterior hippocampus with category-sensitive parts of the neocortex (LOC) during a post-learning rest period-again only for remotely learned information. There was also correspondence in rest connectivity (posterior hippocampus-LOC) and representational change (mPFC) such that for remote memories specifically, the initial post-learning connectivity enhancement during rest related to longer-term mPFC representational change.

This work has many strengths. The topic of this paper is very interesting, and the data provide a really nice package in terms of providing a mechanistic account of how memories become integrated over a delay. The paper is also exceptionally well-written and a pleasure to read. There are two studies, including one large behavioral study, and the findings replicate in the smaller fMRI sample. I do however have two fairly substantive concerns about the analytic approach, where more data will be required before we can know whether the interpretations are an appropriate reflection of the findings. These and other concerns are described below.

Thank you for the positive comments! We are proud of this work, and we feel that the paper is greatly strengthened by the revisions we made in response to your feedback. Please see below for specific changes that we’ve made.

1) One major concern relates to the lack of a pre-encoding baseline scan prior to recent learning.

a) First, I think it would be helpful if the authors could clarify why there was no pre-learning rest scan dedicated to the recent condition. Was this simply a feasibility consideration, or were there theoretical reasons why this would be less "clean"? Including this information in the paper would be helpful for context. Apologies if I missed this detail in the paper.

This is a great point and something that we struggled with when developing this experiment. We considered several factors when deciding whether to include a pre-learning baseline on day two. First, the day 2 scan session was longer than that of day 1 because it included the recognition priming and explicit memory tasks, and the addition of a baseline scan would have made the length of the session longer than a typical scan session – about 2 hours in the scanner in total – and we were concerned that participant engagement would be difficult to sustain across a longer session. Second, we anticipated that the pre-learning scan would not have been a ‘clean’ measure of baseline processing, but rather would include signal related to post-learning processing of the day 1 sequences, as multi-variate reactivation of learned stimuli have been observed in rest scans collected 24-hours after learning (Schlichting & Preston, 2014). We have added these considerations to the Discussion (page 39, lines 1047-1070).

b) Second, I was hoping the authors could speak to what they think is reflected in the post-encoding "recent" scan. Is it possible that these data could also reflect the processing of the remote memories? I think, though am not positive, that the authors may be alluding to this in the penultimate paragraph of the discussion (p. 33) when noting the LOC-mPFC connectivity findings. Could there be the reinstatement of the old memories due to being back in the same experimental context and so forth? I wonder the extent to which the authors think the data from this scan can be reflected as strictly reflecting recent memories, particularly given it is relative to the pre-encoding baseline from before the remote memories, as well (and therefore in theory could reflect both the remote + recent). (I should also acknowledge that, if it is the case that the authors think there might be some remote memory processing during the recent learning session in general, a pre-learning rest scan might not have been "clean" either, in that it could have reflected some processing of the remote memories-i.e., perhaps a clean pre-learning scan for the recent learning session related to point 1a is simply not possible.)

We propose that theoretically, the post-learning recent scan could indeed reflect mixture of remote and recent sequences. This is one of the drawbacks of splitting encoding into two sessions rather than combining encoding into one session and splitting retrieval into an immediate and delayed session; any rest scans that are collected on Day 2 may have signal that relates to processing of the Day 1 remote sequences, which is why we decided against the pre-learning baseline for Day 2, as you had noted.

You are correct that we alluded to in our original submission when discussing the LOC-mPFC coupling result, and we have taken steps to discuss this more explicitly. In Brief, we find greater LOC-mPFC connectivity only after recent learning relative to the pre-learning baseline, and cortical-cortical connectivity could be indicative of processing memories that already have undergone some consolidation (Takashima et al., 2009; Smith et al., 2010). From another vantage point, the mPFC representation of Day 1 learning may have led to increased connectivity with LOC on Day 2 due to Day 1 learning beginning to resemble consolidated prior knowledge (van Kesteren et al., 2010). While this effect is consistent with prior literature and theory, it's unclear why we would find evidence of processing of the remote memories and not the recent memories. Furthermore, the change in LOC-mPFC connectivity in this scan did not correlate with memory behaviors from either learning session, which could be because signal from this scan reflects a mix of processing of the two different learning sessions. With these ideas in mind, we have fleshed out the discussion of the post-encoding ‘recent’ scan in the Discussion (page 38-39, lines 1039-1044).

c) Third, I am thinking about how both of the above issues might relate to the authors' findings, and would love to see more added to the paper to address this point. Specifically, I assume there are fluctuations in baseline connectivity profile across days within a person, such that the pre-learning connectivity on day 1 might be different from on day 2. Given that, and the lack of a pre-learning connectivity measure on day 2, it would logically follow that the measure of connectivity change from pre- to post-learning is going to be cleaner for the remote memories. In other words, could the lack of connectivity change observed for the recent scan simply be due to the lack of a within-day baseline? Given that otherwise, the post-learning rest should be the same in that it is an immediate reflection of how connectivity changes as a function of learning (depending on whether the authors think that the "recent" scan is actually reflecting "recent + remote"), it seems odd that they both don't show the same corresponding increase in connectivity-which makes me think it may be a baseline difference. I am not sure if this is what the authors are implying when they talk about how day 1 is most similar to prior investigation on p. 20, but if so it might be helpful to state that directly.

We agree that it is puzzling that we don’t see that hippocampal-LOC connectivity does not also increase after recent learning, equivalently to what we see after remote learning. However, the fact that there is an increase from baseline rest to post-recent rest in mPFC – LOC connectivity suggests that it’s not an issue with baseline, but rather that the post-recent learning scan is reflecting processing of the remote memories (although as a caveat, there is no relationship with priming).

On what is now page 23, we were referring to the notion that the Day 1 procedure (baseline rest, learning, post-learning rest) is the most straightforward replication of past work that finds a relationship between hippocampal-cortical coupling and later memory. In contrast, the Day 2 learning and rest scan are less ‘clean’ of a replication in that they are taking place in the shadow of Day 1 learning. We have clarified this in the Results (page 23, lines 597-598).

d) Fourth and very related to my point 1c, I wonder if the lack of correlations for the recent scan with behavior is interpretable, or if it might just be that this is a noisy measure due to imperfect baseline correction. Do the authors have any data or logic they might be able to provide that could speak to these points? One thing that comes to mind is seeing whether the raw post-learning connectivity values (separately for both recent and remote) show the same pattern as the different scores. However, the authors may come up with other clever ways to address this point. If not, it might be worth acknowledging this interpretive challenge in the Discussion.

We thought of three different approaches that could help us to understand whether the lack of correlations in between coupling and behavior in the recent scan was due to noise. First, we correlated recognition priming with raw hippocampal-LOC coupling separately for pre- and post-learning scans, as in Author response image 1:

Author response image 1.

Note that the post-learning chart depicts the relationship between post-remote coupling and remote priming and between post-recent coupling and recent priming (middle). Essentially, post-recent learning coupling did not relate to priming of recently learned sequences (middle; green) while there remains a trend for a relationship between post-remote coupling and priming for remotely learned sequences (middle; blue). However, the significant relationship between coupling and priming that we reported in the paper (right, blue) is driven both by the initial negative relationship that is observed in the pre-learning scan and the positive relationship in the post-remote learning scan. This highlights the importance of using a change score, as there may be spurious initial relationships between connectivity profiles and to-be-learned information that would then mask any learning- and consolidation-related changes.

We also reasoned that if comparisons between the post-recent learning scan and the baseline scan are noisier than between the post-remote learning and baseline scan, there may be differences in the variance of the change scores across participants, such that changes in coupling from baseline to post-recent rest may be more variable than coupling from baseline to post-remote rest. We conducted F-tests to compare the variance of the change in these two hippocampal-LO correlations and found no reliable difference (ratio of difference: F(22, 22) = 0.811, p = .63).

Finally, we explored whether hippocampal-LOC coupling is more stable across participants if compared across two rest scans within the same imaging session (baseline and post-remote) versus across two scans across two separate sessions (baseline and post-recent). Interestingly, coupling was not reliably correlated across scans in either case (baseline/post-remote: r = 0.03, p = 0.89 Baseline/post-recent: r = 0.07, p = .74).

Finally, we evaluated whether hippocampal-LOC coupling was correlated across different rest scans (see Author response image 2). We reasoned that if such coupling was more correlated across baseline and post-remote scans relative to baseline and post-recent scans, that would indicate a within-session stability of participants’ connectivity profiles. At the same time, less correlation of coupling across baseline and post-recent scans would be an indication of a noisier change measure as the measure would additionally include a change in individuals’ connectivity profile over time. We found that there was no difference in the correlation of hipp-LO coupling is across sessions, and the correlation was not reliably significant for either session (baseline/post-remote: r = 0.03, p = 0.89; baseline/post-recent: r = 0.07, p = .74; difference: Steiger’s t = 0.12, p = 0.9).

Author response image 2.

We have included the raw correlations with priming (page 25, lines 654-661, Supplemental Figure 6) as well as text describing the comparison of variances (page 25, lines 642-653). We did not add the comparison of hippocampal-LOC coupling across scans to the current manuscript, as an evaluation of stability of such coupling in the context of learning and reactivation seems out of scope of the current focus of the experiment, but we find this result to be worthy of follow-up in future work.

In summary, further analysis of our data did not reveal any indication that a comparison of rest connectivity across scan sessions inserted noise into the change score between baseline and post-recent learning scans. However, these analyses cannot fully rule that possibility out, and the current analyses do not provide concrete evidence that the post-recent learning scan comprises signals that are a mixture of processing of recent and remote sequences. We discuss these drawbacks in the Discussion (page 39, lines 1047-1070).

2) My second major concern is how the authors have operationalized integration and differentiation. The pattern similarity analysis uses an overall correspondence between the neural similarity and a predicted model as the main metric. In the predicted model, C items that are indirectly associated are more similar to one another than they are C items that are entirely unrelated. The authors are then looking at a change in correspondence (correlation) between the neural data and that prediction model from pre- to post-learning. However, a change in the degree of correspondence with the predicted matrix could be driven by either the unrelated items becoming less similar or the related ones becoming more similar (or both!). Since the interpretation in the paper focuses on change to indirectly related C items, it would be important to report those values directly. For instance, as evidence of differentiation, it would be important to show that there is a greater decrease in similarity for indirectly associated C items than it is for unrelated C items (or even a smaller increase) from pre to post, or that C items that are indirectly related are less similar than are unrelated C items post but not pre-learning. Performing this analysis would confirm that the pattern of results matches the authors' interpretation. This would also impact the interpretation of the subsequent analyses that involve the neural integration measures (e.g., correlation analyses like those on p. 16, which may or may not be driven by increased similarity among overlapping C pairs). I should add that given the specificity to the remote learning in mPFC versus recent in LOC and anterior hippocampus, it is clearly the case that something interesting is going on. However, I think we need more data to understand fully what that "something" is.

We recognize the importance of understanding whether model fits (and changes to them) are driven by similarity of overlapping pairs or non-overlapping pairs. We have modified all figures that visualize model fits to the neural integration model to separately show fits for pre- and post-learning (Figure 3 for mPFC, Supp. Figure 5 for LOC, Supp. Figure 9 for AB similarity in anterior hippocampus & LOC). We have additionally added supplemental figures to show the complete breakdown of similarity each region in a 2 (pre/post) x 2 (overlapping/non-overlapping sequence) x 2 (recent/remote) chart. We decided against including only these latter charts rather than the model fits since the model fits strike a good balance between information and readability. We have also modified text in various sections to focus on these new results.

In brief, the decrease in model fit for mPFC for the remote sequences was driven primarily by a decrease in similarity for the overlapping C items and not the non-overlapping ones (Supplementary Figure 3, page 18, lines 468-472).

Interestingly, in LOC, all C items grew more similar after learning, regardless of their overlap or learning session, but the increase in model fit for C items in the recent condition was driven by a larger increase in similarity for overlapping pairs relative to non-overlapping ones (Supp. Figure 5, page 21, lines 533-536).

We also visualized AB similarity in the anterior hippocampus and LOC in a similar fashion (Supplementary Figure 9).

We have also edited the Methods sections with updated details of these analyses (page 52, lines 1392-1397). We think that including these results considerably strengthen our claims and we are pleased to have them included.

3) The priming task occurred before the post-learning exposure phase and could have impacted the representations. More consideration of this in the paper would be useful. Most critically, since the priming task involves seeing the related C items back-to-back, it would be important to consider whether this experience could have conceivably impacted the neural integration indices. I believe it never would have been the case that unrelated C items were presented sequentially during the priming task, i.e., that related C items always appeared together in this task. I think again the specificity of the remote condition is key and perhaps the authors can leverage this to support their interpretation. Can the authors consider this possibility in the Discussion?

It's true that only C items from the same sequence were presented back-to-back during the priming task, and that this presentation may interfere with observations from the post-learning exposure scan that followed it. We agree that it is worth considering this caveat and have added language in the Discussion (page 40, lines 1071-1086). When designing the study, we reasoned that it was more important for the behavioral priming task to come before the exposure scans, as all items were shown only once in that task, whereas they were shown 4-5 times in a random order in the post-learning exposure phase. Because of this difference in presentation times, and because behavioral priming findings tend to be very sensitive, we concluded that it was more important to protect the priming task from the exposure scan instead of the reverse.

We reasoned, however, that the additional presentation of the C items in the recognition priming task would not substantially override the sequence learning, as C items were each presented 16 times in their sequence (ABC1 and ABC2 16 times each). Furthermore, as this reviewer suggests, the order of C items during recognition was the same for recent and remote conditions, so the fact that we find a selective change in neural representation for the remote condition and don’t also see that change for the recent condition is additional assurance that the recognition priming order did not substantially impact the representations.

4) For the priming task, based on the Figure 2A caption it seems as though every sequence contributes to both the control and primed conditions, but (I believe) this means that the control transition always happens first (and they are always back-to-back). Is this a concern? If RTs are changing over time (getting faster), it would be helpful to know whether the priming effects hold after controlling for trial numbers. I do not think this is a big issue because if it were, you would not expect to see the specificity of the remotely learned information. However, it would be helpful to know given the order of these conditions has to be fixed in their design.

This is a correct understanding of the trial orders in the recognition priming task. We chose to involve the baseline items in the control condition to boost power – this way, priming of each sequence could be tested, while only presenting each item once in this task, as repetition in the recognition phase would have further facilitated response times and potentially masked any priming effects. We agree that accounting for trial order would be useful here, so we ran a mixed-effects linear model to examine responses times both as a function of trial number and of priming condition (primed/control). While there is indeed a large effect of trial number such that participants got faster over time, the priming effect originally observed in the remote condition still holds at the same time. We now report this analysis in the Results section (page 14, lines 337-349 for Expt 1 and pages 14-15, lines 360-362 for Expt 2).

