Reviewer #2 (Public Review):

Summary<br /> This paper expands on the literature on spatial metamers, evaluating different aspects of spatial metamers including the effect of different models and initialization conditions, as well as the relationship between metamers of the human visual system and metamers for a model. The authors conduct psychophysics experiments testing variations of metamer synthesis parameters including type of target image, scaling factor, and initialization parameters, and also compare two different metamer models (luminance vs energy). An additional contribution is doing this for a field of view larger than has been explored previously.

General Comments<br /> Overall, this paper addresses some important outstanding questions regarding comparing original to synthesized images in metamer experiments and begins to explore the effect of noise vs image seed on the resulting syntheses. While the paper tests some model classes that could be better motivated, and the results are not particularly groundbreaking, the contributions are convincing and undoubtedly important to the field. The paper includes an interesting Voronoi-like schematic of how to think about perceptual metamers, which I found helpful, but for which I do have some questions and suggestions. I also have some major concerns regarding incomplete psychophysical methodology including lack of eye-tracking, results inferred from a single subject, and a huge number of trials. I have only minor typographical criticisms and suggestions to improve clarity. The authors also use very good data reproducibility practices.

Specific Comments

Experimental Setup<br /> Firstly, the experiments do not appear to utilize an eye tracker to monitor fixation. Without eye tracking or another manipulation to ensure fixation, we cannot ensure the subjects were fixating the center of the image, and viewing the metamer as intended. While the short stimulus time (200ms) can help minimize eye movements, this does not guarantee that subjects began the trial with correct fixation, especially in such a long experiment. While Covid-19 did at one point limit in-person eye-tracked experiments, the paper reports no such restrictions that would have made the addition of eye-tracking impossible. While such a large-scale experiment may be difficult to repeat with the addition of eye tracking, the paper would be greatly improved with, at a minimum, an explanation as to why eye tracking was not included.

Secondly, many of the comparisons later in the paper (Figures 9,10) are made from a single subject. N=1 is not typically accepted as sufficient to draw conclusions in such a psychophysics experiment. Again, if there were restrictions limiting this it should be discussed. Also (P11) Is subject sub-00 is this an author? Other expert? A naive subject? The subject's expertise in viewing metamers will likely affect their performance.

Finally, the number of trials per subject is quite large. 13,000 over 9 sessions is much larger than most human experiments in this area. The reason for this should be justified.

Model<br /> For the main experiment, the authors compare the results of two models: a 'luminance model' that spatially pools mean luminance values, and an 'energy model' that spatially pools energy calculated from a multi-scale pyramid decomposition. They show that these models create metamers that result in different thresholds for human performance, and therefore different critical scaling parameters, with the basic luminance pooling model producing a scaling factor 1/4 that of the energy model. While this is certain to be true, due to the luminance model being so much simpler, the motivation for the simple luminance-based model as a comparison is unclear.

The authors claim that this luminance model captures the response of retinal ganglion cells, often modeled as a center-surround operation (Rodieck, 1964). I am unclear in what aspect(s) the authors claim these center-surround neurons mimic a simple mean luminance, especially in the context of evidence supporting a much more complex role of RGCs in vision (Atick & Redlich, 1992). Why do the authors not compare the energy model to a model that captures center-surround responses instead? Do the authors mean to claim that the luminance model captures only the pooling aspects of an RGC model? This is particularly confusing as Figures 6 and 9 show the luminance and energy models for original vs synth aligning with the scaling of Midget and Parasol RGCs, respectively. These claims should be more clearly stated, and citations included to motivate this. Similarly, with the energy model, the physiological evidence is very loosely connected to the model discussed.

Prior Work:<br /> While the explorations in this paper clearly have value, it does not present any particularly groundbreaking results, and those reported are consistent with previous literature. The explorations around critical eccentricity measurement have been done for texture models (Figure 11) in multiple papers (Freeman 2011, Wallis, 2019, Balas 2009). In particular, Freeman 20111 demonstrated that simpler models, representing measurements presumed to occur earlier in visual processing need smaller pooling regions to achieve metamerism. This work's measurements for the simpler models tested here are consistent with those results, though the model details are different. In addition, Brown, 2023 (which is miscited) also used an extended field of view (though not as large as in this work). Both Brown 2023, and Wallis 2019 performed an exploration of the effect of the target image. Also, much of the more recent previous work uses color images, while the author's exploration is only done for greyscale.

Discussion of Prior Work:<br /> The prior work on testing metamerism between original vs. synthesized and synthesized vs. synthesized images is presented in a misleading way. Wallis et al.'s prior work on this should not be a minor remark in the post-experiment discussion. Rather, it was surely a motivation for the experiment. The text should make this clear; a discussion of Wallis et al. should appear at the start of that section. The authors similarly cite much of the most relevant literature in this area as a minor remark at the end of the introduction (P3L72).

White Noise:<br /> The authors make an analogy to the inability of humans to distinguish samples of white noise. It is unclear however that human difficulty distinguishing samples of white noise is a perceptual issue- It could instead perhaps be due to cognitive/memory limitations. If one concentrates on an individual patch one can usually tell apart two samples. Support for these difficulties emerging from perceptual limitations, or a discussion of the possibility of these limitations being more cognitive should be discussed, or a different analogy employed.

Relatedly, in Figure 14, the authors do not explain why the white noise seeds would be more likely to produce syntheses that end up in different human equivalence classes.

It would be nice to see the effect of pink noise seeds, which mirror the power spectrum of natural images, but do not contain the same structure as natural images - this may address the artifacts noted in Figure 9b.

Finally, the authors note high-frequency artifacts in Figure 4 & P5L135, that remain after syntheses from the luminance model. They hypothesize that this is due to a lack of constraints on frequencies above that defined by the pooling region size. Could these be addressed with a white noise image seed that is pre-blurred with a low pass filter removing the frequencies above the spatial frequency constrained at the given eccentricity?

Schematic of metamerism:<br /> Figures 1,2,12, and 13 show a visual schematic of the state space of images, and their relationship to both model and human metamers. This is depicted as a Voronoi diagram, with individual images near the center of each shape, and other images that fall at different locations within the same cell producing the same human visual system response. I felt this conceptualization was helpful. However, implicitly it seems to make a distinction between metamerism and JND (just noticeable difference). I felt this would be better made explicit. In the case of JND, neighboring points, despite having different visual system responses, might not be distinguishable to a human observer.

In these diagrams and throughout the paper, the phrase 'visual stimulus' rather than 'image' would improve clarity, because the location of the stimulus in relation to the fovea matters whereas the image can be interpreted as the pixels displayed on the computer.

Other<br /> The authors show good reproducibility practices with links to relevant code, datasets, and figures.

Reviewer #1 (Public Review):

Summary:<br /> In this report, Yu et al ascribe potential tumor suppressive functions to the non-core regions of RAG1/2 recombinases. Using a well-established BCR-ABL oncogene-driven system, the authors model the development of B cell acute lymphoblastic leukemia in mice and found that RAG mutants lacking non-core regions show accelerated leukemogenesis. They further report that the loss of non-core regions of RAG1/2 increases genomic instability, possibly caused by increased off-target recombination of aberrant RAG-induced breaks. The authors conclude that the non-core regions of RAG1 in particular not only increase the fidelity of VDJ recombination, but may also influence the recombination "range" of off-target joints, and that in the absence of the non-core regions, mutant RAG1/2 (termed cRAGs) catalyze high levels of off-target recombination leading to the development of aggressive leukemia.

Strengths:<br /> The authors used a genetically defined oncogene-driven model to study the effect of RAG non-core regions on leukemogenesis. The animal studies were well performed and generally included a good number of mice. Therefore, the finding that cRAG expression led to the development of more aggressive BCR-ABL+ leukemia compared to fRAG is solid.

Weaknesses:<br /> In general, I find the mechanistic explanation offered by the authors to explain how the non-core regions of RAG1/2 suppress leukemogenesis to be less convincing. My main concern is that cRAG1 and cRAG2 are overexpressed relative to fRAG1/2. This raises the possibility that the observed increased aggressiveness of cRAG tumors compared to fRAG tumors could be solely due to cRAG1/2 overexpression, rather than any intrinsic differences in the activity of cRAG1/2 vs fRAG1/2; and indeed, the authors allude to this possibility in Fig S8, where it was shown that elevated expression of RAG (i.e. fRAG) correlated with decreased survival in pediatric ALL. Although it doesn't mean the authors' assertions are incorrect, this potential caveat should nevertheless be discussed.

Some of the conclusions drawn were not supported by the data.<br /> 1. I'm not sure that the authors can conclude based on μHC expression that there is a loss of pre-BCR checkpoint in cRAG tumors. In fact, Fig. 2B showed that the differences are not statistically significant overall, and more importantly, μHC expression should be detectable in small pre-B cells (CD43-). This is also corroborated by the authors' analysis of VDJ rearrangements, showing that it has occurred at the H chain locus in cRAG cells.

2. The authors found a high degree of polyclonal VDJ rearrangements in fRAG tumor cells but a much more limited oligoclonal VDJ repertoire in cRAG tumors. They concluded that this explains why cRAG tumors are more aggressive because BCR-ABL induced leukemia requires secondary oncogenic hits, resulting in the outgrowth of a few dominant clones (Page 19, lines 381-398). I'm not sure this is necessarily a causal relationship since we don't know if the oligoclonality of cRAG tumors is due to selection based on oncogenic potential or if it may actually reflect a more restricted usage of different VDJ gene segments during rearrangement.

3. What constitutes a cancer gene can be highly context- and tissue-dependent. Given that there is no additional information on how any putative cancer gene was disrupted (e.g., truncation of regulatory or coding regions), it is not possible to infer whether increased off-target cRAG activity really directly contributed to the increased aggressiveness of leukemia.

4. Fig. 6A, it seems that it is really the first four nucleotide (CACA) that determines fRAG binding and the first three (CAC) that determine cRAG binding, as opposed to five for fRAG and four for cRAG, as the author wrote (page 24, lines 493-497).

5. Fig S3B, I don't really see why "significant variations in NHEJ" would necessarily equate "aberrant expression of DNA repair pathways in cRAG leukemic cells". This is purely speculative. Since it has been reported previously that alt-EJ/MMEJ can join off target RAG breaks, do the authors detect high levels of microhomology usage at break points in cRAG tumors?

6. Fig. S7, CDKN2B inhibits CDK4/6 activation by cyclin D, but I don't think it has been shown to regulate CDK6 mRNA expression. The increase in CDK6 mRNA likely just reflects a more proliferative tumor but may have nothing to do with CDKN2B deletion in cRAG1 tumors.

Insufficient details in some figures. For instance, Fig. 1A, please include statistics in the plot showing a comparison of fRAG vs cRAG1, fRAG vs cRAG2, cRAG1 vs cRAG2. As of now, there's a single p-value (0.0425) stated in the main text and the legend but why is there only one p-value when fRAG is compared to cRAG1 or cRAG2? Similarly, the authors wrote "median survival days 11-26, 10-16, 11-21 days, P < 0.0023-0.0299, Fig. S2B." However, it is difficult for me to figure out what are the numbers referring to. For instance, is 11-26 referring to median survival of fRAG inoculated with three different concentrations of GFP+ leukemic cells or is 11-26 referring to median survival of fRAG, cRAG1, cRAG2 inoculated with 10^5 cells? It would be much clearer if the authors can provide the numbers for each pair-wise comparison, if not in the main text, then at least in the figure legend. In Fig. 5A-B, do the plots depict SVs in cRAG tumors or both cRAG and fRAG cells? Also in Fig. 5, why did 24 SVs give rise to 42 breakpoints, and not 48? Doesn't it take 2 breaks to accomplish rearrangement? In Fig. 6B-C, it is not clear how the recombination sizes were calculated. In the examples shown in Fig. 4, only cRAG1 tumors show intra-chromosomal joins (chr 12), while fRAG and cRAG2 tumors show exclusively inter-chromosomal joins.

Insufficient details on certain reagents/methods. For instance, are the cRAG1/2 mice of the same genetic background as fRAG mice (C57BL/6 WT)? On Page 23, line 481, what is a cancer gene? How are they defined? In Fig. 3C, are the FACS plots gated on intact cells? Since apoptotic cells show high levels of gH2AX, I'm surprised that the fraction of gH2AX+ cells is so much lower in fRAG tumors compared to cRAG tumors. The in vitro VDJ assay shown in Fig 3B is not described in the Method section (although it is described in Fig S5b). Fig. 5A-B, do the plots depict SVs in cRAG tumors or both cRAG and fRAG cells?

In my opinion, this article points out that disability does not solely focus on individual impairment, but also includes social expectations and accommodations. A building without ramps effectively disables someone using a wheelchair - an example that shows how structures create barriers for specific individuals.

There are usually two types of disabilities in society, one is invisible and the other is visible. Some disabilities are so accepted that they are not considered a disability, such as color blindness. Some disabilities that are physically obvious may sometimes be looked at differently by society. However, in today's society, there are always people who want to judge these people with disabilities and don't think that they can get some preferential treatment, and this behavior is immoral. We have not experienced the pain of others, and we cannot judge others arbitrarily.

This quotation emphasizes a significant difference in the perspectives of various challenged cultures about their disability. Some people may be looking for a "cure," but others accept their disability as a part of who they are. It's a complex topic, so we have to be careful not to assume that everyone with a disability feels the same way about it.

Author Response

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

Thank you for reviewing and assessing our paper. Reviewer2 had only posive comments. Reviewer 1 also had posive comments but included a list of suggesons. The revised version includes text edits to address the suggesons.

Reviewer 1:

… First, it is unclear whether the experiments and analyses were set up to be able to rule out more specific candidate funcons of the ZI.

The list of possible funcons performed by the ZI is broad. Nevertheless, our study considers a rather long list of neural processes related to the behaviors listed below.

Second, many important details of the experiments and their results are hard to decipher given the current descripons and presentaons of the data.

The procedures used in the present study have all been used and described in our previous studies (cited). We used the same descripons and presentaons as in the prior studies. We have gone over the Methods and figures to ensure that all details required to understand the experiments are provided, but we also added further details following the suggesons noted below.

The paper could be significantly strengthened by including more details from each experiment, stronger jusficaons for the limited behaviors and experimental analyses performed, and, finally, a broader analysis of how the recorded acvity in the ZI relates to behavioral parameters.

The paper studied several behaviors including: 1) spontaneous movement of head-fixed mice on a spherical treadmill, 2) tacle (whisker, and body parts) and auditory (tones and white noise) smuli applied to head fixed mice, 3) spontaneous movement iniaon, change, and turns in freely moving mice, 4) auditory tone (frequency and SPL) mapping in freely behaving mice, 5) auditory-evoked orienng head movements (responses) in the context of several behavioral tasks, 6) signaled acve avoidance responses and escapes (AA1), 7) unsignaled/signaled passive avoidance responses (AA2ITI/AA3-CS2), 8) sensory discriminaon (AA3), 9) CS-US interval ming discriminaon (AA4), and 10) USevoked unsignaled escape responses.

In freely moving experiments, the behavior is connuously tracked and decomposed into translaonal and rotaonal movement components. Discrete responses are also evaluated (e.g., acve avoids, escapes, passive avoids, errors, intertrial crossings, latencies, etc.). These behavioral procedures evaluate many neural processes, including decision making (Go/NoGo in AA1-3), response control/inhibion (unsignaled and signaled passive avoidance in AA2/3), and smulus discriminaon (AA3). The applied smuli, discrete responses, and tracked movement are always related to the recorded ZI acvity using a variety of techniques (e.g., cross-correlaons, PSTHs, event-triggered me extracons, etc.), which relate the discrete and me-series parameters to the neural acvity. We do not think all this qualifies as, “limited behaviors”.

(1) Anatomical specificaon: The ZI contains many disnct subdivisions--each with its own topographically organized inputs/outputs and putave funcons. The current manuscript doesn't reference these known divisions or their behavioral disncons, and one cannot tell exactly which poron(s) of the ZI was included in the current study. Moreover, the elongated structure of the ZI makes it very difficult to specifically or completely infect virally. The data could be beter interpreted if the paper included basic informaon on the locaons of recordings, the extent of the AAV spread in the ZI in each viral experiment, and what fracon of infected neurons were inside versus outside ZI.

Our experiments employed Vgat-Cre mice to target ZI neurons. In this line, GABAergic neurons from the enre ZI express Cre, including the dorsal and ventral subdivisions (see (Vong et al., 2011; Hormigo et al., 2020)). Consequently, AAV injecons in Vgat-Cre mice produce restricted expression in the ZI that can fully delineate the nucleus as shown in the papers referenced above (including ours). There is nil expression in structures above or below ZI because they do not express Cre in these mice (e.g., thalamus and subthalamic nucleus), which allows for selecve targeng of ZI. Our optogenec manipulaons and photometry recordings were not aimed at specific ZI subdivisions. We targeted the area of ZI indicated by the stereotaxic coordinates (see Methods), which are aimed at the center of the structure to maximize success in recording/manipulang neurons within ZI. While all the animals included in the study expressed opsins and GCaMP within ZI that in many animals fully delineated the nucleus, there was normal variability in the locaon of opcal fibers, but we did not detect any differences in the results related to these variaons.

Fiber photometry and optogenecs experiments are performed with rather large diameter opcal probes, which record/manipulate relavely large areas of the targeted structure. This is useful because our goal was to idenfy funconal roles of the enre ZI, which could then be parsed. In the present study, we did not perform experiments to target specific ZI populaons (e.g., retrograde Cre expression from target areas), which may have revealed differences atributed to their projecon sites. However, in the last experiment, we selecvely excited ZI fibers targeng three different areas (midbrain tegmentum, superior colliculus, and posterior thalamus), which revealed clear differences on movement. Thus, future experiments should explore these different populaons (e.g., using retrograde/anterograde expression systems), which may be in different subdivisions.

We have enhanced the Methods secon to clarify these points, including the addion of these references.

(2) Electrophysiological recording on the treadmill: The authors are commended for this technically very difficult experiment. The authors do not specify, however, how they knew when they were recording in ZI rather than surrounding structures, parcularly given that recording site lesions were only performed during the last recording session. A map of the locaons of the different classes of units would be valuable data to relate to the literature.

We have added details about this procedure in the Methods secon. These recordings are performed based on coordinates, and categorizing neurons as belonging to ZI is obviously an esmate based on the final histological verificaon. Nevertheless, the marking lesions revealed that the electrodes were on target, which likely resulted from the care taken during the surgical procedure to define reference points used later during the recording sessions (see Methods). Regarding a map of the unit locaons, we performed several analyses that did not reveal clear differences based on site. For example, we compared depth vs cell class, “There was no difference in recording depth between the four classes of neurons (ANOVA F(3,337)= 1.06 p=0.3676)”. Future experiments that employ addional methods (labelling, opto-tagging, etc.) would be more appropriate to address mapping quesons. Finally, as we state in the paper, “However, these recordings do not target GABAergic neurons and may sample some neurons in the tissue surrounding the zona incerta. Therefore, we used calcium imaging fiber photometry to target GABAergic neurons in the zona incerta”.

(3) The raonale of the analysis of acvity with respect to “movement peak”: It is unclear why the authors did not assess how ZI acvity correlates with a broad set of movement parameters, but rather grouped heterogeneous behavioral epochs to analyze firing with respect to “movement peaks”.

The reviewer is referring to movement peaks on the spherical treadmill. On the treadmill, we used the forward locomotor movement of the animal because this is the main acvity of the mice on the treadmill. We considered “all peaks” (or movements) and “>4 sec peaks”, which select for movement onsets. Compared to the treadmill, in freely movement condions during various behavioral tasks, there is a richer behavioral repertoire, which was analyzed in more detail (i.e., translaonal, and rotaonal components during spontaneous ongoing movement and movement onsets, movement related to various behaviors such as orienng, acve and passive avoidance, escape, sensory smulaon, discriminaon, etc.). Thus, we focused on a broader set of movement parameters in the Cre-defined ZI cells of freely behaving mice.

(4) The display of mean categorical data in various figures is interesng, however, the reader cannot gather a very detailed view of ZI firing responses or potenal heterogeneity with so litle informaon about their distribuons.

The PCA performs the heterogeneity classificaon in an unbiased manner, which we feel is a thoughul approach. The firing rates and correlaons with movement for each category of neurons are detailed in the results. Furthermore, the sensory responses for these neurons are also detailed. Together, we think this provides a detailed view of the units we recorded in awake/head-fixed mice. As already stated, further study would benefit from an addional level of cell site verificaon.

(5) Somatosensory firing responses in ZI: It is unclear why the authors chose the specific smuli used in the study. How oen did they evoke reflexive motor responses? What was the latency of sensory-evoked responses in ZI acvity and the latency of the reflexive movement?

These are broad quesons, and we assume that the reviewer is asking about somatosensory evoked responses on the spherical treadmill. We used air-puffs applied to the whiskers and on the back (le vs right) because the whiskers represent an important sensory representaon for mice, and the back is a part of the body (trunk), which we oen use to movate the animals to move forward on the treadmill. Regarding the latency of the somatosensory evoked responses, in this case, we did not correct them based on the me it takes the air-puff to travel to the whiskers or body part, and therefore we did not provide latencies. Moreover, air-puffs are not a very good method to quanfy whisker-evoked latencies, which are beter measured using other methods (whisker deflecons of single/mulple whiskers using piezo-devices or other mechanical devices, as we and others have done in many studies). We are not sure what the reviewer means by “reflexive behavior”; we did not measure any reflexive behavior under these condions. We have gone over the Methods and Results to ensure that sufficient details are provided about these experiments.

(6) It would be valuable to see example traces in Figure 3 to get a beter sense of the me course and contexts under which Ca signals in ZI tracks movement. What is the typical latency? What is the typical range of magnitudes of responses? Does the Ca signal track both fast and slow movements? How are the authors sure that there are no movement arfacts contribung to the calcium imaging? It seems there is more informaon in the dataset that could be valuable.

As is well known, fiber photometry calcium imaging is a slow populaon signal. We do not think it would be valuable to get into ming issues beyond what is already detailed in the study (i.e., magnitudes measured as areas or peaks, and ming as me-to-peaks). Regarding “movement arfacts”, these signals are absent (flat) in animals that do not express GCAMP. We agree that there must be addional valuable informaon in our datasets (as in most me-series). However, the current paper is already rather extensive. We will connue to peruse our datasets and report addional findings in new papers.

(7) Figure 4: The raonale for quanfying the F/Fo responses over a 6-second window, rather than with respect to discrete movement parameters, is not well explained. What types of movement are binned in this approach and might this broad binning hinder the ability to detect more specific relaonships between acvity and movement?

Figure 4 is focused on characterizing the relaonship between turns (ipsiversive and contraversive) during movement and ZI acvity. We tested different binning windows to find differences, including the 6 sec window in figure 4 for populaon measures (-3 to 3 sec around the turns). This binning approach is effecve at revealing differences where they exist (e.g., superior colliculus) as shown in our previous studies (e.g. (Zhou et al., 2023)). Moreover, the turns in the different direcons can be considered discrete responses at their peak, and the ming of the related acvaons (e.g., me to peaks), which we evaluated, are rather sensive and would have revealed differences, but we did not find them.

(8) Separaon of sensory and motor responses in Figure 5: The current data do not adequately differenate whether the responses are sensory or motor given the high correlaon of the sensory inputs driving motor responses. Because isoflurane can diminish auditory responses early in the auditory pathway, this reviewer is not convinced the isoflurane experiments are interpretable.

The reviewer is referring to Fig. 5C,D. Indeed, the point of this experiment was to show that it is difficult to differenate whether neural responses are sensory or motor in awake and freely moving condions. As we stated in the Results secon, “Although arousal and movement were not dissected in the present experiment (this would likely require paralyzing and ventilating the animal), the results indicate that activation of zona incerta neurons by sensory stimulation is primarily associated with states when sensory-evoked movement is also present”. This is followed in the Discussion by, “…as already noted, the suppression of sensory responses may be due to changes in arousal (Castro-Alamancos, 2004; Lee and Dan, 2012) and not caused by the abolishment of the movements per se”.

(9) Given the broad duraon of the mean avoidance response (Fig. 6 C, botom), it would be useful to know to what extent this plot reflects a prolonged behavior or is the result of averaging different animals/trials with different latencies. Given that the shapes of the F/Fo responses in ZI appear similar across avoids and escapes (Fig. 6D), despite their apparent different speeds and movement duraons (Fig 6C), it would be valuable to know how the ming of the F/Fo relates to movement on a trial-by-trial basis.

The duraon of the avoidance response cannot be ascertained from CS onset (panel 6C botom) and avoids are not wide but rather sharp. We have now made this clearer when Fig. 6C is first menoned (“note that since avoids occur at different latencies after CS onset they are best measured from their occurrence as in Fig. 6D”). Like other related condioned and uncondioned responses, avoids and escapes are similar, varying in the noted parameters. Regarding ming, as already menoned above, we think that the characteriscs of the populaon calcium signal make it unsuitable for further ming consideraons than what we included, parcularly for movements occurring at the fast speeds of avoids and escapes.

(10) Lesion quanficaon: One cannot tell what rostral-caudal extent of ZI was lesioned and quanfied in this experiment. It would be easier to interpret if also ploted for each animal, so the reader can tell how reliable the method is. The mean ablaon would be beter shown as a normalized fracon of cells. Although the authors claim the lesions have litle impact on behavior, it appears the incompleteness of the lesions could warrant a more conservave interpretaon.

The lesion experiment was a complement to the optogenecs inacvaon experiments we performed in our preceding ZI paper and in the present paper. Thus, the finding that the lesions had litle impact on behavior is supporve of the optogenecs findings. Regarding cell counts, we did not select any parts of the ZI to quanfy the number of neurons in either control or lesion mice. We considered the full rostrocaudal extent in our measurements. We are not sure what “fracon” the reviewer is suggesng, considering that these counts are from two different groups of mice (control vs lesion). Note that the red-marked neurons, as shown in Fig. 8A, reveal healthy non-Vgat-Cre neurons outside ZI that mark the extent of the AAV diffusion, which as shown spanned the full extent of the ZI in the coronal plane (and in other planes as the AAV spreads in all direcons).

(11) Optogenecs: the locaon of infected neurons is poorly described, including the rostral-caudal extent and the fracon of neurons inside and outside of ZI. Moreover, it is unclear how strongly the optogenec manipulaons in this study are expected to affect neuronal acvity in ZI.

We discussed the first point in (1) above. Regarding, how optogenec manipulaons are expected to affect neuronal acvity in ZI and its targets, we have conducted extensive electrophysiological recordings in slices and in vivo to detail the effects of our manipulaons on GABAergic neurons (e.g. (Hormigo et al., 2016; Hormigo et al., 2019; Hormigo et al., 2021a; Hormigo et al., 2021b), including ZI neurons (Hormigo et al., 2020). In fact, we never use an opsin we have not validated ourselves using electrophysiology. Moreover, our experiments employ a spectrum of optogenec light paterns (including trains/cont at different powers) that trate the optogenec effects within each session/animal. As shown in fig. 11 and 12, these paterns produce different behavioral effects related to the different levels of neural firing they induce. For ChR2-expressing neurons in ZI, firing is frequency dependent and maximal during Cont blue light (at the same power). For Arch-expressing neurons only Cont is used, and inhibion is a funcon of the green light power. When blue light is applied in ZI fibers targeng different areas, this relaonship changes. Blue light trains (1-ms pulses) at 40-66 Hz become the most effecve means of inducing sustained postsynapc inhibion compared to Cont or low frequencies.

References

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Hormigo S, Zhou J, Castro-Alamancos MA (2021a) Bidireconal control of orienng behavior by the substana nigra pars reculata: disnct significance of head and whisker movements. eNeuro. Hormigo S, Vega-Flores G, Rovira V, Castro-Alamancos MA (2019) Circuits That Mediate Expression of Signaled Acve Avoidance Converge in the Pedunculoponne Tegmentum. J Neurosci 39:45764594.

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Author Response

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

We thank the editor and the reviewers for their very useful and constructive comments. We went through the list and gladly received all their suggestions. The reviewers mostly pointed to minor revisions in the text, and we acted on all of those. The one suggestion that required major work was the one raised in point 13, about the processing pipeline being unconvincingly scattered between different tools (R → Python → Matlab). I agree that this was a major annoyance, and I am happy to say we have solved it integrating everything in a recent version of the ethoscopy software (available on biorxiv with DOI https://www.biorxiv.org/content/10.1101/2022.11.28.517675v2 and in press with Bioinformatics Advances). End users will now be able to perform coccinella analysis using ethoscopy only, thus relying on nothing else but Python as their data analysis tool. This revised version of the manuscript now includes two Jupyter Notebooks as supplementary material with a “pre-cooked” sample recipe of how to do that. This should really simplify adoption and provides more details on the pipeline used for phenotyping.

Please find below a point-by-point description of how we incorporated all the reviewers’ excellent suggestions.

Recommendations for the authors: please note that you control which, if any, revisions, to undertake

1) Line 38: "collecting data simultaneously from a large number of individuals with no or limited human intervention" is a bit misleading, as the entire condition the individuals are put in are highly modified by humans and most times "unnatural". I understand the point that once the animals are placed in these environments, then recording takes place without intervention, but it would be nice to rephrase this so that it reflects more accurately what is happening.

We have now rephrased this into the following (L39):

Collecting data simultaneously from a large number of individuals, which can remain undisturbed throughout recording.

2) Line 63: please add a reference to the Ethoscopes so that readers can easily find it.

Done.

2b) And also add how much they cost and the time needed to build them, as this will allow readers to better compare the proposed system against other commercially available ones.

This information is available on the ethoscope manual website (http://lab.gilest.ro/ethoscope). The price of one ethoscope, provided all necessary tools are available, is around ~£75 and the building time very much depends on the skillset of the builder and whether they are building their first ethoscope or subsequent ones. In our experience, building and adopting ethoscopes for the first time is not any more time-expensive than building a (e.g.) deeplabcut setup for the first time. We have added this information to L81

Ethoscopes are open source and can be manufactured by a skilled end-user at a cost of about £75 per machine, mostly building on two off-the-shelf component: a Raspberry Pi microcomputer and a Raspberry Pi NoIR camera overlooking a bespoke 3D printed arena hosting freely moving flies.

3) Line 88: The authors describe that in the current setting, their system is capable of an acquisition rate of 2.2 frames per second (FPS). Would reducing the resolution of the PiCamera allow for higher FPS? I raise this point because the authors state that max velocity over a ten second window is a good feature for classifying behaviors. However, if animals move much faster than the current acquisition rate, they could, for instance, be in position X, move about and be close to the initial position when the next data point is acquired, leading to a measured low max velocity, when in fact the opposite happened. I think it would be good to add a statement addressing this (either data from the literature showing that the low FPS does not compromise data acquisition, or a test where increasing greatly FPS leads to the same results).

We have previously performed a comparison of data analysed using videos captured at different FPSs, which is published in Quentin Geissman’s doctoral Thesis (2018, DOI: https://doi.org/10.25560/69514 ) in chapter 2, section 2.8.3, figure 2.9 ). We have now added this work as one of the references at L95 (reference 19).

4) Still on the low FPS, would a Raspberry Pi 4 help with the sampling rate? Given that they are more powerful than the RPi3 used in the paper?

It would, but it would be a minor increase, leading from 2.2 to probably 3-5 FPS. A significantly higher number of FPSs would be best achieved by lowering the camera’s resolution, as the reviewer’s suggested, or by operating offline. I think the interesting point being implied by the reviewers is that, for Drosophila, the current limits of resolution are more than sufficient. For other animals, perhaps moving more abruptly, they may not. The reviewer is right that we should add a line of caveat about this. We now do so in the discussion, lines 215-224.

Coccinella is a reductionist tool, not meant to replace the behavioural categorization that other tools can offer but to complement it. It relies on raspberry PIs as main acquisition devices, with associated advantages and limitations. Ethoscopes are inexpensive and versatile but have limitations in terms of computing power and acquisition rates. Their online acquisition speed is fast enough to successfully capture the motor activity of different species of Drosophilae28, but may not be sufficient for other animals moving more swiftly, such as zebrafish larvae. Moreover, coccinella cannot apply labels to behaviour (“courting”, “lounging”, “sipping”, “jumping” etc.) but it can successfully identify large behavioural phenotypes and generate unbiased hypothesis on how behaviour – and a nervous system at large – can be influenced by chemicals, genetics, artificial manipulations in general.

5) Along the same line of thought, would using a simple webcam (with similar specs to the PiCamera - ELP has cameras that operate on infrared and are quite affordable too) connected to a more powerful computer lead to higher FPS? - The reason for the question about using a simple webcam is that this would make your system more flexible (especially useful in the current shortage of RPi boards on the market) lowering the barrier for others to use it, increasing the chances for adoption.

Completely bypassing ethoscopes would require the users to setup their own tracking solution, with a final result that may or may not match what we describe here. If a greater temporal resolution is necessary, the easiest way to achieve more FPSs would be to either decrease camera resolution or use the Pis to take videos offline and then process those videos at a later stage. The combination of these two would give FPS acquisition of 60 fps at 720p, which is the maximum the camera can achieve. We now made this clear at lines 83-92.

The temporal and spatial resolution of the collected images depends on the working modality the user chooses. When operating in offline mode, ethoscopes are capable to acquire 720p videos at 60 fps, which is a convenient option with fast moving animals. In this study, we instead opted for the default ethoscope working settings, providing online tracking and realtime parametric extraction, meaning that images are analysed by each raspberry Pi at the very moment they were acquired (Figure 1b). This latter modality limits the temporal resolution of information being processed (one frame every 444 ms ± 127 ms, equivalent to 2.2 fps on a Raspberry Pi3 at a resolution of 1280x960 pixels with each animal being constricted in an ellipse measuring 25.8 ± 1.4 x 9.85 ±1.4 pixels - Figure 1a) but provides the most affordable and high-throughput solution, dispensing the researcher from organising video storage or asynchronous video processing for animals tracking.

6) One last point about decreasing use barrier and increasing adoption: Would it be possible to use DeepLabCut (DLC) to simply annotate each animal (instead of each body part) and feed the extracted data into your current analysis with coccinella? This way different labs that already have pipelines in place that use DLC would have a much easier time in testing and eventually switching to coccinella? I understand that extracting simple maximal velocity this way would be an overkill, but the trade-off would again be a lowering of the adoption barrier.

It would certainly be possible to calculate velocity from the whole animal pose measurement and then use this with HCTSA or Catch22, thus mimicking the coccinella pipeline, but it would be definitely overkilled, as the reviewers correctly points out. Given that we are trying to make an argument about high-throughput data acquisition I would rather not suggest this option in the manuscript.

7) Line 96: The authors state that once data is collected, it is put through a computational frameworkthat uses 7700 tests described in the literature so that meaningful discriminative features are found. I think it would be interesting to expand a bit on the explanation of how this framework deals multiple comparison/multiple testing issues.

We always use the full set of features on aggregate to train a classifier (e.g., TS_Classify in HCTSA) and that means no correction is necessary because the trained classifier only ever makes a single prediction (only one test is performed), so as long as it is done correctly (e.g., proper separation of training and test sets, etc.) then multiple hypothesis correction is not appropriate. This has been confirmed with the HCTSA/Catch22 author (Dr Ben Fulcher, personal communication). We have added a clarifying sentence about this to the methods (L315-318)

8) It would be nice to have a couple of lines explaining the choice of compounds used for testing and also why in some tests, 17 compounds were used, while in others 40, and then 12? I understand how much work it must be in terms of experiment preparation and data collection for these many flies and compounds, but these changes in the compounds used for testing without a more detailed explanation is suboptimal.

This is another good point. We have now added this information to the methods, in a section renamed “choice, handling and preparation of drugs” L280-285, which now reads like this:

The initial preliminary analysis was conducted using a group of 12 compounds “proof of principle” compounds and a solvent control. These compounds were initially used to compare both the video method and ethoscope method. After testing these initial compounds, it was found that the ethoscope methodology was more successful, and then the compound list was expanded to 17 (including the control) only using the ethoscope method. As a final test, we included additional compounds for a single concentration, bringing up the total to 40 (including control), also for the ethoscope method.

9) Line 119 states: "A similar drop in accuracy was observed using a smaller panel of 12 treatments (Supplementary Figure 2a)". It is actually Supplementary Figure 1c.

Thank you for noticing that! Now corrected. The Supplementary figures have also been renamed to obey eLife’s expected nomenclature (both Figure 1 – Figure supplements)

10) In some places the language seems a little outlandish and should either be removed or appropriately qualified. a- Lines 56-59 pose three questions that are either rhetorical or ill-posed. For example, "...minimal amount of information...behavior" implies there is a singular response but the response depends on many details such as to what degree do the authors want to "classify behavior".

Yes, those were meant as rhetorical questions indeed, but we prefer to keep them in, because we are hoping to generate this type of thoughts with the readers. These are concepts that may not be so obvious to someone who is just looking to apply an existing tool and may spring some reflection about what kind of data do they really want/need to acquire.

b) Some of the criticisms leveled at the state-of-the-art methods are probably unwarranted because the goals of the different approaches are different. The current method does not yield the type of rich information that DeepLabCut yields. So, depending on the application DeepLabCut may be the method of choice. The authors of the current manuscript should more clearly state that.

In the introduction and discussion we do try to stress that coccinella is not meant to replace tools like DLC. We have now added more emphasis to this concept, for instance to L212:

[tools like deeplabcut] are ideal – and irreplaceable – to identify behavioural patterns and study fine motor control but may be undue for many other uses.

And L215:

Coccinella is a reductionist tool not meant to replace the behavioural categorization that other tools can offer but to complement it

11) The application to sleep data appears suddenly in the manuscript. The authors should attempt to make with text change a smoother transition from drug screen to investigation into sleep.

I agree with this observation. We have now tried to add a couple of sentences to contextualise this experiment and hopefully make the connection appear more natural. Ultimately, this is a proof-ofprinciple example anyway so hopefully the reader will take it for what it is (L169).

Finally, to push the system to its limit, we asked coccinella to find qualitative differences not in pharmacologically induced changes in activity, but in a type of spontaneous behaviour mostly characterised by lack of movement: sleep. In particular, we wondered whether coccinella could provide biological insights comparing conditions of sleep rebound observed after different regimes of sleep deprivation. Drosophila melanogaster is known to show a strong, conserved homeostatic regulation of sleep that forces flies to recover at least in part lost sleep, for instance after a night of forceful sleep deprivation.

11b) Additionally, the beginning section of sleep experiments talks about sleep depth yet the conclusion drawn from sleep rebound says more about the validity of the current 5 min definition of sleep than about sleep depth. If this conclusion was misunderstood, it should be clarified. If it was not, the beginning text of the sleep section should be tailored to better fit the conclusion.

I am afraid we did not a good job at explaining a critical aspect here: the data fed to coccinella are the “raw” activity data, in which we are not making any assumption on the state of the animal. In other words, we do not use the 5-minutes at this or any other point to classify sleep and wakening. Nevertheless, coccinella picks the 300 seconds threshold as the critical one for discerning the two groups. This is interesting because it provides a full agnostic confirmation of the five minutes rule in D. melanogaster. We recognise this was not necessarily obvious from the text and now added a clarification at L189-201:

However, analysis of those same animals during rebound after sleep deprivation showed a clear clustering, segregating the samples in two subsets with separation around the 300 seconds inactivity trigger (Figure 3d). This result is important for two reasons: on one hand, it provides, for the third time, strong evidence that the system is not simply overfitting data of nought biological significance, given that it could not perform any better than a random classifier on the baseline control. On the other hand, coccinella could find biologically relevant differences on rebound data after different regimes of sleep deprivation. Interestingly enough, the 300 seconds threshold that coccinella independently identified has a deep intrinsic significance for the field, for it is considered to be the threshold beyond which flies lose arousal response to external stimuli, defining a “sleep quantum” (i.e.: the minimum amount of time required for transforming inactivity bouts into sleep bouts23,24,28). Coccinella’s analysis ran agnostic of the arbitrary 5-minutes threshold and yet identified the same value as the one able to segregate the two clusters, thus providing an independent confirmation of the fiveminutes rule in D. melanogaster.

12) Line 227: (standard food) - please add a link to a protocol or a detailed description on what is "standard food". This way others can precisely replicate what you are using. This is not my field, but I have the impression that food content/composition for these animals makes big changes in behaviour?

Yes, good point. We have now added the actual recipe to the methods L240:

Fly lines were maintained on a 12-hour light: 12-hour dark (LD) cycle and raised on polenta and yeast-based fly media (agar 96 g, polenta 240 g, fructose 960 g and Brewer’s yeast 1,200 g in 12 litres of water).

13) Data acquisition and processing: please add links to the code used.

Both the code and the raw data used to generate all the figures have been uploaded on Zenodo and available through their repository. Zenodo has a limit of 50GB per uploaded dataset so we had to split everything into two files, with two DOIs, given in the methods (L356, section “code and availability” - DOIs: 10.5281/zenodo.7335575 and 10.5281/zenodo.7393689). We have now also created a landing page for the entire project at http://lab.gilest.ro/coccinella and linked that landing page in the introduction (L64).

13b) Also your pipeline seems to use three different programming languages/environments... Any chance this could be reduced? Maybe there are R packages that can convert csv to matlab compatible formats, so you can avoid the Python step? (nothing against using the current pipeline per se, I am just thinking that for usability and adoption by other labs, the smaller amount of languages, the better?

This is a very important suggestion that highlights a clear limitation of the pipeline. I am happy to say that we worked on this and solved the problem integrating the Python version of Catch22 into the ethoscopy software. This means the two now integrate, and the entire analysis can be run within the Python ecosystem. HCTSA does not have a Python package unfortunately but we still streamlined the process so that one only has to go from Python to Matlab without passing through R. To be honest, Catch22 is the evolution of HCTSA and performs really well so I think that is what most users will want to use. We provide two supplementary notebooks to guide the reader through the process. One explains how to go from ethoscope data to an HCTSA compatible mat file. The other explains how ethoscope data integrate with Catch22 and provides many more examples than the ones found in the paper figures.

14) There are two sections named "References" (which are different from each other) on the manuscript I received and also on BioRxiv. Should one of them be a supplementary reference? Please correct it. I spent a bit of time trying to figure out why cited references in the paper had nothing to do with what was being described...

The second list of references actually applied only to the list of compounds in the supplementary table 1. When generating a collated PDF this appeared at the end of the document and created confusion. We have now amended the heading of that list in the following way, to read more appropriately:

So much to unpack here...

What is the full list of types of links?

There are (associative) links created by the author (of an HTML document) as well as associative (and sometimes unwritten) mental links which may be suggested by either the context of a piece and the author's memory.

There are the links made by the reader as they think or actively analyze the piece they're reading. They may make these explicit in their own note taking or even more strongly explicit with tools like Hypothes.is which make these links visible to others.

tacit/explicit<br /> suggested mentally / directly written or made<br /> made by writer / made by reader<br /> others?

lay these out in a grid by type, creator, modality (paper, online, written/spoken and read/heard, other)

Author Response

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

Thank you for reviewing our manuscript. We do find that the reviews are constructive and meaningful. Accordingly, we incorporated most suggestions into our revision. We provided a point-by-point responses to the reviews below.

Reviewer #1 (Public Review):

The evolution of dioecy in angiosperms has significant implications for plant reproductive efficiency, adaptation, evolutionary potential, and resilience to environmental changes. Dioecy allows for the specialization and division of labor between male and female plants, where each sex can focus on specific aspects of reproduction and allocate resources accordingly. This division of labor creates an opportunity for sexual selection to act and can drive the evolution of sexual dimorphism.

In the present study, the authors investigate sex-biased gene expression patterns in juvenile and mature dioecious flowers to gain insights into the molecular basis of sexual dimorphism. They find that a large proportion of the plant transcriptome is differentially regulated between males and females with the number of sex-biased genes in floral buds being approximately 15 times higher than in mature flowers. The functional analysis of sex-biased genes reveals that chemical defense pathways against herbivores are up-regulated in the female buds along with genes involved in the acquisition of resources such as carbon for fruit and seed production, whereas male buds are enriched in genes related to signaling, inflorescence development and senescence of male flowers. Furthermore, the authors implement sophisticated maximum likelihood methods to understand the forces driving the evolution of sexbiased genes. They highlight the influence of positive and relaxed purifying selection on the evolution of male-biased genes, which show significantly higher rates of nonsynonymous to synonymous substitutions than female or unbiased genes. This is the first report (to my knowledge) highlighting the occurrence of this pattern in plants. Overall, this study provides important insights into the genetic basis of sexual dimorphism and the evolution of reproductive genes in Cucurbitaceae.

Thank you for your positive comments. Greatly appreciated.

There are, however, parts of the manuscript that are not clearly described or could be otherwise improved.

• The number of denovo-assembled unigenes seems large and I would like to know how it compares to the number of genes in other Cucurbitaceae species. The presence of alternatively assembled isoforms or assembly artifacts may be still high in the final assembly and inflate the numbers of identified sex-biased genes.

The majority of unigenes were annotated by homologs in species of Cucurbitaceae (63%), including Momordica charantia (16.3%), Cucumis melo (11.9%), Cucurbita pepo (11.9%), Cucurbita moschata (11.5%), Cucurbita maxima (10.1%) and other species of Cucurbitaceae (Fig. S1C). We admit that in the final assembly, transcripts may be still overestimated due to the unavoidable presence of isoforms, although we have tried our best to filter it by several strategies of clustering methods. Additionally, we assessed the transcripts using BUSCOv5.4.5 and embryophyta_odb10 database with 1,614 plant orthologs assessment. Some 95.0% of these orthologs were covered by the unigenes, in which 1447 (89.7%) BUSCO genes were “Complete BUSCOs”, 85 (5.3%) were “Fragmented BUSCOs”, and only 82 (5.0%) were “Missing BUSCOs” (Table S2). Overall, our assessment suggested that we have generated high-quality reference transcriptomes in the absence of a reference genome. Subsequently, we revised the manuscript (lines 175-181).

• It is interesting that the majority of sex-biased genes are present in the floral buds but not in the mature flowers. I think this pattern could be explored in more detail, by investigating the expression of male and female sex-biased genes throughout the flower development in the opposite sex. It is also not clear how the expression of the sex-biased genes found in the buds changes when buds and mature flowers are compared within each sex.

Thank you for your advice for further understanding of this interesting pattern. In the near future, we would like to study these issues through more development stages of flowers in each sex, probably with the aid of single-cell techniques and a reference genome. We have revised the manuscript to reflect these in Results, in the section "Tissue-biased/stage-biased gene expression" (lines 202216).

• The statistical analysis of evolutionary rates between male-biased, female-biased, and unbiased genes is performed on samples with very different numbers of observations, therefore, a permutation test seems more appropriate here.

Thank you for your suggestion. However, all comparisons between sex-biased and unbiased genes were tested using Wilcoxon rank sum test in R software, which is more commonly used. Additionally, we tested some datasets, which were consistent with Wilcoxon rank sum test.

• The impact of pleiotropy on the evolutionary rates of male-biased genes is speculative since only two tissue samples (buds and mature flowers) are used. More tissue types need to be included to draw any meaningful conclusions here.

Thank you for your advice for further understanding of the impact of pleitropy. In the near future, we would like make further investigations through more development stages of flowers and new technologies in each sex to consolidate the conclusion.

Reviewer #2 (Public Review):

Summary:

This study uses transcriptome sequence from a dioecious plant to compare evolutionary rates between genes with male- and female-biased expression and distinguish between relaxed selection and positive selection as causes for more rapid evolution. These questions have been explored in animals and algae, but few studies have investigated this in dioecious angiosperms, and none have so far identified faster rates of evolution in male-biased genes (though see Hough et al. 2014 https://doi.org/10.1073/pnas.1319227111).

Strengths:

The methods are appropriate to the questions asked. Both the sample size and the depth of sequencing are sufficient, and the methods used to estimate evolutionary rates and the strength of selection are appropriate. The data presented are consistent with faster evolution of genes with male-biased expression, due to both positive and relaxed selection.

This is a useful contribution to understanding the effect of sex-biased expression in genetic evolution in plants. It demonstrates the range of variation in evolutionary rates and selective mechanisms, and provides further context to connect these patterns to potential explanatory factors in plant diversity such as the age of sex chromosomes and the developmental trajectories of male and female flowers.

Weaknesses:

The presence of sex chromosomes is a potential confounding factor, since there are different evolutionary expectations for X-linked, Y-linked, and autosomal genes. Attempting to distinguish transcripts on the sex chromosomes from autosomal transcripts could provide additional insight into the relative contributions of positive and relaxed selection.

Thank you for your meanful suggestions. We agree that the identification of chromosome origins for transcripts would greatly improve the insights of selection, and we will investigate these issues, probably with a reference genome in the near future.

Reviewer #3 (Public Review):

The potential for sexual selection and the extent of sexual dimorphism in gene expression have been studied in great detail in animals, but hardly examined in plants so far. In this context, the study by Zhao, Zhou et al. al represents a welcome addition to the literature.

Relative to the previous studies in Angiosperms, the dataset is interesting in that it focuses on reproductive rather than somatic tissues (which makes sense to investigate sexual selection), and includes more than a single developmental stage (buds + mature flowers).

The main limitation of the study is the very low number of samples analyzed, with only three replicate individuals per sex (i.e. the whole study is built on six individuals only). This provides low power to detect differential expression. Along the same line, only three species were used to evaluate the rates of non-synonymous to synonymous substitutions, which also represents a very limited dataset, in particular when trying to fit parameter-rich models such as those implemented here.

A third limitation relates to the absence of a reference genome for the species, making the use of a de novo transcriptome assembly necessary, which is likely to lead to a large number of incorrectly assembled transcripts. Of course, the production of a reference transcriptome in this non-model species is already a useful resource, but this point should at least be acknowledged somewhere in the manuscript.

Each of these shortcomings is relatively important, and together they strongly limit the scope of the conclusions that can be made, and they should at least be acknowledged more prominently. The study is valuable in spite of these limitations and the topic remains grossly understudied, so I think the study will be of interest to researchers in the field, and hopefully inspire further, more comprehensive analyses.

We acknowledged that our sample size was relatively small. We will investigate these issues at the population level, probably with a reference genome in the near future. We acknowledged in the revised manuscript that there may be some incorrectly assembled transcripts. We assessed the transcripts using BUSCOv5.4.5 and the latest embryophyta_odb10 database with 1,614 plant orthologs assessment. As mentioned, 95.0% of these orthologs were covered by the unigenes, which of 1447 (89.7%) BUSCO genes were “Complete BUSCOs”, 85 (5.3%) were “Fragmented BUSCOs”, and only 82 (5.0%) were “Missing BUSCOs” (Table S2). In short, the quality of transcriptome was high in the absence of a reference genome.

Reviewer #1 (Recommendations For The Authors):

My main criticism of this manuscript is that it refers to gene names and orthogroups throughout the text, however, the assembled transcripts are not accessible. The reference trascriptome, orthology data, and alignments used for evolutionary analysis should be made available through a public repository to support reproducibility and efficient use of produced resources in this study.

We have uploaded these datasets in Researchgate (https://www.researchgate.net/publication/373194650_Trichosanthes_pilosa_datasets Positive_selection_and_relaxed_purifying_selection_contribute_to_rapid_evolution of_male-biased_genes_in_a_dioecious_flowering_plant).

Comments to the authors:

1) I have an issue with the tissue-biased gene expression analysis. Looking at Fig.3, it seems to me there are 3,204 male-biased genes that are expressed at the same level in male buds and mature flowers (same for 5,011 female-biased genes in female buds and flowers), however, only a handful of genes show sex bias between mature male and female flowers. Taking the male-biased genes as an example, if the 3,204 M1BGs experience the same expression levels in mature male flowers and are no longer male-biased when mature male vs female flowers are compared, why there are not found as female tissue biased (F2TGs)? I may be wrong, but one scenario would be that the M1BGs increase their expression in female flowers and become unbiased. However, that increase in expression (low expression in the female buds → higher expression in the female flowers) should classify them as female tissue-biased genes (F2TGs). Can you please clarify how are the M1BGs and F1BGs expressed in the flowers of the opposite sex?

As to Fig. 3A, 3,204 male-biased genes expressed in male floral buds are part of all male-biased genes (3204+286+724=4214), as shown in Fig.2A. However, only 233 male-biased genes (88+1+144=233, Fig.2B and Fig.3B) expressed in male mature flowers. So, they are not expressed at the same level between male floral buds and mature flowers. Only 288 genes are sex-biased (M1BGs), as well as tissue/stage-biased (M1TGs) in male floral buds. M1BGs (4,214 male-biased genes) and F1BGs (5,096 female-biased genes) are 0 overlaps, except for 44,326 unbiasedgenes shown in Fig.2A. That is, F1BGs (5,096 female-biased genes) are low expression or no expression in M1BGs (4,214 male-biased genes). The expression levels of some genes have been shown in Table S14.

2) Paragraph (407-416) describes the analysis of duplicated genes under relaxed selection but there is no mention of this in the results.

In fact, these results have been shown in Table S13. It is not necessary for us to describe them in detail in the results.

3) How did the authors conclude that the identified functions in male flowers make them more adapted to biotic and abiotic environments (line 347-350)? In the paragraph above (line 338-342) the authors describe that female buds are better equipped against herbivores, which are a biotic factor?

Following your concerns, we have revised the manuscript as follows: For line 338-342, we revised the text as “Indeed, functional enrichment analysis in chemical pathways such as terpenoid backbone and diterpenoid biosynthesis indicated that relative to male floral buds, female floral buds had more expressed genes that were equipped to defend against herbivorous insects and pathogens, except for growth and development (Vaughan et al., 2013; Ren et al., 2022) (Fig. S7A and Table S11).” For line 347-350, we revised text as “We also found that male-biased genes with high evolutionary rates in male buds were associated with functions to abiotic stresses and immune responses (Tables S12 and S13), which suggest that male floral buds through rapidly evolving genes are adapted to mountain climate and the environment in Southwest China compared to female floral buds through high gene expression.”

4) Line 417-418: decreasing codon usage bias is linked to decreasing synonymous substitution rates, should this be the opposite?

No. Codon usage bias was positively related to synonymous substitution rates. That is, stronger codon usage bias may be related to higher synonymous substitution rates (Parvathy et al., 2022).

5) Figures and Tables are not standalone and are missing details in the legends. - Fig.2C, which genes are plotted on the heatmap and what is the color scale corresponding to?

• All Supplementary figures are missing the descriptions of individual panels (A, B, C,etc.) in the legends. In addition, please add the numbers of observations under boxplots.

• Supplementary Fig.5 and 6: Panel B is not a Venn diagram, I suggest removing it from the figures.

• Supplementary Fig.7: Should be 'sex-biased genes'. What is the x-axis on the plot?

• Supplementary Fig.8: Please add the description of the abbreviations in the legend. - Supplementary Tables S4, S5, S6: Please add information about the foreground and background branches.

• Supplementary Table S6, S7, S8, S9, S10: Please add more details about the column headers (what is Model-A, background ω 2a, Unconstrained_1.p, K, which was the foreground branch etc.).

• Supplementary Table S11: Please add gene IDs for each KEGG category.

We have revised/fixed these issues following your concerns and suggetions.

Minor comments:

Line 28: 'algae' in place of 'algas'

Line 53-56: Please provide more recent references.

Line65: 'most' instead of 'almost'

Line 86-87: It is not clear from the sentence if the sex-biased expression was detected in flowers compared to leaves, or were the sex-biased genes detected between male and female leaves? Please clarify.

Line 107-108: positive selection is referred to as adaptive evolution, please choose one or the other.

Line 109: 'force' instead of 'forces'

Line 110: 'algae' instead of 'alga'

Line 132: '..mainly distributed from Southwest,' the country is missing.

Line 202: 'protein sequence evolution'?

Line 232: what does the 'number of evolutionary rates' refers to?

Line 253: please provide a reference for the RELAX model.

Line 274: 'relaxed selective male-biased genes' should be 'male-biased genes under relaxed purifying selection'?

Line 318: Please add a sentence explaining why the Cucurbitaceae family is a great model to study the evolution of sexual systems.

Line 321: 'genes' instead of 'gene'.

Line 366: male-biased genes experience 'higher' or 'more rapid' evolutionary rates. line 377: in the present study and in the case of Ectocarpus alga, positive selection plays an important role in male-biased genes evolution, but does not account for the majority of evolutionary change. Therefore, I would not call it a 'primary' force.

Line 477: missing reference for DESeq2 package.

Line 480: 'used'.

Line 498: 'coding sequences'.

Line516: 'to' instead of 'by'.

Line 553: 'the' is repeated twice.

Sorry for the typos and grammatical issues. We have revised them accordingly.

Reviewer #2 (Recommendations For The Authors):

There are two areas for improvement, one empirical and one theoretical.

Empirically, the analyses could be expanded by an attempt to distinguish between genes on the autosomes and the sex chromosomes. Genotypic patterns can be used to provisionally assign transcripts to XY or XX-like behavior when all males are heterozygous and all females are homozygous (fixed X-Y SNPs) and when all females are heterozygous and males are homozygous (lost or silenced Y genes). Comparing such genes to autosomal genes with sex-biased expression would sharpen the results because there are different expectations for the efficacy of selection on sex chromosomes. See this paper (Hough et al. 2014; https://www.pnas.org/doi/abs/10.1073/pnas.1319227111), which should be cited and does in fact identify faster substitution rates in Y-linked genes (and note that pollenexpressed genes, at least, are concentrated on the sex chromosome in this system: https://academic.oup.com/evlett/article/2/4/368/6697528, https://royalsocietypublishing.org/doi/10.1098/rstb.2021.0226).

We have cited Hough et al. 2014 and noticed that several species have been observed to exhibit rapid evolutionary rates of sequences on sex chromosomes compared to autosomes, which has been related to the evolutionary theories of fast-X or fast-Z (lines 482-484).

On the theoretical side, this study is making a very specific intervention, namely identifying more rapid evolutionary rates in genes with male-biased than femalebiased expression in a dioecious plant. The writing in the introduction and the discussion needs to be improved to differentiate between this comparison and similar comparisons, e.g. sex-biased expression in other dioecious plants (76-81), between Xlinked and Y-linked genes (Hough et al. 2014), sex chromosomes and autosome (several studies already cited), gametophytic and sporophytic tissue, and male and female reproductive tissue in hermaphroditic plants. Setting out this distinction early in the introduction will make the specific goals and novelty of this work clearer.

Thank you for your constructive suggestions. We have revised the relevant part of the Introduction accordingly (lines 74-107).

Specific comments by line:

Sorry for the typos or wording issues. We have revised them.

26 - driven not driving

28 - check house style (algae vs algas)

28-29 - consider clarifying the antecedent of "them" (evolutionary forces, not algas) 35 - maybe, but don't the signalling genes involved in stress responses function in many capacities, not just stress? Also, there's evidence that reproductive recognition machinery in plants may ultimately derive from immune function (e.g. https://doi.org/10.1111/j.1469-8137.2008.02403.x), so the GO category "biotic stress" may be too vague

39 - maybe clarify that "for the first time" refers to male rather than female, since there have been other studies in dioecious plants

66-68 - asserting that something is "essential" after describing how rare it is doesn't quite follow, since diecious plants - especially with sex chromosomes - are basically an exception. I agree that understanding the evolution of dioecious plants is important, but this isn't the most compelling way to make that case - perhaps try something else.

137ff - this sentence can be consolidated and streamlined

142 - "floral tissue" rather than "flowers tissue," here and elsewhere

144 - divergence (singular)

235 - "evidence for the contributions of" = "evidences" is unidiomatic 250 - efficiency or efficacy?

300 - why is "inositol" capitalized here and elsewhere?

300ff - are these typical patterns in male tissue in other species?

308 - is that interesting? It seems like exactly what I'd expect. Perhaps start with the unsurprising but reassuring observation (anther and pollen development genes are indeed expressed in male buds) before moving on to the more surprising findings.

319 - remove "the"

321 - genes (plural)

330 - replace "these differences" with "the differences" 336 - perhaps recap proportions / percents here?

340 - unnecessary comma after diterpenoid

341 - this seems like a big leap from the evidence, especially in the absence of supporting information about the chemical defenses of these species and how they differ by sex. Don't terpenoids have a diverse array of functions, not just defense? Here's a review: https://link.springer.com/chapter/10.1007/10_2014_295

We have revised the text as “Indeed, functional enrichment analysis in chemical pathways such as terpenoid backbone and diterpenoid biosynthesis indicated that relative to male floral buds, female floral buds had more expressed genes that were equipped to defend against herbivorous insects and pathogens, except for growth and development (Vaughan et al., 2013; Ren et al., 2022) (Fig. S7A and Table S11)” (lines 373-378).

349 - as mentioned in line 35, this is a big speculative leap. The discussion is the place for speculation, but consider other explanations too. How does the development of flowers work? Are male flowers suppressing or resorbing female primordial organs? Do male flowers in fact senesce faster? perhaps spell out the logic in more detail.

We have revised the text as “In addition, the enrichment in regulation of autophagy pathways could be associated with gamete development and the senescence of male floral buds (Table S14) (Liu and Bassham, 2012; Li et al., 2020; Zhou et al., 2021). In fact, it was observed that male flowers senesced faster (Wu et al., 2011). We also found that homologous genes of two male-biased genes in floral buds (Table S14) that control the raceme inflorescence development (Teo et al., 2014) were highly expressed compared to female floral buds. Taken together, these results indicate that expression changes in sex-biased genes, rather than sex-specific genes play different roles in sexual dimorphic traits in physiology and morphology (Dawson and Geber, 1999).” (lines 390-402).

351 - senescence of, not senescence for

363 - but Hough et al. 2014 did show rapid evolution of Y-linked genes, and those are by definition sex biased ...

391 - perhaps reiterate here that while some sex-BIASED genes did, sex-SPECIFIC genes did not, to avoid confusion

We also revised them accordingly.

Reviewer #3 (Recommendations For The Authors):

1- lines 56-57 : « have facilitated » : this wording confounds correlation with causation. Consider rephrasing as « is associated with »

2- lines 58-60 : vague wording : what are these variations ? e.g. which tissues and stages are generally enriched?

3- line 63 : this sentence is a bit misleading: consider changing it to « Most dioecious plants possess homomorphic sex-chromosomes » [and explain what homomorphic means in this context].

4- line 68 : a reference is missing here. Also perhaps, allude to the fact that sexual selection in plants has long been considered a contentious issue (e.g. https://doi.org/10.1016/j.cub.2010.12.035)

5- lines 72-76 : beyond simply describing the pattern, say what evolutionary processes are revealed by these observations.

6- line 92 : remind the reader what these 5 studies are.

7- line 94-95 : explain why the comparison of vegetative vs vegetative and vegetative vs reproductive tissues is a problem.

The published studies only compared gene expression in vegetative versus vegetative tissues and vegetative versus reproductive tissues. Because it limited our understanding of sexual selection at different floral development stages. Revised accordingly (lines 103-104). We are very interested in flower development stage for sex-biased genes. The datasets could investigate sexual selection using two developmental stage (buds + mature flowers).

8- line 100 « Evolutionary dynamic analyses » : this wording is vague

9- line 110 : brown algae are NOT plants

10- line 137-140 or in M&M : needs to describe somewhere how the male flowers differ from the female flowers and vice-versa: are the whole morphological structures related to female (male) reproduction entirely missing, or is their development arrested later on and they are still present but simply not producing gametes? This has consequences for the interpretation of the genes they express.

We have revised the typos or wording issues accordingly. However, because the sampled floral buds were equal or less than 3 mm in size, we did not observe much morphological structural difference. Indeed, the male and female flowers at antheses were markedly different in this dioecious plant as shown in Fig. 1. Additionally, we found that dioecy is the ancestral state of Trichosanthes, and transitions to monoecy (Guo et al., 2020) based on our analysis (not shown in this study), which suggest that in the early stages of flower development, female floral buds may tend to masculinize, and vice versa (Fig. 2C).

11- line 152 : it is important to be very transparent on the sample sizes here: « from three females and three males of the dioecious ... »

12- line 153 : along the same line, explain here why a de novo transcriptome had to be generated here: « In the absence of an assembled reference genome for this nonmodel species, we de novo assembled ... »

13- line 164-165 : « we have generated high-quality reference trancriptomes » : I am not entirely convinced of the quality of the transcriptome obtained without a reference genome, so I suggest simply removing this subjective sentence.

Our assessment suggested that we have generated high-quality reference transcriptomes in the absence of a reference genome, which will be the next step of our work.

14- line 169 : briefly explain the criteria used to call differentially expressed genes. Given the threshold (log-fold change >=1.3 if I read the figure correctly, but the M&M says >=1), explain how it was chosen.

Sorry, you may have misunderstood the X, Y coordinates. The value of y coordinate represents -log10(FDR), and the value of x coordinate represents log2 (Fold Change).