5) The authors should be cautious about the general conclusion that memories with overlapping temporal regularities become neurally integrated - given their findings in MPFC are more consistent with overall differentiation (though as noted above, I think we need more data on this to know for sure what is going on).

We realize this conclusion was overly simplistic and, in several places, have revised the general conclusions to be more specific about the nuanced similarity findings.

6) It would be worth stating a few more details and perhaps providing additional logic or justification in the main text about the pre- and post-exposure phases were set up and why. How many times each object was presented pre and post, and how the sequencing was determined (were any constraints put in place e.g., such that C1 and C2 did not appear close in time?). What was the cover task (I think this is important to the interpretation & so belongs in the main paper)? Were there considerations involving the fact that this is a different sequence of the same objects the participants would later be learning - e.g., interference, etc.?

These details can be found in the Methods section (pages 50-51, lines 1337-1353) and we’ve added a new summary of that section in the Results (page 17, lines 424- 425 and 432-435). In brief, a visual hash tag appeared on a small subset of images and participants pressed a button when this occurred, and C1 and C2 objects were presented in separate scans (as were A and B objects) to minimize inflated neural similarity due to temporal proximity.

Reviewer #2 (Public Review):

The manuscript by Tompary & Davachi presents results from two experiments, one behavior only and one fMRI plus behavior. They examine the important question of how to separate object memories (C1 and C2) that are never experienced together in time and become linked by shared predictive cues in a sequence (A followed by B followed by one of the C items). The authors developed an implicit priming task that provides a novel behavioral metric for such integration. They find significant C1-C2 priming for sequences that were learned 24h prior to the test, but not for recently learned sequences, suggesting that associative links between the two originally separate memories emerge over an extended period of consolidation. The fMRI study relates this behavioral integration effect to two neural metrics: pattern similarity changes in the medial prefrontal cortex (mPFC) as a measure of neural integration, and changes in hippocampal-LOC connectivity as a measure of post-learning consolidation. While fMRI patterns in mPFC overall show differentiation rather than integration (i.e., C1-C2 representational distances become larger), the authors find a robust correlation such that increasing pattern similarity in mPFC relates to stronger integration in the priming test, and this relationship is again specific to remote memories. Moreover, connectivity between the posterior hippocampus and LOC during post-learning rest is positively related to the behavioral integration effect as well as the mPFC neural similarity index, again specifically for remote memories. Overall, this is a coherent set of findings with interesting theoretical implications for consolidation theories, which will be of broad interest to the memory, learning, and predictive coding communities.

Strengths:

1) The implicit associative priming task designed for this study provides a promising new tool for assessing the formation of mnemonic links that influence behavior without explicit retrieval demands. The authors find an interesting dissociation between this implicit measure of memory integration and more commonly used explicit inference measures: a priming effect on the implicit task only evolved after a 24h consolidation period, while the ability to explicitly link the two critical object memories is present immediately after learning. While speculative at this point, these two measures thus appear to tap into neocortical and hippocampal learning processes, respectively, and this potential dissociation will be of interest to future studies investigating time-dependent integration processes in memory.

2) The experimental task is well designed for isolating pre- vs post-learning changes in neural similarity and connectivity, including important controls of baseline neural similarity and connectivity.

3) The main claim of a consolidation-dependent effect is supported by a coherent set of findings that relate behavioral integration to neural changes. The specificity of the effects on remote memories makes the results particularly interesting and compelling.

4) The authors are transparent about unexpected results, for example, the finding that overall similarity in mPFC is consistent with a differentiation rather than an integration model.

Thank you for the positive comments!

Weaknesses:

1) The sequence learning and recognition priming tasks are cleverly designed to isolate the effects of interest while controlling for potential order effects. However, due to the complex nature of the task, it is difficult for the reader to infer all the transition probabilities between item types and how they may influence the behavioral priming results. For example, baseline items (BL) are interspersed between repeated sequences during learning, and thus presumably can only occur before an A item or after a C item. This seems to create non-random predictive relationships such that C is often followed by BL, and BL by A items. If this relationship is reversed during the recognition priming task, where the sequence is always BL-C1-C2, this violation of expectations might slow down reaction times and deflate the baseline measure. It would be helpful if the manuscript explicitly reported transition probabilities for each relevant item type in the priming task relative to the sequence learning task and discussed how a match vs mismatch may influence the observed priming effects.

We have added a table of transition probabilities across the learning, recognition priming, and exposure scans (now Table 1, page 48). We have also included some additional description of the change in transition probabilities across different tasks in the Methods section. Specifically, if participants are indeed learning item types and rules about their order, then both the control and the primed conditions would violate that order. Since C1 and C2 items never appeared together, viewing C1 would give rise to an expectation of seeing a BL item, which would also be violated. This suggests that our priming effects are driven by sequence-specific relationships rather than learning of the probabilities of different item types. We’ve added this consideration to the Methods section (page 45, lines 1212-1221).

Another critical point to consider (and that the transition probabilities do not reflect) is that during learning, while C is followed either by A or BL, they are followed by different A or BL items. In contrast, a given A is always followed by the same B object, which is always followed by one of two C objects. While the order of item types is semi-predictable, the order of objects (specific items) themselves are not. This can be seen in the response times during learning, such that response times for A and BL items are always slower than for B and C items. We have explained this nuance in the figure text for Table 1.

2) The choice of what regions of interest to include in the different sets of analyses could be better motivated. For example, even though briefly discussed in the intro, it remains unclear why the posterior but not the anterior hippocampus is of interest for the connectivity analyses, and why the main target is LOC, not mPFC, given past results including from this group (Tompary & Davachi, 2017). Moreover, for readers not familiar with this literature, it would help if references were provided to suggest that a predictable > unpredictable contrast is well suited for functionally defining mPFC, as done in the present study.

We have clarified our reasoning for each of these choices throughout the manuscript and believe that our logic is now much more transparent. For an expanded reasoning of why we were motivated to look at posterior and not anterior hippocampus, see pages 6-7, lines 135-159, and our response to R2. In brief, past research focusing on post-encoding connectivity with the hippocampus suggests that posterior aspect is more likely to couple with category-selective cortex after learning neutral, non-rewarded objects much like the stimuli used in the present study.

We also clarify our reasoning for LOC over mPFC. While theoretically, mPFC is thought to be a candidate region for coupling with the hippocampus during consolidation, the bulk of empirical work to date has revealed post-encoding connectivity between the hippocampus and category-selective cortex in the ventral and occipital lobes (page 6, lines 123-134).

As for the use of the predictable > unpredictable contrast for functionally defining cortical regions, we reasoned that cortical regions that were sensitive to the temporal regularities generated by the sequences may be further involved in their offline consolidation and long-term storage (Danker & Anderson, 2010; Davachi & Danker, 2013; McClelland et al., 1995). We have added this justification to the Methods section (page 18, lines 454-460).

3) Relatedly, multiple comparison corrections should be applied in the fMRI integration and connectivity analyses whenever the same contrast is performed on multiple regions in an exploratory manner.

We now correct for multiple comparisons using Bonferroni correction, and this correction depends on the number of regions in which each analysis is conducted. Please see page 55, lines 1483-1490, in the Methods section for details of each analysis.

Reviewer #3 (Public Review):

The authors of this manuscript sought to illuminate a link between a behavioral measure of integration and neural markers of cortical integration associated with systems consolidation (post-encoding connectivity, change in representational neural overlap). To that aim, participants incidentally encoded sequences of objects in the fMRI scanner. Unbeknownst to participants, the first two objects of the presented ABC triplet sequences overlapped for a given pair of sequences. This allowed the authors to probe the integration of unique C objects that were never directly presented in the same sequence, but which shared the same preceding A and B objects. They encoded one set of objects on Day 1 (remote condition), another set of objects 24 hours later (recent condition) and tested implicit and explicit memory for the learned sequences on Day 2. They additionally collected baseline and post-encoding resting-state scans. As their measure of behavioral integration, the authors examined reaction time during an Old/New judgement task for C objects depending on if they were preceded by a C object from an overlapping sequence (primed condition) versus a baseline object. They found faster reaction times for the primed objects compared to the control condition for remote but not recently learned objects, suggesting that the C objects from overlapping sequences became integrated over time. They then examined pattern similarity in a priori ROIs as a measure of neural integration and found that participants showing evidence of integration of C objects from overlapping sequences in the medial prefrontal cortex for remotely learned objects also showed a stronger implicit priming effect between those C objects over time. When they examined the change in connectivity between their ROIs after encoding, they also found that connectivity between the posterior hippocampus and lateral occipital cortex correlated with larger priming effects for remotely learned objects, and that lateral occipital connectivity with the medial prefrontal cortex was related to neural integration of remote objects from overlapping sequences.

The authors aim to provide evidence of a relationship between behavioral and neural measures of integration with consolidation is interesting, important, and difficult to achieve given the longitudinal nature of studies required to answer this question. Strengths of this study include a creative behavioral task, and solid modelling approaches for fMRI data with careful control for several known confounds such as bold activation on pattern analysis results, motion, and physiological noise. The authors replicate their behavioral observations across two separate experiments, one of which included a large sample size, and found similar results that speak to the reliability of the observed behavioral phenomenon. In addition, they document several correlations between neural measures and task performance, lending functional significance to their neural findings.

Thank you for this positive assessment of our study!

However, this study is not without notable weaknesses that limit the strength of the manuscript. The authors report a behavioral priming effect suggestive of integration of remote but not recent memories, leading to the interpretation that the priming effect emerges with consolidation. However, they did not observe a reliable interaction between the priming condition and learning session (recent/remote) on reaction times, meaning that the priming effect for remote memories was not reliably greater than that observed for recent. In addition, the emergence of a priming effect for remote memories does not appear to be due to faster reaction times for primed targets over time (the condition of interest), but rather, slower reaction times for control items in the remote condition compared to recent. These issues limit the strength of the claim that the priming effect observed is due to C items of interest being integrated in a consolidation-dependent manner.

We acknowledge that the lack of a day by condition interaction in the behavioral priming effect should discussed and now discuss this data in a more nuanced manner. While it’s true that the priming effect emerges due to a slowing of the control items over time, this slowing is consistent with classic time-dependent effects demonstrating slower response times for more delayed memories. The fact that the response times in the primed condition does not show this slowing can be interpreted as a protection against this slowing that would otherwise occur. Please see page 29, lines 758-766, for this added discussion.

Similarly, the interactions between neural variables of interest and learning session needed to strongly show a significant consolidation-related effect in the brain were sometimes tenuous. There was no reliable difference in neural representational pattern analysis fit to a model of neural integration between the short and long delays in the medial prefrontal cortex or lateral occipital cortex, nor was the posterior hippocampus-lateral occipital cortex post-encoding connectivity correlation with subsequent priming significantly different for recent and remote memories. While the relationship between integration model fit in the medial prefrontal cortex and subsequent priming (which was significantly different from that occurring for recent memories) was one of the stronger findings of the paper in favor of a consolidation-related effect on behavior, is it possible that lack of a behavioral priming effect for recent memories due to possible issues with the control condition could mask a correlation between neural and behavioral integration in the recent memory condition?

While we acknowledge that lack of a statistically reliable interaction between neural measures and behavioral priming in many cases, we are heartened by the reliable difference in the relationship between mPFC similarity and priming over time, which was our main planned prediction. In addition to adding caveats in the discussion about the neural measures and behavioral findings in the recent condition (see our response to R1.1 and R1.4 for more details), we have added language throughout the manuscript noting the need to interpret these data with caution.

These limitations are especially notable when one considers that priming does not classically require a period of prolonged consolidation to occur, and prominent models of systems consolidation rather pertain to explicit memory. While the authors have provided evidence that neural integration in the medial prefrontal cortex, as well as post-encoding coupling between the lateral occipital cortex and posterior hippocampus, are related to faster reaction times for primed objects of overlapping sequences compared to their control condition, more work is needed to verify that the observed findings indeed reflect consolidation dependent integration as proposed.

We agree that more work is needed to provide converging evidence for these novel findings. However, we wish to counter the notion that systems consolidation models are relevant only for explicit memories. Although models of systems consolidation often mention transformations from episodic to semantic memory, the critical mechanisms that define the models involve changes in the neural ensembles of a memory that is initially laid down in the hippocampus and is taught to cortex over time. This transformation of neural traces is not specific to explicit/declarative forms of memory. For example, implicit statistical learning initially depends on intact hippocampal function (Schapiro et al., 2014) and improves over consolidation (Durrant et al., 2011, 2013; Kóbor et al., 2017).

Second, while there are many classical findings of priming during or immediately after learning, there are several instances of priming used to measure consolidation-related changes to newly learned information. For instance, priming has been used as a measure of lexical integration, demonstrating that new word learning benefits from a night of sleep (Wang et al., 2017; Gaskell et al., 2019) or a 1-week delay (Tamminen & Gaskell, 2013). The issue is not whether priming can occur immediately, it is whether priming increases with a delay.

Finally, it is helpful to think about models of memory systems that divide memory representations not by their explicit/implicit nature, but along other important dimensions such as their neural bases, their flexibility vs rigidity, and their capacity for rapid vs slow learning (Henke, 2010). Considering this evidence, we suggest that systems consolidation models are most useful when considering how transformations in the underlying neural memory representation affects its behavioral expression, rather than focusing on the extent that the memory representation is explicit or implicit.

With all this said, we have added text to the discussion reminding the reader that there was no statistically significant difference in priming as a function of the delay (page 29, lines 764 - 766). However, we are encouraged by the fact that the relationship between priming and mPFC neural similarity was significantly stronger for remotely learned objects relative to recently learned ones, as this is directly in line with systems consolidation theories.

References

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Author Response:

Reviewer #3:

The authors modified a previously reported hybrid cytochrome bcc-aa3 supercomplex, consisting of bcc from M. tuberculosis and aa3 from M. smegmatis, (Kim et al 2015) by appending an affinity tag facilitating purification. The cryo-EM experiments are based on the authors' earlier work (Gong et al. 2018) on the structure of the bcc-aa3 supercomplex from M. smegmatis. The authors then determine the structure of the bcc part alone and in complex with Q203 and TB47.

The manuscript is well written and the obtained results are presented in a concise, clear-cut manner. In general, the data support the conclusions drawn.

We thank the reviewer for this evaluation.

To this reviewer, the following points are unclear:

1. The purified enzyme elutes from the gel filtration column as one peak, but there seems to be no information given on the subunit composition and the enzymatic activity of the purified hybrid cytochrome bcc-aa3 supercomplex.

See answers to Question 1 from the major Essential Revisions and Question 1 from the minor Essential Revisions.

"We have now shown that the purified chimeric supercomplex is a functional assembly with a (mean ± s.d., n = 4), in agreement with the previous study that shows M. tuberculosis CIII can functionally complement native M. smegmatis CIII and maintain the growth of M. smegmatis (Kim et al., 2015). The in vitro inhibitions of this enzyme by Q203 and TB47 was determined by means of an DMNQH2/oxygen oxidoreductase activity assay. In the assay, 500 nM Q203 or TB47 was chosen, which is close to the median inhibitory concentration (IC50) obtained from the menadiol-induced oxygen consumption in our previous study (Gong et al., 2018). After addition of Q203 and TB47, the values of turnover number of the hybrid supercomplex are reduced to 5.8 +/- 2.4 e-s-1 (Figure 4-figure supplement 4) and 5.1 +/- 2.9 e-s-1 (Figure 5-figure supplement 4) respectively, from 23.3 +/- 2.4 e-s-1. We have incorporated this new data into the text (lines 90-93, 187-189, 206-209)."

"The subunit composition of the purified enzyme has now been provided in Figure 2-figure supplement 1."

1. It is unclear what is the conclusion of the structure comparison (Fig 6) is regarding the affinity of Q203 for M. smegmatis.

The structural comparison indicates that Q203 should have a similar binding mechanism and a similar effect on the activity of cytochrome bcc from M. smegmatis and M. tuberculosis. This is in good agreement with previous antimycobacterial activity data and inhibition data for the bcc complexes from M. smegmatis and M. tuberculosis (Gong et al., 2018; Lu et al., 2018a). These have now been incorporated into the revised manuscript (line 223-227).

Author Response

Reviewer #1 (Public Review):

This study used a multi-day learning paradigm combined with fMRI to reveal neural changes reflecting the learning of new (arbitrary) shape-sound associations. In the scanner, the shapes and sounds are presented separately and together, both before and after learning. When they are presented together, they can be either consistent or inconsistent with the learned associations. The analyses focus on auditory and visual cortices, as well as the object-selective cortex (LOC) and anterior temporal lobe regions (temporal pole (TP) and perirhinal cortex (PRC)). Results revealed several learning-induced changes, particularly in the anterior temporal lobe regions. First, the LOC and PRC showed a reduced bias to shapes vs sounds (presented separately) after learning. Second, the TP responded more strongly to incongruent than congruent shape-sound pairs after learning. Third, the similarity of TP activity patterns to sounds and shapes (presented separately) was increased for non-matching shape-sound comparisons after learning. Fourth, when comparing the pattern similarity of individual features to combined shape-sound stimuli, the PRC showed a reduced bias towards visual features after learning. Finally, comparing patterns to combined shape-sound stimuli before and after learning revealed a reduced (and negative) similarity for incongruent combinations in PRC. These results are all interpreted as evidence for an explicit integrative code of newly learned multimodal objects, in which the whole is different from the sum of the parts.

The study has many strengths. It addresses a fundamental question that is of broad interest, the learning paradigm is well-designed and controlled, and the stimuli are real 3D stimuli that participants interact with. The manuscript is well written and the figures are very informative, clearly illustrating the analyses performed.

There are also some weaknesses. The sample size (N=17) is small for detecting the subtle effects of learning. Most of the statistical analyses are not corrected for multiple comparisons (ROIs), and the specificity of the key results to specific regions is also not tested. Furthermore, the evidence for an integrative representation is rather indirect, and alternative interpretations for these results are not considered.

We thank the reviewer for their careful reading and the positive comments on our manuscript. As suggested, we have conducted additional analyses of theoretically-motivated ROIs and have found that temporal pole and perirhinal cortex are the only regions to show the key experience-dependent transformations. We are much more cautious with respect to multiple comparisons, and have removed a series of post hoc across-ROI comparisons that were irrelevant to the key questions of the present manuscript. The revised manuscript now includes much more discussion about alternative interpretations as suggested by the reviewer (and also by the other reviewers).

Additionally, we looked into scanning more participants, but our scanner has since had a full upgrade and the sequence used in the current study is no longer supported by our scanner. However, we note that while most analyses contain 17 participants, we employed a within-subject learning design that is not typically used in fMRI experiments and increases our power to detect an effect. This is supported by the robust effect size of the behavioural data, whereby 17 out of 18 participants revealed a learning effect (Cohen’s D = 1.28) and which was replicated in a follow-up experiment with a larger sample size.

We address the other reviewer comments point-by-point in the below.

Reviewer #2 (Public Review):

Li et al. used a four-day fMRI design to investigate how unimodal feature information is combined, integrated, or abstracted to form a multimodal object representation. The experimental question is of great interest and understanding how the human brain combines featural information to form complex representations is relevant for a wide range of researchers in neuroscience, cognitive science, and AI. While most fMRI research on object representations is limited to visual information, the authors examined how visual and auditory information is integrated to form a multimodal object representation. The experimental design is elegant and clever. Three visual shapes and three auditory sounds were used as the unimodal features; the visual shapes were used to create 3D-printed objects. On Day 1, the participants interacted with the 3D objects to learn the visual features, but the objects were not paired with the auditory features, which were played separately. On Day 2, participants were scanned with fMRI while they were exposed to the unimodal visual and auditory features as well as pairs of visual-auditory cues. On Day 3, participants again interacted with the 3D objects but now each was paired with one of the three sounds that played from an internal speaker. On Day 4, participants completed the same fMRI scanning runs they completed on Day 2, except now some visual-auditory feature pairs corresponded with Congruent (learned) objects, and some with Incongruent (unlearned) objects. Using the same fMRI design on Days 2 and 4 enables a well-controlled comparison between feature- and object-evoked neural representations before and after learning. The notable results corresponded to findings in the perirhinal cortex and temporal pole. The authors report (1) that a visual bias on Day 2 for unimodal features in the perirhinal cortex was attenuated after learning on Day 4, (2) a decreased univariate response to congruent vs. incongruent visual-auditory objects in the temporal pole on Day 4, (3) decreased pattern similarity between congruent vs. incongruent pairs of visual and auditory unimodal features in the temporal pole on Day 4, (4) in the perirhinal cortex, visual unimodal features on Day 2 do not correlate with their respective visual-auditory objects on Day 4, and (5) in the perirhinal cortex, multimodal object representations across Days 2 and 4 are uncorrelated for congruent objects and anticorrelated for incongruent. The authors claim that each of these results supports the theory that multimodal objects are represented in an "explicit integrative" code separate from feature representations. While these data are valuable and the results are interesting, the authors' claims are not well supported by their findings.

We thank the reviewer for the careful reading of our manuscript and positive comments. Overall, we now stay closer to the data when describing the results and provide our interpretation of these results in the discussion section while remaining open to alternative interpretations (as also suggested by Reviewer 1).

(1) In the introduction, the authors contrast two theories: (a) multimodal objects are represented in the co-activation of unimodal features, and (b) multimodal objects are represented in an explicit integrative code such that the whole is different than the sum of its parts. However, the distinction between these two theories is not straightforward. An explanation of what is precisely meant by "explicit" and "integrative" would clarify the authors' theoretical stance. Perhaps we can assume that an "explicit" representation is a new representation that is created to represent a multimodal object. What is meant by "integrative" is more ambiguous-unimodal features could be integrated within a representation in a manner that preserves the decodability of the unimodal features, or alternatively the multimodal representation could be completely abstracted away from the constituent features such that the features are no longer decodable. Even if the object representation is "explicit" and distinct from the unimodal feature representations, it can in theory still contain featural information, though perhaps warped or transformed. The authors do not clearly commit to a degree of featural abstraction in their theory of "explicit integrative" multimodal object representations which makes it difficult to assess the validity of their claims.

Due to its ambiguity, we removed the term “explicit” and now make it clear that our central question was whether crossmodal object representations require only unimodal feature-level representations (e.g., frogs are created from only the combination of shape and sound) or whether crossmodal object representations also rely on an integrative code distinct from the unimodal features (e.g., there is something more to “frog” than its original shape and sound). We now clarify this in the revised manuscript.

“One theoretical view from the cognitive sciences suggests that crossmodal objects are built from component unimodal features represented across distributed sensory regions.8 Under this view, when a child thinks about “frog”, the visual cortex represents the appearance of the shape of the frog whereas the auditory cortex represents the croaking sound. Alternatively, other theoretical views predict that multisensory objects are not only built from their component unimodal sensory features, but that there is also a crossmodal integrative code that is different from the sum of these parts.9,10,11,12,13 These latter views propose that anterior temporal lobe structures can act as a polymodal “hub” that combines separate features into integrated wholes.9,11,14,15” – pg. 4

For this reason, we designed our paradigm to equate the unimodal representations, such that neural differences between the congruent and incongruent conditions provide evidence for a crossmodal integrative code different from the unimodal features (because the unimodal features are equated by default in the design).

“Critically, our four-day learning task allowed us to isolate any neural activity associated with integrative coding in anterior temporal lobe structures that emerges with experience and differs from the neural patterns recorded at baseline. The learned and non-learned crossmodal objects were constructed from the same set of three validated shape and sound features, ensuring that factors such as familiarity with the unimodal features, subjective similarity, and feature identity were tightly controlled (Figure 2). If the mind represented crossmodal objects entirely as the reactivation of unimodal shapes and sounds (i.e., objects are constructed from their parts), then there should be no difference between the learned and non-learned objects (because they were created from the same three shapes and sounds). By contrast, if the mind represented crossmodal objects as something over and above their component features (i.e., representations for crossmodal objects rely on integrative coding that is different from the sum of their parts), then there should be behavioral and neural differences between learned and non-learned crossmodal objects (because the only difference across the objects is the learned relationship between the parts). Furthermore, this design allowed us to determine the relationship between the object representation acquired after crossmodal learning and the unimodal feature representations acquired before crossmodal learning. That is, we could examine whether learning led to abstraction of the object representations such that it no longer resembled the unimodal feature representations.” – pg. 5

Furthermore, we agree with the reviewer that our definition and methodological design does not directly capture the structure of the integrative code. With experience, the unimodal feature representations may be completely abstracted away, warped, or changed in a nonlinear transformation. We suggest that crossmodal learning forms an integrative code that is different from the original unimodal representations in the anterior temporal lobes, however, we agree that future work is needed to more directly capture the structure of the integrative code that emerges with experience.

“In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

(2) After participants learned the multimodal objects, the authors report a decreased univariate response to congruent visual-auditory objects relative to incongruent objects in the temporal pole. This is claimed to support the existence of an explicit, integrative code for multimodal objects. Given the number of alternative explanations for this finding, this claim seems unwarranted. A simpler interpretation of these results is that the temporal pole is responding to the novelty of the incongruent visual-auditory objects. If there is in fact an explicit, integrative multimodal object representation in the temporal pole, it is unclear why this would manifest in a decreased univariate response.

We thank the reviewer for identifying this issue. Our behavioural design controls unimodal feature-level novelty but allows object-level novelty to differ. Thus, neural differences between the congruent and incongruent conditions reflects sensitivity to the object-level differences between the combination of shape and sound. However, we agree that there are multiple interpretations regarding the nature of how the integrative code is structured in the temporal pole and perirhinal cortex. We have removed the interpretation highlighted by the reviewer from the results. Instead, we now provide our preferred interpretation in the discussion, while acknowledging the other possibilities that the reviewer mentions.

As one possibility, these results in temporal pole may reflect “conceptual combination”. “hummingbird” – a congruent pairing – may require less neural resources than an incongruent pairing such as “bark-frog”.

“Furthermore, these distinct anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).”– pg. 18

(3) The authors ran a neural pattern similarity analysis on the unimodal features before and after multimodal object learning. They found that the similarity between visual and auditory features that composed congruent objects decreased in the temporal pole after multimodal object learning. This was interpreted to reflect an explicit integrative code for multimodal objects, though it is not clear why. First, behavioral data show that participants reported increased similarity between the visual and auditory unimodal features within congruent objects after learning, the opposite of what was found in the temporal pole. Second, it is unclear why an analysis of the unimodal features would be interpreted to reflect the nature of the multimodal object representations. Since the same features corresponded with both congruent and incongruent objects, the nature of the feature representations cannot be interpreted to reflect the nature of the object representations per se. Third, using unimodal feature representations to make claims about object representations seems to contradict the theoretical claim that explicit, integrative object representations are distinct from unimodal features. If the learned multimodal object representation exists separately from the unimodal feature representations, there is no reason why the unimodal features themselves would be influenced by the formation of the object representation. Instead, these results seem to more strongly support the theory that multimodal object learning results in a transformation or warping of feature space.

We apologize for the lack of clarity. We have now overhauled this aspect of our manuscript in an attempt to better highlight key aspects of our experimental design. In particular, because the unimodal features composing the congruent and incongruent objects were equated, neural differences between these conditions would provide evidence for an experience-dependent crossmodal integrative code that is different from its component unimodal features.

Related to the second and third points, we were looking at the extent to which the original unimodal representations change with crossmodal learning. Before crossmodal learning, we found that the perirhinal cortex tracked the similarity between the individual visual shape features and the crossmodal objects that were composed of those visual shapes – however, there was no evidence that perirhinal cortex was tracking the unimodal sound features on those crossmodal objects. After crossmodal learning, we see that this visual shape bias in perirhinal cortex was no longer present – that is, the representation in perirhinal cortex started to look less like the visual features that comprise the objects. Thus, crossmodal learning transformed the perirhinal representations so that they were no longer predominantly grounded in a single visual modality, which may be a mechanism by which object concepts gain their abstraction. We have now tried to be clearer about this interpretation throughout the paper.

Notably, we suggest that experience may change both the crossmodal object representations, as well as the unimodal feature representations. For example, we have previously shown that unimodal visual features are influenced by experience in parallel with the representation of the conjunction (e.g., Liang et al., 2020; Cerebral Cortex). Nevertheless, we remain open to the myriad possible structures of the integrative code that might emerge with experience.