15- line 174 : Not clear to me how Fig2C is « revealing strong sexual dimorphism », since genes cluster neither by sex nor by tissue. This should be explained more clearly.

16- line 174-177 : The fact that more ex-biased genes were identified in early buds than in mature flowers is an interesting observation that could be given more prominence in the manuscript, but it is not really explained. Could it reflect the fact that more genes are expressed in early buds because meiotic processes happen early in flower development? Also, the genes involved in male and female organ cell fate determination might also be expected to be expressed early, with mostly organ growth genes being expressed in the mature flower.

17- line 181 : a wrap-up sentence might be useful here to drive the point home that sex-bias is more prevalent in buds than mature flowers.

18- line 184 : « tissue-biased » : a more appropriate wording here would be « stagebiased », no ? These are indeed the same tissues but at different developmental stages.

19- line 183-195 : this section could benefit from setting clear expectations in a hypothesis testing framework laying out the reasons to expect a different bias between stages and between sexes. How does that fit with the level of morphological divergence between sexes (relates to my point 10 above).

20- line 197-204. A number of essential pieces of information are missing here: how many species, how divergent, say that one other is dioecious, and precise their relative phylogenetic placement (which is important to understand the models used below). Maybe adding a phylogeny of these species in Figure 4 could be useful. Also, briefly explain the « two-ratio » and « free-ratio » models here.

21- line 196 and following: In these analyses, I could not understand the rationale for keeping buds vs mature flowers as separate analyses throughout. Why not combine both and use the full set of genes showing sex-bias in any tissue? This would increase the power and make the presentation of the results a lot more straightforward.

As you pointed earlier (in the public review, paragraphy 2), “the dataset is interesting in that it focuses on reproductive rather than somatic tissues (which makes sense to investigate sexual selection), and includes more than a single developmental stage (buds + mature flowers)”, we totally agree with your points and were very interested in floral development stages for sex-biased genes.

22- line 216 : say explicitly that the reason for not detecting a significant difference in spite of a relatively large effect size is probably related to the low number of genes, conferring low statistical power to detect a difference. An important feature also not highlighted here is that the trend (though not significant) is in the opposite direction than in the buds, and that both the 2-ratio and the free-ratio models agree on these inverted trends. This could be the basis for an interesting comparison.

Thank you for your suggestions.

23- line 220 : needs to explain more clearly how this « free-ratio » differs from the « two-ratio » model.

24- line 232-234 : I don't see why this is necessary. Why not combine both? See also my comment 21 above.

25- line 237 : the «A-model » was not defined before.

26- line 237 : « male-biased » is missing after 343.

27- line 253-258 : briefly explain what these other models are based on and how they are not redundant and instead complement the previous analyses and each other. 28- line 266-268 : the use of a more precise set of codons for male-biased genes than the others (if I understood correctly) could also be interpreted as another sign of stronger selective constraint, no?

Codon usage bias is influenced by many factors, such as levels of gene expression. Highly expressed genes have a stronger codon usage bias and could be encoded by optimal codons for more efficient translation (Frumkin et al., 2018; Parvathy et al., 2022).

29- line 269-291 : removing genes on a post-hoc basis seems statistically suspicious to me. I don't think your analysis has enough power to hand-pick specific categories of genes, and it is not clear what this brings here. I suggest simply removing these analyses and paragraphs.

30- line 325 : say whether this patterns parallels / or not those in animals.

31- line 335 : yes, these biological pieces of information are important and should be given in the introduction already.

32- the discussion should focus at some point on the observation that more femalebiased genes are found in general, but that male-biased genes seem to be under greater selection. How do you reconcile these two apparently contradictory observations?

We found that male-biased genes with high evolutionary rates in male floral buds were associated with functions to abiotic stresses and immune responses (Tables S12 and S13), which suggests that male floral buds through rapidly evolving genes are adapted to mountain climate and the environment in Southwest China compared to female floral buds through high gene expression (lines 387-390).

33- line 355 : not clear how this follows from the previous sentences.

34- line 356-358 : vagiue. not clear what the message of this sentence is.

35- line 378-383 : say that these conclusions rely on the quality of gene annotation in this non-model species, which is probably pretty low (just like any other non-model species).

36- line 403 : this conclusion seems far-fetched. Explain how exactly you reached this conclusion.

37- line 406-416: these speculations on the role of paralogs seem unnecessary, in particular since the de novo transcriptome onto which all analyses are based cannot distinguish orthologs from paralogs.

38- line 417-424. The discussion should not contain new results.

39- line 510 : why were genes with dN/dS >2 discarded here? This might strongly bias the comparison, no? This needs to be properly justified.

40- lines 516-523 : references to the models are missing.

41- line 527: « omega = 1.5 » : why/how was this arbitrary threshold chosen?

42- Fig 2 : write out « buds » and « mature flowers » on top of the graphs

43- Fig 4 : add a phylogeny of the species showing the branch being compared. Also, add the number of genes in each category on each plot.

Thanks, we revised/fixed these issues accordingly.

Author Response

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

We thank the reviewers and editors for their thoughtful assessment and critiques. As detailed below in the point-by-point replies, we have modified the text and figures to clarify points of ambiguity and to document statistical significance in places where we had inadvertently neglected to do so. The manuscript is clearer and more rigorous as a result of the review process.

Reviewer #1 (Public Review):

This study addresses the fundamental question of how the nucleotide, associated with the beta-subunit of the tubulin dimer, dictates the tubulin-tubulin interaction strength in the microtubule polymer. This problem has been a topic of debate in the field for over a decade, and it is essential for understanding microtubule dynamics.

McCormick and colleagues focus their attention on two hypotheses, which they call the "self-acting" model and the "interface-acting" model. Both models have been previously discussed in the literature and they are related to the specific way, in which the GTP hydrolysis in the beta-tubulin subunit exerts an effect on the microtubule lattice. The authors argue that the two considered models can be discriminated based on a quantitative analysis of the sensitivity of the growth rates at the plus- and minus-ends of microtubules to the concentration of GDP-tubulins in mixed nucleotide (GDP/GMPCPP) experiments. By combing computational simulations and in vitro observations, they conclude that the tubulin-tubulin interaction strength is determined by the interfacial nucleotide.

The major strength of the paper is a systematic and thorough consideration of GDP as a modulator of microtubule dynamics, which brings novel insights about the structure of the stabilizing cap on the growing microtubule end.

I think that the study is interesting and valuable for the field, but it could be improved by addressing the following critical points and suggestions. They concern (1) the statistical significance of the main experimental finding about the distinct sensitivity of the plus- and minus-ends of microtubules to the GTP-tubulin concentration in solution, and (2) the validity of the formulation of the "self-acting" model with an emphasis solely on the longitudinal bonds.

We thank the reviewer for the comment about statistical significance, and we regret our oversight to have not included that analysis in the original manuscript. We have now included an analysis of statistical significance for the main experimental results supporting the interface-acting model (Fig. 2C and the replotting of those data against a different abscissa in Fig. 3C,D), and more broadly we have ensured that all figure legends contain information about the number of measurements and whether error bars indicate SD or SEM.

The reviewers comment about the sole emphasis on longitudinal bonds helped us realize that a change to Fig. 1 (where we illustrate the two models) would improve clarity. We had originally chosen to illustrate Figure 1 using ‘pure’ longitudinal interactions (with no lateral contacts), and this may be what triggered the reviewer’s comment. We have now revised the figure to show ‘corner’ (longitudinal + lateral) interactions. There are two main reasons for this decision. First, the corner interactions are more long-lived and therefore more important for the phenomena under study. Second, because illustrating corner interactions provides a better basis for us to discuss what is a subtle aspect of our model – that the ‘GDP penalty’ affecting longitudinal or lateral interactions in a corner site is completely equivalent. Thus, our model is not quite as narrow/exclusive as the reviewer suggested. We appreciate having had the chance to clarify this.

Reviewer #2 (Public Review):

McCormick, Cleary et al., explore the question of how the nucleotide state of the tubulin heterodimer affects the interaction between adjacent tubulins.

(1) The setup of the authors' model, which attributes the dynamic properties of the growing microtubule only to the differences in interface binding affinities, is unrealistic. They excluded the influence of the nucleotide-dependent global conformational changes even in the 'Self-Acting Nucleodide' model (Fig. 1A). As the authors have found earlier, tubulin in its unassembled state may be curved irrespective of the species of the bound nucleotide (Rice et al., 2008, doi: 10.1073/pnas.0801155105), but at the growing end of microtubules, the situation could be different. Considering the recently published papers from other laboratories, it may be more appropriate to include the nucleotide-dependent change in the tubulin conformation in the Self-Acting Nucleotide model.

We understand the reviewer’s perspective, which may be summarized as: “We know conformational changes are happening and that they affect tubulin:tubulin interactions, so why isn’t your model trying to account for that?” In text added to the revised manuscript, we address this critique in the following ways. First, there is not a consensus in the field about how to parameterize the different conformations of tubulin and how they influence tubulin:tubulin interactions. Second, any attempt to explicitly account for different conformations of tubulin would substantially increase the number of adjustable model parameters, which in turn makes the fitting to growth rates more complicated. Third, compared to traditional ‘dynamics’ assays that use GTP, using mixtures of GMPCPP and GDP simplifies the biochemistry by eliminating GTPase. This results in a more uniform composition of nucleotide state in the body of the microtubule polymer, which diminishes the importance of explicitly modeling nucleotide-influenced changes in conformation. Fourth, it seems likely that different conformations of tubulin will modulate both longitudinal interactions (as tubulin becomes straighter the longitudinal contact area grows larger) and lateral interactions (as tubulin becomes straighter, the lateral contact areas on α- and β-tubulin come into better alignment). Our model treats longitudinal and corner (defined as longitudinal + lateral) interactions as independent, so in principle it could be implicitly capturing some of these conformational effects. By refining the strengths of the longitudinal and corner interactions independently, the model effectively allows the strength of longitudinal contacts to be different for pure longitudinal and corner interactions, which might implicitly capture some variations in longitudinal contacts for different tubulin conformations. Our model treats ‘bucket’-type sites (one longitudinal and two lateral interactions) as simply having an additional lateral interaction of equal strength as the first, but because bucket sites have such a high affinity, they rarely dissociate and this small oversimplification is unlikely to have a substantial effect. We have introduced text in several places (bottom of p. 7 and elsewhere) to cover these points.

(2) The result that the minus end is insensitive to GDP (Fig. 2) was previously published in a paper by Tanaka-Takiguchi et al. (doi: 10.1006/jmbi.1998.1877). The exact experimental condition was different from the one used in Fig. 2, but the essential point of the finding is the same. The authors should cite the preceding work, and discuss the similarities and differences, as compared to their own results.

Thank you for reminding us of this paper! We agree that it is an ‘on target’ citation, and have cited and discussed it in the revised manuscript (last paragraph of Introduction, third paragraph of Discussion).

Reviewer #1 (Recommendations For The Authors):

1) In my opinion, the way in which the authors have depicted their "self-acting" model in Fig. 1 and in Supplementary Figure 1, makes the model look intuitively implausible. The drawings seem to imply that at the plus-end the GTP hydrolysis in the beta-tubulin subunit somehow allosterically affects the alpha-tubulin subunit of the same dimer to weaken its longitudinal bond with adjacent tubulin dimer. Conversely, at the minus end, the same reaction now affects the very same beta-tubulin subunit, and modulates its longitudinal interaction with the next dimer.

However, a more realistic formulation of the "self-acting" model would be that the exchangeable nucleotide affects the lateral bonds, formed by the same beta-tubulin with its lateral neighbors. Although the experimental data in this regard are controversial, at least some supporting evidence for this idea comes from structural arguments, e.g. [Manka, S.W., Moores, C.A. Nat Struct Mol Biol 25, 607-615 (2018).] This "lateral selfacting", but not the "longitudinal self-acting" hypothesis, seems more natural, and it was the one previously implemented in the seminal paper by [Vanburen et al, 2002 Proceedings of the National Academy of Sciences 99.9 (2002): 6035-6040.] and later by other some other models as well.

This point has been addressed above, in part by modifying the cartoon in Fig. 1.

2) To better clarify, which exact models are considered in this manuscript, it would be helpful if the authors provided a detailed table with all simulation parameters, including, k_off_loner, k_off_bucket and k_off_corner, for both nucleotide states, in both the selfacting and the interface-acting models.

Thank you for the suggestion. We have added tables that show all simulation parameters, as well as the corresponding calculated on- and off-rates for each interaction.

3) I am not sure that using some 'arbitrarily chosen' parameters is very helpful in Chapter 1 of Results. In fact, the results, obtained with an unconstrained set of parameters may be misleading or provide ambiguous answers. In other words, how reliable are the conclusions, based on the arbitrary parameter set? For example, could the dependences of the microtubule growth rate on the GDP-tubulin content be more or less pronounced with a different set of arbitrarily chosen parameters, compared to the graphs in Fig. 1BC?

This is a fair criticism. In response, we have added three new sets of simulations that each test different choices of the biochemical parameters used in Figure 1. With respect to the original parameters, we tested a weaker and stronger choice for the longitudinal interaction (KDlong, a 100-fold range), the corner interaction (KDcorner, a 25-fold range), and the GDP weakening factor (a 100-fold range). The predicted supersensitivity of plus-end growth rates to GDP in the self-acting vs interface-acting mechanisms is robust across the range of different choices for the above parameters (Figure 1 Supplements 1 and 2). Parameters for these new simulations are shown in Tables 3 and 4.

4) It took me some time to comprehend why the minus-end growth rate is assumed to be dependent only on the concentration of the GMPCPP-tubulin (in section 2 of Results). It would be great if the authors simply plotted the simulated dependence of the growth rate on the GMPCPP-tubulin concentration in the case when no GDP-tubulin was added. As I understand, that curve should almost exactly match the dependence observed in Fig 1B, correct? Otherwise, it does not seem obvious, why GDP-tubulin does not impede the minus-end growth. Again, is this conclusion model- and parameterdependent? This question is related to point 3 above.

The minus-end growth rates decrease in proportion to the concentration of GMPCPPtubulin. We have added a note on minus-end growth rates in the Figure 1 legend.

5) I was not quite convinced by the evidence for distinct sensitivities of the plus- and minus-end growth rates to GDP-tubulin concentration (Figure 2C and Fig 3C, D). These are the key experimental measurements in the paper. Therefore, I suggest that the authors try to strengthen this point by additional measurements to increase statistics. Or at least, please, explain the data points, the error bars, and provide some information on the number of independent measurements and the statistical significance between the curves. Maybe, they could be directly compared after normalizing by the "all GMPCPP growth rate"? How was the "1.5-fold" ratio obtained in Fig 2C? Does that number refer only to a certain GDP-tubulin concentration or does that value somehow characterize the whole range of the concentrations measured?

This has been addressed above.

Reviewer #2 (Recommendations For The Authors):

These look identical to above and were addressed there.

(1) The setup of the authors' model, which attributes the dynamic properties of the growing microtubule only to the differences in interface binding affinities, is unrealistic. They excluded the influence of the nucleotide-dependent global conformational changes even in the 'Self-Acting Nucleodide' model (Fig. 1A). As the authors have found earlier, tubulin in its unassembled state may be curved irrespective of the species of the bound nucleotide (Rice et al., 2008, doi: 10.1073/pnas.0801155105), but at the growing end of microtubules, the situation could be different. Considering the recently published papers from other laboratories, it may be more appropriate to include the nucleotide-dependent change in the tubulin conformation in the Self-Acting Nucleotide model.

(2) The result that the minus end is insensitive to GDP (Fig. 2) was previously published in a paper by Tanaka-Takiguchi et al. (doi: 10.1006/jmbi.1998.1877). The exact experimental condition was different from the one used in Fig. 2, but the essential point of the finding is the same. The authors should cite the preceding work, and discuss the similarities and differences, as compared to their own results.

Author Response

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

Response to Public Reviews

Reviewer #1:

We thank this reviewer for their comments on our paper. We have adjusted the methods secon to ensure it is clear, including an updated descripon of the stascs and in some cases updated stascal methods to ensure uniformity in analyses across datasets. The discussion has been modified so that the message regarding our results is set appropriately in the literature.

Reviewer #2:

We are grateful to this reviewer for their insight. We have modified the text of the discussion to address the points of this reviewer, including providing a greater focus on the significance of our results without overgeneralizing. We have addionally reframed our argument regarding the detecon of pescides by Bombus terrestris to more carefully consider conflicng results from other papers.

Response to Recommendaons For The Authors

Response to Reviewer #1

We thank this reviewer for their thoughul comments and ideas. We have made several changes to the text of the manuscript to improve the clarity of our wring, and we are grateful to the reviewer for raising several important points that we had not sufficiently discussed in the paper previously. We feel the paper has been improved with the inclusion of a more thorough discussion and clarified methods. Please see below our responses to the points they raised.

A few general thoughts that I had when reading your manuscript: I assume you have only tested the acve pescide ingredients, but not the formula generally applied in the field. Given that these formulas contain addional compounds but the acve ingredients, might it not be possible that they could be perceived by bees?

For this study, we were interested specifically with the taste of acve pescide compounds, although we agree it could be interesng to explore the taste of other formula compounds, it was not within the scope of this paper to test these.

Is there an alternave to quinine as a negave control? As you state, quinine is generally used in studies and likely oen in concentraons which are beyond what can be seen in e.g. floral nectar, which might explain its aversive effect. I would like to see it tested in natural concentraons and ideally in combinaon with other potenally toxic plant secondary metabolites (PSMs).

The purpose of including quinine in our study was to provide an in-depth characterizaon of “biter” taste responses using the sensilla on bumblebee labial palps and galea (i.e., through the atenuaon of GRN firing). This was not to show how bumblebees may interact with plants containing quinine in the field, or other PSMs. It would indeed be interesng to explore other plant secondary metabolites, however this was beyond the scope of our paper.

L177-187 AND 233-238 Could you, please, provide a photo or schemac drawing to illustrate your assay? I have a very hard me picturing the actual set-up.

We have provided a labeled diagram of the bumblebee mouthparts and sensillum types (Fig 1A), as well as an image of the bumblebee feeding from a capillary in the behavioural assay (Fig 1G). Further details about the feeding assay (including a JoVe video) can be found with the Ma 2016 paper that we cite throughout our methods secon.

L219 Why did you choose 5 sec here?

This feeding bout duraon was selected based on the criteria defined in Ma et al 2016. We have added a citaon to that sentence.

L221-224 How precisely was the behavior scored? Just length of bouts or also repeated short contacts? Please, specify.

We used the first bout duraon and the cumulave bout duraon in our analyses. A sentence has been added to specify this.

L231/233 Please, provide some brief details here, as many readers may find it annoying to find and read another study for methods' details.

We have added three sentences in the methods to further explain the electrophysiological method.

L238-245 See also my general methods comment: concentraons used for pescides and quinine differ quite substanally, which may explain their different effects on the bees' percepon. Are the concentraons used for quinine realisc? If not that is totally fine for a negave control, but it would be interesng to see a comparison of effects conducted for similar concentraons.

The concentraons used of quinine were selected so that they would elicit a known “biter response” – these concentraons are not meant to be field-realisc, and our data (and others, e.g., Tiedeken et al 2014) show that lower concentraons of quinine are not detected by bumblebees.

L277-301 I assume that this is a standard stascal approach to analyze electrophysiological data. However, I am really struggling with fully understanding what you did here. It might be good to add some addional explanaon/detail, e.g. on why you constructed firing rate histograms or how you derived slopes (aren't smulus and bin categorical variables?).

Firing rate histograms are indeed very commonly used for visualizing neuron spikes over me. We have changed the text somewhat in an effort to make it more clear. Likewise, the “slopes” were derived from the LMEs, and in this case “bin” is a connuous me variable – any me variable will involve some binning depending on the resoluon used but should not be considered categorical.

L291-295 As you were averaging and normalizing your data, could you, please, provide some informaon on variaon within animals?

We have now included informaon on the coefficient of variaon for spike rates across sensilla for a given animal/smulus (CV range, median, and IQR).

L295 I assume t-SNE represent a mulvariate approach for ordinaon, correct? Can you explain why you chose to use this approach? Did you use Euclidean Distance?

Yes, t-SNE is a mulvariate technique for dimensionality reducon. It is parcularly well-suited for the visualizaon of high-dimensional datasets, as it can reveal the underlying structure of the data by embedding it in a lower-dimensional space (e.g., 2D) while preserving the local structure of the data as much as possible. We used t-SNE because it has been shown to be effecve in visualizing clusters of similar data points in high-dimensional data. Euclidean distance was used as the distance metric for the t-SNE embedding. Euclidean distance is the default distance metric for most implementaons of t-SNE and is appropriate for connuous data like the spike counts in this study. We have adjusted the methods to clarify this.

L304 Why did you not always use LMEs?

We have adjusted the text to show that we used LME for all comparisons, and the stascs have been updated accordingly in the results secon. None of the outcomes changed with the implementaon of LME for all tests.

L306 Would it not make sense to also include the interacon between smulus and concentraon in your models?

We have now included a sentence to explain that the interacon term was removed due to it being nonsignificant, and the models without the interacon term having beter model fit (determined by having lower AIC and BIC values).

Results:<br /> L337, 339 and more: I would prefer to see actual p-values, not just "p > 0.05".

This has been adjusted on L337 and 339. As far as we are aware, there are no other instances where exact p-values were not given (except when p < 0.0001).

Discussion:<br /> L470 This is true, but the bees' behavior changed significantly, indicang that they may respond to this small change in firing paterns already?

It is true that the bees’ behaviour changed significantly with 0.1mM QUI, but this was not the case with the pescides. Bees drank less overall of 0.1mM QUI than OSR because of the rapid posngesve effects of this compound. It’s important that the duraon of the first bout was not affected (i.e., they didn’t directly avoid it by taste upon first encountering it, as they do with 1mM QUI), but just that they drank less of the 0.1mM QUI over 2 minutes. Post-ingesve effects may occur as quickly as 30s aer inial consumpon. For the pescides, the small changes in GRN firing were not associated with any effects on consumpon or our other measures of feeding behaviour, and we suggest this results from a lack of rapid negave posngesve consequences. We now include further discussion of these important points.

L481 But they consumed significantly less of the 0.1 mM QUI!?

This is true, but they did not reject it (i.e., not drink it at all), and there were no changes in the amount of me the bees spent in contact with the 0.1mM QUI soluon compared to OSR. We have adjusted the text for clarificaon.

L504/505 AND 520/521 AND 533-536 I see your point, but I am wondering whether the bees may need some me but are generally able to learn the taste of pescides, which may explain why e.g. Arce et al. only saw an effect over me. For example, learning to 'focus' on the pescide taste may require some internal feedback (bees not feeling well) or larvae feedback. If I understood right, you tested workers only, which might be less sensive than queens or larvae. I think these aspects should be discussed.

In our study, we invesgated the mechanism of taste detecon of pescides. We agree that bees likely use posngesve mechanisms to learn to associate the locaon (or another cue) of a food source with posive or negave posngesve cues. ‘Focus’ is a higher-order process that involves increased atenon to sensory smuli but does not affect sensaon at the level of the receptor. We show that bees are unable to taste pescides using the gustatory receptors on their mouthparts, so post-ingesve learning would not be able to associate the pescides with any taste cue. Indeed, there may be caste-specific differences with foraging queens, however a discussion of this would be beyond the scope of our paper.

I also recommend broadening the scope of your discussion. For example, you only focus on nectar, while the story might be different for pollen, which is also contaminated with pescides but represents a different chemical matrix with potenally different taste properes. Also, unlike nectar, pollen is collected with tarsae and hence on contact with other bee body parts.<br /> I would also like to see a discussion of your study's implicaons for other bee species and other potenally toxic compounds (e.g. PSMs).

We do not include any data in this paper regarding tarsal or antennal taste or other potenally toxic compounds. In this paper we present one mechanism of biter taste percepon (i.e., of quinine) and specifically show that the buff-tailed bumblebee is unable to taste certain pescides using their mouthparts. To avoid overgeneralizing, we have not included discussions about other species or compounds, which may or may not share similaries with our study.

Response to Reviewer #2

We thank this reviewer for their comments. We have adjusted the text to avoid overgeneralizaons with our conclusions, and atempted to soen language in the discussion that may have been construed as combave towards the Arce et al (2018) paper. We hope this reviewer finds these adjustments to be in line with their expectaons.

1) In two parts of the manuscript, the authors made broad predicons and conclusions beyond what the evidence in the paper can support and wrote "Future studies will be necessary to confirm this." (Lines 508-509) and " Future studies that survey a greater variety of compounds will be necessary to confirm this." (563-564). Instead of making conclusions based on what experimental data in future studies may support, I would ask the authors instead to make conclusions that their current study can support based on experimental evidence in this paper.

We have removed these predicons that extend beyond the scope of the paper.

2) Line 315 "GRNs encode differences in sugar soluon composion". The logic of the tle is wrong.

This has been fixed.

3) Since this study is only performed in one bumblebee species, then I would suggest that the tle be more specific e.g., "Mouthparts of the bumblebee Bombus terrestris exhibit poor acuity for the detecon of pescides in nectar".

We have made this change.

Authorr Response

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

Reviewer #1 (Public Review):

The objective of this investigation was to determine whether experimental pain could induce alterations in cortical inhibitory/facilitatory activity observed in TMS-evoked potentials (TEPs). Previous TMS investigations of pain perception had focused on motor evoked potentials (MEPs), which reflect a combination of cortical, spinal, and peripheral activity, as well as restricting the focus to M1. The main strength of this investigation is the combined use of TMS and EEG in the context of experimental pain. More specifically, Experiment 1 investigated whether acute pain altered cortical excitability, reflected in the modulation of TEPs. The main outcome of this study is that relative to non-painful warm stimuli, painful thermal stimuli led to an increase on the amplitude of the TEP N45, with a larger increase associated with higher pain ratings. Because it has been argued that a significant portion of TEPs could reflect auditory potentials elicited by the sound (click) of the TMS, Experiment 2 constituted a control study that aimed to disentangle the cortical response related to TMS and auditory activity. Finally, Experiment 3 aimed to disentangle the cortical response to TMS and reafferent feedback from muscular activity elicited by suprathreshold TMS applied over M1. The fact that the authors accompanied their main experiment with two control experiments strengthens the conclusion that the N45 TEP peak could be implicated in the perception of painful stimuli.

Perhaps, the addition of a highly salient but non-painful stimulus (i.e. from another modality) would have further ruled out that the effects on the N45 are not predominantly related to intensity/saliency of the stimulus rather than to pain per se.

We thank the reviewer for their comment on the possibility of whether stimulus intensity influences the N45 as opposed to pain per se. We agree that the ideal experiment would have included multiple levels of stimulation. We would argue, however, that that in Experiment 1, despite the same level of stimulus intensity for all participants (46 degrees), individual differences in pain ratings were associated with the change in the N45 amplitude, suggesting that the results cannot be explained by stimulus intensity, but rather by pain intensity.

Reviewer #2 (Public Review):

The authors have used transcranial magnetic stimulation (TMS) and motor evoked potentials (MEPs) and TMS-electroencephalography (EEG) evoked potentials (TEPs) to determine how experimental heat pain could induce alterations in these metrics.
In Experiment 1 (n = 29), multiple sustained thermal stimuli were administered over the forearm, with the first, second, and third block of stimuli consisting of warm but non-painful (pre-pain block), painful heat (pain block) and warm but non-painful (post-pain block) temperatures respectively. Painful stimuli led to an increase in the amplitude of the fronto-central N45, with a larger increase associated with higher pain ratings. Experiments 2 and 3 studied the correlation between the increase in the N45 in pain and the effects of a sham stimulation protocol/higher stimulation intensity. They found that the centro-frontal N45 TEP was decreased in acute pain. The study comes from a very strong group in the pain fields with long experience in psychophysics, experimental pain, neuromodulation, and EEG in pain. They are among the first to report on changes in cortical excitability as measured by TMS-EEG over M1. While their results are in line with reductions seen in motor-evoked responses during pain and effort was made to address possible confounding factors (study 2 and 3), there are some points that need attention. In my view the most important are:

1) The method used to calculate the rest motor threshold, which is likely to have overestimated its true value : calculating highly abnormal RMT may lead to suprathreshold stimulations in all instances (Experiment 3) and may lead to somatosensory "contamination" due to re-afferent loops in both "supra" and "infra" (aka. less supra) conditions.

The method used to assess motor threshold was the TMS motor threshold Assessment Tool (MTAT) which estimates motor threshold using maximum likelihood parametric estimation by sequential testing (Awiszus et al., 2003; Awiszus and Borckardt, 2011). This was developed as a quicker alternative for calculating motor threshold compared to the traditional Rossini-Rothwell method which involves determining the lowest intensity that evokes at least 5/10 MEPs of at least 50 microvolts. The method has been shown to achieve the same accuracy of determining motor threshold as the traditional Rossini-Rothwell method, but with fewer pulses (Qi et al., 2011; Silbert et al., 2013).

We have now made this clearer in the manuscript:

“The RMT was determined using the TMS motor thresholding assessment tool, which estimates the TMS intensity required to induce an MEP of 50 microvolts with a 50% probability using maximum likelihood parametric estimation by sequential testing (Awiszus, 2003; Awiszus & Borckardt, 2011). This method has been shown to achieve the accuracy of methods such as the Rossini-Rothwell method (Rossini et al., 1994; Rothwell et al., 1999) but with fewer pulses (Qi, Wu, & Schweighofer, 2011; Silbert, Patterson, Pevcic, Windnagel, & Thickbroom, 2013). The test stimulus intensity was set at 110% RMT to concurrently measure MEPs and TEPs during pre-pain, pain and post-pain blocks.”

Therefore, the high RMTs in our study cannot be explained by the threshold assessment method. Instead, they are likely explained by aspects of the experimental setup that increased the distance between the TMS coil and the scalp, including the layer of foam placed over the coil, the EEG cap and the fact that the electrodes we used had a relatively thick profile. This has been explained in the paper:

“We note that the relatively high RMTs are likely due to aspects of the experimental setup that increased the distance between the TMS coil and the scalp, including the layer of foam placed over the coil, the EEG cap and relatively thick electrodes (6mm)”

Awiszus, F. (2003). TMS and threshold hunting. In Supplements to Clinical neurophysiology (Vol. 56, pp. 13-23). Elsevier.

Qi, F., Wu, A. D., & Schweighofer, N. (2011). Fast estimation of transcranial magnetic stimulation motor threshold. Brain stimulation, 4(1), 50-57.

Silbert, B. I., Patterson, H. I., Pevcic, D. D., Windnagel, K. A., & Thickbroom, G. W. (2013). A comparison of relative-frequency and threshold-hunting methods to determine stimulus intensity in transcranial magnetic stimulation. Clinical Neurophysiology, 124(4), 708-712.

2) The low number of pulses used for TEPs (close to ⅓ of the usual and recommended)

We agree that increasing the number of pulses can increase the signal to noise ratio. During piloting, participants were unable to tolerate the painful stimulus for long periods of time and we were required to minimize the number of pulses per condition.

We note that there is no set advised number of trials in TMS-EEG research. According to the recommendations paper, the number of trials should be based on the outcome measure e.g., TEP peaks vs. frequency domain measures vs. other measures and based on previous studies investigating test-retest reliability (Hernandez-Pavon et al., 2023). The choice of 66 pulses per condition was based on the study by Kerwin et al., (2018) showing that optimal concordance between TEP peaks can be found with 60-100 TMS pulses delivered in the same run (as in the present study). The concordance was particularly higher for the N40 peak at prefrontal electrodes, which was the key peak and electrode cluster in our study. We have made this clearer:

“Current recommendations (Hernandez-Pavon et al., 2023) suggest basing the number of TMS trials per condition on the key outcome measure (e.g., TEP peaks vs. frequency measures) and based on previous test-retest reliability studies. In our study the number of trials was based on a test-retest reliability study by (Kerwin, Keller, Wu, Narayan, & Etkin, 2018) which showed that 60 TMS pulses (delivered in the same run) was sufficient to obtain reliable TEP peaks (i.e., sufficient within-individual concordance between the resultant TEP peaks of each trial).”

Further supporting the reliability of the TEP data in our experiment, we note that the scalp topographies of the TEPs for active TMS at various timepoints (Figures 5, 7 and 9) were similar across all three experiments, especially at 45 ms post-TMS (frontal negative activity, parietal-occipital positive activity).

In addition to this, the interclass correlation coefficient (Two-way fixed, single measure) for the N45 to active suprathreshold TMS across timepoints for each experiment was 0.90 for Experiment 1 (across pre-pain, pain, post-pain time points), 0.74 for Experiment 2 (across pre-pain and pain conditions), and 0.95 for Experiment 3 (across pre-pain conditions). This suggests that even with the fluctuations in the N45 induced by pain, the N45 for each participant was stable across time, further supporting the reliability of our data. These ICCs are now reported in the supplementary material (subheading: Test-retest reliability of N45 Peaks).

Hernandez-Pavon, J. C., Veniero, D., Bergmann, T. O., Belardinelli, P., Bortoletto, M., Casarotto, S., ... & Ilmoniemi, R. J. (2023). TMS combined with EEG: Recommendations and open issues for data collection and analysis. Brain Stimulatio, 16(3), 567-593

Kerwin, L. J., Keller, C. J., Wu, W., Narayan, M., & Etkin, A. (2018). Test-retest reliability of transcranial magnetic stimulation EEG evoked potentials. Brain stimulation, 11(3), 536-544.

Lack of measures to mask auditory noise.

In TMS-EEG research, various masking methods have been proposed to suppress the somatosensory and auditory artefacts resulting from TMS pulses, such as white noise played through headphones to mask the click sound (Ilmoniemi and Kičić, 2010), and a thin layer of foam placed between the TMS coil and EEG cap to minimize the scalp sensation (Massimini et al., 2005). However, recent studies have shown that even when these methods are used, sensory contamination of TEPs is still present, as shown by studies that show commonalities in the signal between active and sensory sham conditions that mimic the auditory/somatosensory aspects of real TMS (Biabani et al., 2019; Conde et al., 2019; Rocchi et al., 2021). This has led many authors (Biabani et al., 2019; Conde et al., 2019) to recommend the use of sham conditions to control for sensory contamination. To separate the direct cortical response to TMS from sensory evoked activity, Experiment 2 included a sham TMS condition that mimicked the auditory/somatosensory aspects of active TMS to determine whether any alterations in the TEP peaks in response to pain were due to changes in sensory evoked activity associated with TMS, as opposed to changes in cortical excitability. Therefore, the lack of auditory masking does not impact the main conclusions of the paper.

We have made this clearer:

“… masking methods have been used to suppress these sensory inputs, (Ilmoniemi and Kičić, 2010; Massimini et al., 2005). However recent studies have shown that even when these methods are used, sensory contamination of TEPs is still present, as shown by commonalities in the signal between active and sensory sham conditions that mimic the auditory/somatosensory aspects of real TMS (Biabani et al., 2019; Conde et al., 2019; Rocchi et al., 2021). This has led many leading authors (Biabani et al., 2019; Conde et al., 2019) to recommend the use of sham conditions to control for sensory contamination.”

Ilmoniemi, R. J., & Kičić, D. (2010). Methodology for combined TMS and EEG. Brain topography, 22, 233-248.

Massimini, M., Ferrarelli, F., Huber, R., Esser, S. K., Singh, H., & Tononi, G. (2005). Breakdown of cortical effective connectivity during sleep. Science, 309(5744), 2228-2232.

Biabani, M., Fornito, A., Mutanen, T. P., Morrow, J., & Rogasch, N. C. (2019). Characterizing and minimizing the contribution of sensory inputs to TMS-evoked potentials. Brain stimulation, 12(6), 1537-1552.

Conde, V., Tomasevic, L., Akopian, I., Stanek, K., Saturnino, G. B., Thielscher, A., ... & Siebner, H. R. (2019). The non-transcranial TMS-evoked potential is an inherent source of ambiguity in TMS-EEG studies. Neuroimage, 185, 300-312.

Rocchi, L., Di Santo, A., Brown, K., Ibáñez, J., Casula, E., Rawji, V., ... & Rothwell, J. (2021). Disentangling EEG responses to TMS due to cortical and peripheral activations. Brain stimulation, 14(1), 4-18.

3) A supra-stimulus heat stimulus not based on individual HPT, that oscillates during the experiment and that lead to large variations in pain intensity across participants is unfortunate.

The choice of whether to calibrate or fix stimulus intensity is a contentious question in experimental pain research. A recent discussion by Adamczyk et al., (2022) explores the pros and cons of each approach and recommends situations where one method may be preferred over the other. That paper suggests that the choice of the methodology is related to the research question – when the main outcome of the research is objective (neurophysiological measures) and researchers are interested in the variability in pain ratings, the fixed approach is preferrable. Given we explored the relationship between MEP/N45 modulation by pain and pain intensity, this question is better explored by using the same stimulus intensity for all participants, as opposed to calibrating the intensity to achieve a similar level of pain across participants.

We have made this clearer:

“Given we were interested in the individual relationship between pain and excitability changes, the fixed temperature of 46ºC ensured larger variability in pain ratings as opposed to calibrating the temperature of the thermode for each participant (Adamczyk et al., 2022).”.

Adamczyk, W. M., Szikszay, T. M., Nahman-Averbuch, H., Skalski, J., Nastaj, J., Gouverneur, P., & Luedtke, K. (2022). To calibrate or not to calibrate? A methodological dilemma in experimental pain research. The Journal of Pain, 23(11), 1823-1832.

So is the lack of report on measures taken to correct for a fortuitous significance (multiple comparison correction) in such a huge number of serial paired tests.

Note that we used a Bayesian approach for all analyses as opposed to the traditional frequentist approach. In contrast to the frequentist approach, the Bayesian approach does not require corrections for multiple comparisons (Gelman et al., 2000) given that they provide a ratio representing the strength of evidence for the null vs. alternative hypotheses as opposed to accepting or rejecting the null hypothesis based on p-values. As such, throughout the paper, we frame our interpretations and conclusions based on the strength of evidence (e.g. anecdotal/weak, moderate, strong, very strong) as opposed to referring to the significance of the effects.

Gelman A, Tuerlinckx F. (2000). Type S error rates for classical and Bayesian single and multiple comparison procedures. Computational statistics, 15(3):373-90.

Reviewer #3 (Public Review):

The present study aims to investigate whether pain influences cortical excitability. To this end, heat pain stimuli are applied to healthy human participants. Simultaneously, TMS pulses are applied to M1 and TMS-evoked potentials (TEPs) and pain ratings are assessed after each TMS pulse. TEPs are used as measures of cortical excitability. The results show that TEP amplitudes at 45 msec (N45) after TMS pulses are higher during painful stimulation than during non-painful warm stimulation. Control experiments indicate that auditory, somatosensory, or proprioceptive effects cannot explain this effect. Considering that the N45 might reflect GABAergic activity, the results suggest that pain changes GABAergic activity. The authors conclude that TEP indices of GABAergic transmission might be useful as biomarkers of pain sensitivity.

Pain-induced cortical excitability changes is an interesting, timely, and potentially clinically relevant topic. The paradigm and the analysis are sound, the results are mostly convincing, and the interpretation is adequate. The following clarifications and revisions might help to improve the manuscript further.

1) Non-painful control condition. In this condition, stimuli are applied at warmth detection threshold. At this intensity, by definition, some stimuli are not perceived as different from the baseline. Thus, this condition might not be perfectly suited to control for the effects of painful vs. non-painful stimulation. This potential confound should be critically discussed.

In Experiment 3, we also collected warmth ratings to confirm whether the pre-pain stimuli were perceived as different from baseline. This detail has been added to them methods:

“In addition to the pain rating in between TMS pulses, we collected a second rating for warmth of the thermal stimulus (0 = neutral, 10 = very warm) to confirm that the participants felt some difference in sensation relative to baseline during the pre-pain block. This data is presented in the supplementary material”.

We did not include these data in the initial submission but have now included it in the supplemental material. These data showed warmth ratings were close to 2/10 on average. This confirms that the non-painful control condition produced some level of non-painful sensation.

2) MEP differences between conditions. The results do not show differences in MEP amplitudes between conditions (BF 1.015). The analysis nevertheless relates MEP differences between conditions to pain ratings. It would be more appropriate to state that in this study, pain did not affect MEP and to remove the correlation analysis and its interpretation from the manuscript.

The interindividual relationship between changes in MEP amplitude and individual pain rating is statistically independent from the overall group level effect of pain on MEP amplitude. Therefore, conclusions for the individual and group level effects can be made independently.

It is also important to note that in the pain literature, there is now increasing emphasis placed on investigating the individual level relationship between changes in cortical excitability and pain as opposed to the group level effect (Seminowicz et al., 2019; Summers et al., 2019). As such, it is important to make these results readily available for the scientific community.

We have made this clearer:

‘As there is now increasing emphasis placed on investigating the individual level relationship between changes in cortical excitability and pain and not only the group level effect, (Chowdhury et al., 2022; Seminowicz et al., 2018; Seminowicz, Thapa, & Schabrun, 2019; Summers et al., 2019) we also investigated the correlations between pain ratings and changes in MEP (and TEP) amplitude”

Chowdhury, N. S., Chang, W. J., Millard, S. K., Skippen, P., Bilska, K., Seminowicz, D. A., & Schabrun, S. M. (2022). The Effect of Acute and Sustained Pain on Corticomotor Excitability: A Systematic Review and Meta-Analysis of Group and Individual Level Data. The Journal of Pain, 23(10), 1680-1696.

Summers, S. J., Chipchase, L. S., Hirata, R., Graven-Nielsen, T., Cavaleri, R., & Schabrun, S. M. (2019). Motor adaptation varies between individuals in the transition to sustained pain. Pain, 160(9), 2115-2125.

Seminowicz, D. A., Thapa, T., & Schabrun, S. M. (2019). Corticomotor depression is associated with higher pain severity in the transition to sustained pain: a longitudinal exploratory study of individual differences. The Journal of Pain, 20(12), 1498-1506.

3) Confounds by pain ratings. The ISI between TMS pulses is 4 sec and includes verbal pain ratings. Considering this relatively short ISI, would it be possible that verbal pain ratings confound the TEP? Moreover, could the pain ratings confound TEP differences between conditions, e.g., by providing earlier ratings when the stimulus is painful? This should be carefully considered, and the authors might perform control analyses.

It is unlikely that the verbal ratings contaminated the TEP response as the subsequent TMS pulse was not delivered until the verbal rating was complete and given that each participant was cued by the experimenter to provide the pain rating after each pulse (rather than the participant giving the rating at any time). As such, it would not be possible for participants to provide earlier ratings to more painful stimuli.

We have made this clearer:

"To avoid contamination of TEPs by verbal ratings, the subsequent TMS pulse was not delivered until the verbal rating was complete, and the participant was cued by the experimenter to provide the pain rating after each pulse.”

4) Confounds by time effects. Non-painful and painful conditions were performed in a fixed order. Potential confounds by time effects should be carefully considered.

Previous research suggests that pain alters neural excitability even after pain has subsided. In a recent meta-analysis (Chowdhury et al., 2022) we found effect sizes of 0.55-0.9 for MEP reductions 0-30 minutes after pain had resolved. As such, we avoided intermixing pain and warm blocks given subsequent warm blocks would not serve as a valid baseline, as each subsequent warm block would have residual effects from the previous pain blocks.

Chowdhury, N. S., Chang, W. J., Millard, S. K., Skippen, P., Bilska, K., Seminowicz, D. A., & Schabrun, S. M. (2022). The Effect of Acute and Sustained Pain on Corticomotor Excitability: A Systematic Review and Meta-Analysis of Group and Individual Level Data. The Journal of Pain, 23(10), 1680-1696.

At the same time, given there was no conclusive evidence for a difference in N45 amplitude between pre-pain and post-pain conditions of Experiment 1 (Supplementary Figure 1), it is unlikely that the effect of pain was an artefact of time i.e., the explanation that successive thermal stimuli applied to the skin results an increase in the N45, regardless of whether the stimuli are painful or not. We will make this point in our next revision.

We have discussed this issue:

“Lastly, future research should consider replicating our experiment using intermixed pain and no pain blocks, as opposed to fixed pre-pain and pain blocks, to control for order effects i.e., the explanation that successive thermal stimuli applied to the skin results an increase in the N45 peak, regardless of whether the stimuli are painful or not. However, we note that there was no conclusive evidence for a difference in N45 peak amplitude between pre-pain and post-pain conditions of Experiment 1 (Supplementary Figure 1), suggesting it is unlikely that the observed effects were an artefact of time.”

5) Data availability. The authors should state how they make the data openly available.

We have uploaded the MEP, TEP and pain data on the Open science framework https://osf.io/k3psu/

Reviewer #1 (Recommendations For The Authors):

I think the study is quite solid and I only have very minor recommendations for the authors:

• Introduction, p. 3: "Functional magnetic resonance imaging has helped us understand where in the brain pain is processed". This is an overstatement. fMRI provides us with potential biomarkers (e.g. "the pain signature"), but the specificity of these responses for pain is debated and we still do not know where in the brain pain is processed.

We have amended to:

“functional magnetic resonance imaging has assisted in the localization of brain structures implicated in pain processing”

• Introduction, p. 5: "neural baseline" should be "neutral baseline"?

We thank the reviewer for identifying this – this has now been amended.

Reviewer #2 (Recommendations For The Authors):

INTRODUCTION

The introduction mentions how important extra-motor areas can be explored by TMS-EEG, then the effects of DLPFC rTMS on TEPs ... but you do not explore the DLPFC... Perhaps the introduction should be reframed.

The current work explores cortical excitability throughout the brain (as shown in our cluster-based permutation and source localization analyses), so our investigations are in line with the introductions statement about the importance of studying non-motor areas.

The reference to DLPFC rTMS was to highlight current existing research that has applied TMS-EEG to understand pain. It was not used as a methodological rationale to investigate the DLPFC in the present study. To make the research gap clearer, we state:

“While these studies assist us in understanding whether TEPs might mediate rTMS-induced pain reductions, no study has investigated whether TEPs are altered in direct response to pain”

Lignes 63-65 the term "TMS" is used to refer to motor corticospinal excitability measures, in contrast to TMS-EEG measures of TEPs. Then the authors come back to TMS-EEG and then again back to MEPs. This is rather confusing: TMS means TMS... the concept of MEP/ motor corticospinal excitability measures is not intuitive when using the term "TMS". I suggest using motor corticospinal excitability measures when referring to MEP/MEP-based measures of cortical excitability...) and M1TMS-EEG-evoked potentials (usually abbreviated to TEPs) to refer to TMS-EEG responses as measured here.

Throughout the manuscript, we now use the term TEPs when referring to TMS-EEG measures, and MEPs when referring to TMS-EMG measure. The use of TEPs vs. MEPs will make it easier for readers to follow which measures we are referring to.

Line 83: "As such, the precise origin of the pain mechanism cannot be localized." Please rephrase, the sentence conveys the idea that it is indeed possible to localize the origin of a pain mechanism with a different approach, and we know this is not currently possible, irrespective of the methodological setup.

We have replaced this with:

“This makes it unclear as to whether pain processes occur at the cortical, spinal or peripheral level.”

How can one predetermine the temperature that will be perceived as painful by someone else, and not base it on individual HPT? This is against principles of psychophysics. Please comment. Attesting all participants had HPT below 46 is important, but then being stimulated at 46C when our HPT is 45C is different from when our HPT is 39C. Please explain why the pain intensity was not standardised based on individual HPT.

Please refer to our response to the public review related to the issue

Line 38: "if we had used an alternative design with blocks of warm stimuli intermixed with blocks of painful stimuli, the warm stimuli blocks would not serve as a valid non-painful baseline". I do not understand why it is not possible to have a pain-free baseline, followed by a pain/warm sequence.

In our study, we had the choice of either intermixing blocks or to use a fixed sequence. Previous research suggests that pain alters neural excitability even after pain has subsided. In a recent meta-analysis (Chowdhury et al., 2022) we found effect sizes of 0.55-0.9 for MEP reductions 0-30 minutes after pain had resolved. As such, we avoided intermixing pain and warm blocks given subsequent warm blocks would not serve as a valid baseline, as each subsequent warm block would have residual effects from the previous pain blocks.

We have updated the manuscript to be clearer about why we used a fixed sequence:

“The pre-pain/pain/post-pain design has been commonly used in the TMS-MEP pain literature, as many studies have demonstrated strong changes in corticomotor excitability that persist beyond the painful period. Indeed, in a systematic review, we showed effect sizes of 0.55-0.9 for MEP reductions 0-30 minutes after pain had resolved (Chowdhury et al., 2022). As such, if we had used an alternative design with blocks of warm stimuli intermixed with blocks of painful stimuli, the warm stimuli blocks would not serve as a valid non-painful baseline”

Chowdhury, N. S., Chang, W. J., Millard, S. K., Skippen, P., Bilska, K., Seminowicz, D. A., & Schabrun, S. M. (2022). The Effect of Acute and Sustained Pain on Corticomotor Excitability: A Systematic Review and Meta-Analysis of Group and Individual Level Data. The Journal of Pain, 23(10), 1680-1696.

Please explain, and provide evidence that stimulation of people with predetermined temperatures is able to create warm/pain/warm sensations, without entraining pain in the last warm stimulation.

A previous study by Dube et al. (2011) used sequences of warm (36°C), painful and neutral (32° C) and found that participants did not experience pain at any time when the temperature was at a warm temperature of 36°C. We have now cited this study:

“Based on a previous study (Dubé & Mercier, 2011) which also used sequences of painful (50ºC) and warm (36°C) thermal stimuli, we did not anticipate that the stimulus in the pain block would entrain pain in the post-pain block”

Dubé, J. A., & Mercier, C. (2011). Effect of pain and pain expectation on primary motor cortex excitability. Clinical neurophysiology, 122(11), 2318-2323.

METHODS

It is not clear if participants with chronic pain, present in 20% of the general population, were excluded. If they were, please provide "how" in methods.

We excluded participants with a history or presence of acute/chronic pain. This has now been clarified:

“Participants were excluded if they had a history of chronic pain condition or any current acute pain”

Line 489: the definition of warm detection threshold is unusual, please provide a reference.

We used an identical method to Furman et al., (2020). We have made the reference to this clearer: “Warmth, cold and pain thresholds were assessed in line with a previous study (Furman et al., 2020)”

Furman, A. J., Prokhorenko, M., Keaser, M. L., Zhang, J., Chen, S., Mazaheri, A., & Seminowicz, D. A. (2020). Sensorimotor peak alpha frequency is a reliable biomarker of prolonged pain sensitivity. Cerebral Cortex, 30(12), 6069-6082.

In Experiment 2, please explain how the lack of randomisation between "pre-pain" and "pain" may have influenced results.

Given we tried to replicate Experiment 1’s methodology as close as possible (to isolate the source of the effect from Experiment 1) we chose to repeat the same sequence of blocks as Experiment 1: pre-pain followed by pain.

Given there was no conclusive evidence for a difference in N45 amplitude between pre-pain and post-pain conditions of Experiment 1 (Supplementary Figure 1), it is unlikely that the effect of pain was an order effect i.e., the explanation that successive thermal stimuli applied to the skin results an increase in the N45, regardless of whether the stimuli are painful or not.

We now discuss the issue of randomization:

“Lastly, future research should consider replicating our experiment using intermixed pain and no pain blocks, as opposed to fixed pre-pain and pain blocks, to control for order effects i.e. the explanation that successive thermal stimuli applied to the skin results an increase in the N45 peak, regardless of whether the stimuli are painful or not. However, we note that there was no conclusive evidence for a difference in N45 peak amplitude between pre-pain and post-pain conditions of Experiment 1 (Supplementary Figure 1), suggesting it is unlikely that the observed effects were an artefact of time”

Also, in Methods in general, disclose how pain intensity was assessed, and how.

Pain intensity was assessed using a verbal rating scale (0 = no pain, and 10 = most pain imaginable). We have provided more detail:

“During each 40 second thermal stimulus, TMS pulses were manually delivered, with a verbal pain rating score (0 = no pain, and 10 = worst pain imaginable) obtained between pulses. To avoid contamination of TEPs by verbal ratings, the subsequent TMS pulse was not delivered until the verbal rating was complete, and the participant was cued by the experimenter to provide the pain rating after each pulse”

Please explain how auditory masking was made during data collection.

Auditory masking noise was not played through the headphones, given that Experiment 2 controlled for auditory evoked potentials. We have made this clearer:

“Auditory masking was not used. Instead, auditory evoked potentials resulting from the TMS click sound were controlled for in Experiment 2”

Please explain if online TEP monitoring was used during data collection

Online TEP monitoring was not available with our EEG software. We have made this clearer in the manuscript:

“Online TEP monitoring was not available with the EEG software”

Line 499: what is subthreshold TMS here? You are measuring TEPs, and not MEPs initially, so you may have a threshold for MEPs and TEPs, which are not the same.

The intensity was calibrated relative to the MEP response (rather than TEP response) - this has now been clarified:

“… and the inclusion of a subthreshold TMS (90% of resting motor threshold) condition intermixed within both the pre-pain and pain blocks.”

Please provide a reference and a figure to illustrate the electric stimulation used in the sham procedure in Study 2

The apparatus for the electrical stimulation is shown in Figure 7A, and was based on previous papers using electrical stimulation over motor cortex to simulate the somatosensory aspect of real TMS (Chowdhury et al., 2022; Gordon et al., 2022; Rocchi et al., 2021). We have made this clearer:

“Electrical stimulation was based on previous studies attempting to simulate the somatosensory component of active TMS (Chowdhury et al., 2022; Gordon et al., 2022; Rocchi et al., 2021)”

Gordon, P. C., Jovellar, D. B., Song, Y., Zrenner, C., Belardinelli, P., Siebner, H. R., & Ziemann, U. (2021). Recording brain responses to TMS of primary motor cortex by EEG–utility of an optimized sham procedure. Neuroimage, 245, 118708.

Chowdhury, N. S., Rogasch, N. C., Chiang, A. K., Millard, S. K., Skippen, P., Chang, W. J., ... & Schabrun, S. M. (2022). The influence of sensory potentials on transcranial magnetic stimulation–Electroencephalography recordings. Clinical Neurophysiology, 140, 98-109.

Rocchi, L., Di Santo, A., Brown, K., Ibánez, J., Casula, E., Rawji, V., ... & Rothwell, J. (2021). Disentangling EEG responses to TMS due to cortical and peripheral activations. Brain stimulation, 14(1), 4-18.

It is not so common to use active electrodes for TMS-EEG. Please confirm the electrodes used and if they are c-ring TMS compatible and provide reference if otherwise (or actual papers recommending active ones)

To be more specific about the electrode type we have indicated:

“Signals were recorded from 63 TMS-compatible active electrodes (6mm height, 13mm width), embedded in an elastic cap (ActiCap, Brain Products, Germany), in line with the international 10-10 system”

A paper directly comparing TEPs between active and passive electrodes found no difference between the two and concluded TEPs can be reliably obtained using active electrodes (Mancuso et al., 2021). There is also evidence that active electrodes have better signal quality than passive electrodes at higher impedance levels (Laszlo et al., 2014).

This information has now been added to the paper:

“Active electrodes result in similar TEPs (both magnitude and peaks) to more commonly used passive electrodes (Mancuso et al., 2021). There is also evidence that active electrodes have higher signal quality than passive electrodes at higher impedance levels (Laszlo, Ruiz-Blondet, Khalifian, Chu, & Jin, 2014).”

There is a growing literature showing that monophonic pulses are not reliable for TEPs when compared to biphasic ones, please provide references. https://doi.org/10.1016/j.brs.2023.02.009

The reference provided by the reviewer states that biphasic and monophasic pulses both have advantages and disadvantages, rather than stating “monophonic pulses are not reliable for TEPs”. While there is some evidence that the artefacts resulting from monophasic pulses are larger than biphasic pulses, the EEG signal still returns to baseline levels within 5ms of the TMS pulse (Rogasch et al., 2013). Moreover, one paper (Casula et al. 2018) found that the resultant TEPs evoked by monophasic pulses are larger than those resulting from biphasic pulses. The authors postulated that monophasic pulses are more effective at activating widespread cortical areas than biphasic pulses. Ultimately the reference provided by the reviewer concludes that “effect of pulse shape on TEPs has not been systematically investigated and more studies are needed”.

Rogasch, N. C., Thomson, R. H., Daskalakis, Z. J., & Fitzgerald, P. B. (2013). Short-latency artifacts associated with concurrent TMS–EEG. Brain stimulation, 6(6), 868-876.

Casula, E. P., Rocchi, L., Hannah, R., & Rothwell, J. C. (2018). Effects of pulse width, waveform and current direction in the cortex: A combined cTMS-EEG study. Brain stimulation, 11(5), 1063-1070.

In most heads, a pulse in the PA direction is not obtained by a coil oriented 45o to the midline. The later induced later-medial pulses, good to obtain MEPs

We followed previous studies measuring MEPs from the ECRB elbow muscle (Schabrun et al., 2016; de Martino et al., 2019) whereby the TMS coil handle was angled at 45 degrees relative to the midline in order to induce a posterior-anterior current. We are not aware of literature that shows that the 45 degrees orientation does not induce a posterior anterior current in most heads.

Schabrun, S. M., Christensen, S. W., Mrachacz-Kersting, N., & Graven-Nielsen, T. (2016). Motor cortex reorganization and impaired function in the transition to sustained muscle pain. Cerebral Cortex, 26(5), 1878-1890.

De Martino, E., Seminowicz, D. A., Schabrun, S. M., Petrini, L., & Graven-Nielsen, T. (2019). High frequency repetitive transcranial magnetic stimulation to the left dorsolateral prefrontal cortex modulates sensorimotor cortex function in the transition to sustained muscle pain. Neuroimage, 186, 93-102.

The definition of RMT is (very) unusual. RMT provides small 50microV MEPs in 50% of times. If you obtain MEPs at 50microV you are supra threshold!

The TMS motor threshold assessment tool calculates threshold in the same manner as other threshold tools – it calculates the intensity that elicits an MEP of 50 microvolts, 50% of the time. We have made this clearer:

“The RMT was determined using the TMS motor thresholding assessment tool, which estimates the TMS intensity required to induce an MEP of 50 microvolts with a 50% probability using maximum likelihood parametric estimation by sequential testing (Awiszus and Borckardt, 2011). This method has been shown to achieve the accuracy of methods such as the Rossini-Rothwell method (Rossini et al., 1994; Rothwell et al., 1999) but with fewer pulses (Qi et al., 2011; Silbert et al., 2013).”

Please inform the inter TMS pulse interval used of TEPs and whether they were randomly generated.

The pulses were delivered manually – the interval was not randomly generated – as stated:

“As TMS was delivered manually, there was no set interpulse interval. However, the 40 second stimulus duration allowed for 11 pulses for each heat stimulus …. (~ 4 seconds in between …)”

Why have you stimulated suprathreshold on M1 when assessing TEP´s? The whole idea is that large TEPs can be obtained at lower intensities below real RMT and that prevents re-entering loops of somatosensory and joint movement inputs that insert "noise" to the TEPs.

The suprathreshold intensity was used to concurrently measure MEPs during pre-pain, pain and post-pain blocks.

We have made this clearer:

“The test stimulus intensity was set at 110% RMT to concurrently measure MEPs and TEPs during pre-pain, pain and post-pain blocks.”

The influence of re-afferent muscle activity was controlled for in Experiment 3.

Did you assess pain intensity after each of the TEP pulses? Please discuss how such a cognitive task may have influenced results

Pain intensity was assessed after each TMS pulse, as stated:

“TMS pulses were manually delivered, with a verbal pain rating score (0 = no pain, and 10 = most pain imaginable) obtained between pulses”

Reviewer 3 also brought up a concern of whether the verbal rating task might have influenced the TEPs. However, it is unlikely that the task contaminated the TEP response as the subsequent TMS pulse was not delivered until the verbal rating was complete and given that each participant was cued by the experimenter to provide the pain rating after each pulse (rather than the participant giving the rating at any time). We have made this clearer where we state:

“To avoid contamination of TEPs by verbal ratings, the subsequent TMS pulse was not delivered until the verbal rating was complete, and the participant was cued by the experimenter to provide the pain rating after each pulse”

The QST approach is unusual. Please confirm the sequence of CDT, WDT and HPT were not randomised and that no interval beyond 6sec were used. Proper references are welcome.

In line with a previous study (Furman et al., 2020), the sequence of the CPT, WDT and HPT were not randomized, and the interval was not more than 6 seconds.

We have made this clearer:

“A total of three trials was conducted for each test to obtain an average, with an interstimulus interval of six seconds. The sequence of cold, warmth and pain threshold was the same for all participants (Furman et al. 2020)”

Performing 60 pulses for TEPs is unusual, and against the minimum number in recommendations

Please explain and comment.https://doi.org/10.1016/j.brs.2023.02.009

Please refer to our previous response to this concern in the public reviews.

Line 578: when you refer to "heat" the reader may confound warm/heat with heat meaning suprathreshold. Please revise the wording.

We have now replaced the word heat stimulus with thermal stimulus.

Why were Bayesian statistics used instead as frequentist ones?

We have made this clearer:

“Given we were interested in determining the evidence for pain altering TEP peaks in certain conditions (e.g., active TMS) and pain not altering TEP peaks in other conditions (sham TMS), we used a Bayesian approach as opposed to a frequentist approach, which considers the strength of the evidence for the alternative vs. null hypothesis”

RESULTS

There is a huge response with high power after 100ms- Please discuss if you believe auditory potentials may have influenced it.

It is indeed possible that auditory potentials were present at 100ms. We now state:

“Indeed, the signal at ~100ms post-TMS from Experiment 1 may reflect an auditory N100 response”

The presence of auditory contamination does not impact the main conclusions of the paper given this was controlled for in Experiment 2.

Please discuss how pain ranging from 3-10 may have influenced results in the "PAIN" situation,

It is anticipated that the fixed thermal stimulus intensity approach would lead to large variations in pain ratings (Adamczyk et al., 2022). This is a recommended approach when the aim of the research is to determine relationships between neurophysiological measures and individual differences in pain sensitivity (Adamczyk et al., 2022). Indeed, we were interested in whether alterations in neurophysiological measures were associated with pain intensity, and we found that higher pain ratings were associated with smaller reductions in MEP amplitude and larger increases in N45 amplitude.

Adamczyk, W. M., Szikszay, T. M., Nahman-Averbuch, H., Skalski, J., Nastaj, J., Gouverneur, P., & Luedtke, K. (2022). To calibrate or not to calibrate? A methodological dilemma in experimental pain research. The Journal of Pain, 23(11), 1823-1832.

Please indicate if any participants offered pain after warm stimulation ( possible given secondary hyperalgesia after so many plateaux of heat stimulation).

As stated in the results “All participants reported 0/10 pain during the pre-pain and post-pain blocks”.

Please discuss the potential effects of having around 10% of "bad channels) In average per experiment per participants, its impacts in source localisation and in TEP measurement. Same for >5 epochs excluded by participant.

The number of bad channels has been incorrectly stated by the reviewer as being 10% on average per experiment per participant, whereas the correct number of reported bad channels was 3%, 4.7% and 9.8% for Experiment 1, 2 and 3 respectively (see supplementary material). These numbers are below the accepted number of bad channels to interpolate (10%) in EEG pipelines (e.g., Debnath et al., 2020; Kayhan et al., 2022), so it is unlikely that our channel exclusions significantly influenced the quality of our source localization an TEP data.

Debnath, R., Buzzell, G. A., Morales, S., Bowers, M. E., Leach, S. C., & Fox, N. A. (2020). The Maryland analysis of developmental EEG (MADE) pipeline. Psychophysiology, 57(6), e13580.

Kayhan, E., Matthes, D., Haresign, I. M., Bánki, A., Michel, C., Langeloh, M., ... & Hoehl, S. (2022). DEEP: A dual EEG pipeline for developmental hyperscanning studies. Developmental cognitive neuroscience, 54, 101104.

The number of excluded epochs is unlikely to have influenced the results given there was evidence for no difference in the number of rejected epochs between conditions (E1 BF10 = 0.145, E2 BF10 = 0.27, E3 BF10 = 0.169 – these BFs have now been reported in the supplementary material), and given the reliability of the N45 was high (see response to previous comment on the number of trials per condition).

HPT of 42.9 {plus minus} 2.5{degree sign}C means many participants had HPT close to 46oC. Please discuss

While some participants did indeed have pain thresholds close to 46 degrees, they nonetheless reported pain during the test blocks. While such participants may have reported less pain compared to others, we aimed for larger variations in pain ratings, given one of the research questions was to determine why pain intensity differs between individuals (given the same noxious stimulus). Indeed, we showed that this variation was meaningful (pain intensity was related to alterations in N45 and MEP amplitude).

Please explain the sentence : line 139 "As such, if we had used an alternative design with blocks of warm stimuli intermixed with blocks of painful stimuli, the warm stimuli blocks would not serve as a valid non-painful baseline." I cannot see why.