We now clarify these points throughout the manuscript. For example:

“We then examined whether the original representations would change after participants learned how the features were paired together to make specific crossmodal objects, conducting the same analysis described above after crossmodal learning had taken place (Figure 5b). With this analysis, we sought to measure the relationship between the representation for the learned crossmodal object and the original baseline representation for the unimodal features. More specifically, the voxel-wise activity for unimodal feature runs before crossmodal learning was correlated to the voxel-wise activity for crossmodal object runs after crossmodal learning (Figure 5b). Another linear mixed model which included modality as a fixed factor within each ROI revealed that the perirhinal cortex was no longer biased towards visual shape after crossmodal learning (F1,32 = 0.12, p = 0.73), whereas the temporal pole, LOC, V1, and A1 remained biased towards either visual shape or sound (F1,30-32 between 16.20 and 73.42, all p < 0.001, η2 between 0.35 and 0.70).” – pg. 14

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

“Importantly, the initial visual shape bias observed in the perirhinal cortex was attenuated by experience (Figure 5, Supplemental Figure S5), suggesting that the perirhinal representations had become abstracted and were no longer predominantly grounded in a single modality after crossmodal learning. One possibility may be that the perirhinal cortex is by default visually driven as an extension to the ventral visual stream,10,11,12 but can act as a polymodal “hub” region for additional crossmodal input following learning.” – pg. 19

(4) The most compelling evidence the authors provide for their theoretical claims is the finding that, in the perirhinal cortex, the unimodal feature representations on Day 2 do not correlate with the multimodal objects they comprise on Day 4. This suggests that the learned multimodal object representations are not combinations of their unimodal features. If unimodal features are not decodable within the congruent object representations, this would support the authors' explicit integrative hypothesis. However, the analyses provided do not go all the way in convincing the reader of this claim. First, the analyses reported do not differentiate between congruent and incongruent objects. If this result in the perirhinal cortex reflects the formation of new multimodal object representations, it should only be true for congruent objects but not incongruent objects. Since the analyses combine congruent and incongruent objects it is not possible to know whether this was the case. Second, just because feature representations on Day 2 do not correlate with multimodal object patterns on Day 4 does not mean that the object representations on Day 4 do not contain featural information. This could be directly tested by correlating feature representations on Day 4 with congruent vs. incongruent object representations on Day 4. It could be that representations in the perirhinal cortex are not stable over time and all representations-including unimodal feature representations-shift between sessions, which could explain these results yet not entail the existence of abstracted object representations.

We thank the reviewer for this suggestion and have conducted the two additional analyses. Specifically, we split the congruent and incongruent conditions and also investigated correlations between unimodal representations on Day 4 with crossmodal object representations on Day 4. There was no significant interaction between modality and congruency in any ROI across or within learning days. One possible explanation for these findings is that both congruent and incongruent crossmodal objects are represented differently from their underlying unimodal features, and all of these representations can transform with experience.

However, the new analyses also revealed that perirhinal cortex was the only region without a modality-specific bias after crossmodal learning (e.g., Day 4 Unimodal Feature runs x Day 4 Crossmodal Object runs; now shown in Supplemental Figure S5). Overall, these results are consistent with the notion of a crossmodal integrative code in perirhinal cortex that has changed with experience and is different from the component unimodal features. Nevertheless, we explore alternative interpretations for how the crossmodal code emerges with experience in the discussion.

“To examine whether these results differed by congruency (i.e., whether any modality-specific biases differed as a function of whether the object was congruent or incongruent), we conducted exploratory linear mixed models for each of the five a priori ROIs across learning days. More specifically, we correlated: 1) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs before crossmodal learning (Day 2 vs. Day 2), 2) the voxel-wise activity for Unimodal Feature Runs before crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 2 vs Day 4), and 3) the voxel-wise activity for Unimodal Feature Runs after crossmodal learning to the voxel-wise activity for Crossmodal Object Runs after crossmodal learning (Day 4 vs Day 4). For each of the three analyses described, we then conducted separate linear mixed models which included modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object) and congruency (congruent vs. incongruent)….There was no significant relationship between modality and congruency in any ROI between Day 2 and Day 2 (F1,346-368 between 0.00 and 1.06, p between 0.30 and 0.99), between Day 2 and Day 4 (F1,346-368 between 0.021 and 0.91, p between 0.34 and 0.89), or between Day 4 and Day 4 (F1,346-368 between 0.01 and 3.05, p between 0.082 and 0.93). However, exploratory analyses revealed that perirhinal cortex was the only region without a modality-specific bias and where the unimodal feature runs were not significantly correlated to the crossmodal object runs after crossmodal learning (Supplemental Figure S5).” – pg. 14

“Taken together, the overall pattern of results suggests that representations of the crossmodal objects in perirhinal cortex were heavily influenced by their consistent visual features before crossmodal learning. However, the crossmodal object representations were no longer influenced by the component visual features after crossmodal learning (Figure 5, Supplemental Figure S5). Additional exploratory analyses did not find evidence of experience-dependent changes in the hippocampus or inferior parietal lobes (Supplemental Figure S4c-e).” – pg. 14

“The voxel-wise matrix for Unimodal Feature runs on Day 4 were correlated to the voxel-wise matrix for Crossmodal Object runs on Day 4 (see Figure 5 in the main text for an example). We compared the average pattern similarity (z-transformed Pearson correlation) between shape (blue) and sound (orange) features specifically after crossmodal learning. Consistent with Figure 5b, perirhinal cortex was the only region without a modality-specific bias. Furthermore, perirhinal cortex was the only region where the representations of both the visual and sound features were not significantly correlated to the crossmodal objects. By contrast, every other region maintained a modality-specific bias for either the visual or sound features. These results suggest that perirhinal cortex representations were transformed with experience, such that the initial visual shape representations (Figure 5a) were no longer grounded in a single modality after crossmodal learning. Furthermore, these results suggest that crossmodal learning formed an integrative code different from the unimodal features in perirhinal cortex, as the visual and sound features were not significantly correlated with the crossmodal objects. * p < 0.05, ** p < 0.01, *** p < 0.001. Horizontal lines within brain regions indicate a significant main effect of modality. Vertical asterisks denote pattern similarity comparisons relative to 0.” – Supplemental Figure S5

“We found that the temporal pole and perirhinal cortex – two anterior temporal lobe structures – came to represent new crossmodal object concepts with learning, such that the acquired crossmodal object representations were different from the representation of the constituent unimodal features (Figure 5, 6). Intriguingly, the perirhinal cortex was by default biased towards visual shape, but that this initial visual bias was attenuated with experience (Figure 3c, 5, Supplemental Figure S5). Within the perirhinal cortex, the acquired crossmodal object concepts (measured after crossmodal learning) became less similar to their original component unimodal features (measured at baseline before crossmodal learning); Figure 5, 6, Supplemental Figure S5. This is consistent with the idea that object representations in perirhinal cortex integrate the component sensory features into a whole that is different from the sum of the component parts, which might be a mechanism by which object concepts obtain their abstraction…. As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation.” – pg. 18

In sum, the authors have collected a fantastic dataset that has the potential to answer questions about the formation of multimodal object representations in the brain. A more precise delineation of different theoretical accounts and additional analyses are needed to provide convincing support for the theory that “explicit integrative” multimodal object representations are formed during learning.

We thank the reviewer for the positive comments and helpful feedback. We hope that our changes to our wording and clarifications to our methodology now more clearly supports the central goal of our study: to find evidence of crossmodal integrative coding different from the original unimodal feature parts in anterior temporal lobe structures. We furthermore agree that future research is needed to delineate the structure of the integrative code that emerges with experience in the anterior temporal lobes.

Reviewer #3 (Public Review):

This paper uses behavior and functional brain imaging to understand how neural and cognitive representations of visual and auditory stimuli change as participants learn associations among them. Prior work suggests that areas in the anterior temporal (ATL) and perirhinal cortex play an important role in learning/representing cross-modal associations, but the hypothesis has not been directly tested by evaluating behavior and functional imaging before and after learning cross- modal associations. The results show that such learning changes both the perceived similarities amongst stimuli and the neural responses generated within ATL and perirhinal regions, providing novel support for the view that cross-modal learning leads to a representational change in these regions.

This work has several strengths. It tackles an important question for current theories of object representation in the mind and brain in a novel and quite direct fashion, by studying how these representations change with cross-modal learning. As the authors note, little work has directly assessed representational change in ATL following such learning, despite the widespread view that ATL is critical for such representation. Indeed, such direct assessment poses several methodological challenges, which the authors have met with an ingenious experimental design. The experiment allows the authors to maintain tight control over both the familiarity and the perceived similarities amongst the shapes and sounds that comprise their stimuli so that the observed changes across sessions must reflect learned cross-modal associations among these. I especially appreciated the creation of physical objects that participants can explore and the approach to learning in which shapes and sounds are initially experienced independently and later in an associated fashion. In using multi-echo MRI to resolve signals in ventral ATL, the authors have minimized a key challenge facing much work in this area (namely the poor SNR yielded by standard acquisition sequences in ventral ATL). The use of both univariate and multivariate techniques was well-motivated and helpful in testing the central questions. The manuscript is, for the most part, clearly written, and nicely connects the current work to important questions in two literatures, specifically (1) the hypothesized role of the perirhinal cortex in representing/learning complex conjunctions of features and (2) the tension between purely embodied approaches to semantic representation vs the view that ATL regions encode important amodal/crossmodal structure.

There are some places in the manuscript that would benefit from further explanation and methodological detail. I also had some questions about the results themselves and what they signify about the roles of ATL and the perirhinal cortex in object representation.

We thank the reviewer for their positive feedback and address the comments in the below point-by-point responses.

(A) I found the terms "features" and "objects" to be confusing as used throughout the manuscript, and sometimes inconsistent. I think by "features" the authors mean the shape and sound stimuli in their experiment. I think by "object" the authors usually mean the conjunction of a shape with a sound---for instance, when a shape and sound are simultaneously experienced in the scanner, or when the participant presses a button on the shape and hears the sound. The confusion comes partly because shapes are often described as being composed of features, not features in and of themselves. (The same is sometimes true of sounds). So when reading "features" I kept thinking the paper referred to the elements that went together to comprise a shape. It also comes from ambiguous use of the word object, which might refer to (a) the 3D- printed item that people play with, which is an object, or (b) a visually-presented shape (for instance, the localizer involved comparing an "object" to a "phase-scrambled" stimulus---here I assume "object" refers to an intact visual stimulus and not the joint presentation of visual and auditory items). I think the design, stimuli, and results would be easier for a naive reader to follow if the authors used the terms "unimodal representation" to refer to cases where only visual or auditory input is presented, and "cross-modal" or "conjoint" representation when both are present.

We thank the reviewer for this suggestion and agree. We have replaced the terms “features” and “objects” with “unimodal” and “crossmodal” in the title, text, and figures throughout the manuscript for consistency (i.e., “crossmodal binding problem”). To simplify the terminology, we have also removed the localizer results.

(B) There are a few places where I wasn't sure what exactly was done, and where the methods lacked sufficient detail for another scientist to replicate what was done. Specifically:

(1) The behavioral study assessing perceptual similarity between visual and auditory stimuli was unclear. The procedure, stimuli, number of trials, etc, should be explained in sufficient detail in methods to allow replication. The results of the study should also minimally be reported in the supplementary information. Without an understanding of how these studies were carried out, it was very difficult to understand the observed pattern of behavioral change. For instance, I initially thought separate behavioral blocks were carried out for visual versus auditory stimuli, each presented in isolation; however, the effects contrast congruent and incongruent stimuli, which suggests these decisions must have been made for the conjoint presentation of both modalities. I'm still not sure how this worked. Additionally, the manuscript makes a brief mention that similarity judgments were made in the context of "all stimuli," but I didn't understand what that meant. Similarity ratings are hugely sensitive to the contrast set with which items appear, so clarity on these points is pretty important. A strength of the design is the contention that shape and sound stimuli were psychophysically matched, so it is important to show the reader how this was done and what the results were.

We agree and apologize for the lack of sufficient detail in the original manuscript. We now include much more detail about the similarity rating task. The methodology and results of the behavioral rating experiments are now shown in Supplemental Figure S1. In Figure S1a, the similarity ratings are visualized on a multidimensional scaling plot. The triangular geometry for shape (blue) and sound (red) indicate that the subjective similarity was equated within each unimodal feature across individual participants. Quantitatively, there was no difference in similarity between the congruent and incongruent pairings in Figure S1b and Figure S1c prior to crossmodal learning. In addition to providing more information on these methods in the Supplemental Information, we also now provide a more detailed description of the task in the manuscript itself. For convenience, we reproduce these sections below.

“Pairwise Similarity Task. Using the same task as the stimulus validation procedure (Supplemental Figure S1a), participants provided similarity ratings for all combinations of the 3 validated shapes and 3 validated sounds (each of the six features were rated in the context of every other feature in the set, with 4 repeats of the same feature, for a total of 72 trials). More specifically, three stimuli were displayed on each trial, with one at the top and two at the bottom of the screen in the same procedure as we have used previously27. The 3D shapes were visually displayed as a photo, whereas sounds were displayed on screen in a box that could be played over headphones when clicked with the mouse. The participant made an initial judgment by selecting the more similar stimulus on the bottom relative to the stimulus on the top. Afterwards, the participant made a similarity rating between each bottom stimulus with the top stimulus from 0 being no similarity to 5 being identical. This procedure ensured that ratings were made relative to all other stimuli in the set.”– pg. 28

“Pairwise similarity task and results. In the initial stimulus validation experiment, participants provided pairwise ratings for 5 sounds and 3 shapes. The shapes were equated in their subjective similarity that had been selected from a well-characterized perceptually uniform stimulus space27 and the pairwise ratings followed the same procedure as described in ref 27. Based on this initial experiment, we then selected the 3 sounds from the that were most closely equated in their subjective similarity. (a) 3D-printed shapes were displayed as images, whereas sounds were displayed in a box that could be played when clicked by the participant. Ratings were averaged to produce a similarity matrix for each participant, and then averaged to produce a group-level similarity matrix. Shown as triangular representational geometries recovered from multidimensional scaling in the above, shapes (blue) and sounds (orange) were approximately equated in their subjective similarity. These features were then used in the four-day crossmodal learning task. (b) Behavioral results from the four-day crossmodal learning task paired with multi-echo fMRI described in the main text. Before crossmodal learning, there was no difference in similarity between shape and sound features associated with congruent objects compared to incongruent objects – indicating that similarity was controlled at the unimodal feature-level. After crossmodal learning, we observed a robust shift in the magnitude of similarity. The shape and sound features associated with congruent objects were now significantly more similar than the same shape and sound features associated with incongruent objects (p < 0.001), evidence that crossmodal learning changed how participants experienced the unimodal features (observed in 17/18 participants). (c) We replicated this learning-related shift in pattern similarity with a larger sample size (n = 44; observed in 38/44 participants). *** denotes p < 0.001. Horizontal lines denote the comparison of congruent vs. incongruent conditions. – Supplemental Figure S1

(2) The experiences through which participants learned/experienced the shapes and sounds were unclear. The methods mention that they had one minute to explore/palpate each shape and that these experiences were interleaved with other tasks, but it is not clear what the other tasks were, how many such exploration experiences occurred, or how long the total learning time was. The manuscript also mentions that participants learn the shape-sound associations with 100% accuracy but it isn't clear how that was assessed. These details are important partly b/c it seems like very minimal experience to change neural representations in the cortex.