Please refer to our previous point on why the fixed sequence was included.

And on the top of that heat was not individualised according to HPT.

Please refer to our previous point on why we used a fixed stimulus approach.

Sequences of warm/heat were not randomised. Please refer to our previous point on the why the sequence of blocks was not randomized.

Line 197: "However, as this is the first study investigating the effects of experimental pain on TEPsamplitude, there were no a priori regions or timepoints of interest to compare betweenconditions". This is not clear. It means you have not measured the activity (size of the N45) under the electrode closest to the TMS coil? The TEP is supposed to by higher under the stimulated target/respective corresponding electrode…

We are not aware of any current recommendations that state that the region of interest should be based on the site of stimulation. The advantage of TMS-EEG is that it allows characterisation of cortical excitability changes throughout the brain, not just the site of stimulation. We based our region of interest on a cluster-based permutation analysis, as recommended by Frömer, Maier, & Abdel Rahman, (2018)

Frömer, R., Maier, M., & Abdel Rahman, R. (2018). Group-level EEG-processing pipeline for flexible single trial-based analyses including linear mixed models. Frontiers in neuroscience, 12, 48.

Please explain where N45 values came from.

The N45 was calculated using the TESA peak function (Rogasch et al., 2017) which identifies a data point which is larger/smaller than +/- 5 data points within a specified time window (e,g, 40-70ms post-TMS as in the present study). Where multiple peaks are found, the amplitude of the largest peak is returned. Where no peak is found, the amplitude at the specified latency is returned.

Rogasch, N. C., Sullivan, C., Thomson, R. H., Rose, N. S., Bailey, N. W., Fitzgerald, P. B., ... & Hernandez-Pavon, J. C. (2017). Analysing concurrent transcranial magnetic stimulation and electroencephalographic data: A review and introduction to the open-source TESA software. Neuroimage, 147, 934-951.

If only the cluster assessment was made please provide the comparison between P45 from the target TMS channel location in pre pain vs pain.

We assume the reviewer is referring to the N45 rather than P45, and that by “target” TMS channel they are referring to the stimulated region.

We first clarify that there is no “target” channel given the motor hotspot differs between individuals and so the channel that is closest to the site of stimulation will always differ.

Secondly, as stated above, we are not aware of any current recommendations in TMS-EEG research that states that the region of interest for TEP analysis should be based on the site of stimulation. The advantage of TMS-EEG is that it allows characterisation of cortical excitability throughout the brain, not just the site of stimulation. If we based our ROI on the target channel only, we would lose valuable information about excitability changes occurring in other brain regions.

Lastly, the N45 was localized at frontocentral electrodes, which is also where the cluster differences emerged. As such, we do not believe it would be informative to compare N45 peak amplitude at the region of stimulation.

Also explain how correction for multiple comparisons was made

Please refer to our response to the public review related to this issue.

And report data from pain vs post-pain.

The pain vs. post-pain comparisons are now reported in the Supplementary material.

There is a strong possibility the response at N85 is an auditory /muscle signal. Please provide the location of this response.

We have opted not to include the topography at 85ms in the main paper as it would introduce too much clutter into the figures (which are already very dense), and because the topography was very similar to the topography at 100ms. As an example, for the reviewer, in Author response image 1 we have shown the topography for the pre-pain condition of Experiment 1.

Author response image 1.

Experiment 2: I have a strong impression both active TEPs and sham TEPs were contaminated by auditory (and muscle) noise. Please explain.

While it possible that auditory noise may have influenced TEPs in the active and sham groups, it does not impact the main conclusions of the paper, given that the purpose of the sham condition was to control for auditory and somatosensory stimulation resulting from TMS.

While muscle activity may also affect have influenced the TEPs in active and sham conditions, we used fastICA in all conditions to suppress muscle activity. The fastICA algorithm (Rogasch et al., 2017) runs an independent component analysis on the data, and classifies components as neural, TMS-evoked muscle, eye movements and electrode noise, based on a set of heuristic thresholding rules (e.g., amplitude, frequency and topography of the components). Components classified as TMS-evoked muscle/other muscle artefacts are then removed. In the supplementary material, we further report that the number of components removed did not differ between conditions, suggesting the impact of muscle artefacts are not larger in some conditions vs. others.

Rogasch, N. C., Sullivan, C., Thomson, R. H., Rose, N. S., Bailey, N. W., Fitzgerald, P. B., ... & Hernandez-Pavon, J. C. (2017). Analysing concurrent transcranial magnetic stimulation and electroencephalographic data: A review and introduction to the open-source TESA software. Neuroimage, 147, 934-951.

Experiment 3: One interpretation can be that both supra and sub-threshold TMS were leading to somatosensory re-afferent responses, based on the way RMT was calculated, which hyper estimate the RMT and delivers in reality 2 types of supra-threshold stimulations. Please discuss

Please refer to our response to the public review related to this issue.

Please provide correlation between N45 size and MEPs amplitudes.

This has now been included:

“There was no conclusive evidence of any relationship between alterations in MEP amplitude during pain, and alterations in N100, N45 and P60 amplitude during pain (see supplementary material).”<br /> The supporting statistics for these analyses have been included in the supplementary material.

DISCUSSION

Line 303: " The present study determined whether acute experimental pain induces alterations in cortical inhibitory and/or facilitatory activity observed in TMS-evoked potentials".

Well, no. The study assessed the N45, and was based on it. It did not really explore other metrics in a systematic fashion. P60 and N100 changes were not replicated in experiments 2 and 3..

We assume the reviewer is stating that we did not assess other TEP peaks (such as the N15, P30 and P180). However, we did indeed assess these peaks in a systematic fashion. First, we identified the ROI by using a cluster-based analysis. This is a recommended approach when the ROI is unclear (Frömer, Maier, & Abdel Rahman, 2018). We then analysed the TEP representing the mean voltage across the electrodes within the cluster, and then identified any differences in all peaks between conditions (not just the N45). This has been made clearer in the manuscript.

This has now been included:

“For all experiments, the mean TEP waveform of any identified clusters from Experiment 1 were plotted, and peaks (e.g., N15, P30, N45, P60, N100) were identified using the TESA peak function (Rogasch et al., 2017)”

Frömer, R., Maier, M., & Abdel Rahman, R. (2018). Group-level EEG-processing pipeline for flexible single trial-based analyses including linear mixed models. Frontiers in neuroscience, 12, 48.

And the N45 is not related to facilitatory or inhibitory activity, it is a measure of an evoked response indicating excitability

Evidence suggests the N45 is mediated by GABAAergic neurotransmission (inhibitory activity), as drugs which increase GABAA receptor activity increase the amplitude of the N45 (Premoli et al., 2014) and drugs which decrease GABAA receptor activity decrease the amplitude of the N45 (Darmani et al., 2016). As such, we and various other empirical papers (e.g., Bellardinelli et al., 2021; Noda et al., 2021; Opie at 2019 ) and review papers (Farzan & Bortoletto, 2022; Tremblay et al., 2019) have interpreted changes in the N45 peak as reflecting changes in cortical inhibitory/GABAA mediated activity.

Premoli, I., Castellanos, N., Rivolta, D., Belardinelli, P., Bajo, R., Zipser, C., ... & Ziemann, U. (2014). TMS-EEG signatures of GABAergic neurotransmission in the human cortex. Journal of Neuroscience, 34(16), 5603-5612.

Belardinelli, P., König, F., Liang, C., Premoli, I., Desideri, D., Müller-Dahlhaus, F., ... & Ziemann, U. (2021). TMS-EEG signatures of glutamatergic neurotransmission in human cortex. Scientific reports, 11(1), 8159.

Darmani, G., Zipser, C. M., Böhmer, G. M., Deschet, K., Müller-Dahlhaus, F., Belardinelli, P., ... & Ziemann, U. (2016). Effects of the selective α5-GABAAR antagonist S44819 on excitability in the human brain: a TMS–EMG and TMS–EEG phase I study. Journal of Neuroscience, 36(49), 12312-12320.

Noda, Y., Barr, M. S., Zomorrodi, R., Cash, R. F., Lioumis, P., Chen, R., ... & Blumberger, D. M. (2021). Single-pulse transcranial magnetic stimulation-evoked potential amplitudes and latencies in the motor and dorsolateral prefrontal cortex among young, older healthy participants, and schizophrenia patients. Journal of Personalized Medicine, 11(1), 54.

Farzan, F., & Bortoletto, M. (2022). Identification and verification of a'true'TMS evoked potential in TMS-EEG. Journal of neuroscience methods, 378, 109651.

Opie, G. M., Foo, N., Killington, M., Ridding, M. C., & Semmler, J. G. (2019). Transcranial magnetic stimulation-electroencephalography measures of cortical neuroplasticity are altered after mild traumatic brain injury. Journal of Neurotrauma, 36(19), 2774-2784.

Tremblay, S., Rogasch, N. C., Premoli, I., Blumberger, D. M., Casarotto, S., Chen, R., ... & Daskalakis, Z. J. (2019). Clinical utility and prospective of TMS–EEG. Clinical Neurophysiology, 130(5), 802-844.

Line 321: why have you not measured SEPs in experiment 3?

It is not possible to directly measure the somatosensory evoked potentials resulting from a TMS pulse, given that the TMS pulse produces a range of signals including cortical activity, muscle/eye blink responses, auditory responses, somatosensory responses and other artefacts. While some researchers attempt to isolate the SEP from TMS using pre-processing methods such as ICA, others use control conditions such as sensory sham conditions (to control for the “tapping” artefact) or subthreshold intensity conditions (to control for reafferent muscle activity), as we have done in Experiment 2 and 3 of our study.

We have now stated this in the manuscript:

“As it is extremely challenging to isolate and filter these auditory and somatosensory evoked potentials using pre-processing pipelines, masking methods have been used to suppress these sensory inputs, (Ilmoniemi and Kičić, 2010; Massimini et al., 2005). However recent studies have shown that even when these methods are used, sensory contamination of TEPs is still present, as shown by commonalities in the signal between active and sensory sham conditions that mimic the auditory/somatosensory aspects of real TMS (Biabani et al., 2019; Conde et al., 2019; Rocchi et al., 2021). This has led many leading authors (Biabani et al., 2019; Conde et al., 2019) to recommend the use of sham conditions to control for sensory contamination”

Line 365: SICI is dependent on GABAa activity. But the way the text is written if conveys the idea that TMS pulses "activate" GABA receptors, which is weird...Please rephrase.

This has now been reworded.

“SICI refers to the reduction in MEP amplitude to a TMS pulse that is preceded 1-5ms by a subthreshold pulse, with this reduction believed to be mediated by GABAA neurotransmission (Chowdhury et al., 2022)”

Reviewer #3 (Recommendations For The Authors):

-Key references Ye et al., 2022 and Che et al., 2019 need to be included in the reference list.

These references have now been included in the reference list.

-Heat pain stimuli and TMS stimuli are applied simultaneously. Sometimes the term "stimulus" is used without specifying whether it refers to TMS pulses or heat pain stimuli. Clarifying this whenever the word "stimulus" is used would enhance clarity for the reader.

We have now clarified the use of the word “stimulus” throughout the paper.

-Panels A-D in Figure 6 should be correctly labeled in the text and the figure legend.

Figure 6 Panel labels have now been amended.

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

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Reply to the reviewers

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

1. General Statements [optional]

In this paper we describe the new finding that the epicardial deposits the extracellular matrix component laminin onto the apical ventricular surface during cardiac development. We identify a novel role for the apicobasal polarity protein Llgl1in timely emergence of the epicardium and deposition of this apical laminin, alongside a requirement for Llgl1 in maintaining integrity of the ventricular wall at the onset of trabeculation.

We thank the reviewers for their very positive appraisal of our manuscript, and for their helpful suggestions for useful revisions. In particular we would like to highlight the broad interest they feel this manuscript holds, not only contributing conceptual advances to our understanding of multiple aspects of cardiac development, but also to cell and developmental biologists working in epithelial polarity and extracellular matrix function. We also note their positive appraisal of the rigor of the study and quality of the manuscript.

2. Description of the planned revisions

Reviewer 1

1a) It is mentioned that llgl1 CRISPR/Cas9 mutants are viable as adults on pg. 3 of the Results section. Have the authors examined heart morphology in these mutants in juvenile or adult fish?

We have some historical data on adult llgl1 mutant survival that we plan to include in the study.

Reviewer 2

2a) The authors note an interesting observation with apical and basal laminin deposition dynamics surrounding cardiomyocytes, and that Llg1 has a role in apical Laminin deposition (however, highly variable at 80 hpf as Figure 3M shows). They carry out a very nice study in which they overexpress Llgl1 tagged with mCherry in the myocardium and show that there is no rescue of the extruding cardiomyocyte defect or Laminin deposition. However, there is still a possibility that the tagged Llgl1 in the transgene Tg(myl7:Llg1-mCherry)sh679 might not be functional due to improper protein folding or interference by the mCherry tag. The authors should supplement their approach with a transplantation experiment to generate mosaic llgl1 mutant animals and assess whether llgl1 mutant cardiomyocytes extrude at a higher rate than the control. This would provide definitive evidence that Llg1l acts in a cell non-autonomous manner.

We agree with the reviewer, and propose to perform transplant experiments, transplanting cells from llgl1 mutants into wild type siblings, and quantify cell extrusion to determine whether llgl1 mutant cells are extruded more frequently than wild type.

2b) The data in this manuscript appears to point that Llgl1 regulates Laminin deposition mainly in epicardial cells to regulate their dissemination/migration across the ventricular myocardial surface. It would be important to test this cell-autonomous function with the transplant experiment (above point) and examine whether llgl1 mutant epicardial cells fail to migrate and deposit Laminin. It might be possible to perform a rescue experiment through overexpression of Llgl1 in epicardial cells (if possible, there is a tcf21:Gal4 line available).

Similar to above, we propose to perform transplant experiments, transplanting cells from llgl1 mutants or wild type siblings into wild type siblings or llgl1 mutants, respectively, and in this instance quantify contribution of transplanted cells to epicardial coverage.

2c) In the Discussion, the authors propose that Llgl1 acts in two ways: Laminin deposition in epicardial cells that suppress cell extrusion and polarity regulation in cardiomyocytes to promote trabeculation. It would be important to test the second hypothesis on trabeculation and polarity regulation by using the myocardial-specific overexpression/rescue of Llgl1 in llgl1 mutants, and then quantifying the trabeculating cardiomyocytes and analyze Crb2a localization. This experiment can distinguish whether this trabeculation phenotype is rescued independently of the apical Laminin deposition that has been included in Figure S5.

To help address the second part of our hypothesis laid out in the discussion, we propose to quantify trabecular organisation and Crb2a localisation in llgl1 mutants either carrying the myl7:llgl1-mCherry construct, or mCherry-negative controls.

2d) The potential mis-localization of Crb2a in the llgl1 mutants is interesting, but this effect appears to be quite mild, and as the authors note, resolve by 80 hpf. Considering the role of Lgl in Drosophila in shifting Crb complex localization during early epithelial morphogenesis, it would be worth performing the analysis at earlier timepoints (between 55 and 72 hpf) to determine whether Llgl1 is indeed important for the progressive apical relocalization of Crb2a.

We will expand our description of this in the mutants by performing analysis of Crb2a at earlier timepoints in the llgl1 mutant (55hpf and 60hpf).

2e) OPTIONAL: It might be worth testing other antibodies that could mark the apical (particularly aPKC which is known to phosphorylate and regulate the Crb complex) and basolateral domains (Par1, Dlg) of the cardiomyocytes to definitively conclude that the epithelial integrity of the cells is affected. Although there are no reports of working antibodies marking the basal domain in zebrafish, there is at least a Tg(myl7:MARCK3A-RFP) line published (Jimenez-Amilburu et al. (2016)) - which the authors can inject to examine the localization in mosaic hearts.

We plan to assess localisation of aPKC (see section 4 for response to other suggested polarity protein analyses).

2f) Have the authors quantified the numbers of total cardiomyocytes in llgl1 mutants to correlate how many cells are lost as a consequence of extrusion? What is the physiological impact of this extrusion (ejection fraction, total cardiac volumes, sarcomere organization)?

We have some of this data already which we will include in the manuscript (cell number, myocardial volume). We agree that the analysis of cardiac function could be more extensive, and we will perform more detailed analysis of cardiac function, including e.g. ejection fraction. Sarcomere organisation has been previously described in llgl1 mutants by Flinn et al, 2020, so we do not plan to replicate this data.

2g) The lamb1a and lamc1 mutant phenotypes were nicely analyzed. However, there is basement membrane deposition on both the apical and basal sides of the cardiomyocytes. Therefore, it is unclear whether the cardiomyocyte extrusion is completely caused by loss of apical basement membrane, or whether the loss of basal basement membrane could compromise the myocardial tissue integrity. The authors should clarify this conclusion in the text.

We will address this further in the text, but will also include 55hpf Laminin staining data for llgl1 mutants to reinforce our message.

2h) The authors note that Llgl1-mCherry in the Tg(myl7:Llg1-mCherry)sh679 line localizes to the basolateral domain of the cardiomyocytes, which is valuable confirmation that Llgl1 protein is spatially restricted. However, only 1 timepoint (55 hpf) is noted. It would be important to perform Llgl1 localization across different developmental timepoints (at least until 80 hpf) to examine the dynamics of this protein during trabeculation and apical extrusion, and potentially correlate it with Crb2a localization for a better understanding of the apicobasal machinery in cardiomyocytes.

We already have some of this data and will include extra timepoints in a revised version of the manuscript

2i) The phenotypes of llgl1 mutants described here differ compared to the previous study by Flinn et al. (2020). In particular, whereas the mutants generated in this study have only mild pericardial edema and are adult viable, approximately one third of llgl1mw3 (Flinn et al. (2020)) died at 6 dpf. Is this caused by the different natures of the mutations in the llgl1 gene? Is there a possibility that the llgl1sh598 is a hypomorphic allele since the targeted deletion is in a more downstream sequence (in exon 2) compared to the llgl1mw3 (deletion in exon 1) allele?

We thank the reviewer for noticing these subtle differences between the two llgl1 mutants. Indeed, while we occasionally see llgl1sh598 mutants with the severe phenotype described by Flinn et al, this is a small minority which we did not quantify. Our mutation is indeed slightly further downstream than that described by Flinn et al, however we believe that this will have a neglible effect on Llgl1 function. Our llgl1sh589 mutation results in truncation shortly into the WD40 domain, and importantly completely lacks the Lgl-like domain, which is responsible for the specific function of Llgl1 likely through its ability to interact with SNAREs to regulate cargo delivery to membranes (Gangar et al, Current Biology 2005).

Interestingly, Flinn et al report no increased phenotypic severity in their maternal-zygotic llgl1 mutants when compared to zygotic mutants. Conversely, we often observed very severe phenotypes in MZ llgl1sh589 mutants, including failure of embryos during blastula stages, apparently through poor blastula integrity. We did not include this information in the manuscript due to space constraints. However, we argue that together these differences between the two alleles may not be due to hypomorphism of our llgl1sh589 allele, but rather differences in genetic background that may amplify specific phenotypes. We plan to include a short sentence summarising the above in combination with planned experiments described below to address the reviewer’s next comment.

2j) Suggested experiment: qPCR of regions downstream of the deletion to make sure that the transcript is absent/reduced in the llgl1sh598 mutants. Alternatively, immunostaining or Western blot would be an even better option to ensure there is no Llgl1 protein production - there is an anti-Llgl1 antibody available that works for Western blots in zebrafish (Clark et al. (2012)).

We plan to analyse llgl1 expression in llgl1 mutants using qPCR.

Reviewer 3

3a) Major - the authors describe that llgl1 mutants exhibit transient cardiac edema at 3 dpf, which is resolved by 5 dpf, and claim that the mutants are viable. This statement needs to be better supported - What is the proportion of mutants that survive to adulthood? The embryonic phenotypes are pretty variable - are the mutants that survive the ones with a less severe phenotype? Is there a gross defect in the adult heart of these animals?

In line with comments from Reviewers 1 and 2 above, we will include a description of the data we have from adult animals (historical data, not generation of new animals).

3b) Major - Many of the phenotypes described here -most importantly, the defects on epicardial development- could result from hemodynamic defects in llgl1 mutants. The authors claim that function is unaffected in these animals, but this has only been addressed by measuring heartbeat. The observation that the cardiac function in these animals is normal would conflict with a previous description (PMID: 32843528) that demonstrates that llgl1 mutant animals show significant hemodynamic defects, which would cause epicardial defects. Thus, this aspect of the work needs to be better addressed.

In line with our comments to point 2f) from Reviewer 2, we will perform a more in-depth functional analysis on llgl1 mutant larvae.

3c) The phenotypes related to forming multiple layers in the heart (Fig. 1) could be more convincing. In some figures, the authors use a reporter that labels the myocardial cell membrane, but in Figure 1 this is not used. Showing a myocardial membrane marker (for example, the antibody Alcama, Zn-8) would significantly strengthen this observation.

We will describe trabecular phenotypes in more detail using the suggested antibody to highlight membranes.

3d) The analysis of Crumbs redistribution (Fig. 2) is quite interesting. Still, given that the authors have a transgenic model to rescue llgl1 expression in cardiomyocytes, they could move from correlative evidence to experimental demonstration of the role of llgl1 in Crumbs localization.

Similar to our response to comment 2c) from Reviewer 2, we plan to address this

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

Reviewer 1:

Although information is provided in the introduction and discussion on the role of the Llgl1 homolog in Drosophila and speculation on LLGL1 contributing to heart defects in SMS patients in the discussion, have Llgl1 homologs been examined in other vertebrate animal models during heart development or regeneration?

With the exception of the Flinn et al paper, we find no published studies assessing the role of Llgl1 in heart development or regeneration in other vertebrates, and have updated the introduction to highlight this fact:

‘Zebrafish have two Lgl homologues, llgl1 and llgl2, and llgl1 has previously been shown to be required for early stages of heart morphogenesis (Flinn et al. 2020). However, although Llgl1 expression has also been reported in the developing mouse heart and both adult mouse and human hearts (Uhlén et al. 2015; Klezovitch et al. 2004), whether llgl1 plays a role in ventricular wall development has not been examined.’

In Fig. 4J-M', there is no Cav1 signals after wt1a MO but still laminin signals. Where these laminins come from?

The residual laminin staining observed in wt1a morphants is located at the basal surface of cardiomyocytes (while the apical laminin signal is lost, in line with the epicardial deposition of laminin at the apical ventricle surface). This basal laminin is likely deposited earlier during heart tube development by either the myocardium, endocardium or both, and thus unaffected by later formation of the epicardium. We reason this since a) it is present at the basal cardiomyocyte surface at 55hpf (see Fig 2); b) we have previously identified both myocardial and endocardial expression of laminin subunits at 26hpf and 55hpf (Derrick et al, Development, 2021); c) sc-RNA-seq analysis of hearts at 48hpf demonstrates that laminin subunits, e.g. lamc1 are expressed in myocardial and endocardial cells (Nahia et al, bioRxiv, 2023), also in line with our previous ISH analysis. We have included a sentence to reflect this in the results section:

Conversely, *wt1a* morphants retain deposition of laminin at the basal CM surface, likely from earlier expression and deposition of laminin by either myocardial or endocardial cells (Derrick et al. 2021; Nahia et al. 2023), which is unaffected by later epicardial development.

On page 3 of the manuscript, Fig. 1A should be included with Fig. 1B in the first sentence of paragraph 2 of the Results subsection "Llgl1 regulates ventricular wall integrity and trabeculation".

Amended

It would be beneficial to readers to briefly describe what cell type the transgenic reporters label when mentioned in the Results section to help readers unfamiliar with zebrafish.

We have updated the text to read:

We further analysed heart morphology using live lightsheet microscopy of *Tg(myl7:LifeActGFP);Tg(fli1a:AC-TagRFP)* double transgenic wild-type and *llgl1* mutant embryos, allowing visualisation of myocardium (green) and endocardium (magenta) respectively. Comparative analysis of overall heart morphology between 55hpf and 120hpf when looping morphogenesis is complete, revealing that *llgl1* mutants continue to exhibit defects in heart morphogenesis (Fig S1S-X).

Reviewer 3

(Optional) There is laminin in the luminal side of the heart before there is any epicardial invasion. What is the source of this laminin? The techniques the authors have used (i.e., chromogenic ISH) are fine, but a more detailed analysis using fluorescent ISH (i.e., RNAScope) would be much more definitive.

This is related to our response to Reviewer 1 (above) – where we have included the following text included in manuscript: Conversely, *wt1a* morphants retain deposition of laminin at the basal CM surface, likely from earlier expression and deposition of laminin by either myocardial or endocardial cells (Derrick et al. 2021; Nahia et al. 2023), which is unaffected by later epicardial development. We hope this clarifies our proposed origins for the earlier laminin deposition.

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

Reviewer 1:

As pan-epicardial transgenes like tcf21 reporters have been widely used, the authors should use such reporters to verify the expression of laminin gene expression in epicardial cells, and the efficacy and efficiency of depleting epicardial cells after wt1 MO injection.

Several studies have demonstrated that the epicardium is not a heterogeneous population – for example, tcf21 is not expressed in all epicardial cells and thus not a pan-epicardial reporter (Plavicki et al, BMC Dev Biol, 2014, Weinberger et al, Dev Cell, 2020) – the suggested analysis would not necessarily be conclusive, and more detailed study would require acquisition of three new transgenic lines. Furthermore, we believe the evidence we present in the paper supports our claim: 1) We show expression of two laminin subunits in a thin mesothelial layer directly adjacent to the myocardium, specifically in the location of the epicardium; 2) sc-RNA seq analyses have also identified laminin expression in epicardial cells at 72hpf (where lamc1a is identified as a marker of the epicardium); 3) We demonstrate 100% efficacy of our wt1a knockdown as assayed by Cav1 expression, an established epicardial marker (Grivas et al, 2020, Marques et al, 2022) which in sc-RNA seq data is expressed at high levels broadly in the epicardial cell population (Nahia et al, 2023), representing a good assay for presence of epicardium. However, we propose to perform ISH analysis of laminin subunit expression in wt1a MO to investigate whether the mesothelial laminin-expressing layer we observe adjacent to the myocardium is absent upon loss of wt1a.

Reviewer 2:

The data in this manuscript appears to point that Llgl1 regulates Laminin deposition mainly in epicardial cells to regulate their dissemination/migration across the ventricular myocardial surface. It would be important to test this cell-autonomous function with the transplant experiment (above point) and examine whether llgl1 mutant epicardial cells fail to migrate and deposit Laminin. It might be possible to perform a rescue experiment through overexpression of Llgl1 in epicardial cells (if possible, there is a tcf21:Gal4 line available).

We do not propose to perform this experiment using a tcf21:Gal4 line, as this would likely require at least 6 months to either import and quarantine, or generate the necessary stable lines. Furthermore, as mentioned above, tcf21 is not a pan-epicardial marker, and the extent and timing of the Gal4:UAS system may make this challenging to determine whether llgl1 has been expressed early or broadly enough. We will instead attempt transplantation experiments.

OPTIONAL: It might be worth testing other antibodies that could mark the apical (particularly aPKC which is known to phosphorylate and regulate the Crb complex) and basolateral domains (Par1, Dlg) of the cardiomyocytes to definitively conclude that the epithelial integrity of the cells is affected. Although there are no reports of working antibodies marking the basal domain in zebrafish, there is at least a Tg(myl7:MARCK3A-RFP) line published (Jimenez-Amilburu et al. (2016)) - which the authors can inject to examine the localization in mosaic hearts.

We will assess localisation of aPKC, but we do not plan to analyse the other components. Analysis of basolateral domains (Par1, Dlg, Mark3a-RGP), will not necessarily assess epithelial integrity, as suggested, but rather apicobasal polarity – which we already assess using Crb2a, and additionally plan to assess aPKC to accompany the Crb2a analysis. Since the reviewer suggests this as an optional experiment we prioritise their other suggested experiments that we think more directly address the main messages of the manuscript.

OPTIONAL: Gentile et al. (2021) found that reducing heartbeat led to decreased cardiomyocyte extrusion in snai1b mutants. The authors could look into the contribution of mechanical pressure through contraction in the apical cardiomyocyte extrusion, and test whether reducing contraction (tnnt2 morpholino, chemical treatments) partly rescues the llgl1 mutant phenotypes.

The relationship between cardiac function and myocardial wall integrity appears to be complex. The paper referred to by the reviewer indeed finds that reduction in heartbeat leads to decreased CM extrusion upon loss of the EMT-factor Snai1b. Previous studies have also found that endothelial flow-responsive genes klf2a/b are required to maintain myocardial ventricular wall integrity at later stages in a contractility-dependent manner (Rasouli et al, 2018). However, contractility is also required early for pro-epicardial emergence, but plays a lesser role in expansion of the epicardial layer on the myocardial surface (Peralta, 2013). Unpicking the relationship between the forces induced by mechanical contraction of the ventricular wall, contractility-based induction of e.g klf2 expression, and the impact of contractile forces on proepicardial development or epicardial expansion will be complex. We therefore think the proposed experiment will be difficult to interpret whatever the outcome, and argue that dissecting this relationship is beyond the scope of revisions for this paper.

Reviewer 3

How llgl1 relates to epicardial biology is left entirely unexplored in this work. Do proepicardial cells show any defect in cell polarization related to llgl1 absence?

We agree with the reviewer that we do not delve into the mechanisms underlying regulation of epicardial development by llgl1, and that this is an interesting question. Our scope for this manuscript was to understand the mechanisms by which llgl1 regulates integrity of the ventricular wall, and feel that uncovering the molecular mechanisms by which llgl1 regulates timely epicardial emergence is a larger question that would require substantial investigation (for example, if and when llgl1 PE cells do exhibit apicobasal defects, how this impacts timing of cluster release etc). We think these are important questions that would be better answered in detail in a separate manuscript.

Author Response

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

Reviewer #1 (Public Review):

This work provides a new dataset of 71,688 images of different ape species across a variety of environmental and behavioral conditions, along with pose annotations per image. The authors demonstrate the value of their dataset by training pose estimation networks (HRNet-W48) on both their own dataset and other primate datasets (OpenMonkeyPose for monkeys, COCO for humans), ultimately showing that the model trained on their dataset had the best performance (performance measured by PCK and AUC). In addition to their ablation studies where they train pose estimation models with either specific species removed or a certain percentage of the images removed, they provide solid evidence that their large, specialized dataset is uniquely positioned to aid in the task of pose estimation for ape species.

The diversity and size of the dataset make it particularly useful, as it covers a wide range of ape species and poses, making it particularly suitable for training off-the-shelf pose estimation networks or for contributing to the training of a large foundational pose estimation model. In conjunction with new tools focused on extracting behavioral dynamics from pose, this dataset can be especially useful in understanding the basis of ape behaviors using pose.

We thank the reviewer for the kind comments.

Since the dataset provided is the first large, public dataset of its kind exclusively for ape species, more details should be provided on how the data were annotated, as well as summaries of the dataset statistics. In addition, the authors should provide the full list of hyperparameters for each model that was used for evaluation (e.g., mmpose config files, textual descriptions of augmentation/optimization parameters).

We have added more details on the annotation process and have included the list of instructions sent to the annotators. We have also included mmpose configs with the code provided. The following files include the relevant details:

File including the list of instructions sent to the annotators: OpenMonkeyWild Photograph Rubric.pdf

Mmpose configs:

i) TopDownOAPDataset.py

ii) animal_oap_dataset.py

iii) init.py

iv) hrnet_w48_oap_256x192_full.py

Anaconda environment files:

i) OpenApePose.yml

ii) requirements.txt

Overall this work is a terrific contribution to the field and is likely to have a significant impact on both computer vision and animal behavior.

Strengths:

• Open source dataset with excellent annotations on the format, as well as example code provided for working with it.

• Properties of the dataset are mostly well described.

• Comparison to pose estimation models trained on humans vs monkeys, finding that models trained on human data generalized better to apes than the ones trained on monkeys, in accordance with phylogenetic similarity. This provides evidence for an important consideration in the field: how well can we expect pose estimation models to generalize to new species when using data from closely or distantly related ones? - Sample efficiency experiments reflect an important property of pose estimation systems, which indicates how much data would be necessary to generate similar datasets in other species, as well as how much data may be required for fine-tuning these types of models (also characterized via ablation experiments where some species are left out).

• The sample efficiency experiments also reveal important insights about scaling properties of different model architectures, finding that HRNet saturates in performance improvements as a function of dataset size sooner than other architectures like CPMs (even though HRNets still perform better overall).

We thank the reviewer for the kind comments.

Weaknesses:

• More details on training hyperparameters used (preferably full config if trained via mmpose).

We have now included mmpose configs and anaconda environment files that allow researchers to use the dataset with specific versions of mmpose and other packages we trained our models with. The list of files is provided above.

• Should include dataset datasheet, as described in Gebru et al 2021 (arXiv:1803.09010).

We have included a datasheet for our dataset in the appendix lines 621-764.

• Should include crowdsourced annotation datasheet, as described in Diaz et al 2022 (arXiv:2206.08931). Alternatively, the specific instructions that were provided to Hive/annotators would be highly relevant to convey what annotation protocols were employed here.

We have included the list of instructions sent to the Hive annotators in the supplementary materials. File: OpenMonkeyWild Photograph Rubric.pdf

• Should include model cards, as described in Mitchell et al (arXiv:1810.03993).

We have included a model card for the included model in the results section line 359. See Author response image 1.

Author response image 1.  

• It would be useful to include more information on the source of the data as they are collected from many different sites and from many different individuals, some of which may introduce structural biases such as lighting conditions due to geography and time of year.

We agree that the source could introduce structural biases. This is why we included images from so many different sources and captured images at different times from the same source—in hopes that a large variety of background and lighting conditions are represented. However, doing so limits our ability to document each source background and lighting condition separately.

• Is there a reason not to use OKS? This incorporates several factors such as landmark visibility, scale, and landmark type-specific annotation variability as in Ronchi & Perona 2017 (arXiv:1707.05388). The latter (variability) could use the human pose values (for landmarks types that are shared), the least variable keypoint class in humans (eyes) as a conservative estimate of accuracy, or leverage a unique aspect of this work (crowdsourced annotations) which affords the ability to estimate these values empirically.

The focus of this work is on overall keypoint localization accuracy and hence we wanted a metric that is easy to interpret and implement, in this case we made use of PCK (Percentage of Correct Keypoints). PCK is a simple and widely used metric that measures the percentage of correctly localized keypoints within a certain distance threshold from their corresponding groundtruth keypoints.

• A reporting of the scales present in the dataset would be useful (e.g., histogram of unnormalized bounding boxes) and would align well with existing pose dataset papers such as MS-COCO (arXiv:1405.0312) which reports the distribution of instance sizes and instance density per image.

RESPONSE: We have now included a histogram of unnormalized bounding boxes in the manuscript, Author response image 2.

Author response image 2.

Reviewer #2 (Public Review):

The authors present the OpenApePose database constituting a collection of over 70000 ape images which will be important for many applications within primatology and the behavioural sciences. The authors have also rigorously tested the utility of this database in comparison to available Pose image databases for monkeys and humans to clearly demonstrate its solid potential.

We thank the reviewer for the kind comments.

However, the variation in the database with regards to individuals, background, source/setting is not clearly articulated and would be beneficial information for those wishing to make use of this resource in the future. At present, there is also a lack of clarity as to how this image database can be extrapolated to aid video data analyses which would be highly beneficial as well.

I have two major concerns with regard to the manuscript as it currently stands which I think if addressed would aid the clarity and utility of this database for readers.

1) Human annotators are mentioned as doing the 16 landmarks manually for all images but there is no assessment of inter-observer reliability or the such. I think something to this end is currently missing, along with how many annotators there were. This will be essential for others to know who may want to use this database in the future.

We thank the reviewer for pointing this out. Inter-observer reliability is important for ensuring the quality of the annotations. We first used Amazon MTurk to crowd source annotations and found that the inter-observer reliability and the annotation quality was poor. This was the reason for choosing a commercial service such as Hive AI. As the crowd sourcing and quality control are managed by Hive through their internal procedures, we do not have access to data that can allow us to assess inter-observer reliability. However, the annotation quality was assessed by first author ND through manual inspections of the annotations visualized on all of the images the database. Additionally, our ablation experiments with high out of sample performances further vaildate the quality of the annotations.

Relevant to this comment, in your description of the database, a table or such could be included, providing the number of images from each source/setting per species and/or number of individuals. Something to give a brief overview of the variation beyond species. (subspecies would also be of benefit for example).

Our goal was to obtain as many images as possible from the most commonly studied ape species. In order to ensure a large enough database, we focused only on the species and combined images from as many sources as possible to reach our goal of ~10,000 images per species. With the wide range of people involved in obtaining the images, we could not ensure that all the photographers had the necessary expertise to differentiate individuals and subspecies of the subjects they were photographing. We could only ensure that the right species was being photographed. Hence, we cannot include more detailed information.

2) You mention around line 195 that you used a specific function for splitting up the dataset into training, validation, and test but there is no information given as to whether this was simply random or if an attempt to balance across species, individuals, background/source was made. I would actually think that a balanced approach would be more appropriate/useful here so whether or not this was done, and the reasoning behind that must be justified.

This is especially relevant given that in one test you report balancing across species (for the sample size subsampling procedure).

We created the training set to reflect the species composition of the whole dataset, but used test sets balanced by species. This was done to give a sense of the performance of a model that could be trained with the entire dataset, that does not have the species fully balanced. We believe that researchers interested in training models using this dataset for behavior tracking applications would use the entire dataset to fully leverage the variation in the dataset. However, for those interested in training models with balanced species, we provide an annotation file with all the images included, which would allow researchers to create their own training and test sets that meet their specific needs. We have added this justification in the manuscript to guide the other users with different needs. Lines 530-534: “We did not balance our training set for the species as we wanted to utilize the full variation in the dataset and assess models trained with the proportion of species as reflected in the dataset. We provide annotations including the entire dataset to allow others to make create their own training/validation/test sets that suit their needs.”

And another perhaps major concern that I think should also be addressed somewhere is the fact that this is an image database tested on images while the abstract and manuscript mention the importance of pose estimation for video datasets, yet the current manuscript does not provide any clear test of video datasets nor engage with the practicalities associated with using this image-based database for applications to video datasets. Somewhere this needs to be added to clarify its practical utility.

We thank the reviewer for this important suggestion. Since we can separate a video into its constituent frames, one can indeed use the provided model or other models trained using this dataset for inference on the frames, thus allowing video tracking applications. We now include a short video clip of a chimpanzee with inferences from the provided model visualized in the supplementary materials.

Reviewer #1 (Recommendations For The Authors):

• Please provide a more thorough description of the annotation procedure (i.e., the instructions given to crowd workers)! See public review for reference on dataset annotation reporting cards.

We have included the list of instructions for Hive annotators in the supplementary materials.

• An estimate of the crowd worker accuracy and variability would be super valuable!

While we agree that this is useful, we do not have access to Hive internal data on crowd worker IDs that could allow us to estimate these metrics. Furthermore, we assessed each image manually to ensure good annotation quality.

• In the methods section it is reported that images were discarded because they were either too blurry, small, or highly occluded. Further quantification could be provided. How many images were discarded per species?

It’s not really clear to us why this is interesting or important. We used a large number of photographers and annotators, some of whom gave a high ratio of great images; some of whom gave a poor ratio. But it’s not clear what those ratios tell us.

• Placing the numerical values at the end of the bars would make the graphs more readable in Figures 4 and 5.

We thank the reviewer for this suggestion. While we agree that this can help, we do not have space to include the number in a font size that would be readable. Smaller font sizes that are likely to fit may not be readable for all readers. We have included the numerical values in the main text in the results section for those interested and hope that the figures provide a qualitative sense of the results to the readers.

Author Response

eLife assessment

Building on their own prior work, the authors present valuable findings that add to our understanding of cortical astrocytes, which respond to synaptic activity with calcium release in subcellular domains that can proceed to larger calcium waves. The proposed concept of a spatial "threshold" is based on solid evidence from in vivo and ex vivo imaging data and the use of mutant mice. However, details of the specific threshold should be taken with caution and appear incomplete unless supported by additional experiments with higher resolution in space and time.

We thank the reviewers and editors for the positive assessment of our work as containing valuable findings that add to our understanding of cortical astrocytes. We also appreciate their positive appraisal of the proposed concept of a spatial threshold supported by solid evidence.

Regarding their specific comments, we truly appreciate them because they have helped to clarify issues and to improve the study. Provisional point-by-point responses to these comments are provided below. Regarding the general comment on the spatial and temporal resolution of our study, we would like to clarify that the spatial and temporal resolution used in the current study (i.e., 2 - 5 Hz framerate using a 25x objective with 1.7x digital zoom with pixels on the order of 1 µm2) is within the norm in the field, does not compromise the results, nor diminish the main conceptual advancement of the study, namely the existence of a spatial threshold for astrocyte calcium surge.

We respect the thoughtfulness of the reviewers and editors and look forward to improving the paper to fully answer both public and private comments with a revised manuscript.

Reviewer #1 (Public Review):

Lines et al., provide evidence for a sequence of events in vivo in adult anesthetized mice that begin with a footshock driving activation of neural projections into layer 2/3 somatosensory cortex, which in turn triggers a rise in calcium in astrocytes within "domains" of their "arbor". The authors segment the astrocyte morphology based on SR101 signal and show that the timing of "arbor" Ca2+ activation precedes somatic activation and that somatic activation only occurs if at least {greater than or equal to}22.6% of the total segmented astrocyte "arbor" area is active. Thus, the authors frame this {greater than or equal to}22.6% activation as a spatial property (spatial threshold) with certain temporal characteristics - i.e., must occur before soma and global activation. The authors then elaborate on this spatial threshold by providing evidence for its intrinsic nature - is not set by the level of neuronal stimulus and is dependent on whether IP3R2, which drives Ca2+ release from the endoplasmic reticulum (ER) in astrocytes, is expressed. Lastly, the authors suggest a potential physiologic role for this spatial threshold by showing ex vivo how exogenous activation of layer 2/3 astrocytes by ATP application can gate glutamate gliotransmission to layer 2/3 cortical neurons - with a strong correlation between the number of active astrocyte Ca2+ domains and the slow inward current (SIC) frequency recorded from nearby neurons as a readout of glutamatergic gliotransmission. This is interesting and would potentially be of great interest to readers within and outside the glia research community, especially in how the authors have tried to systematically deconstruct some of the steps underlying signal integration and propagation in astrocytes. Many of the conclusions posited by the authors are potentially important but we think their approach needs experimental/analytical refinement and elaboration.

We thank the reviewer for her/his positive appraisal and comments that has helped us to improve the study. In response to their insights, we aim to address the key points raised below:

1. Sequence of Events: We acknowledge the reviewer's interest in our findings regarding the sequence of events. We will provide a more detailed description of the methods and results to clarify the temporal relationships between neural activation, astrocyte calcium dynamics, and astrocyte morphology segmentation.

2. Spatial Threshold: The reviewer accurately identifies our characterization of a spatial threshold (≥22.6% activation) with temporal characteristics as a crucial aspect of our study. We will expand upon this concept by offering a clearer illustration of how this threshold relates to somatic and global activation.

3. Intrinsic Nature of Spatial Threshold: The reviewer's insightful observation regarding the inherent quality of the spatial threshold, regardless of its dependence on neuronal stimuli is noteworthy. We will provide additional details to substantiate this claim, shedding more light on the fundamental nature of this phenomenon.

4. Physiological Implications: The reviewer rightly highlights the potential physiological significance of our findings, particularly in relation to gliotransmission in cortical neurons. We will enhance our discussion by elaborating on the implications of these observations.

The primary issue for us, and which we would encourage the authors to address, relates to the low spatialtemporal resolution of their approach. This issue does not necessarily compromise the concept of a spatial threshold, but more refined observations and analyses are likely to provide more reliable quantitative parameters and a more comprehensive view of the mode of Ca2+ signal integration in astrocytes.

We agree with the reviewer that our spatial-temporal resolution (2 – 5 Hz framerate using a 25x objective and 1.7x digital zoom with pixels on the order of 1 µm) does not compromise the proposed concept of the existence of a spatial threshold for the intracellular calcium expansion.

For this reason, and because their observations might be perceived as both a conceptual and numerical standard in the field, we believe that the authors should proceed with both experimental and analytical refinement. Notably, we have difficulty with the reported mean delays of astrocyte Ca2+ elevations upon sensory stimulation. The 11s delay for response onset in "arbor" and 13s in the soma are extremely long, and we do not think they represent a true physiologic latency for astrocyte responses to the sensory activity. Indeed, such delays appear to be slower even than those reported in the initial studies of sensory stimulation in anesthetized mice with limited spatial-temporal resolution (Wang et al. Nat Neurosci., 2006) - not to say of more recent and refined ones in awake mice (Stobart et al. Neuron, 2018) that identified even sub-second astrocyte Ca2+ responses, largely preserved in IP3R2KO mice. Thus, we are inclined to believe that the slowness of responses reported here is an indicator of experimental/analytical issues. There can be several explanations of such slowness that the authors may want to consider for improving their approach: (a) The authors apparently use low zoom imaging for acquiring signals from several astrocytes present in the FOV: do all of these astrocytes respond homogeneously in terms of delay from sensory stimulus? Perhaps some are faster responders than others and only this population is directly activated by the stimulus. Others could be slower in activation because they respond secondarily to stimuli. In this case, the authors could focus their analysis specifically on the "fast-responding population". (b) By focusing on individual astrocytes and using higher zoom, the authors could unmask more subtle Ca2+ elevations that precede those reported in the current manuscript. These signals have been reported to occur mainly in regions of the astrocyte that are GCaMP6-positive but SR101-negative and constitute a large percentage of its volume (Bindocci et al., 2017). By restricting analysis to the SR101-positive part of the astrocyte, the authors might miss the fastest components of the astrocyte Ca2+ response likely representing the primary signals triggered by synaptic activity. It would be important if they could identify such signals in their records, and establish if none/few/many of them propagate to the SR-101-positive part of the astrocyte. In other words, if there is only a single spatial threshold, the one the authors reported, or two or more of them along the path of signal propagation towards the cell soma that leads eventually to the transformation of the signal into a global astrocyte Ca2+ surge.

We thank the reviewer for these excellent and important comments. The qualm with the mean delays of astrocyte activation is indeed a result of averaging together astrocyte responses to a 20 second stimulus. Indeed, astrocyte responses are heterogeneous and many astrocytes respond much quicker, as can be seen in example traces in Figs. 1D, 1G, and 3C. Indeed, with any biological system variability exists, however here we take the averaged responses in order to identify a general property of astrocyte calcium dynamics: the existence of the concept of a spatial threshold for astrocyte calcium surge.

Further, we used a lower stimulus frequency (2Hz) than Stobart et al. (90 Hz) to assess subthreshold activities. We found that stronger stimuli decreased response delays and will include this result in the revised manuscript. Interestingly, from Fig 4F, higher stimulus did not significantly alter the spatial threshold. In the revised version of the manuscript, we will provide a more detailed analysis and the consequent discussion of this analysis.

In this context, there is another concept that we encourage the authors to better clarify: whether the spatial threshold that they describe is constituted by the enlargement of a continuous wavefront of Ca2+ elevation, e.g. in a single process, that eventually reaches 22.6% of the segmented astrocyte, or can it also be constituted by several distinct Ca2+ elevations occurring in separate domains of the arbor, but overall totaling 22.6% of the segmented surface? Mechanistically, the latter would suggest the presence of a general excitability threshold of the astrocyte, whereas the former would identify a driving force threshold for the centripetal wavefront. In light of the above points, we think the authors should use caution in presenting and interpreting the experiments in which they use SIC as a readout. Their results might lead some readers to bluntly interpret the 22.6% spatial threshold as the threshold required for the astrocyte to evoke gliotransmitter release. Indeed, SIC are robust signals recorded somatically from a single neuron and likely integrate activation of many synapses all belonging to that neuron. On the other hand, an astrocyte impinges in a myriad of synapses belonging to several distinct neurons. In our opinion, it is quite possible that more local gliotransmission occurs at lower Ca2+ signal thresholds (see above) that may not be efficiently detected by using SIC as a readout; a more sensitive approach, such as the use of a gliotransmitter sensor expressed all along the astrocyte plasma-membrane could be tested to this aim.

The reviewer raised an excellent point. Whether the spatial threshold of 22.6% occur in the segmented astrocyte or may be reached occurring in separate domains of the arbor, is an important question and we aim to address this by novel analysis that will be provided in the revised version of the manuscript.

Regarding comments on SIC, we fully agree with the reviewer. In the revised version of the manuscript, we will include text in the discussion to ensure the correct interpretation of the results, i.e., the observed 22.6% spatial threshold for the SIC does not necessarily indicates an intrinsic property of gliotransmitter release; rather, since SICs have been shown to be calcium-dependent, it is not surprising that their presence, monitored at the whole-cell soma, matches the threshold for the intracellular calcium extension.

Additional considerations are that the authors propose an event sequence as follows: stimulus - synaptic drive to L2/3 - arbor activation - spatial threshold - soma activation - post soma activation - gliotransmission. This seems reminiscent of the sequence underlying neuronal spike propagation - from dendrite to soma to axon, and the resulting vesicular release. However, there is no consensus within the glial field about an analogous framework for astrocytes. Thus, "arbor activation", "soma activation", and "post soma activation" are not established `terms-of-art´. Similarly, the way the authors use the term "domain" contrasts with how others have (Agarwal et al., 2017; Shigetomi et al., 2013; Di Castro et al., 2011; Grosche et al., 1999) and may produce some confusion. The authors could adopt a more flexible nomenclature or clarify that their terms do not have a defined structural-functional basis, being just constructs that they justifiably adapted to deal with the spatial complexity of astrocytes in line with their past studies (Lines et al., 2020; Lines et al., 2021).

We agree there is no consensus within the glial field about this event sequence. One major difference between this sequence of events and neuronal spike propagation is directionality from dendrite to soma to axon. It is unknown whether directionality of the calcium signal exists in astrocytes. The term “microdomain” is used in the references above to define distal subcellular domains in contact with synapses, and in order to dissociate from this term we adopt the nomenclature “domain” to define all subcellular domains in the astrocyte arborization. These items will be discussed and clarified in the revised version of the manuscript.

Our previous points suggest that the paper would be significantly strengthened by new experimental observations focusing on single astrocytes and using acquisitions at higher spatial and temporal resolution. If the authors will not pursue this option, we encourage them to at least improve their analysis, and at the same time recognize in the text some limitations of their experimental approach as discussed above. We indicate here several levels of possible analytical refinement.

We believe our spatial (25x objective and 1.7x digital zoom with pixels on the order of 1µm) and temporal (2 – 5 Hz framerate) resolution is within the range used in the glial field. In any case the existence of a spatial threshold for astrocyte calcium surge is not compromised with the use of this imaging resolution.

The first relates to the selection of astrocytes being analyzed, and the need to focus on a much narrower subpopulation than (for example) 987 astrocytes used for the core data. This selection would take into greater consideration the aspects of structure and latency. With the structural and latency-based criteria for selection, the number of astrocytes to analyze might be reduced by 10-fold or more, making our second analytical recommendation much more feasible.

We agree that individual differences exist, however, establishing a general concept requires the sampling of many astrocytes. Nevertheless, we aim to further address this issue in the revised version of the manuscript by analyzing the calcium dynamics in individual domains.

For structure-based selection - Genetically-encoded Ca2+ indicators such as GCaMP6 are in principle expressed throughout an astrocyte, even in regions that are not labelled by SR101. Moreover, astrocytes form independent 3D territories, so one can safely assume that the GCaMP6 signal within an astrocyte volume belongs to that specific astrocyte (this is particularly evident if the neighboring astrocytes are GCaMP6negative). Therefore, authors could extend their analysis of Ca2+ signals in individual astrocytes to the regions that are SR101-negative and try to better integrate fast signals in their spatial threshold concept. Even if they decided to be conservative on their methods, and stick to the astrocyte segmentation based on the SR-101 signal, they should acknowledge that SR101 dye staining quality can vary considerably between individual astrocytes within a FOV - some astrocytes will have much greater structural visibility in the distal processes than others. This means that some astrocytes may have segmented domains extending more distally than others and we think that authors should privilege such astrocytes for analysis. However, cases like the representative astrocytes shown in Figure 4A or Figure S1B, have segmented domains localized only to proximal processes near the soma. Accordingly, given the reported timing differences between "arbor" and "soma" activation, one might expect there to be comparable timing differences between domains that are distal vs proximal to the soma as well. Fast signals in peripheral regions of astrocytes in contact with synapses are largely IP3R2-independent (Stobart et al., 2018). However, the quality of SR101 staining has implications for interpreting the IP3R2 KO data. There is evidence IP3R2 KO may preferentially impact activity near the soma (Srinivasan et al., 2015). Thus, astrocytes with insufficient staining - visible only in the soma and proximal domains - might show a biased effect for IP3R2 KO. While not necessarily disrupting the core conclusions made by the authors based on their analysis of SR101-segmented astrocytes, we think results would be strengthened if astrocytes with sufficient SR101 staining - i.e. more consistent with previous reports of L2/3 astrocyte area (Lanjakornsiripan et al., 2018) - were only included. This could be achieved by using max or cumulative projections of individual astrocytes in combination with SR101 staining to construct more holistic structural maps (Bindocci et al., 2017).

We agree with the ideas concerning SR101, and indeed there could be variability in the origins of the astrocyte calcium signal. Astrocyte territory boundaries can be difficult to discern when both astrocytes express GCaMP6. Here we take a conservative approach to constrain ROIs to SR101-positive astrocyte territory outlines without invading neighboring cells in order to reduce error in the estimate of a spatial threshold. The effect of IP3R2 KO preferentially impacting activity near the soma is interesting, and in line with our conclusions. We agree that the findings from SR101-negative pixels would not necessarily disrupt the core conclusions of the study, and the additional analysis suggested would further strengthen results.

For latency-based selection - The authors record calcium activity within a FOV containing at least 20+ astrocytes over a period of 60s, during which a 2Hz hindpaw stimulation at 2mA is applied for 20s. As discussed above, presumably some astrocytes in a FOV are the first to respond to the stimulus series, while others likely respond with longer latency to the stimulus. For the shorter-latency responders <3s, it is easier to attribute their calcium increases as "following the sensory information" projecting to L2/3. In other cases, when "arbor" responses occur at 10s or later, only after 20 stimulus events (at 2Hz), it is likely they are being activated by a more complex and recurrent circuit containing several rounds of neuron-glia crosstalk etc., which would be mechanistically distinct from astrocytes responding earlier. We suggest that authors focus more on the shorter latency response astrocytes, as they are more likely to have activity corresponding to the stimulus itself.

We agree that different times of astrocyte calcium increases may be due to different mechanisms outside of the astrocyte. We believe the spatial threshold will be intrinsic to these external variables; yet we believe that longer latency responses are physiological and may carry important information to determining the astrocyte calcium responses.

The second level of analysis refinement we suggest relates specifically to the issue of propagation and timing for the activity within "arbor", "soma" and "post-soma". Currently, the authors use an ROI-based approach that segments the "arbor" into domains. We suggest that this approach could be supplemented by a more robust temporal analysis. This could for example involve starting with temporal maps that take pixels above a certain amplitude and plot their timing relative to the stimulus-onset, or (better) the first active pixel of the astrocyte. This type of approach has become increasingly used (Bindocci et al., 2017; Wang et al., 2019; Ruprecht et al., 2022) and we think its use can greatly help clarify both the proposed sequence and better characterize the spatial threshold. We think this analysis should specifically address several important points:

We agree that the creation of temporal maps from our own data will be interesting. We will provide the results of the suggested analysis in the revised version of the manuscript.

1) Where/when does the astrocyte activation begin? Understanding the beginning is very important, particularly because another potential spatial threshold - preceding the one the authors describe in the paper - could gate the initial activation of more distal processes, as discussed above. This sequentially earlier spatial threshold could (for example) rely on microdomain interaction with synaptic elements and (in contrast) be IP3R2 independent (Srinivasan et al., 2015, Stobart et al., 2018). We would be interested to know whether, in a subset of astrocytes that meet the structure and latency criteria proposed above and can produce global activation, there is an initial local GCaMP6f response of a minimal size that must occur before propagation towards the soma begins. The data associated with varying stimulus parameters could potentially be useful here and reveal stimulus intensity/duration-dependent differences.

This is a very important point. It is difficult to pinpoint the beginning of the signal, which is why we rely on the average of responses.

2) Whether the propagation in the authors' experimental model is centripetal? This is implied throughout the manuscript but never shown. We think establishing whether (or not) the calcium dynamics are centripetal is important because it would clarify whether spatially adjacent domains within the "arbor" need to be sequentially active before reaching the threshold and then reaching the soma. More broadly, visualizing propagation will help to better visualize summation, which is presumably how the threshold is first reached (and overcome). The alternative hypothesis of a general excitability threshold, as discussed above, would be challenged here and possibly rejected, thereby clarifying the nature of the Ca2+ process that needs to reach a threshold for further expansion to the soma and other parts of the astrocyte.

We agree that our view is centripetal. Indeed, we have found arborization activity precedes soma activity. However, whether this is intrinsic or due to the fact that synapses are more likely to occur in the periphery requires further studies.

3) In complement to the previous point: we understand that the spatial threshold does not per se have a location, but is there some spatial logic underlying the organization of active domains before the soma response occurs? One can easily imagine multiple scenarios of sparse heterogeneous GCaMP6f signal distributions that correspond to {greater than or equal to}22.6% of the arborization, but that would not be expected to trigger soma activation. For example, the diagram in Figure 4C showing the astrocyte response to 2Hz stim (which lacks a soma response) underscores this point. It looks like it has {greater than or equal to}22.6% activation that is sparsely localized throughout the arborization. If an alternative spatial distribution for this activity occurred, such that it localized primarily to a specific process within the arbor, would it be more likely to trigger a soma response?

This is an interesting point and an analysis of spatial clustering on pre-soma domain activation may be useful to answer it.

4) Does "pre-soma" activation predict the location and onset time of "post-soma" activation? For example, are arbor domains that were part of the "pre-soma" response the first to exhibit GCaMP6f signal in the "post-soma" response?

This is another interesting analysis that can be done with a spatial clustering analysis.

Reviewer #2 (Public Review):

Lines et al investigated the integration of calcium signals in astrocytes of the primary somatosensory cortex. Their goal was to better characterize the mechanisms that govern the spatial characteristics of calcium signals in astrocytes. In line with previous reports in the field, they found that most events originated and stayed localized within microdomains in distal astrocyte processes, occasionally coinciding with larger events in the soma, referred to as calcium surges. As a single astrocyte communicates with hundreds of thousands of synapses simultaneously, understanding the spatial integration of calcium signals in astrocytes and the mechanisms governing the latter is of tremendous importance to deepen our understanding of signal processing in the central nervous system. The authors thus aimed to unveil the properties governing the emergence of calcium surges. The main claim of this manuscript is that there would be a spatial threshold of ~23% of microdomain activation above which a calcium surge, i.e. a calcium signal that spreads to the soma, is observed. Although the study provides data that is highly valuable for the community, the conclusions of the current version of the manuscript seem a little too assertive and general compared with what can be deduced from the data and methods used.

The major strength of this study is the experimental approach that allowed the authors to obtain numerous and informative calcium recordings in vivo in the somatosensory cortex in mice in response to sensory stimuli as well as in situ. Notably, they developed an interesting approach to modulating the number of active domains in peripheral astrocyte processes by varying the intensity of peripheral stimulation (its amplitude, frequency, or duration).

We thank the reviewer for their kind and thoughtful review of our study.

The major weakness of the manuscript is the method used to analyze and quantify calcium activity, which mostly relies on the analysis of averaged data and overlooks the variability of the signals measured. As a result, the main claims from the manuscript seem to be incompletely supported by the data. The choice of the use of a custom-made semi-automatic ROI-based calcium event detection algorithm rather than established state-of-the-art software, such as the event-based calcium event detection software AQuA (DOI: 10.1038/s41593-019-0492-2), is insufficiently discussed and may bias the analysis. Some references on this matter include: Semyanov et al, Nature Rev Neuro, 2020 (DOI: 10.1038/s41583-020-0361-8); Covelo et al 2022, J Mol Neurosci (DOI: 10.1007/s12031-022-02006-w) & Wang et al, 2019, Nat Neuroscience (DOI: 10.1038/s41593-019-0492-2). Moreover, the ROIs used to quantify calcium activity are based on structural imaging of astrocytes, which may not be functionally relevant.

Unfortunately, there is no general consensus for calcium analysis in the astrocyte or neuronal field, and many groups use custom made software made in lab or custom software such as GECIquant or AQuA. While AQuA is an event-based calcium event detection software, it may be that not including inactive domains that are SR101 positive could underestimate the spatial threshold for calcium surge. Our data is not based on the functional events but is based on calcium with structural constraints within a single astrocyte. This is crucial to properly determine the ratio of active vs inactive pixels within a single astrocyte.

For the reasons listed above, the manuscript would probably benefit from some rephrasing of the conclusions and a discussion highlighting the advantages and limitations of the methodological approach. The question investigated by this study is of great importance in the field of neuroscience as the mechanisms dictating the spatio-temporal properties of calcium signals in astrocytes are poorly characterized, yet are essential to understand their involvement in the modulation of signal integration within neural circuits.

We thank the reviewer for their suggestions to benefit the conclusions and discussion.

Reviewer #3 (Public Review):

Summary:

The study aims to elucidate the spatial dynamics of subcellular astrocytic calcium signaling. Specifically, they elucidate how subdomain activity above a certain spatial threshold (~23% of domains being active) heralds a calcium surge that also affects the astrocytic soma. Moreover, they demonstrate that processes on average are included earlier than the soma and that IP3R2 is necessary for calcium surges to occur. Finally, they associate calcium surges with slow inward currents.

Strengths:

The study addresses an interesting topic that is only partially understood. The study uses multiple methods including in vivo two-photon microscopy, acute brain slices, electrophysiology, pharmacology, and knockout models. The conclusions are strengthened by the same findings in both in vivo anesthetized mice and in brain slices.

We thank the reviewer for the positive assessment of the study and his/her comments.

Weaknesses:

The method that has been used to quantify astrocytic calcium signals only analyzes what seems to be a small proportion of the total astrocytic domain on the example micrographs, where a structure is visible in the SR101 channel (see for instance Reeves et al. J. Neurosci. 2011, demonstrating to what extent SR101 outlines an astrocyte). This would potentially heavily bias the results: from the example illustrations presented it is clear that the calcium increases in what is putatively the same astrocyte goes well beyond what is outlined with automatically placed small ROIs. The smallest astrocytic processes are an order of magnitude smaller than the resolution of optical imaging and would not be outlined by either SR101 or with the segmentation method judged by the ROIs presented in the figures. Completely ignoring these very large parts of the spatial domain of an astrocyte, in particular when making claims about a spatial threshold, seems inappropriate. Several recent methods published use pixel-by-pixel event-based approaches to define calcium signals. The data should have been analyzed using such a method within a complete astrocyte spatial domain in addition to the analyses presented. Also, the authors do not discuss how two-dimensional sampling of calcium signals from an astrocyte that has processes in three dimensions (see Bindocci et al, Science 2017) may affect the results: if subdomain activation is not homogeneously distributed in the three-dimensional space within the astrocyte territory, the assumptions and findings between a correlation between subdomain activation and somatic activation may be affected.

In order to reduce noise from individual pixels, we chose to segment astrocyte arborizations into domains of several pixels. As pointed out previously, including pixels outside of the SR101-positive territory runs the risk of including a pixel that may be from a neighboring cell, and we chose to avoid this source of error. We agree that the results have limitations from being acquired in 2D instead of 3D, but it is likely to assume the 3D astrocyte is homogeneously distributed and that the 2D plane is representative of the whole astrocyte. Indeed, no dimensional effects were reported in Bindocci et al, Science 2017. We plan to include a paragraph in the discussion to address this limitation in our study.

The experiments are performed either in anesthetized mice, or in slices. The study would have come across as much more solid and interesting if at least a small set of experiments were performed also in awake mice (for instance during spontaneous behavior), given the profound effect of anesthesia on astrocytic calcium signaling and the highly invasive nature of preparing acute brain slices. The authors mention the caveat of studying anesthetized mice but claim that the intracellular machinery should remain the same. This explanation appears a bit dismissive as the response of an astrocyte not only depends on the internal machinery of the astrocyte, but also on how the astrocyte is stimulated: for instance synaptic stimulation or sensory input likely would be dependent on brain state and concurrent neuromodulatory signaling which is absent in both experimental paradigms. The discussion would have been more balanced if these aspects were dealt with more thoroughly.

Yes, we agree that this is a limitation, and we will acknowledge this is in the discussion.