We apologize for the lack of detail and agree with the reviewer’s suggestions – we now include much more information in the methods section. Each behavioral day required about 1 hour of total time to complete, and indeed, participants rapidly learned their associations with minimal experience. For example:

“Behavioral Tasks. On each behavioral day (Day 1 and Day 3; Figure 2), participants completed the following tasks, in this order: Exploration Phase, one Unimodal Feature 1-back run (26 trials), Exploration Phase, one Crossmodal 1-back run (26 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), Exploration Phase, Pairwise Similarity Task (24 trials), and finally, Exploration Phase. To verify learning on Day 3, participants also additionally completed a Learning Verification Task at the end of the session. – pg. 27

“The overall procedure ensured that participants extensively explored the unimodal features on Day 1 and the crossmodal objects on Day 3. The Unimodal Feature and the Crossmodal Object 1-back runs administered on Day 1 and Day 3 served as practice for the neuroimaging sessions on Day 2 and Day 4, during which these 1-back tasks were completed. Each behavioral session required less than 1 hour of total time to complete.” – pg. 27

“Learning Verification Task (Day 3 only). As the final task on Day 3, participants completed a task to ensure that participants successfully formed their crossmodal pairing. All three shapes and sounds were randomly displayed in 6 boxes on a display. Photos of the 3D shapes were shown, and sounds were played by clicking the box with the mouse cursor. The participant was cued with either a shape or sound, and then selected the corresponding paired feature. At the end of Day 3, we found that all participants reached 100% accuracy on this task (10 trials).” – pg. 29

(3) I didn't understand the similarity metric used in the multivariate imaging analyses. The manuscript mentions Z-scored Pearson's r, but I didn't know if this meant (a) many Pearson coefficients were computed and these were then Z-scored, so that 0 indicates a value equal to the mean Pearson correlation and 1 is equal to the standard deviation of the correlations, or (b) whether a Fisher Z transform was applied to each r (so that 0 means r was also around 0). From the interpretation of some results, I think the latter is the approach taken, but in general, it would be helpful to see, in Methods or Supplementary information, exactly how similarity scores were computed, and why that approach was adopted. This is particularly important since it is hard to understand the direction of some key effects.

The reviewer is correct that the Fisher Z transform was applied to each individual r before averaging the correlations. This approach is generally recommended when averaging correlations (see Corey, Dunlap, & Burke, 1998). We are now clearer on this point in the manuscript:

“The z-transformed Pearson’s correlation coefficient was used as the distance metric for all pattern similarity analyses. More specifically, each individual Pearson correlation was Fisher z-transformed and then averaged (see 61).” – pg. 32

(C) From Figure 3D, the temporal pole mask appears to exclude the anterior fusiform cortex (or the ventral surface of the ATL generally). If so, this is a shame, since that appears to be the locus most important to cross-modal integration in the "hub and spokes" model of semantic representation in the brain. The observation in the paper that the perirhinal cortex seems initially biased toward visual structure while more superior ATL is biased toward auditory structure appears generally consistent with the "graded hub" view expressed, for instance, in our group's 2017 review paper (Lambon Ralph et al., Nature Reviews Neuroscience). The balance of visual- versus auditory-sensitivity in that work appears balanced in the anterior fusiform, just a little lateral to the anterior perirhinal cortex. It would be helpful to know if the same pattern is observed for this area specifically in the current dataset.

We thank the reviewer for this suggestion. After close inspection of Lambon Ralph et al. (2017), we believe that our perirhinal cortex mask appears to be overlapping with the ventral ATL/anterior fusiform region that the reviewer mentions. See Author response image 1 for a visual comparison:

Author response image 1.

The top four figures are sampled from Lambon Ralph et al (2017), whereas the bottom two figures visualize our perirhinal cortex mask (white) and temporal pole mask (dark green) relative to the fusiform cortex. The ROIs visualized were defined from the Harvard-Oxford atlas.

We now mention this area of overlap in our manuscript and link it to the hub and spokes model:

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 – pg. 20

(D) While most effects seem robust from the information presented, I'm not so sure about the analysis of the perirhinal cortex shown in Figure 5. This compares (I think) the neural similarity evoked by a unimodal stimulus ("feature") to that evoked by the same stimulus when paired with its congruent stimulus in the other modality ("object"). These similarities show an interaction with modality prior to cross-modal association, but no interaction afterward, leading the authors to suggest that the perirhinal cortex has become less biased toward visual structure following learning. But the plots in Figures 4a and b are shown against different scales on the y-axes, obscuring the fact that all of the similarities are smaller in the after-learning comparison. Since the perirhinal interaction was already the smallest effect in the pre-learning analysis, it isn't really surprising that it drops below significance when all the effects diminish in the second comparison. A more rigorous test would assess the reliability of the interaction of comparison (pre- or post-learning) with modality. The possibility that perirhinal representations become less "visual" following cross-modal learning is potentially important so a post hoc contrast of that kind would be helpful.

We apologize for the lack of clarity. We conducted a linear mixed model to assess the interaction between modality and crossmodal learning day (before and after crossmodal learning) in the perirhinal cortex as described by the reviewer. The critical interaction was significant, which is now clarified in the text as well as in the rescaled figure plots.

“To investigate this effect in perirhinal cortex more specifically, we conducted a linear mixed model to directly compare the change in the visual bias of perirhinal representations from before crossmodal learning to after crossmodal learning (green regions in Figure 5a vs. 5b). Specifically, the linear mixed model included learning day (before vs. after crossmodal learning) and modality (visual feature match to crossmodal object vs. sound feature match to crossmodal object). Results revealed a significant interaction between learning day and modality in the perirhinal cortex (F1,775 = 5.56, p = 0.019, η2 = 0.071), meaning that the baseline visual shape bias observed in perirhinal cortex (green region of Figure 5a) was significantly attenuated with experience (green region of Figure 5b). After crossmodal learning, a given shape no longer invoked significant pattern similarity between objects that had the same shape but differed in terms of what they sounded like. Taken together, these results suggest that prior to learning the crossmodal objects, the perirhinal cortex had a default bias toward representing the visual shape information and was not representing sound information of the crossmodal objects. After crossmodal learning, however, the visual shape bias in perirhinal cortex was no longer present. That is, with crossmodal learning, the representations within perirhinal cortex started to look less like the visual features that comprised the crossmodal objects, providing evidence that the perirhinal representations were no longer predominantly grounded in the visual modality.” – pg. 13

We note that not all effects drop in Figure 5b (even in regions with a similar numerical pattern similarity to PRC, like the hippocampus – also see Supplemental Figure S5 for a comparison for patterns only on Day 4), suggesting that the change in visual bias in PRC is not simply due to noise.

“Importantly, the change in pattern similarity in the perirhinal cortex across learning days (Figure 5) is unlikely to be driven by noise, poor alignment of patterns across sessions, or generally reduced responses. Other regions with numerically similar pattern similarity to perirhinal cortex did not change across learning days (e.g., visual features x crossmodal objects in A1 in Figure 5; the exploratory ROI hippocampus with numerically similar pattern similarity to perirhinal cortex also did not change in Supplemental Figure S4c-d).” – pg. 14

(E) Is there a reason the authors did not look at representation and change in the hippocampus? As a rapid-learning, widely-connected feature-binding mechanism, and given the fairly minimal amount of learning experience, it seems like the hippocampus would be a key area of potential import for the cross-modal association. It also looks as though the hippocampus is implicated in the localizer scan (Figure 3c).

We thank the reviewer for this suggestion and now include additional analyses for the hippocampus. We found no evidence of crossmodal integrative coding different from the unimodal features. Rather, the hippocampus seems to represent the convergence of unimodal features, as evidenced by …[can you give some pithy description for what is meant by “convergence” vs “integration”?]. We provide these results in the Supplemental Information and describe them in the main text:

“Analyses for the hippocampus (HPC) and inferior parietal lobe (IPL). (a) In the visual vs. auditory univariate analysis, there was no visual or sound bias in HPC, but there was a bias towards sounds that increased numerically after crossmodal learning in the IPL. (b) Pattern similarity analyses between unimodal features associated with congruent objects and incongruent objects. Similar to Supplemental Figure S3, there was no main effect of congruency in either region. (c) When we looked at the pattern similarity between Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 2, we found that there was significant pattern similarity when there was a match between the unimodal feature and the crossmodal object (e.g., pattern similarity > 0). This pattern of results held when (d) correlating the Unimodal Feature runs on Day 2 to Crossmodal Object runs on Day 4, and (e) correlating the Unimodal Feature runs on Day 4 to Crossmodal Object runs on Day 4. Finally, (f) there was no significant pattern similarity between Crossmodal Object runs before learning correlated to Crossmodal Object after learning in HPC, but there was significant pattern similarity in IPL (p < 0.001). Taken together, these results suggest that both HPC and IPL are sensitive to visual and sound content, as the (c, d, e) unimodal feature-level representations were correlated to the crossmodal object representations irrespective of learning day. However, there was no difference between congruent and incongruent pairings in any analysis, suggesting that HPC and IPL did not represent crossmodal objects differently from the component unimodal features. For these reasons, HPC and IPL may represent the convergence of unimodal feature representations (i.e., because HPC and IPL were sensitive to both visual and sound features), but our results do not seem to support these regions in forming crossmodal integrative coding distinct from the unimodal features (i.e., because representations in HPC and IPL did not differentiate the congruent and incongruent conditions and did not change with experience). * p < 0.05, ** p < 0.01, *** p < 0.001. Asterisks above or below bars indicate a significant difference from zero. Horizontal lines within brain regions in (a) reflect an interaction between modality and learning day, whereas horizontal lines within brain regions in reflect main effects of (b) learning day, (c-e) modality, or (f) congruency.” – Supplemental Figure S4.

“Notably, our perirhinal cortex mask overlaps with a key region of the ventral anterior temporal lobe thought to be the central locus of crossmodal integration in the “hub and spokes” model of semantic representations.9,50 However, additional work has also linked other brain regions to the convergence of unimodal representations, such as the hippocampus51,52,53 and inferior parietal lobes.54,55 This past work on the hippocampus and inferior parietal lobe does not necessarily address the crossmodal binding problem that was the main focus of our present study, as previous findings often do not differentiate between crossmodal integrative coding and the convergence of unimodal feature representations per se. Furthermore, previous studies in the literature typically do not control for stimulus-based factors such as experience with unimodal features, subjective similarity, or feature identity that may complicate the interpretation of results when determining regions important for crossmodal integration. Indeed, we found evidence consistent with the convergence of unimodal feature-based representations in both the hippocampus and inferior parietal lobes (Supplemental Figure S4), but no evidence of crossmodal integrative coding different from the unimodal features. The hippocampus and inferior parietal lobes were both sensitive to visual and sound features before and after crossmodal learning (see Supplemental Figure S4c-e). Yet the hippocampus and inferior parietal lobes did not differentiate between the congruent and incongruent conditions or change with experience (see Supplemental Figure S4).” – pg. 20

(F) The direction of the neural effects was difficult to track and understand. I think the key observation is that TP and PRh both show changes related to cross-modal congruency - but still it would be helpful if the authors could articulate, perhaps via a schematic illustration, how they think representations in each key area are changing with the cross-modal association. Why does the temporal pole come to activate less for congruent than incongruent stimuli (Figure 3)? And why do TP responses grow less similar to one another for congruent relative to incongruent stimuli after learning (Figure 4)? Why are incongruent stimulus similarities anticorrelated in their perirhinal responses following cross-modal learning (Figure 6)?

We thank the author for identifying this issue, which was also raised by the other reviewers. The reviewer is correct that the key observation is that the TP and PRC both show changes related to crossmodal congruency (given that the unimodal features were equated in the methodological design). However, the structure of the integrative code is less clear, which we now emphasize in the main text. Our findings provide evidence of a crossmodal integrative code that is different from the unimodal features, and future studies are needed to better understand the structure of how such a code might emerge. We now more clearly highlight this distinction throughout the paper:

“By contrast, perirhinal cortex may be involved in pattern separation following crossmodal experience. In our task, participants had to differentiate congruent and incongruent objects constructed from the same three shape and sound features (Figure 2). An efficient way to solve this task would be to form distinct object-level outputs from the overlapping unimodal feature-level inputs such that congruent objects are made to be orthogonal from the representations before learning (i.e., measured as pattern similarity equal to 0 in the perirhinal cortex; Figure 5b, 6, Supplemental Figure S5), whereas non-learned incongruent objects could be made to be dissimilar from the representations before learning (i.e., anticorrelation, measured as patten similarity less than 0 in the perirhinal cortex; Figure 6). Because our paradigm could decouple neural responses to the learned object representations (on Day 4) from the original component unimodal features at baseline (on Day 2), these results could be taken as evidence of pattern separation in the human perirhinal cortex.11,12 However, our pattern of results could also be explained by other types of crossmodal integrative coding. For example, incongruent object representations may be less stable than congruent object representations, such that incongruent objects representation are warped to a greater extent than congruent objects (Figure 6).” – pg. 18

“As one solution to the crossmodal binding problem, we suggest that the temporal pole and perirhinal cortex form unique crossmodal object representations that are different from the distributed features in sensory cortex (Figure 4, 5, 6, Supplemental Figure S5). However, the nature by which the integrative code is structured and formed in the temporal pole and perirhinal cortex following crossmodal experience – such as through transformations, warping, or other factors – is an open question and an important area for future investigation. Furthermore, these anterior temporal lobe structures may be involved with integrative coding in different ways. For example, the crossmodal object representations measured after learning were found to be related to the component unimodal feature representations measured before learning in the temporal pole but not the perirhinal cortex (Figure 5, 6, Supplemental Figure S5). Moreover, pattern similarity for congruent shape-sound pairs were lower than the pattern similarity for incongruent shape-sound pairs after crossmodal learning in the temporal pole but not the perirhinal cortex (Figure 4b, Supplemental Figure S3a). As one interpretation of this pattern of results, the temporal pole may represent new crossmodal objects by combining previously learned knowledge. 8,9,10,11,13,14,15,33 Specifically, research into conceptual combination has linked the anterior temporal lobes to compound object concepts such as “hummingbird”.34,35,36 For example, participants during our task may have represented the sound-based “humming” concept and visually-based “bird” concept on Day 1, forming the crossmodal “hummingbird” concept on Day 3; Figure 1, 2, which may recruit less activity in temporal pole than an incongruent pairing such as “barking-frog”. For these reasons, the temporal pole may form a crossmodal object code based on pre-existing knowledge, resulting in reduced neural activity (Figure 3d) and pattern similarity towards features associated with learned objects (Figure 4b).” – pg. 18

This work represents a key step in our advancing understanding of object representations in the brain. The experimental design provides a useful template for studying neural change related to the cross-modal association that may prove useful to others in the field. Given the broad variety of open questions and potential alternative analyses, an open dataset from this study would also likely be a considerable contribution to the field.