The study uses a heaviside step function to define a spatial 'threshold' for somata either being included or not in a calcium signal. However, Fig 4E and 5D showing how the method separates the signal provide little understanding for the reader. The most informative figure that could support the main finding of the study, namely a ~23% spatial threshold for astrocyte calcium surges reaching the soma, is Fig. 4G, showing the relationship between the percentage of arborizations active and the soma calcium signal. A similar plot should have been presented in Fig 5 as well. Looking at this distribution, though, it is not clear why ~23% would be a clear threshold to separate soma involvement, one can only speculate how the threshold for a soma event would influence this number. Even if the analyses in Fig. 4H and the fact that the same threshold appears in two experimental paradigms strengthen the case, the results would have been more convincing if several types of statistical modeling describing the continuous distribution of values presented in Fig. 4E (in addition to the heaviside step function) were presented.

We agree with the reviewer that we should add to the paper a discussion for our justification on the use of the Heaviside step function, and plan to include this. We chose the Heaviside step function to represent the on/off situation that we observed in the data. We agree with the reviewer that Fig. 4G is informative and demonstrates that under 23% most of the soma fluorescence values are clustered at baseline. We agree that a similar graph should be included in Fig. 5 as well. We agree that a different statistical model describing the data would be more convincing and also confirmed the spatial threshold with the use of a confidence interval in the text.

The description of methods should have been considerably more thorough throughout. For instance which temperature the acute slice experiments were performed at, and whether slices were prepared in ice-cold solution, are crucial to know as these parameters heavily influence both astrocyte morphology and signaling. Moreover, no monitoring of physiological parameters (oxygen level, CO2, arterial blood gas analyses, temperature etc) of the in vivo anesthetized mice is mentioned. These aspects are critical to control for when working with acute in vivo two-photon microscopy of mice; the physiological parameters rapidly decay within a few hours with anesthesia and following surgery.

We will increase the thoroughness of our methods section. Especially including that body temperature and respiration were indeed monitored throughout anesthesia.

Reviewer #1 (Public Review):

Lines et al., provide evidence for a sequence of events in vivo in adult anesthetized mice that begin with a foot-shock driving activation of neural projections into layer 2/3 somatosensory cortex, which in turn triggers a rise in calcium in astrocytes within "domains" of their "arbor". The authors segment the astrocyte morphology based on SR101 signal and show that the timing of "arbor" Ca2+ activation precedes somatic activation and that somatic activation only occurs if at least {greater than or equal to}22.6% of the total segmented astrocyte "arbor" area is active. Thus, the authors frame this {greater than or equal to}22.6% activation as a spatial property (spatial threshold) with certain temporal characteristics - i.e., must occur before soma and global activation. The authors then elaborate on this spatial threshold by providing evidence for its intrinsic nature - is not set by the level of neuronal stimulus and is dependent on whether IP3R2, which drives Ca2+ release from the endoplasmic reticulum (ER) in astrocytes, is expressed. Lastly, the authors suggest a potential physiologic role for this spatial threshold by showing ex vivo how exogenous activation of layer 2/3 astrocytes by ATP application can gate glutamate gliotransmission to layer 2/3 cortical neurons - with a strong correlation between the number of active astrocyte Ca2+ domains and the slow inward current (SIC) frequency recorded from nearby neurons as a readout of glutamatergic gliotransmission. This is interesting and would potentially be of great interest to readers within and outside the glia research community, especially in how the authors have tried to systematically deconstruct some of the steps underlying signal integration and propagation in astrocytes. Many of the conclusions posited by the authors are potentially important but we think their approach needs experimental/analytical refinement and elaboration.

The primary issue for us, and which we would encourage the authors to address, relates to the low spatial-temporal resolution of their approach. This issue does not necessarily compromise the concept of a spatial threshold, but more refined observations and analyses are likely to provide more reliable quantitative parameters and a more comprehensive view of the mode of Ca2+ signal integration in astrocytes. For this reason, and because their observations might be perceived as both a conceptual and numerical standard in the field, we believe that the authors should proceed with both experimental and analytical refinement. Notably, we have difficulty with the reported mean delays of astrocyte Ca2+ elevations upon sensory stimulation. The 11s delay for response onset in "arbor" and 13s in the soma are extremely long, and we do not think they represent a true physiologic latency for astrocyte responses to the sensory activity. Indeed, such delays appear to be slower even than those reported in the initial studies of sensory stimulation in anesthetized mice with limited spatial-temporal resolution (Wang et al. Nat Neurosci., 2006) - not to say of more recent and refined ones in awake mice (Stobart et al. Neuron, 2018) that identified even sub-second astrocyte Ca2+ responses, largely preserved in IP3R2KO mice. Thus, we are inclined to believe that the slowness of responses reported here is an indicator of experimental/analytical issues. There can be several explanations of such slowness that the authors may want to consider for improving their approach: (a) The authors apparently use low zoom imaging for acquiring signals from several astrocytes present in the FOV: do all of these astrocytes respond homogeneously in terms of delay from sensory stimulus? Perhaps some are faster responders than others and only this population is directly activated by the stimulus. Others could be slower in activation because they respond secondarily to stimuli. In this case, the authors could focus their analysis specifically on the "fast-responding population". (b) By focusing on individual astrocytes and using higher zoom, the authors could unmask more subtle Ca2+ elevations that precede those reported in the current manuscript. These signals have been reported to occur mainly in regions of the astrocyte that are GCaMP6-positive but SR101-negative and constitute a large percentage of its volume (Bindocci et al., 2017). By restricting analysis to the SR101-positive part of the astrocyte, the authors might miss the fastest components of the astrocyte Ca2+ response likely representing the primary signals triggered by synaptic activity. It would be important if they could identify such signals in their records, and establish if none/few/many of them propagate to the SR-101-positive part of the astrocyte. In other words, if there is only a single spatial threshold, the one the authors reported, or two or more of them along the path of signal propagation towards the cell soma that leads eventually to the transformation of the signal into a global astrocyte Ca2+ surge. In this context, there is another concept that we encourage the authors to better clarify: whether the spatial threshold that they describe is constituted by the enlargement of a continuous wavefront of Ca2+ elevation, e.g. in a single process, that eventually reaches 22.6% of the segmented astrocyte, or can it also be constituted by several distinct Ca2+ elevations occurring in separate domains of the arbor, but overall totaling 22.6% of the segmented surface? Mechanistically, the latter would suggest the presence of a general excitability threshold of the astrocyte, whereas the former would identify a driving force threshold for the centripetal wavefront. In light of the above points, we think the authors should use caution in presenting and interpreting the experiments in which they use SIC as a readout. Their results might lead some readers to bluntly interpret the 22.6% spatial threshold as the threshold required for the astrocyte to evoke gliotransmitter release. Indeed, SIC are robust signals recorded somatically from a single neuron and likely integrate activation of many synapses all belonging to that neuron. On the other hand, an astrocyte impinges in a myriad of synapses belonging to several distinct neurons. In our opinion, it is quite possible that more local gliotransmission occurs at lower Ca2+ signal thresholds (see above) that may not be efficiently detected by using SIC as a readout; a more sensitive approach, such as the use of a gliotransmitter sensor expressed all along the astrocyte plasma-membrane could be tested to this aim.

Additional considerations are that the authors propose an event sequence as follows: stimulus - synaptic drive to L2/3 - arbor activation - spatial threshold - soma activation - post soma activation - gliotransmission. This seems reminiscent of the sequence underlying neuronal spike propagation - from dendrite to soma to axon, and the resulting vesicular release. However, there is no consensus within the glial field about an analogous framework for astrocytes. Thus, "arbor activation", "soma activation", and "post soma activation" are not established `terms-of-art´. Similarly, the way the authors use the term "domain" contrasts with how others have (Agarwal et al., 2017; Shigetomi et al., 2013; Di Castro et al., 2011; Grosche et al., 1999) and may produce some confusion. The authors could adopt a more flexible nomenclature or clarify that their terms do not have a defined structural-functional basis, being just constructs that they justifiably adapted to deal with the spatial complexity of astrocytes in line with their past studies (Lines et al., 2020; Lines et al., 2021).

Our previous points suggest that the paper would be significantly strengthened by new experimental observations focusing on single astrocytes and using acquisitions at higher spatial and temporal resolution. If the authors will not pursue this option, we encourage them to at least improve their analysis, and at the same time recognize in the text some limitations of their experimental approach as discussed above. We indicate here several levels of possible analytical refinement.

The first relates to the selection of astrocytes being analyzed, and the need to focus on a much narrower subpopulation than (for example) 987 astrocytes used for the core data. This selection would take into greater consideration the aspects of structure and latency. With the structural and latency-based criteria for selection, the number of astrocytes to analyze might be reduced by 10-fold or more, making our second analytical recommendation much more feasible.

For structure-based selection - Genetically-encoded Ca2+ indicators such as GCaMP6 are in principle expressed throughout an astrocyte, even in regions that are not labelled by SR101. Moreover, astrocytes form independent 3D territories, so one can safely assume that the GCaMP6 signal within an astrocyte volume belongs to that specific astrocyte (this is particularly evident if the neighboring astrocytes are GCaMP6-negative). Therefore, authors could extend their analysis of Ca2+ signals in individual astrocytes to the regions that are SR101-negative and try to better integrate fast signals in their spatial threshold concept. Even if they decided to be conservative on their methods, and stick to the astrocyte segmentation based on the SR-101 signal, they should acknowledge that SR101 dye staining quality can vary considerably between individual astrocytes within a FOV - some astrocytes will have much greater structural visibility in the distal processes than others. This means that some astrocytes may have segmented domains extending more distally than others and we think that authors should privilege such astrocytes for analysis. However, cases like the representative astrocytes shown in Figure 4A or Figure S1B, have segmented domains localized only to proximal processes near the soma. Accordingly, given the reported timing differences between "arbor" and "soma" activation, one might expect there to be comparable timing differences between domains that are distal vs proximal to the soma as well. Fast signals in peripheral regions of astrocytes in contact with synapses are largely IP3R2-independent (Stobart et al., 2018). However, the quality of SR101 staining has implications for interpreting the IP3R2 KO data. There is evidence IP3R2 KO may preferentially impact activity near the soma (Srinivasan et al., 2015). Thus, astrocytes with insufficient staining - visible only in the soma and proximal domains - might show a biased effect for IP3R2 KO. While not necessarily disrupting the core conclusions made by the authors based on their analysis of SR101-segmented astrocytes, we think results would be strengthened if astrocytes with sufficient SR101 staining - i.e. more consistent with previous reports of L2/3 astrocyte area (Lanjakornsiripan et al., 2018) - were only included. This could be achieved by using max or cumulative projections of individual astrocytes in combination with SR101 staining to construct more holistic structural maps (Bindocci et al., 2017).

For latency-based selection - The authors record calcium activity within a FOV containing at least 20+ astrocytes over a period of 60s, during which a 2Hz hindpaw stimulation at 2mA is applied for 20s. As discussed above, presumably some astrocytes in a FOV are the first to respond to the stimulus series, while others likely respond with longer latency to the stimulus. For the shorter-latency responders <3s, it is easier to attribute their calcium increases as "following the sensory information" projecting to L2/3. In other cases, when "arbor" responses occur at 10s or later, only after 20 stimulus events (at 2Hz), it is likely they are being activated by a more complex and recurrent circuit containing several rounds of neuron-glia crosstalk etc., which would be mechanistically distinct from astrocytes responding earlier. We suggest that authors focus more on the shorter latency response astrocytes, as they are more likely to have activity corresponding to the stimulus itself.

The second level of analysis refinement we suggest relates specifically to the issue of propagation and timing for the activity within "arbor", "soma" and "post-soma". Currently, the authors use an ROI-based approach that segments the "arbor" into domains. We suggest that this approach could be supplemented by a more robust temporal analysis. This could for example involve starting with temporal maps that take pixels above a certain amplitude and plot their timing relative to the stimulus-onset, or (better) the first active pixel of the astrocyte. This type of approach has become increasingly used (Bindocci et al., 2017; Wang et al., 2019; Ruprecht et al., 2022) and we think its use can greatly help clarify both the proposed sequence and better characterize the spatial threshold. We think this analysis should specifically address several important points:

1. Where/when does the astrocyte activation begin? Understanding the beginning is very important, particularly because another potential spatial threshold - preceding the one the authors describe in the paper - could gate the initial activation of more distal processes, as discussed above. This sequentially earlier spatial threshold could (for example) rely on microdomain interaction with synaptic elements and (in contrast) be IP3R2 independent (Srinivasan et al., 2015, Stobart et al., 2018). We would be interested to know whether, in a subset of astrocytes that meet the structure and latency criteria proposed above and can produce global activation, there is an initial local GCaMP6f response of a minimal size that must occur before propagation towards the soma begins. The data associated with varying stimulus parameters could potentially be useful here and reveal stimulus intensity/duration-dependent differences.

2. Whether the propagation in the authors' experimental model is centripetal? This is implied throughout the manuscript but never shown. We think establishing whether (or not) the calcium dynamics are centripetal is important because it would clarify whether spatially adjacent domains within the "arbor" need to be sequentially active before reaching the threshold and then reaching the soma. More broadly, visualizing propagation will help to better visualize summation, which is presumably how the threshold is first reached (and overcome). The alternative hypothesis of a general excitability threshold, as discussed above, would be challenged here and possibly rejected, thereby clarifying the nature of the Ca2+ process that needs to reach a threshold for further expansion to the soma and other parts of the astrocyte.

3. In complement to the previous point: we understand that the spatial threshold does not per se have a location, but is there some spatial logic underlying the organization of active domains before the soma response occurs? One can easily imagine multiple scenarios of sparse heterogeneous GCaMP6f signal distributions that correspond to {greater than or equal to}22.6% of the arborization, but that would not be expected to trigger soma activation. For example, the diagram in Figure 4C showing the astrocyte response to 2Hz stim (which lacks a soma response) underscores this point. It looks like it has {greater than or equal to}22.6% activation that is sparsely localized throughout the arborization. If an alternative spatial distribution for this activity occurred, such that it localized primarily to a specific process within the arbor, would it be more likely to trigger a soma response?

4. Does "pre-soma" activation predict the location and onset time of "post-soma" activation? For example, are arbor domains that were part of the "pre-soma" response the first to exhibit GCaMP6f signal in the "post-soma" response?

This is one of those things that makes me feel really connected to people of the past. We are more similar than we are different. It's funny to know that children in twelfth century London were playing dress up and pretending to be knights when I did the same thing with other children in elementary school. The text says that the older boys had real weapons while the younger ones had altered, less-dangerous ones. It reminds me of kids pretending large sticks were swords. The more things change the more they stay the same. Some things do change for the better though, like the end of deadly "gladiatorial combat and wild animal hunts" (Milliman 588). When I was young, a lot of kids would pretend to be knights, soldiers, cops, cowboys, pirates, you name it...so it's kind of funny to think about kids pretending to be knights in front of actual real life knights. Of course their games and costume were probably a lost more accurate to real knights than kids of the 21st century. I'm sure people back in the twelfth century had a problem with kids playing "violently" just as people do nowadays. How much have we heard about video games making kids violent, or that Nerf shouldn't make guns, and so on and so forth. Regardless if you agree or disagree with these sentiments, it's clear this train of thought is not new. I also like how the younger boys had spears with no tips. Even though one day they may have grown up to be real knights or gone off to fight in a war, their parents still made sure to keep them safe as they possibly could which I find adorable. Nowadays parents put a helmet or knee pads on their young athletes. I hate when people spout the rhetoric that no one loved their kids back then, because they often died of disease so they had a bunch just in case. This idea couldn't be further from the truth. People back then were so much like people today.

Aza Raskin introduction of the infinite scroll in 2006, completely reshaped and changed how we navigate the internet for content. With the infinite scroll. You can finally scroll down smoothly and fresh content will load immediately, saving you the trouble of clicking to turn to the next page. Making it easier and more accessible for more people to locate content online, wherever it may be. Although it provides a seamless experience, its extensive usage in social media has come under fire for making it more difficult for users to leave these platforms. While constant scrolling can lead to prolonged usage of online platforms, I also think that you have the freedom to put down your phone. making it less dangerous than it would seem.

Author Response

Reviewer #1 (Pulic Review):

The authors aimed to understand whether the superficial, retinorecipient layers of the mouse superior colliculus (sSC) participate in figure-ground segregation and object recognition. To address this question, they use a combination of optogenetic perturbations of sSC and recordings. These data are consistent with SC being causally involved in object recognition. This would be useful information for the field and likely to be cited.

Thank you for your positive evaluation.

However, I have several concerns regarding their conclusions.

A significant limitation of this study is methodological. The major novelty is the effect of optogenetic silencing, because the recordings are largely correlative, but the optogenetic silencing approach lacks appropriate controls for the effects of the optogenetic excitation light. The authors acknowledge that the optogenetic light is a potential confound, but attempt to address this by shielding the fiber to eliminate light leak and strobing a blue led in the arena. The former does not account for the effects of excitation light scattering intracerebrally--during optogenetic experiments, intracerebral scattering causes the eyes to light up--and for the latter, there is no way to compare the intensity or qualia of the externally strobed LED and the intracerebral light. The proper control would be a cohort of mice lacking channelrhodopsin expression in sSC. Regardless, it is essential to acknowledge this potential confound.

This is a good point. We have added discussion of this in lines 90-95. The proposed experiment was done in Kirchberger et al. (Sci Adv 2021, Suppl Figure 3). In mice without expression of channelrhodopsin trained on the same task as in our study, blue laser light in the cortex did not affect accuracy. Although the exact location of these fibers is different from ours, the distance from the fiber to the eye is very similar. Furthermore, in answer to this comment, we have done a new set of experiments with 4 wild type mice, in which we recorded neural activity in the sSC while delivering optogenetic light stimulation. The procedure was similar to our previous experimental animals except that they did not receive a virus injection. In these mice, we did not see any response in the superior colliculus to the laser light, but we noticed a 5% reduction in response to the visual stimuli (new Figure 1—figure supplement 3). This small reduction could be a small reduction of contrast of the visual stimulus due to the laser light hitting the retina, but given that we did not see any response to the laser alone, it is more likely to come from the known inhibiting effects of light on neural activity (e.g. through heat, see Owen et al. Nat Neurosci 2019). Because our aim was to silence sSC, this particular effect is not a strong confound for our study.

Relatedly, as the authors note, there are GABAergic projection neurons in sSC that may be driving these effects via gain of function. This is a significant concern that has limited the widespread adoption of this approach in sSC despite its popularity in studies in cortex. Indeed, one recently published study of behavioral functions of deep SC found that activating inhibitory neurons actually caused paradoxical behavioral effects consistent with gain of function in the targeted hemisphere, due to the effects of long-range inhibitory projections on the other SC hemisphere. Given the presence of inhibitory projections in sSC, it would be preferable to use an orthogonal method for silencing and at least to thoroughly acknowledge these concerns and cite these recent studies.

This is a valid point. When we started our study, we had some experience with inhibitory opsin (archaerhodopsin and halorhodopsin) and were not confident that we could widely inhibit the sSC reversibly, repeatedly and consistently for an extended period. Other labs have now shown this is feasible with improved inhibitory opsins, so this would now be our preferred option too. The method of silencing sSC by inhibition of GABAergic neurons, however, is still the most common optogenetic method to silence sSC for an extended period (e.g. Hu et al. Neuron 2019, Brenner et al. Neuron 2023) .

We thank the reviewer pointing us to recently published paradoxical behavioral effects. These effects, that we found in Essig et al. (Comm. Biol. 2021) are very interesting, but are not really a concern for the interpretation of our results, partially because as the reviewer pointed out, the GABAergic neurons activated there were in the deep and intermediate layers of the SC, below the sSC that we targeted. The paradoxical effects in that manuscript were attributed to direct inhibition of the contralateral superior colliculus. In our case, we activated the inhibitory neurons bilaterally, and this interhemispheric GABAergic connectivity, if it extends to sSC, only strengthened the bilateral silencing of the sSC. However, we have now discussed the possibility of our transfection of these deeper GABAergic neurons (lines 272-278). The more general point that activating GABAergic neurons in the sSC may also cause inhibition in other structures is indeed a concern. GABAergic neurons in the sSC project to the PBG and the LGN (in particular the vLGN) (Gale & Murphy, 2014; Whyland et al., 2019; Li et al., 2023). Although the primary effect of our manipulation is silencing of the superior colliculus, including the GABAergic neurons (see our answer further below), we cannot exclude the possibility that activating these extracollicular GABAergic projections has an effect. We have edited our discussion of this and updated the references (lines 268-272). However, our measurements in anesthetized (previous submission) and in awake mice (new Figure 1—figure supplement 2) show that apart from a short period directly after the onset of the laser, also almost all putative GABAergic neurons are reduced in their response (see also our answer to the next comment).

A minor point is that although activation of GABAergic neurons in sSC is expected to cause inhibition of neighboring neurons, I would expect channelrhodopsin-expressing GABAergic cells to show an increase in firing during optogenetic excitation. However, it seems that none of the cells plotted (assuming each point in Supplementary Fig 4D is a cell, which the legend does not specify) had such an increase. Do these extracellular recordings not detect inhibitory neurons well?

This is indeed an intriguing observation. The data in the original figure (Supp Fig 1D) was spiking data from 15 recording sites and not from sorted units. This was mentioned in panel C, but not in the caption. For the purpose of the amount of silencing, there was no need to sort single units. Still, it is surprising to see the reduction on almost all channels. The data of Supp Fig 1D came from experiments in anesthetized mice. Prompted by a question from another reviewer, we have now redone these experiments in head-fixed awake mice. The new Figure 1—figure supplement 2 shows these results, for single- and multi-unit clusters. In response to a short laser pulse (50 ms), we find that many units significantly increase their firing rate (Figure 1—figure supplement 2A-B). However, almost all activated then reduce there firing rate and again, we see an overall reduction of responses to visual stimuli. Only one unit fires significantly more when the laser is on during the period of visual stimulation compared to when the laser is off, and the overall firing rate is strongly reduced (Figure 1—figure supplement 2C-E). It appears that optogenetically activating the inhibitory neurons in the sSC for a longer period also reduces the activity of these neurons. The effect that we are seeing might be similar to the paradoxical effects that may occur in visual cortex, where additional excitation of inhibitory neurons leads also leads to their reduced activity due to network dynamics (see e.g. Sadeh & Clopath, Nat Neurosci Rev 2021). However, the effect may also be due to a few inhibitory neurons having a strong inhibitory effect on other inhibitory neurons. This is an interesting point worthy of more investigation, but it falls out to scope of this manuscript.

Finally, the relationship between these stimuli and objects is not entirely clear. The authors acknowledge this but it would be worthwhile to devote more attention to this point. In effect, as the authors note, the gray screen and sinuisoidal grating do not have any sharp edges on the screen, whereas each of the behaviorally relevant stimuli will create a sharp, step-like edge on the screen. Whether edge detection is truly object detection or simply a variant of more general visual detection is unclear.

Indeed, the task can be solved by detection of texture edges, and it is not necessary to integrate the edge components into an object to successfully perform the task. A linear decoder fed with simple cell-like inputs is able to do the orientation task (Luongo et al., 2023). The same network failed to learn the phase task, but also the image of a phase-defined figure contains features that are not present in the background image, and could be solved by learning only local features. Even the texture-defined figures used in Kirchberger et al. (2021) and in earlier monkey studies (Lamme, 1995) which do not contain any sharp stimulus edges can be detected without integrating the local edges into objects and segregation the figure from the background. Several monkey studies show that late neuronal responses in V1 are enhanced for neurons with receptive fields on what we, humans, perceive as the figure. This effect has also been seen in mouse V1, even in the case where there are no local features distinguishing the figure from the background (Fig 7. in Kirchberger et al. 2021). Interfering with activity in V1 in this late phase reduces the ability to detect the figure in human (by TMS) and mouse (by optogenetics). This is suggestive that this figure-ground modulation is used in solving the task, but not a proof. To understand if mice solve the tasks by detecting a figure or by detecting specific features, we can look at generalization. Mice were previously shown to generalize to some degree for size, position and spatial phase of the figure grating patch (Schnabel et al., 2018), suggesting that the mice did not train to detect specific features at specific locations. Rats trained on a similar task had difficulty generalizing from a luminance-defined object to an orientation-defined object (De Keyser et al., 2015), as do mice (Khastkhodaei et al., 2016), but once the rats were acquainted with one set of oriented figures, they immediately generalized to other texture-orientations above chance. On a slightly different figure-detection task mice also showed generalization for different orientations once the initial task was learned (Luongo et al. 2023). This suggests that at least some generalization to object detection occurs in this task. We have added these observation to the discussion (line 301-305).

Reviewer #2 (Public Review):

The goal of this study is to show that the superficial superior colliculus (sSC) of mouse signals figure-ground differences defined by contrast, orientation, and phase, and that these signals are necessary for the animal to detect such figure-ground differences. By inhibiting sSC while the animals perform a figure-ground detection task, the study shows that detection performance decreases when sSC activity is suppressed during the onset of the visual stimulus. The study then intends to show that sSC neurons exhibit surround suppression based on orientation differences, and that surround suppression is stronger when the animal detects the correct location of the figure on the background.

The major strength of this study is the use of a behavioural paradigm to test detection performance of figure-ground stimuli while manipulating neural activity in the sSC during different times after stimulus onset. This paradigm would show whether activity in the sSC is relevant for performing the task. Secondly, the study collected data to confirm previous findings: sSC neurons exhibit orientation specific surround suppression. Additionally, it is impressive that the authors were able to train mice to generalize their task performance across different stimulus categories (figure-ground differences in orientation and phase). This should be highlighted as it may inform future studies.

Thank you for your positive evaluation. We have extended our discussion on the generalization in object detection tasks in mice.

The study has, however, methodological and analytical weaknesses so that the stated conclusions are not supported by the presented results.

1) Optogenetic inhibition is not limited to sSC (even expression may not be limited) About 30% of inhibitory neurons in the sSC project to other areas, e.g. ventral LGN, parabigeminal nucleus and pretectum (Whyland et al, 2019, see ref in manuscript). This means that these areas receive direct inhibition when inhibitory sSC neurons are optogenetically stimulated. This fact is mentioned in the discussion but the consequences and implications for the results are ignored. This is a major flaw of the optogenetic experiments of this study. Additionally, no evidence is given that opsin expression was limited to the superficial layers (except for one histological slice), which the authors acknowledge in line 285. Deeper layers may have other inhibitory neurons with long-range projections.

The finding that sSC neurons show no figure-ground modulation for phase while the optogenetic manipulation has behavioural effects may be an indication for other areas being affected by the optogenetic manipulation.

This is a valid point, also raised by reviewer 1. Although the primary effect of activating the GABAergic neurons in the sSC is a strong reduction of activity in the sSC (see also new figure S1), we cannot rule out that we also activate GABAergic neurons below the sSC and that there are some effects of activating GABAergic connections to the LGN and PBG. We have extended our discussion of this point in lines 269-277. However, as shown in new Figure 1—figure supplement 2, the effect of optogenetically activating Gad2-positive neurons appears to lead to a counter-intuitive reduction of their activity. This effect has previously been observed in cortex.

2) Could other behavioural variables explain the results?

a) Are there any task events other than the visual stimuli that the mice could use to make their decisions? The authors state the use of a custom made lick spout but it is not clear how this spout works, i.e. how do mechanics of the spout deliver water to the right versus the left output and could the mouse perceive these mechanics?

We believe there were no task events besides the visual stimuli that the mice could use to make their decisions. The lick spout was Y-shaped (see Figure 1B) to facilitate the two-alternative forced choice task. Each side of the lick spout was connected to a separate water tube. The water flow in each tube was controlled using a valve. Also, each side of the lick spout was connected to its own lick detector wire. The two valves and the two detector wires were connected to an Arduino which was controlled by our MATLAB task script. The task script was coded such that, when the lick of the mouse had been on the correct side, the valve controlling the water flow on the correct side would briefly open to deliver the water reward. To summarize, the water would only flow after the mouse had licked and if the first lick had been on the correct side. Hence, the water reward did not produce additional cues. We have edited the description of the lick spout in the Methods section to make the functioning of the lick spout more clear (lines 511-513).

b) Could the different neural responses to figure versus ground shown in Fig 2I-J and Fig 3B be explained by behaviours varying between the trial types, e.g. by early lick movements (which are conceivable even if the spout is not present), eye movements or changes in pupil-linked arousal? A behavioural difference seems even more likely to occur between hit and error/miss trials (Fig 4). If these behaviours were not measured, the possibility of behavioural modulation should be discussed.

In the awake behaving electrophysiology experiments, the lick spout was not present until 500 ms after stimulus onset, so the mouse could not lick the spout. We did not record whisking or other face and jaw movements, hence we cannot say for sure whether the mice performed early ‘licks’ in the absence of the lick spout. We did, however, add a supplementary figure showing the licking behavior of the mice in the optogenetic interference experiments (see Figure 1—figure supplement 5). In this experiment, the lick spout was present at all times so all early licks would be recorded. Any licks before 200 ms after stimulus onset were disregarded as this would be too early for the decision to include knowledge about the stimulus. Figure 1—figure supplement 5B shows that the mice indeed only performed very few early licks as they probably knew this would not yield reward. The mice that performed the awake electrophysiology experiments were trained on the same task as these mice before introducing the lick spout delay of 500 ms. So although we cannot rule out early licks during electrophysiology, we think early licks would be an unlikely explanation for the neural response differences.

We have added a new supplementary figure (Figure 2—figure supplement 2) showing data for eye movements and pupil dilation during the tasks. We had excluded all trials where the mice performed eye movements between 0-450 ms after stimulus onset, and indeed we saw no eye movements during the peak of the visual response (0-250 ms). Furthermore, the pupil dilation of the mice also did not change in this period.

All in all, we view it as unlikely that the differences in neural activity in sSc were caused by either licking, eye movements or pupil-linked arousal.

3) What is the behavioural strategy of the animals? Only licks beyond 200 ms after stimulus onset determine the choice of the animal because "mice made early random licks" from 0 to 200 ms. To better understand the behavioural strategies of the animals we need to see their behavioural data, i.e. left and right licks aligned to stimulus onset. It would be particularly interesting to see how number and latency of licks changes during optogenetic manipulation.

Based on these suggestions, we investigated the licking behavior of the mice during the optogenetic experiments in more detail. Our new Figure 1—figure supplement 5 taught us several things:

1) The fully trained mice hardly perform any early licks; they seem to understand that early licks cannot yield reward.

2) The mice typically only lick one side of the lick spout during one trial. In correct trials the fluid reward is given directly after a correct lick, which causes the mouse to lick the correct side of the spout even more. However, even if the first lick is incorrect (bottom rows), the mouse generally does not lick the other (correct) side afterward. They seem to know that correct licks after an incorrect lick do not yield reward.

3) The maximum licking rates were not significantly affected by laser onset.

4) The latency of the first lick (reaction time) was not significantly affected by laser onset. (Please also see our response to question 2b).

4) Data relating to misses should be included in analyses to provide a complete picture of behaviour and neural responses

a) In the optogenetic manipulations, an increase in misses seems to dominate the decreased accuracy (please, explain when a response was counted as a miss). A separate analysis of miss trials may be more robust than of error trials and also offers a different interpretation of the data, namely that the mouse did not see the stimulus rather than perceiving the figure on the opposite side. However, if the mice reduced their lick rate in general during optogenetic stimulation, this begs the question whether their motor performance was affected by optogenetic manipulation. Can this possibility be excluded?

Trials were counted as follows: A trial was counted as a hit when the first lick after 200 ms after stimulus onset was on the correct side. A trial was counted as an error, when the first lick after 200 ms after stimulus onset was on the incorrect side. A trial was counted as a miss, when the mouse did not lick in the window between 200 and 2000 ms after stimulus onset. We have clarified this in the methods section (line 517-526).

Our previous text may not have been sufficiently clear but the decrease in accuracy during optogenetic trials is not dominated by an increase in missed trials. As we have now indicated explicitly in its caption, in figure 1, missed trials are excluded from the analysis. Hence, the significant effects shown in figure 1 are not driven by an increase in missed trials but rather by an increase in erroneous licks. When comparing figure 1 vs figure S3, where the missed trials are added to the analysis as if they were error trials, we can see an overall downward shift of the performances. Indeed, mice miss more trials when the laser is on. The increase in number of missed trials is lower than the increase in number of wrong choices. Furthermore, the range between the performances at early laser onset and late laser onset is still very similar. This indicates that the mice on average do not have higher miss rates when laser onset is early.