Author Response

Reviewer #3 (Public Review):

Gavanetto et al. propose an interesting method to identify membrane proteins based on the analysis of single-molecule AFM (smAFM) force-extension traces obtained from native plasma membranes. In the proposed pipeline, the authors use smAFM to non-specifically probe isolated plasma membranes by recording a large number (millions) of force-extension traces. While, as expected, most of them lack any binding or represent spurious events, the authors use an unsupervised clustering algorithm to identify groups of force-extension curves with a similar mechanical pattern, suggesting that each cluster corresponds to a unique protein species that can be fingerprinted by its specific force-extension pattern. By implementing a Bayesian framework, the authors contrast the identified groups with proteomics databases, which provide the most likely proteins that correspond to the identified force-extension clusters. A set of control experiments complements the manuscript to validate the proposed methodology, such as the application of their pipeline using purified samples or overexpressing a specific protein species to enrich its population.

The primary strength of the manuscript is its originality, as it proposes a novel application of smAFM as a protein-detection method that can be applied in native samples. This methodology combines ingredients from conventional mass spectrometry and cryoEM; the contour length released upon extending a protein is a direct measure of its sequence extension (related to its mass), but the force pattern contains insightful information about the protein's structure. In this sense, the authors' proposal is very smart. However, the relationship between protein structure and mechanics is far from straightforward, and here perhaps lies one of the main limitations of the proposed method. This is particularly true for the case of membrane proteins, where we cannot talk about protein unfolding in its classical sense but rather about pullout events which is likely what each peak corresponds to (indeed, the authors speak throughout the paper about unfolding events, which I believe is not the correct term).

We fully agree with the semantics concern of reviewer #3 about the term unfolding. A membrane protein when pulled with the tip of the AFM is pulled out of the membrane (see 2 in the image below) and, simultaneously, the segment that is pulled out unfolds (see 3). To our knowledge, force peaks corresponding to a contour length equal to 2 where not consistently observed or reported (when e.g. a transmembrane alpha helix is out of the membrane but folded).

Since the field evolved with the practice of using the term ‘unfolding’ even for membrane proteins (see for instance (Kessler and Gaub, 2006; Oesterhelt et al., 2000; Yu et al., 2017) and many others), we would prefer to stick with this term.

In the context of membrane proteins the term unfolding therefore refers to at least the tertiary structure of the protein, because it is not clear when and at which timescale the secondary structures really unfolds.

We pointed this out in Line 131 (and following Lines).

Author Response

Reviewer #1 (Public Review):

This is a well performed study to demonstrate the antiviral function and viral antagonism of the dynein activating adapter NINL. The results are clearly presented to support the conclusions.

This reviewer has only one minor suggestion to improve the manuscript.

Add a discussion (1) why the folds of reduction among VSV, SinV and CVB3 were different in the NINL KO cells and (2) why the folds of reduction of VSV in the NINL KO A549 and U-2 OS cells.

Thank you for this suggestion. We have amended the results section to include additional information about these observations and possible explanations for these results.

Reviewer #2 (Public Review):

This manuscript is of interest to readers for host-viral co-evolution. This study has identified a novel human-virus interaction point NINL-viral 3C protease, where NINL is actively evolving upon the selection pressure against viral infect and viral 3Cpro cleavage. This study demonstrates that the viral 3Cpros-mediated cleavage of host NINL disrupts its adaptor function in dynein motor-mediated cargo transportation to the centrosome, and this disruption is both host- and virus-specific. In addition, this paper indicates the role of NINL in the IFN signaling pathway. Data shown in this manuscript support the major claims.

In this paper, the authors have identified a novel host-viral interaction, where viral 3C proteases (3Cpro) cleave at specific sites on a host activating adaptor of dynein intracellular transportation machinery, ninein-like protein (NINL or NLP in short) and inhibit its role in the antiviral innate immune response.

The authors firstly found that, unlike other activating adaptors of dynein intracellular transportation machinery, NINL (or NLP) is rapidly evolving. Thus, the authors hypothesized that this rapid evolution of NINL was caused by its interaction with viral infection. The authors found that viruses replicated higher in NINL knock-out (KO) cells than in wild-type (WT) cells and the replication level was not attenuated upon IFNa treatment in NINL KO cells, unlike in WT cells. Next, the authors investigated the role of NINL in type I IFN-mediated immune response and found that the induction of Janus kinase/signal transducer and activation of transcription (JAK/STAT) genes were attenuated in NINL KO cells upon IFNa treatment. The author further showed that the reduction of replication IFNa sensitive Vaccinia virus mutant upon IFNa treatment was decreased in NINL KO A549 cells compared to WT cells. The authors further showed that the virus antagonized NINL function by cleaving it with viral 3Cpro at its specific cleavage sites. NINL-peroxisome ligation-based cargo trafficking visualization assay showed that the redistribution of immobile membrane-bound peroxisome was disrupted by cleavage of NINL or viral infection.

This paper has revealed a novel host-virus interaction, and an antiviral function of a rapidly evolving activating adaptor of dynein intracellular transportation machinery, NINL. The major conclusions of this paper are well supported by data, but several aspects can be improved.

1) It would be necessary to include a couple of other pathways involved in innate immune response besides JAK/STAT pathway.

We are very interested in this question as well. Our RNAseq data (Supplementary file 4 and Figure 3 – Figure supplement 4) suggest that there are several transcriptional changes that result from NINL KO. Our goal in this manuscript was to focus on IFN signaling in order to understand this specific effect of NINL KO since it might have wide-ranging consequences on viral replication. While we agree that broadening our studies to other signaling pathways, including other pathways involved in innate immune response, is a good idea, we feel that those experiments would take longer than two months to perform and therefore fall outside of the scope of this paper.

2) The in-cell cleavages of NINL by viral 3Cpros were well demonstrated and supported by data of high quality. A direct biochemical demonstration of the cleavage is needed with purified proteins.

We agree with the reviewer that a direct biochemical cleavage assay would further demonstrate that viral 3Cpros cleave NINL specifically. However, our attempts to purify full-length NINL have been unsuccessful due to solubility issues (see example gel below), which is not surprising given that NINL is a >150 kDa human protein that has multiple surfaces that bind to other human proteins. As such, we focused our efforts on in-cell cleavage assays using specificity controls for cleavage. Specifically, we used catalytically inactive CVB3 3Cpro to show a dependence on protease catalytic activity and a variety of NINL constructs in which the glutamine in the P1 position is replaced by an arginine to show site specificity of cleavage. Notably, the cleavage sites in NINL that we mapped using this mutagenesis were predicted bioinformatically from known sites of 3Cpro cleavage in viral polyproteins, further indicating that cleavage is 3Cpro-dependent. We believe these results thus demonstrate that cleavage of NINL is dependent on viral protease activity and occurs in a sequence-specific manner. In light of the difficulty of purifying full-length NINL that would make biochemical experiments very challenging and likely take longer than two months to perform, we believe that our in cell data should be sufficient to demonstrate activity-dependent site-specific cleavage of NINL by viral 3Cpros.

Sypro stained SDS-PAGE gel showing supernatant (S) and insoluble pellet (P) fractions across multiple purifications with altered buffer conditions.

3) The author used different cell types in different assays. Explain the rationale with a sentence for each assay.

Throughout this work, we choose to use a variety of cell lines for specific purposes. A549 cells were chosen as our main cell line as they are widely used in virology, are susceptible to the viruses we used, are responsive to interferon, and express both NINL and our control NIN at moderate levels. In the case of our virology and ISG expression data, we performed the same experiments with NINL KOs in other cell lines confirm that the phenotypes we observed in A549 cells could be attributed to the absence of NINL rather than off-target CRISPR perturbations or cell-line specific effects. All cleavage experiments were performed in HEK293T for their ease of transfection and protein expression. The inducible peroxisome trafficking assays were performed in U-2 OS cells as their morphology is ideal for observing the spatial organization of peroxisomes via confocal microscopy, and based on the fact that we had recapitulated the virology results and ISG expression results in those cells. At the suggestion of the reviewer, we have amended the text to include rationales where appropriate.

4) While cell-based assays well support the conclusions in this paper, further demonstration in vivo would be helpful to provide an implication on the pathogenicity impact of NINL.

We agree. However, we believe that examining the impact of the loss of or antagonism of NINL on the pathogenesis of infectious diseases in an in vivo model is outside the scope of this study.

In summary, this manuscript contributes to a novel antiviral target. In addition, it is important to understand the host-virus co-evolution. The use of the evolution signatures to identify the "conflict point" between host and virus is novel.

Author Response

Reviewer #1 (Public Review):

Cui and colleagues have performed a longitudinal analysis of blood cell counts in a cohort of ALS patients. The major findings include increases in neutrophils and monocytes that negatively correlated with ALSFRS-R score, but not disease progression rate. Increases in NK and central memory TH2 T cells correlated with a lower risk of death, while increased CD4 CD45RA effector memory and CD8 T cells were correlated with a higher risk of death.

Strengths of the study include the sample size and effort to broadly include data.

Thank you for the positive comment.

Limitations of the study include indication bias, as the authors acknowledge, because the timing of the blood draws is not predefined. The specific review for possibility of infection does not, in this reviewer's opinion, sufficiently address this potential for bias. Also concerning is the fact that half the subjects have only a single measurement, and how well the findings generalize to more or late measurements is not clear. Similarly, the number of later measurements driving some of the main findings is much lower, further raising concern about the potential bias. Given these issues, one really would want to see disease controls, and how the different cell counts change in another disease. Finally, there is not discussion about how or whether treatments, or changes in treatment, could influence observed counts.

We agree with the reviewer regarding indication bias and that is precisely why we performed the sensitivity analyses including 1) restricting the analysis to the first cell measure of each patient and 2) excluding cell measures with signs of ongoing infection at the time of blood draw. Reassuringly, both analyses provided rather similar results as those of the main analysis. We also agree with the reviewer regarding the varying numbers of measurements between patients. This is an unavoidable challenge to any longitudinal study of ALS patients, primarily due to the high mortality rate of this patient group. We have now added this limitation to the discussion:

“First, the main cohort was heterogeneous in terms of the numbers of cell measurements and the time intervals between measurements, as the timing of blood sampling was not predefined. Indication bias due to, for example, ongoing infections might therefore be a concern. The sensitivity analysis excluding all samples taken at the time of infections provided however rather similar results. Further, the longitudinal analysis of cell counts should be interpreted with caution because not all patients contributed repeated cell measurements. This is however an unavoidable problem for any longitudinal study of ALS patients, given the high mortality rate of this patient group. Regardless, when focusing on the first cell measures, we obtained similar results as in the main analysis.”

We further agree with the reviewer regarding the use of disease control. We have access to a cohort of patients with relapsing-remitting MS (RRMS) treated by rituximab (n=34), who had been measured with all the studied cell populations at the start of treatment and the 6-month follow-up. These cell measurements were processed during the same time-period using the identical setup at Karolinska University Hospital as the ones studied in the present study. In brief, we found different longitudinal changes of the studied immune cell populations between RRMS patients and ALS patients (please see below figure for details). The declining B cells are most likely due to rituximab treatment.

Given the largely different disease mechanisms, phenotypes, and treatments between RRMS and ALS, we are not confident that RRMS would be a good disease control for the present study. We are certainly willing to reconsider our position if the reviewer and editors would disagree with us. We have regardless now added discussion about this in the manuscript:

“It would therefore be interesting to compare ALS with other diseases, especially other neurodegenerative diseases, regarding the studied cell counts, in terms of both their longitudinal trajectories during disease course and their prognostic values in predicting patient outcome.”

Finally, we agree that it is interesting to consider treatment in the analysis of cell counts. Among the ALS patients of the main cohort, majority (89.6%) were treated with Riluzole. We have now added a supplementary figure to demonstrate the leukocyte counts before and after start of Riluzole treatment. The corresponding analysis is however not possible for the FlowC cohort as majority of the patients started Riluzole treatment around time of diagnosis and almost all measurements were taken after Riluzole treatment. Th17 of CD4+ CM cells CD4+ EMRA cells CD8+ T cells Naïve CD8+ T cells CD8+ EM cells CD8+ CM cells CD8+ EMRA cells CD4+ HLA-DR+ CD38- cells CD4+ HLA-DR+ CD38+ cells CD8+ HLA-DR+ CD38- cells CD8+ HLA-DR+ CD38+ cells.

We have now added this analysis to Methods and Results, including a new Figure 1—figure supplement 2.

“To evaluate whether ALS treatment would influence the cell counts, we further visualized the temporal patterns of differential leukocyte counts before and after Riluzole treatment.”

“The levels of leukocytes, neutrophils and monocytes increased, whereas the levels of lymphocytes decreased, after Riluzole treatment, compared with before such treatment (Figure 1—figure supplement 2).”

Reviewer #2 (Public Review):

Cui et al. investigated the correlation of immune profiles in ALS patients to functional status (by ALSFRS-R score), disease progression (rate of ALSFRS-R decline) and/or risk of death (or invasive ventilation use). The study longitudinally assessed basic immune profiles from a large cohort of ALS patients (n=288). Additionally, they deeply immunophenotyped a subset of ALS patients (n=92) to examine immune cell subtypes on ALS status, progression rate, and survival. The longitudinal design, deep immunophenotyping, and large cohort are significant strengths. Using various statistical models, the authors found leukocyte, neutrophil, and monocyte counts increased gradually over time as ALSFRS-R score declined. Within lymphocyte subpopulations, increasing natural killer cells and Th2-diffrentiated CD4+ central memory T cell counts correlated with a lower risk of death. Increasing CD4+ effector memory cells re-expressing CD45RA T cell and CD8+ T cell levels associated with a higher risk of death. These findings have broad implications for ALS pathogenesis and the development of immune-based ALS therapies tailored to specific immune cell populations.

Thank you for the very positive comments.

Author Response:

Reviewer #1:

In this manuscript Hill et al, analyze immune responses to vaccination of adults with the seasonal influenza vaccine. They perform a detailed analysis of the hemagglutinin-specific binding antibody responses against several different strains of influenza, and antigen-specific CD4+ T cells/T follicular cells, and cytokines in the plasma. Their analysis reveals that: (i) tetramer positive, HA-specific T follicular cells induced 7 days post vaccination correlate with the binding Ab response measured 42 days later; (ii) the HA-specific T fh have a diverse TCR repertoire; (iii) Impaired differentiation of HA-specific T fh in the elderly; and (iv) identification of an "inflammatory" gene signature within T fh in the elderly, which is associated with the impaired development of HA-specific Tfh.

The paper addresses a topic of considerable interest in the fields of human immunology and vaccinology. In general the experiments appear well performed, and support the conclusions. However, the following points should be addressed to enhance the clarity of the paper, and add support to the key conclusions drawn.

We thank the reviewer for their supportive evaluation of the manuscript, and have provided the details of how we have addressed each the points raised below.

1) Abstract: "(cTfh) cells are the best predictor of high titre antibody responses.." Since the authors have not done any blind prediction using machine learning tools with independent cohort, the sentence should be rephrased thus: "cTfh) cells are were associated with high titre antibody responses."

We agree that this phrasing better reflects the presented data. The sentence in the abstract (page 2) now reads “we show that formation of circulating T follicular helper (cTfh) cells was associated with high titre antibody responses.”

2) Figure 1A: Please indicate the age range of the subjects.

Figure 1 has been updated to include the age range of the subjects.

3) Almost all the data in the paper shows binding Ab titers. Yet, typically HAI titers of MN titers are used to assess Ab responses to influenza. Fig 1C shows HAI titers against the H1N1 Cal 09 strain. Can the authors show HAI titers for Cal 09 and the other A and B strains contained in the 2 vaccine cohorts? Do such HAI titers correlate with the tetramer positive cells, similar to the correlations show in Fig 2e.

In this manuscript we have deliberately focussed on the immune response to the H1N1 Cal09 strain, as it is the only influenza strain in the vaccine common to both cohorts. The HAI titre for this strain is now shown as supplementary figure 4. In addition, the class II tetramers were specifically selected to recognise unique epitopes in the Cal 09 strain (J. Yang, {..} W. W. Kwok, CD4+ T cells recognize unique and conserved 2009 H1N1 influenza hemagglutinin epitopes after natural infection and vaccination. Int Immunol 25, 447-457, 2013) because of this we do not think it is appropriate to correlate HAI titres for the non-Cal 09 strains with tetramer positive cells. We agree that showing the correlation of cTfh and other immune parameters with the HAI titres for Cal 09 is important and have included this as supplementary figure 7. The new data and text are presented below:

Figure 1-figure supplement 4: HAI responses before and after vaccination A) Log2 HAI titres at baseline (d0), d7 and d42 for cohort 1 (n=16) and B) cohort 2 (n = 21). C) Correlation between HAI and A.Cali09 IgG as measured by Luminex assay for cohort 1 and 2 combined. p-values determined using paired Wilcoxon signed rank-test, and Pearson’s correlation.

Text changes. Page 4. “The increase in anti-HA antibody titre was coupled with an increase in hemagglutination inhibitory antibodies to A.Cali09, the one influenza A strain contained in the TIVs that was shared across the two cohorts and showed a positive correlation with the A.Cali09 IgG titres measured by Luminex assay (Fig. 1C, Figure 1-figure supplement 4).”

Figure 2-figure supplement 1: Correlations between HAI assay titres and selected immune parameters. Correlation between vaccine-induced A.Cali09 HAI titres at d42 with selected immune parameters in both Cohort 1 and Cohort 2 (n=37). Dot color corresponds to the cohort (black = Cohort 1, grey = Cohort 2). Coefficient (Rho) and p-value determined using Spearman’s correlation, and line represents linear regression fit.

Results text Changes: Page 5. “Similar trends were seen when these immune parameters were correlated to HAI titres against A/Cali09 (Fig Figure 2-figure supplement 1).”

4) Fig 2d to i: what % of all bulk activated Tfh at day 7 are tetramer positive? The tetramer positive T cells constitute roughly 0.094% of all CD4 T cells (Fig 2d), of which 1/3rd are CXCR5+, PD1+ (i.e. ~0.03% of CD4 T cells). What fraction of all activated Tfh is this subset of tetramer positive cells? Presumably, there will also be Tfh generated against other viral proteins in the vaccine, and these will constitute a significant fraction of all activated Tfh.

This is an important point, as the tetramers only recognise one peptide epitope of the Cal.09 HA protein, so there will be many other influenza reactive CD4+ T cells that are responding to other Cal 09 epitopes as well as other proteins in the vaccine. The analysis suggested by the reviewer shows that the frequency of Tet+ cells amongst bulk cTfh cells ranges from 0.14%-1.52% in cohort 1, and from 0.022-2.7% in cohort 2. These data have been included as Figure Figure 1-figure supplement 6C, D in the revised manuscript. In addition, Tet+ cells as a percentage of bulk cTfh cells were reduced in older people compared to younger adults. This data has been included in Figure 5-figure supplement 1C in the revised manuscript.

Figure 1-figure supplement 6: Percentage of cTfh cells that are Tet+ and CXCR3 and CCR6 expression on HA-specific CD4+ T cells. A) Representative flow cytometry gating strategy for CXCR5+PD-1+ cTfh cells on CD4+CD45RA- T cells, and the proportion of HA-specific Tet+ cells within the CXCR5+PD-1+ cTfh cell gate. B) Percentage Tet+ cells within the CXCR5+PD-1+ cTfh cell population. Within-cohort age group differences were determined using the Mann-Whitney U test.

Results text, page 4: These antigen-specific T cells had upregulated ICOS after immunisation, indicating that they have been activated by vaccination (Fig. 1F, G). In addition, a median of one third of HA-specific T cells upregulated the Tfh markers CXCR5 and PD1 on d7 after immunisation (Fig. 1H, I). The tetramer binding cells represented between 0.022-2.7% of the total CXCR5+PD-1+ bulk population (Fig Figure 1-figure supplement 6A, B).

Figure 5-figure supplement 1C: Age-related differences in cytokines and HA-specific CD4+ T cell parameters. C) Percentage Tet+ cells within the CXCR5+PD-1+ cTfh cell population. Within-cohort age group differences were determined using the Mann-Whitney U test.

Results text, page 8: Across both cohorts, the only CD4+ T cell parameters consistently reduced in older individuals at d7 were the frequency of polyclonal cTfh cells and HA-specific Tet+ cTfh cells, with the strongest effect within the antigen-specific cTfh cell compartment (Fig. 5H-J, Figure 5-figure supplement 1C).

Reviewer #2:

Hill and colleagues present a comprehensive dataset describing the recall and expansion of HA-specific cTFH cells following influenza immunisation in two cohorts. Using class II tetramers, IgG titres against a large panel of HA antigens, and quantification of plasma cytokines, they find that activated and HA-specific cTFH cells were a strong predictor of the IgG response against the vaccine after 6 weeks. Using RNAseq and TCR clonotype analysis, they find that, in 10/15 individuals, the HA-specific cTFH response at day 7 post-vaccination is recalled from the available CD4 T cell memory pool present prior to vaccination. Post-vaccination HA-specific cTFH cells exhibited a transcriptional profile consistent with lymph node-derived GC TFH, as well as evidence of downregulation of IL-2 signaling pathways relative to pre-vaccine CD4 memory cells.

The authors then apply these findings to a comparison of vaccine immunogenicity between younger (18-36) and older (>65) adults. As expected, they found lower levels of vaccine-specific IgG responses among the older cohort. Analysis of HA-specific T cell responses indicated that tet+ cTFH fail to properly develop in the older cohort following vaccination. Further analysis suggests that development of HA-specific cTFH in older individuals is not caused by a lack of TCR diversity, but is associated with higher expression of inflammation-associated transcripts in tet+ cTFH.

Overall this is an impressive study that provides clarity around the recall of HA-specific CD4 T cell memory, and the burst of HA-specific cTFH cells observed 7 days post-vaccination. The association between defective cTFH recall and lower IgG titres post-vaccination in older individuals provides new targets for improving influenza vaccine efficacy in this age group. However, as currently presented, the model of impaired cTFH differentiation in the older cohort and the link to inflammation is somewhat unclear. There are several issues that could be clarified to improve the manuscript in its current form:

We thank the reviewer for their supportive and comprehensive summary of our work. We agree that the link between impaired inflammation and cTfh differentiation is correlative, we have added new data to address this, including mechanistic data to support chronic IL-2 signalling as antagonistic to cTfh development, as well as providing new analyses to address the other points raised.

1) It is somewhat unclear the extent to which the reduction in HA-specific cTFH in the older cohort is also related to an overall reduction in T cell expansion - cohort 1 shows a significant reduction in total tet+ CD4 T cells post-vaccination as well as in the cTFH compartment, and while this difference may not reach statistical significance, a similar trend is shown for cohort 2.

We agree that a possible interpretation is a global failure in T cell expansion in the older individuals. To determine whether there is a relationship between the degree of Tet+ CD4+ T cell expansion and cTfh cell differentiation with age, we performed correlation analyses. There is no correlation between the expansion of Tet+ cells and the frequency of cTfh cells formed seven days after immunisation in either age group. This suggests that the impaired cTfh cell differentiation in older persons is most likely caused by factors other than the capacity of CD4+ T cells to expand after vaccination. These data have been added as Figure 5-figure supplement 1D, and included in the results text on page 8.

Figure 5-figure supplement 1D: Age-related differences in cytokines and HA-specific CD4+ T cell parameters. D) Correlation between Tet+ cells (d7-d0, % of CD4+) and cTfh (d7-d0, % of TET+) in both cohorts for each age-group (18- 36 y.o n=37, 65+ y.o. n= 39). Dot color corresponds to the cohort (black = Cohort 1, grey = Cohort 2). Coefficient (Rho) and p-value determined using Spearman’s correlation, and line represents linear regression fit.

Text changes, Page 8: There was no consistent difference in the total d7 Tet+ HA-specific T cell population with age for both cohorts (Fig. 5H) and we observed no age-related correlation between the ability of an individual to differentiate Tet+ cells into a cTfh cell and the overall expansion of Tet+ HA-specific T cell population (Figure 5-figure supplement 1D). Thus, our data suggests that the poor vaccine antibody responses in older individuals is impacted by impaired cTfh cell differentiation (Fig. 5J) rather than size of the vaccine-specific CD4+ T cell pool.

2) Transcriptomic analysis indicates that HA-specific cTFH in the older cohort show impaired downregulation of inflammation, TNF and IL-2-related signaling pathways. The authors therefore conclude that excess inflammation can limit the response to vaccination. In its current presentation, the data does not necessarily support this conclusion. While it is clear that downregulation of TNF and IL-2 signalling pathways occur during cTFH/TFH differentiation, there is no evidence presented to support the idea that (a) vaccination results in increased pro-inflammatory cytokine production in lymphoid organs in older individuals or that (b) these pro-inflammatory cytokines actively promote CXCR5-, rather than cTFH, differentiation of existing memory T cells.

We agree with the reviewer that the data presented in figure 7 are correlative, rather than causative. Unfortunately, we do not have access to secondary lymphoid tissues from younger and older people after vaccination to test point (a) above. In order to test the hypothesis that increased inflammatory cytokine production in lymphoid organs limits Tfh cell differentiation we have used Il2cre/+; Rosa26stop-flox-Il2/+ transgenic mice. In this mouse model, IL-2-dependent cre- recombinase activity facilitates the expression of low levels of IL-2 in cells that have previously expressed IL-2. This creates a scenario in which cells that physiologically express IL-2 cannot turn its expression off therefore increasing expression IL-2 after antigenic stimulation (mice reported in Whyte et al., bioRxiv, 2020, doi: https://doi.org/10.1101/2020.12.18.423431).

Twelve days after influenza A infection, Il2cre/+; Rosa26stop-flox-Il2/+ transgenic mice have fewer Tfh cells in the draining mediastinal lymph node and in the spleen (Fig. 8A-C), this is accompanied by a reduction in the magnitude of the GC B cell response (Fig. 8D-E). These data provide a proof of concept that sustained IL-2 production limit the formation of Tfh cells, consistent with the negative correlation of an IL-2 signalling gene signature and cTfh cell formation in humans (Figure 7). These new data support the conclusion that excess IL-2 signalling can limit the Tfh cell response. These data are presented in Figure 8, and are discussed on page 12 in the results, and pages 12-13 in the discussion.

Figure 8: Increased IL-2 production impairs Tfh cell formation and the germinal centre response. Assessment of the Tfh cell and germinal centre response in Il2cre/+; Rosa26stop-flox-Il2/+ transgenic mice that do not switch off IL-2 production, and Il2cre/+; Rosa26+/+ control mice 12 days after influenza A infection. Flow cytometric contour plots (A) and quantification of the percentage of CXCR5highPD-1highFoxp3-CD4+ Tfh cells in the mediastinal lymph node (B) and spleen (C). Flow cytometric contour plots (D) and quantification of the percentage of Bcl6+Ki67+B220+ germinal centre B cells in the mediastinal lymph node (E) and spleen (F). The height of the bars indicates the median, each symbol represents one mouse, data are pooled from two independent experiments. P-values calculated between genotype-groups by Mann Whitney U test.

Results text, page 12: Sustained IL-2 production inhibits Tfh cell frequency and the germinal centre response. To test the hypothesis that cytokine signalling needs to be curtailed to facilitate Tfh cell differentiation turned to a genetically modified mouse model in which cells that have initiated IL-2 production cannot switch it off, Il2cre/+; Rosa26stop-flox-Il2/+ mice (37). Twelve days after influenza infection Il2cre/+; Rosa26stop-flox-Il2/+ mice have fewer Tfh cells in the draining lymph node and spleen (Fig. 8A-C), which is associated with a reduced frequency of germinal center B cells (Fig. 8D-F). This provides a proof of concept that proinflammatory cytokine production needs to be limited to enable full Tfh cell differentiation in secondary lymphoid organs.

Discussion text, pages 12, 13: These enhanced inflammatory signatures associated with poor antibody titre in an independent cohort of influenza vaccinees. The dampening of Tfh cell formation by enhanced cytokine production was confirmed by the use of genetically modified mice where IL-2 production is restricted to the appropriate anatomical and cellular compartments, but once initiated cannot be inactivated. Together, this suggests that formation of antigen-specific Tfh cells is essential for high titre antibody responses, and that excessive inflammatory factors can contribute to poor cTfh cell responses.

Author Response

Reviewer #1 (Public Review):

In the article "Neuroendocrinology of the lung revealed by single cell RNA sequencing", Kuo et. al. described various aspects of pulmonary neuroendocrine cells (PNECs) including the scRNA-seq profile of one human lung carcinoid sample. Overall, although this manuscript does not have any specific storyline, it is informative and would be an asset for researchers exploring various new roles of PNECs.

Thank you for appreciating the significance of the data presented. Our storyline focuses on the newly uncovered molecular diversity of PNECs and the extraordinary repertoire of peptidergic signals they express and cell types these signals can directly target in (and outside) the lung, in mice and human, and in health and disease (human carcinoid tumor).

Major comments:

The major concern about the work is most results are preliminary, and at a descriptive level, conclusions or sub-conclusions are derived from scRNA-seq analysis only, lacking in-depth functional analysis and validation in other methods or systems. There are many open-end results that have been predicted by the authors based on their scRNA-seq data analysis without functional validation. In order to give them a constructive roadmap, it would be better to investigate literature and put them in a potential or probable hypothesis by citing the available literature. This should be done in each section of the result part. The paper lacks a main theme or specific biology question to address. In addition, the description about the human lung carcinoid by scRNA-seq is somehow disconnected from the main study line. Also, these results are derived from the study on only one single patient, lacking statistical power.

We agree that much of the data and analysis presented in the paper is descriptive and hypothesis-generating for PNECs, however we do not consider it preliminary. We focused on validating two key conclusions from the scRNA-seq analysis: PNECs are extraordinarily diverse molecularly (as validated by multiplex in situ hybridization and immunostaining) and they express many different combinations of peptidergic signals (and appear to package them in separate vesicles). From the lung expression profiles of the cognate receptors, we also predicted the direct lung targets of the dozens of new PNEC peptidergic signals we uncovered, and validated the cell target (PSN4, a recently identified subtype of pulmonary sensory neuron) of one of the newly identified PNEC signals (the classic hormone angiotensin) by confirming expression of the cognate receptor gene in PSN4 neurons that innervate PNECs and showing that the hormone can directly activate PSN4 neurons. The characterized human carcinoid provided evidence that during tumorigenesis, the amplified PNECs retain a memory (albeit imperfect) of the molecular subtype of PNEC from which they originated. As suggested by the Reviewer, we have provided more background in Results by adding additional citations from the literature to clarify the rationale for each analysis and what was known prior to the analysis. We feel that our paper provides a broad foundation for exploring the diversity and signaling functions of PNECs, and although each molecular type of PNEC and new PNEC peptidergic signal we uncovered and potential target cell in (and outside) the lung warrants follow up (as do the sensory and other properties of PNECs we inferred from their expression profiles), such studies will require the effort of many individuals in many labs studying both normal and disease physiology in mouse and human, and exploiting the data, hypotheses, approaches, and framework we provide.

Reviewer #2 (Public Review):

Pulmonary neuroendocrine cells (PNECs) are known to monitor oxygen levels in the airway and can serve as stem cells that repair the lung epithelium after injury. Due to their rarity, however, their functions are still poorly understood. To identify potential sensory functions of PNECs, the authors have used single-cell RNA-sequencing (scRNA-seq) to profile hundreds of mouse and human PNECs. They report that PNECs express over 40 distinct peptidergic genes, and over 150 distinct combinations of these genes can be detected. Receptors for these neuropeptides and peptide hormones are expressed in a wide range of lung cell types, suggesting that PNECs may have mechanical, thermal, acid, and oxygen sensory roles, among others. However, since some of these cognate receptors are not expressed in the lung, PNECs may also have systemic endocrine functions. Although these data are largely descriptive, the results represent a significant resource for understanding the potential roles of PNECs in normal biology as well as in pulmonary diseases and cancer and are likely to be relevant for understanding neuroendocrine cells in other tissue contexts.

However, there are several aspects of the data analysis that are unclear and require clarification, most notably the definition of a neuroendocrine cell (points #1 and #2 below).

1) Figure S1 shows the sorting strategy used for isolation of putative PNECs from Ascl1CreER/+; Rosa26ZsGreen/+ mice, and distinguishes neuroendocrine cells defined as ZsGreen+ EpCAM+ and "neural" cells defined as ZsGreen+ EpCAM-; the figure legend also refers to the ZsGreen+ EpCAM- cells as "control" cells. However, the table shown in panel D indicates that the NE population combines 112 ZsGreen+ EpCAM+ cells together with 64 ZsGreen+ EpCAM- cells to generate the 176 cells used for subsequent analyses. Why are these ZsGreen+ EpCAM- cells initially labeled as neural or control, but are then defined as neuroendocrine? If these do not express an epithelial marker, can they be rigorously considered as neuroendocrine?

As explained above in the response to Essential Revision point 1, we define pulmonary neuroendocrine cells (PNECs) throughout the paper by their transcriptomic clustering and signatures, which includes the dozens of newly identified PNEC markers as well as the few extant marker genes available before this study (listed in Table S2). The confusion here arises from the two previously known markers (Ascl1 lineage marker ZsGreen, EpCAM) we used for flow sorting to enrich for these rare cells for transcriptomic profiling (Fig. S1). Although most of the cells with PNEC transcriptomic profiles were from the ZsGreenhi EpCAMhi sorted population (as expected), some were from the ZsGreenhi EpCAMlo sorted population. The latter resulted from the high EpCAM gating threshold we used during flow sorting, which excluded some PNECs with intermediate levels of surface EpCAM. Indeed, nearly all PNECs (> 95%) expressed EpCAM by scRNAseq, and there was no difference in EpCAM transcript levels or transcriptomic clustering of PNECs that were from the ZsGreenhi EpCAMhi vs. ZsGreenhi EpCAMlo sorted populations, as we now show in the new panels (C', C'') added to Fig S1C. This point is now clarified in the legend to Fig. S1C, and it nicely demonstrates that transcriptomic profiling is a more robust method of identifying PNECs than flow sorting based on two classical markers.

2) Similarly, in the human scRNA-seq analysis, how were PNECs defined? The methods description states that these cells were identified by their expression of CALCA and ASCL1, but does not indicate whether they also expressed epithelial markers.

Human PNECs were identified in the single cell transcriptomic analysis by the same strategy described above for mouse PNECs: by their transcriptomic clustering and signatures, which includes the dozens of newly identified PNEC markers as well as the few extant marker genes available before this study (listed in Table S2). In addition to expression of classic and new markers, the human PNEC cluster defined by scRNA-seq indeed showed the expected expressed of epithelial markers (e.g, EPCAM, see dotplot below), like other epithelial cells.

3) The presentation of sensitivity and specificity in Figure 1 is confusing and potentially misleading. According to Figure 1B, Psck1 and Nov are two of the top-ranked differentially expressed genes in PNECs with respect to both sensitivity and specificity. However, the specificity of these two genes appears to be lower than that of Scg5, Chgb, and several other genes, as suggested in Figure 1C and Figure S1E. In contrast, Chgb appears to have higher specificity and sensitivity than Psck1 in Figures 1C and E but is not shown in the list of markers in Figure 1B.

As explained above in the response to Essential Revision point 2, because different marker features are important for different applications, we have provided several different graphical formats (Figs. 1B,C, Fig. S1E) and a table (Table S1) to aid in selection of the optimal markers for each application. Fig. 1B shows the most sensitive and specific PNEC markers identified by ratio of the natural logs of the average expression of the marker in PNECs vs. non-PNEC epithelial cells (Table S1), and we have added a two-dimensional plot of this sensitivity and specificity for a large set of PNEC markers (new panel E of Fig. S1). The violin plots in Fig. 1C allow visual comparison of expression of selected markers across PNECs and 40 other lung cell types including non-epithelial cells (from our extensive mouse lung atlas in Travaglini, Nabhan et al, Nature 2020). Pcsk1 and Nov score high in the analysis of Fig. 1B because they are highly sensitive and specific markers within the pulmonary epithelium, and they are also valuable markers because they are highly expressed in PNECs. However, they appear slightly less specific in the violon plots of Fig. 1C (Pcsk1) and Fig. S1F (Nov) because of expression (though at much lower levels) in individual lung cell types outside the epithelium: Pcsk1 is expressed also at low levels in some Alox5+ lymphocytes, and Nov is expressed at low levels in some smooth muscle cells. Chgb is a new PNEC marker that did not make the cutoff for the list in Fig. 1B because it is expressed in a slightly higher percentage of non-PNEC epithelial cells than the markers shown, which ranked slightly above it by this metric (see Table S1).

4) The expression of serotonin biosynthetic genes in mouse versus human PNECs deserves some comment. The authors fail to detect the expression of Tph1 and Tph2 in any of the mouse PNECs analyzed, but TPH1 is expressed in 76% of the human PNECs (Table S8). Is it possible that Tph1 and Tph2 are not detected in the mouse scRNA-seq data due to gene drop-out? If serotonin signaling by mouse PNECs is due to protein reuptake, as implied on p. 5, is there a discrepancy between serotonin expression as detected by smFISH versus immunostaining?

It is always possible that the failure to detect expression of Tph1 and Tph2 in the mouse scRNA-seq dataset is due to technical dropout, however when we analyzed this in our other mouse PNEC scRNA-seq dataset obtained using a microfluidic platform and also deeply-sequenced (Ouadah et al, Cell 2019), we found similar values as in the previously analyzed dataset: no Tph2 expression was detected and only 3% (3 of 92) of PNECs had detected Tph1 expression, whereas 24% (22 of 92) had detected expression of serotonin re-uptake transporter Slc6a4. Because our mouse and human scRNA-seq datasets were prepared similarly and sequenced to a similar depth (105 to 106 reads/cell), the difference observed in Tph1/TPH1 expression between mouse (0-3% PNECs) and human (76% PNECs) is more likely a true biological difference. We also analyzed serotonin levels in mouse PNECs by immunohistochemistry (not shown) and detected serotonin in nearly all (~90%) embryonic PNECs but only ~10% of adult PNECs. Systematic follow up studies will be necessary to resolve the mechanism of serotonin biogenesis and uptake in PNECs, and the potential stage and species-specific differences in these processes suggested by this initial data.

5) The smFISH and immunostaining analyses are often presented without any indication of the number of independent replicate samples analyzed (e.g., Figure 2B, Figure 3F, G).

The number of samples analyzed have been added (the values for Fig. 2B are given in legend to Fig. 2C, the quantification of Fig. 2B).

6) It would be helpful to provide a statistical analysis of the similarities and differences shown in the graphs in Figures 1E and G.

We added a statistical analysis (Fisher's exact test, two-sided) of Fig. 1E comparing expression of each examined gene in the two scRNA-seq datasets (Table S4). We added a similar statistical analysis of Fig. 1G comparing the expression values of each examined gene by scRNA-seq vs smFISH (see Fig. 1G legend).

Author Responses

Reviewer #1 (Public Review):

This study uses a nice longitudinal dataset and performs relatively thorough methodological comparisons. I also appreciate the systematic literature review presented in the introduction. The discussion of confound control is interesting and it is great that a leave-one-site-out test was included. However, the prediction accuracy drops in these important leave-one-site-out analyses, which should be assessed and discussed further.

Furthermore, I think there is a missed opportunity to test longitudinal prediction using only pre-onset individuals to gain clearer causal insights. Please find specific comments below, approximately in order of importance.

We thank the reviewers for their positive remarks and for providing important suggestions to improve the analysis. Please see our detailed comments below.

1) The leave-one-site-out results fail to achieve significant prediction accuracy for any of the phenotypes. This reveals a lack of cross-site generalizability of all results in this work. The authors discuss that this variance could be caused by distributed sample sizes across sites resulting in uneven folds or site-specific variance. It should be possible to test these hypotheses by looking at the relative performance across CV folds. The site-specific variance hypothesis may be likely because for the other results confounds are addressed using oversampling (i.e., sampling with replacement) which creates a large sample with lower variance than a random sample of the same size. This is an important null finding that may have important implications, so I do not think that it is cause for rejection. However, it is a key element of this paper and I think it should be assessed further and discussed more widely in the abstract and conclusion.

We thank the reviewer for raising this point and providing specific suggestions. As mentioned by the reviewer, the leave-one-site-out results showed high-variance across sites, that is, across cross validation (CV) folds. Therefore, as suggested by the reviewer, we further investigated the source of this variance by observing how the model accuracies correlates with each site and its sample sizes, ratio of AAM-to-controls, and the sex distribution in each site. We ranked the sites from low to high accuracy and observed different performance metrics such as sensitivity and specificity:

As shown, the models performed close-to-chance for sites ‘Dublin’, ‘Paris’ and ‘Berlin’ (<60% mean balanced accuracy) in the leave-one-site-out experiment, across all time-points and metrics. Notably, the order of the performance at each site does not correspond to the sample sizes (please refer to the ‘counts’ column in the above figure). It also does not correspond to the ratio of AAM-to-controls, or to the sex distribution.

To further investigate this, we performed another additional leave-one-site-out experiment with all 8 sites. Here, we repeated the ML (Machine Learning) exploration by using the entire data, including the data from the Nottingham site that was kept aside as the holdout. Since there are 8 sites now, we used a 8-fold cross validation and observed how the model accuracy varied across each site:

The results were comparable to the original leave-one-site-out experiment. Along with ‘Dublin’ and Berlin’, the models additionally performed poorly on the ‘Nottingham’ site. Results on ‘London’ and ‘Paris’ also fell below 60% mean balanced accuracy.

Finally, we compared the above two results to the main experiment from the paper where the test samples were randomly sampled across all sites. The performance on test subjects from each site was compared:

As seen, the models struggled with subjects from ‘Dublin’ followed by ‘Nottingham’ ‘London’ and ‘Berlin’ respectively, and performed well on subjects from ‘Dresden’, ‘Mannheim’, ‘Hamburg’ and ‘Paris’.

Across all the three results discussed above, the models consistently struggle to generalize to subjects particularly from ‘Dublin’ and ‘Nottingham’. As already pointed out by the reviewer, the variance in the main experiment in the manuscript is lower because of the random sampling of the test set across all sites. Since these results have important implications, we have included them in the manuscript and also provided these figures in the Appendix.

2) The authors state that "83.3% of subjects reported having no or just one binge drinking experience until age 14". To gain clearer insights into the causality, I recommend repeating the MRIage14 → AAMage22 prediction using only these 83% of subjects.

We thank the reviewer for this valuable comment. As suggested by the reviewer, we now repeated the MRIage14 → AAMage22 analysis by including (a) only the subjects who had no binge drinking experiences (n=477) by age 14 and (b) subjects who had one or less binge drinking experiences (n=565). The results are shown below. The balanced accuracy on the holdout set were 72.9 +/- 2% and 71.1 +/- 2.3% respectively, which is comparable to the main result of 73.1 +/- 2%.

These results provide further evidence that certain form of cerebral predisposition might be preceding the observed alcohol misuse behavior in the IMAGEN dataset. We discuss these results now in the Results section and the 2nd paragraph of Discussion.

3) The feature importance results for brain regions are quite inconsistent across time points. As such, the study doesn't really address one of the main challenges with previous work discussed in the introduction: "brain regions reported were not consistent between these studies either and do not tell a coherent story". This would be worth looking into further, for example by looking at other indices of feature importance such as permutation-based measures and/or investigating the stability of feature importance across bootstrapped CV folds.

The feature importance results shown in Figure 9 is intended to be illustrative and show where the most informative structural features are mainly clustered around in the brain, for each time point. We would like to acknowledge that this figure could be a bit confusing. Hence, we have now provided an exhaustive table in the Appendix, consisting of all important features and their respective SHAP scores obtained across the seven repeated runs. In addition, we address the inconsistencies across time points in the 3rd paragraph in the Discussion chapter and contrast our findings with previous studies. These claims can now be verified from the table of features provided in the Appendix.

Addressing the reviewer's suggestions, we would like to point out that SHAP is itself a type of permutation-based measure of feature importance. Since it derives from the theoretically-sound shapley values, is model agnostic, and has been already applied for biomedical applications, we believe that running another permutation-based analysis would not be beneficial. We have also investigated the stability of our feature importance scores by repeating the SHAP estimation with different random permutations. This process is explained in the Methods section Model Interpretation.

Additionally now, the SHAP scores across the seven repetitions are also provided in the Appendix table 6 for verification.