Finally, nor maximum licking rate, nor the reaction time is affected by the laser onset (see the new figure S2)

Related to Fig 4, it would be equally interesting to see how FGM changes during misses. Do the changes support the observations for error trials?

We are not convinced that the neural data from missed trials can be interpreted in a simple way. Mice may have various reasons to miss a trial: they may be tired or not paying attention, they may not have seen the stimulus well, they may not feel thirsty enough, they might be distracted by some sensory input that humans might not be aware of, etc. This is why we specifically opted to not use a go-no/go task but instead opted to use a 2-alternative forced choice task.

5) Statistical tests do not support the conclusions, are missing or inadequate

a) In Fig 1E, accuracy is significantly affected at only 1-2 time points in each task, specifically either the 1st and 3rd or the 2nd time point. How do the authors interpret these results? If inhibition starting at the 2nd time point has no significant effects, why would it be significant when inhibition starts later (at the 3rd time)? Furthermore, given that all other starting points of laser stimulation have no significant effects, there is no reason to trust the latency of inhibition effects based on mostly insignificant data points. This analysis in its current form should be removed, including a comparison of latencies between tasks, which was not tested for significance. It may be more meaningful to analyse accuracy for each animal separately. This may reduce variability.

We can understand that the reviewer may have concerns regarding the post-hoc analysis of Fig 1E, but we feel these concerns stem from a misinterpretation of our goal with this analysis. In Figure 1E, we use a 1-way repeated-measures ANOVA. By using this test, we ask whether the performance of the animals is affected by the laser onset. More specifically “does the performance increase or decrease with increasing laser onset?” The test is significant, so indeed the performance goes up as laser onset goes up. This indicates that the performance of the mice is affected by the inhibition of sSC. For the sake of completeness we had included the post-hoc tests for each latency in the statistics table. Indeed, some individual latencies are not significantly different to the no-laser condition. However, this does not invalidate the conclusion of the main test: a repeated measures ANOVA can only be performed on data with 3 or more groups, so the conclusion of the repeated measures ANOVA could not have been drawn from simply those laser onset(s) that is/are significantly different from the no-laser condition. The main effect of higher performance with higher latencies is significant, even if some individual comparisons are non-significant. The difference in significance of the post-hoc tests does not indicate a significant difference between the groups, but insufficient power to do six individual tests.

We have changed the wording in the reporting of the statistics of Figure 1E to hopefully more precisely indicate the conclusions we drew from the statistics. We do not draw conclusions from the post hoc tests. We have considered removing them from the statistics table 1, but believe that some readers might be interested. We can remove them if the reviewer believes that would be better.

b) Analyses regarding the difference in neural response to figure and ground (Fig 2I-J, Fig 3B, Fig 4B, Fig 5C) would be more convincing and informative if the differences were analysed on the level of single neurons in response to the same orientation within their RF (or at the location where the figure is presented, for edge-RF neurons). A histogram of these differences would show how many neurons are affected and how large the effect is in single neurons.

We fully appreciate this idea, but the way we set up the behavioural task does not quite allow for this type of statistical analysis. This is because we tested all three of the tasks during single sessions (contrast/orientation/phase), and on top of that, we varied the orientations of the stimuli (0/90deg), as well as the phase of the gratings (60 different phases). This all was done with the idea that it would prevent the mice from memorizing the individual stimuli of the task. This also had the effect that only very few trials per session contained the exact same stimulus type, figure-ground condition, orientation and phase. For example, if a mouse would perform around 120 trials in a session. 25% of those were contrast-stimulus-trials, 37.5% of those were orientation-stimulus-trials and 37,5% were phase trials. If we look into 120*0.375 = 45 orientation-stimulus-trials, half of those were figure trials, half were ground trials: 22 trials each. If we split these trials up by their individual orientations, we are left with only about 11 trials per condition to analyse for figure-ground effects, each of which would probably have a different grating phase. Given the firing rate variations that the individual neurons show in awake mice, this amount of trials would not provide enough statistical power to test the significance of modulation in single neurons.

Although we feel the study design would not allow analysis of individual neurons in response to the same orientation within their RF, we did perform an aggregated analysis on orientation selectivity. For this analysis, we included all the trials where the RF of the recorded neurons was on the background-half of the screen. We then computed the responses of each neuron to the trials where the background orientation was 0 and 90, respectively. This analysis showed that most neurons had no preference for either of the two tested orientations of the other. Only 4 out of 64 (6%) neurons showed a significant preference. We therefore believe that splitting the data by orientation preference would not be very informative.

c) All statistical tests performed across neurons should account for dependencies due to simultaneous recordings (dependency on session) and due to recordings in the same animal (dependency on animal). This can be done in most cases by using linear mixed-effects models.

We agree with the reviewer and have changed the analysis for figure 2I, 3B and 3E to an LME analysis (see also Table 1).

d) There was no significant difference between model weights (Fig 3D), so the statement in line 210 (RF-edge neurons had higher weights) should be removed.

In answer to previous we question changed the analysis for what is now Figure 3E to an LME. This shows that relative weights were significantly higher for the orientation compared to the phase task. We have adapted our conclusion accordingly (line 214-218).

e) Fig 4B compares FGM during correct and error trials. This comparison has to be performed with the same set of neurons in correct and error trials (not the case for orientation). Again, the most compelling and informative comparison would be on the level of single neurons: response difference between figure and ground (same visual features at figure position) during hits versus errors.

As described above, we feel the study design does not allow analysis on the level of individual neurons. The analysis in 4B was actually performed using the same set of neurons, we have removed the typo.

f) There is no evidence that FGM for phase was different between hit and error trials as stated in line 234.

Indeed, we had phrased this incorrectly. Since we recorded all task during single recording sessions, we have data for each task for most neurons. We were therefore able to pool the results from the different tasks, and the main d-prime difference between hit vs. error was significant. Post-hoc tests showed that this is mainly driven by the difference in the orientation task. We have edited the wording to be more accurate (line 239-242).

g) It is not clear why and how the mixed linear effects model was used pooling data across tasks (Fig 4C and Fig 5D). Different neurons were recorded for each task, so the sample points (neurons) are not affected by both task effects (orientation and phase). Each task should be analysed separately.

Since we recorded all three task versions during single behavioral sessions, we have data for multiple tasks from each neuron. This is why the linear mixed effects model pools the data across the tasks. We have added a note in the main text for clarity (line 238-242)

h) Bonferroni correction in Fig 1E should correct multiple comparisons across time points, not across tasks (see Table 1).

The multiple time points all belong to the same one-way repeated measures ANOVA, so there’s no need to correct the post-hoc analysis. We did run the ANOVA for three tasks, which is why we corrected the p-values of each task. We think that this is best way, but can also present uncorrected p-values if needed.

i) What is the reason to perform some tests one-tailed, others two-tailed?

Following the reviewer comments, we changed some analyses to LME models. The remaining tests that require definition of the tails are all two-tailed.

6) The results relating to "multisensory neurons" are ambiguous regarding their interpretation (if significant at all) and seem unrelated to the goal of the study. It is particularly likely that behaviours like licking or other movements cause the response differences between figure and ground.

We agree with the reviewer that finding these neurons was not the aim of the study. We did not include enough type of tests in our paradigm to fully determine the properties of these neurons. Furthermore, we note that we have recorded too few of these neurons to draw strong conclusions. The data shown in new Figure 2—figure supplement 1H suggest that the responses of these neurons or not as strongly time-locked to the first lick as they are to the trial onset. We presented the behavior of these neurons in our manuscript, because, whatever their exact behavior, they are clearly distinct from the visually responsive cells that show a short latency response to the visual stimulus (Figure 2—figure supplement 1). We still feel that it is useful for the reader to know there are cells in the sSC that show such a distinct behavior, but we have moved the figure and the accompanying text to a figure supplement to avoid distraction from the main message of the manuscript.

7) What depth were neurons recorded from (Fig 3 and 4)?

The depths of the recorded visually responsive neurons is now shown in Figure 2—figure supplement 1E.

Reviewer #3 (Public Review):

The authors used optogenetic manipulations and electrophysiology recordings to study a causal role and the coding of superficial part of the mouse Superior Colliculus (SCs) during figure detection tasks.

Authors previously reported that figure-ground perception relies on V1 activity (Kirchberger et al. 2021) and pointed out that silencing of V1 reduced the accuracy of the mice but still the performance was above the chance level. Therefore, visual information necessary in this task, could be processed via alternative pathways. In this study, authors investigated specifically SCs and used similar approach and analysis as in Kirchberger et al. 2021. Optogenetic silencing of the activity of visual neurons in SCs impaired the accuracy in all 3 versions of the figure detection task: contrast, orientation, and phase. Electrophysiology recordings revealed that SCs neurons are figure-ground modulated, but only by contrast- and orientation-based figures. They show SCs visually responsive neurons reflect behavioral performance in orientation-based figure task. The authors conclusion is that SCs is involved in figure detection task.

Overall, this study provides evidence that mouse SCs is involved in a figure detection task, and codes for task-related events. Authors heroically compared results between 3 different versions of the figure-based detection task. The logic of the study flows through the manuscript and authors prepared a detailed description of methods.

Thank you for your positive comments.

However, my main concern is with 1) the amount of data used to make the key arguments, and 2) the interpretation of results. The key findings of this study (figure-ground modulations in SCs) could be a result of the visual cortical feedback in SCs during the task, or pupil diameter changes. Unfortunately, the authors did not rule out these possibilities.

Still, this study can be relevant to a general neuroscience audience, and results could be more convincing if the authors could clarify:

1) Optogenetic inactivation

a) The impact of laser stimulation on neural activity is not satisfactory (Supplementary Figure 1). The method seems to be insufficient to fully salience neurons. Electrophysiology control recordings of inactivation are performed in anesthetized mice, which is not a fair estimation of the effect in awake state. Therefore, it rises a major question how effective the inactivation is during the task?

We have conducted new control experiments for the impact of laser stimulation on neural activity, now in awake animals (see Figure 1—figure supplement 2). The reviewer was right to ask for these experiments. We had not expected much difference in the effect of silencing in the awake and anesthetized state. To minimize the animal discomfort, we had therefore done these control experiments in terminal experiments under anesthesia. However, these new set of experiments showed that the impact of laser stimulation was much stronger in awake mice than anesthetized mice. We see an average spike rate reduction of 90% when the laser is on. Although it is not full silencing, we think this reduction is sufficient to draw some conclusions on the role of sSC in the behavioral tasks.

b) Could authors provide more details if laser stimulation has an effect only on visual, or all sampled units? How many of units were recorded, and how many show positive and negative laser modulation?

We defined visually responsive units as units that have an evoked rate of at least 2 spikes/s. In the new figure 1—figure supplement 2D from the new set of control experiments, we plotted, for every unit, the mean rate in laser ON and OFF trials - also including the non-visually responsive units. It is evident that the spiking activity of most units – including those that were not classified as ‘visual’ – is reduced in the laser ON compared to OFF trials. We observed 1 unit that showed strong positive laser modulation over the entire duration (figure 1—figure supplement 1D). Many units were activated by shorter laser pulses directly after laser onset (Figure 1—figure supplement 2A-B), but these also reduced in activity as the stimulation continued.

c) How local the inactivation effect is? Where was the silicon probe placed in relation to AAV expression and optical fiber position?

The AAV was injected at 0.3 mm anterior and 0.5 mm lateral to the lambda cranial landmark. With this injection location we aimed to focus the expression at low/nasal receptive fields, in front of the mouse, because that is where the visual stimulation would take place. From there, the expression did spread laterally across sSC (see Figure 1C). The silicon probe was placed roughly in the same location as the viral injection. The optical fiber was positioned such that the tip would shine on the surface of the sSC at a slight angle, from a lateral distance of ~200 µm from the silicon probe. We have edited the methods section to make this more clear (line 583-585). This procedure allowed us to record only relatively local effects of the inactivation. Although we did not record neural activity across the entirety of sSC, we did record from multiple electrode penetrations per mouse, each time slightly varying the recording location with up to ~300µm and ~500µm in the anterior and lateral directions, respectively. In these variations of recording location the optogenetic effect was always present (see new Figure 1—figure supplement 2G). Moreover, the suppressive effect of optogenetic stimulation of GAD2+ neurons was observed across the entire depth of the sSC (new Figure 1—figure supplement 2H).

2) Number of sessions and units

a) The inactivation effect on behavior (Figure 1E) during phase-task has a significantly larger effect at 66ms after stimulus onset. How can authors explain this? Could this result be biased by one animal/session, or low number of trials for this condition? There is no information about number of trials, or sessions from individual animals. Adding a single example of animal's performance, and sessions for individual mice could clarify results in Figure 1.

The criterium for each mouse to be included in the analysis for one of the tasks was to have 100 trials where optogenetics were used (aggregated across the latencies). So at minimum, we would have about 100 trials/6 latencies = 17 trials per latency per mouse. For most mice though, the number of trials per latency was closer to about 40. We have added more information about this to the methods section (lines 567-570). Despite these inclusion criteria, the 66 ms effect is present for multiple mice (we have now added data visualizations for the individual mice in Figure 1—figure supplement 4). To address the reviewer’s concerns, we can only speculate as to why this happens. It might be random variation. A more speculative conclusion would be that perhaps this 66ms laser onset is particularly disturbing to the visual processing and/or decision-making of the mouse. But we feel that we do not have enough evidence to conclude this.

b) Figure 2H shows an example of neuron with an effect in the figure detection task based on phase difference, but Figure 2I/J (population response) shows there is no effect. Overall, the conclusion is that SCs neurons are not modulated by a phase-defined object. It seems that number of mice and hence units are smaller in phase-detection task comparing to two other tasks. How many of single units are modulated in each version of the task? How big is the FGM effect on single neuron response (could authors provide values in spikes/s)? One task is dropped from analysis which it is one of the main points of the paper: to compare responses across different versions of the figure detection task in SCs. But Figures 3-5 only focuses on two tasks, because there is not enough of data for figure-based contrast task.

We have updated Figure 2H to show spikes/s of the example single neuron response. For the population responses, we explicitly normalized the individual neurons because they all have different baseline and peak firing rates. This normalization was important for the decoding, so we decided to print the data such that the data from Figures 2I and 3B went into the decoding as printed. If we look at the non-normalized values, the maximum amplitude of the average FGM effect is 22.3, 5.9 and 2.9 sp/s respectively for the three tasks (for neurons with RF on stimulus center).

We have furthermore updated the FGM analysis such that the clustered statistic is now based on linear mixed effects statistics instead of T-test statistics. The results based on this new analysis are largely the same (see statistics table T1). We checked the significance of individual neurons in the time window where the grouped LME analysis was significant. For the phase task (n.s. in grouped analysis), we used the significant window from the orientation task. For this analysis, we want to stress that the number of trials for each version of the task for each individual neurons is quite limited as we recorded all three of the tasks during each recording session. Individually, 7/23 neurons were significant for the contrast task, 1/49 were significant for the orientation task, 0/32 were significant for the phase task (after Bonferroni-holm correction).

To address the final part of this comment on dropping the contrast task: we indeed have recorded too few data points to draw conclusions on decoding (Fig. 3) and discriminability (Fig. 4) for the contrast task. However, we do not see the contrast detection task as the main point of the paper. As earlier work had already shown involvement of the sSC in visually-evoked behaviours based on objects that are clearly isolated from the background, the main focus in this work is to show involvement of sSC in complex object detection, where the visual contrast and luminance is the same across object and background.

3) Figure-ground modulation in SCs

a) How is neural activity correlated with pupil size, movement (eg. whisking, or face), or jaw movement (preparation to lick)? Can activity of FGM neurons in SCs be explained by these behavioral variables?

We did not record whisking or other face and jaw movements. We did record the eye of the mice, so have included a new Figure 2—figure supplement 2 which shows eye position and pupil dilation during the task. For the analysis in the originally submitted paper, trials with substantial eye movement (Z-score of eye speed > 2.5) between 0 and 450 ms had already been removed from the analysis. This way, we could exclude effects of eye movements (but not pupil dilation) on the visual responses in sSC. The additional figures and analyses have been done using the same inclusion criteria. Indeed, in the included trials mice did not move their eyes during the peak of the visual response (0-250 ms). The pupil dilation also did not change in this period.

b) Could authors describe in more detail how they measure a pupil position and diameter, by showing raw data, pupil size aligned to task events?

We have added a new Figure 2—figure supplement 2 to show the pupil position and diameter aligned to task onset.

c) How does pupil diameter change between tasks? Small pupil changes can affect responses of visual neurons, and this could be an explanation of FGM effect in SCs. Can authors rule out this possibility, by for example showing pupil size and changes in position at stimulus onset in different tasks?

Our new Figure 2—figure supplement 2B shows that pupil dilation changes and differences in pupil dilation between figure/ground trials do occur, but only after ~300 ms, so after the peak of the visual response and after the FGM is present in sSC.

d) Authors in discussion mentioned that the modulation of V1 could be transferred to SCs through the direct projection. Moreover, animals perform above chance in both inactivation experiments (V1 and SC), which could be also an effect of geniculate projections to HVAs (eg. Sincich et al. 2004). Could authors discuss different possibilities?

The direct geniculate projection to HVAs is an interesting possibility that we had not considered yet. The dLGN in the mouse projects (apart from V1) mostly to the medial HVAs (Bienkowski et al. 2018). The lateral extrastriate regions receive only very sparse input from the dLGN. The medial HVAs, however, could be silenced without drop in performance in a simple visual detection task (Goldback et al., 2020). Therefore, it does not seem likely that this geniculate to HVAs projections would be important in the figure detection task.

4) Interpretation of multisensory neurons is not clear. In Figure 5B, there is an example of neuron with two peaks of response. Authors speculate about the activity (pre-motor) but there is lack of clear measurement showing "multisensory" response of these neurons. Could these responses be related to the movement of the lick spout towards the mouth of the mouse (500 ms after the presentation of the stimulus)? Moreover, the number of "multisensory" units is very low (5 units, and 8 units).

We have not done definitive test to show what these putative multisensory neurons exactly respond to. Because of their response was after the appearance of the lick and time locking to the trial start, rather than to the licking response, we think that is likely that these neurons responded to the appearance of the spout. There might have been visual, auditory, vibrational or touch clues to which these neurons respond. We believe it is interesting for the reader to know that there is class of neurons in the sSC that did not show a visual stimulus but was time locked to the trial. This was the reason that we had included this figure in the manuscript. However, given the reviewers comments we have decided to move the figure and accompanying text to a figure supplement (Figure 2—figure supplement 1) in order to not distract from the main message of the manuscript.

Author Response

eLife assessment

This study presents potentially valuable results on glutamine-rich motifs in relation to protein expression and alternative genetic codes. The author's interpretation of the results is so far only supported by incomplete evidence, due to a lack of acknowledgment of alternative explanations, missing controls and statistical analysis and writing unclear to non experts in the field. These shortcomings could be at least partially overcome by additional experiments, thorough rewriting, or both.

We thank both the Reviewing Editor and Senior Editor for handling this manuscript and will submit our revised manuscript after the reviewed preprint is published by eLife.  

Reviewer #1 (Public Review):

Summary

This work contains 3 sections. The first section describes how protein domains with SQ motifs can increase the abundance of a lacZ reporter in yeast. The authors call this phenomenon autonomous protein expression-enhancing activity, and this finding is well supported. The authors show evidence that this increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance, and that this phenomenon is not affected by mutants in translational quality control. It was not completely clear whether the increased protein abundance is due to increased translation or to increased protein stability.

In section 2, the authors performed mutagenesis of three N-terminal domains to study how protein sequence changes protein stability and enzymatic activity of the fusions. These data are very interesting, but this section needs more interpretation. It is not clear if the effect is due to the number of S/T/Q/N amino acids or due to the number of phosphorylation sites.

In section 3, the authors undertake an extensive computational analysis of amino acid runs in 27 species. Many aspects of this section are fascinating to an expert reader. They identify regions with poly-X tracks. These data were not normalized correctly: I think that a null expectation for how often poly-X track occur should be built for each species based on the underlying prevalence of amino acids in that species. As a result, I believe that the claim is not well supported by the data.

Strengths

This work is about an interesting topic and contains stimulating bioinformatics analysis. The first two sections, where the authors investigate how S/T/Q/N abundance modulates protein expression level, is well supported by the data. The bioinformatics analysis of Q abundance in ciliate proteomes is fascinating. There are some ciliates that have repurposed stop codons to code for Q. The authors find that in these proteomes, Q-runs are greatly expanded. They offer interesting speculations on how this expansion might impact protein function.

Weakness

At this time, the manuscript is disorganized and difficult to read. An expert in the field, who will not be distracted by the disorganization, will find some very interesting results included. In particular, the order of the introduction does not match the rest of the paper.

In the first and second sections, where the authors investigate how S/T/Q/N abundance modulates protein expression levels, it is unclear if the effect is due to the number of phosphorylation sites or the number of S/T/Q/N residues.

There are three reasons why the number of phosphorylation sites in the Q-rich motifs is not relevant to their autonomous protein expression-enhancing (PEE) activities:

First, we have reported previously that phosphorylation-defective Rad51-NTD (Rad51-3SA) and wild-type Rad51-NTD exhibit similar autonomous PEE activity. Mec1/Tel1-dependent phosphorylation of Rad51-NTD antagonizes the proteasomal degradation pathway, increasing the half-life of Rad51 from ∼30 min to ≥180 min (Ref 27; Woo, T. T. et al. 2020).

1. T. T. Woo, C. N. Chuang, M. Higashide, A. Shinohara, T. F. Wang, Dual roles of yeast Rad51 N-terminal domain in repairing DNA double-strand breaks. Nucleic Acids Res 48, 8474-8489 (2020).

Second, in our preprint manuscript, we have also shown that phosphorylation-defective Rad53-SCD1 (Rad51-SCD1-5STA) also exhibits autonomous PEE activity similar to that of wild-type Rad53-SCD (Figure 2D, Figure 4A and Figure 4C).

Third, as revealed by the results of our preprint manuscript (Figure 4), it is the percentages, and not the numbers, of S/T/Q/N residues that are correlated with the PEE activities of Q-rich motifs.

The authors also do not discuss if the N-end rule for protein stability applies to the lacZ reporter or the fusion proteins.

The autonomous PEE function of S/T/Q-rich NTDs is unlikely to be relevant to the N-end rule. The N-end rule links the in vivo half-life of a protein to the identity of its N-terminal residues. In S. cerevisiae, the N-end rule operates as part of the ubiquitin system and comprises two pathways. First, the Arg/N-end rule pathway, involving a single N-terminal amidohydrolase Nta1, mediates deamidation of N-terminal asparagine (N) and glutamine (Q) into aspartate (D) and glutamate (E), which in turn are arginylated by a single Ate1 R-transferase, generating the Arg/N degron. N-terminal R and other primary degrons are recognized by a single N-recognin Ubr1 in concert with ubiquitin-conjugating Ubc2/Rad6. Ubr1 can also recognize several other N-terminal residues, including lysine (K), histidine (H), phenylalanine (F), tryptophan (W), leucine (L) and isoleucine (I) (Bachmair, A. et al. 1986; Tasaki, T. et al. 2012; Varshavshy, A. et al. 2019). Second, the Ac/N-end rule pathway targets proteins containing N-terminally acetylated (Ac) residues. Prior to acetylation, the first amino acid methionine (M) is catalytically removed by Met-aminopeptides, unless a residue at position 2 is non-permissive (too large) for MetAPs. If a retained N-terminal M or otherwise a valine (V), cysteine (C), alanine (A), serine (S) or threonine (T) residue is followed by residues that allow N-terminal acetylation, the proteins containing these AcN degrons are targeted for ubiquitylation and proteasome-mediated degradation by the Doa10 E3 ligase (Hwang, C. S., 2019).

A. Bachmair, D. Finley, A. Varshavsky, In vivo half-life of a protein is a function of its amino-terminal residue. Science 234, 179-186 (1986).

T. Tasaki, S. M. Sriram, K. S. Park, Y. T. Kwon, The N-end rule pathway. Annu Rev Biochem 81, 261-289 (2012).

A. Varshavsky, N-degron and C-degron pathways of protein degradation. Proc Natl Acad Sci 116, 358-366 (2019).

C. S. Hwang, A. Shemorry, D. Auerbach, A. Varshavsky, The N-end rule pathway is mediated by a complex of the RING-type Ubr1 and HECT-type Ufd4 ubiquitin ligases. Nat Cell Biol 12, 1177-1185 (2010).

The PEE activities of these S/T/Q-rich domains are unlikely to arise from counteracting the N-end rule for two reasons. First, the first two amino acid residues of Rad51-NTD, Hop1-SCD, Rad53-SCD1, Sup35-PND, Rad51-ΔN, and LacZ-NVH are MS, ME, ME, MS, ME, and MI, respectively, where M is methionine, S is serine, E is glutamic acid and I is isoleucine. Second, Sml1-NTD behaves similarly to these N-terminal fusion tags, despite its methionine and glutamine (MQ) amino acid signature at the N-terminus.

The most interesting part of the paper is an exploration of S/T/Q/N-rich regions and other repetitive AA runs in 27 proteomes, particularly ciliates. However, this analysis is missing a critical control that makes it nearly impossible to evaluate the importance of the findings. The authors find the abundance of different amino acid runs in various proteomes. They also report the background abundance of each amino acid. They do not use this background abundance to normalize the runs of amino acids to create a null expectation from each proteome. For example, it has been clear for some time (Ruff, 2017; Ruff et al., 2016) that Drosophila contains a very high background of Q's in the proteome and it is necessary to control for this background abundance when finding runs of Q's.

We apologize for not explaining sufficiently well the topic eliciting this reviewer’s concern in our preprint manuscript. In the second paragraph of page 14, we cite six references to highlight that SCDs are overrepresented in yeast and human proteins involved in several biological processes (32, 74), and that polyX prevalence differs among species (43, 75-77).

1. Cheung HC, San Lucas FA, Hicks S, Chang K, Bertuch AA, Ribes-Zamora A. An S/T-Q cluster domain census unveils new putative targets under Tel1/Mec1 control. BMC Genomics. 2012;13:664.

2. Mier P, Elena-Real C, Urbanek A, Bernado P, Andrade-Navarro MA. The importance of definitions in the study of polyQ regions: A tale of thresholds, impurities and sequence context. Comput Struct Biotechnol J. 2020;18:306-13.

3. Cara L, Baitemirova M, Follis J, Larios-Sanz M, Ribes-Zamora A. The ATM- and ATR-related SCD domain is over-represented in proteins involved in nervous system development. Sci Rep. 2016;6:19050.

4. Kuspa A, Loomis WF. The genome of Dictyostelium discoideum. Methods Mol Biol. 2006;346:15-30.

5. Davies HM, Nofal SD, McLaughlin EJ, Osborne AR. Repetitive sequences in malaria parasite proteins. FEMS Microbiol Rev. 2017;41(6):923-40.

6. Mier P, Alanis-Lobato G, Andrade-Navarro MA. Context characterization of amino acid homorepeats using evolution, position, and order. Proteins. 2017;85(4):709-19.

We will cite the two references by Kiersten M. Ruff in our revised manuscript.

K. M. Ruff and R. V. Pappu, (2015) Multiscale simulation provides mechanistic insights into the effects of sequence contexts of early-stage polyglutamine-mediated aggregation. Biophysical Journal 108, 495a.

K. M. Ruff, J. B. Warner, A. Posey and P. S. Tan (2017) Polyglutamine length dependent structural properties and phase behavior of huntingtin exon1. Biophysical Journal 112, 511a.

The authors could easily address this problem with the data and analysis they have already collected. However, at this time, without this normalization, I am hesitant to trust the lists of proteins with long runs of amino acid and the ensuing GO enrichment analysis.

Ruff KM. 2017. Washington University in St.

Ruff KM, Holehouse AS, Richardson MGO, Pappu RV. 2016. Proteomic and Biophysical Analysis of Polar Tracts. Biophys J 110:556a.

We thank Reviewer #1 for this helpful suggestion and now address this issue by means of a different approach described below.

Based on a previous study (43; Palo Mier et al. 2020), we applied seven different thresholds to seek both short and long, as well as pure and impure, polyX strings in 20 different representative near-complete proteomes, including 4X (4/4), 5X (4/5-5/5), 6X (4/6-6/6), 7X (4/7-7/7), 8-10X (≥50%X), 11-10X (≥50%X) and ≥21X (≥50%X).

To normalize the runs of amino acids and create a null expectation from each proteome, we determined the ratios of the overall number of X residues for each of the seven polyX motifs relative to those in the entire proteome of each species, respectively. The results of four different polyX motifs are shown below, i.e., polyQ (Author response image 1), polyN (Author response image 2), polyS (Author response image 3) and polyT (Author response image 4).

Author response image 1.

Q contents in 7 different types of polyQ motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.  

Author response image 2.

N contents in 7 different types of polyN motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author response image 3.

S contents in 7 different types of polyS motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.  

Author response image 4.

T contents in 7 different types of polyT motifs in 20 near-complete proteomes. The five ciliates with reassigned stops codon (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

The results summarized in these four new figures support that polyX prevalence differs among species and that the overall X contents of polyX motifs often but not always correlate with the X usage frequency in entire proteomes (43; Palo Mier et al. 2020).

Most importantly, our results reveal that, compared to Stentor coeruleus or several non-ciliate eukaryotic organisms (e.g., Plasmodium falciparum, Caenorhabditis elegans, Danio rerio, Mus musculus and Homo sapiens), the five ciliates with reassigned TAAQ and TAGQ codons not only have higher Q usage frequencies, but also more polyQ motifs in their proteomes (Figure 1). In contrast, polyQ motifs prevail in Candida albicans, Candida tropicalis, Dictyostelium discoideum, Chlamydomonas reinhardtii, Drosophila melanogaster and Aedes aegypti, though the Q usage frequencies in their entire proteomes are not significantly higher than those of other eukaryotes (Figure 1). Due to their higher N usage frequencies, Dictyostelium discoideum, Plasmodium falciparum and Pseudocohnilembus persalinus have more polyN motifs than the other 23 eukaryotes we examined here (Figure 2). Generally speaking, all 26 eukaryotes we assessed have similar S usage frequencies and percentages of S contents in polyS motifs (Figure 3). Among these 26 eukaryotes, Dictyostelium discoideum possesses many more polyT motifs, though its T usage frequency is similar to that of the other 25 eukaryotes (Figure 4).

In conclusion, these new normalized results confirm that the reassignment of stop codons to Q indeed results in both higher Q usage frequencies and more polyQ motifs in ciliates.  

Reviewer #2 (Public Review):

Summary:

This study seeks to understand the connection between protein sequence and function in disordered regions enriched in polar amino acids (specifically Q, N, S and T). While the authors suggest that specific motifs facilitate protein-enhancing activities, their findings are correlative, and the evidence is incomplete. Similarly, the authors propose that the re-assignment of stop codons to glutamine-encoding codons underlies the greater user of glutamine in a subset of ciliates, but again, the conclusions here are, at best, correlative. The authors perform extensive bioinformatic analysis, with detailed (albeit somewhat ad hoc) discussion on a number of proteins. Overall, the results presented here are interesting, but are unable to exclude competing hypotheses.

Strengths:

Following up on previous work, the authors wish to uncover a mechanism associated with poly-Q and SCD motifs explaining proposed protein expression-enhancing activities. They note that these motifs often occur IDRs and hypothesize that structural plasticity could be capitalized upon as a mechanism of diversification in evolution. To investigate this further, they employ bioinformatics to investigate the sequence features of proteomes of 27 eukaryotes. They deepen their sequence space exploration uncovering sub-phylum-specific features associated with species in which a stop-codon substitution has occurred. The authors propose this stop-codon substitution underlies an expansion of ploy-Q repeats and increased glutamine distribution.

Weaknesses:

The preprint provides extensive, detailed, and entirely unnecessary background information throughout, hampering reading and making it difficult to understand the ideas being proposed. The introduction provides a large amount of detailed background that appears entirely irrelevant for the paper. Many places detailed discussions on specific proteins that are likely of interest to the authors occur, yet without context, this does not enhance the paper for the reader.

The paper uses many unnecessary, new, or redefined acronyms which makes reading difficult. As examples:

(1) Prion forming domains (PFDs). Do the authors mean prion-like domains (PLDs), an established term with an empirical definition from the PLAAC algorithm? If yes, they should say this. If not, they must define what a prion-forming domain is formally.

The N-terminal domain (1-123 amino acids) of S. cerevisiae Sup35 was already referred to as a “prion forming domain (PFD)” in 2006 (Tuite, M. F. 2006). Since then, PFD has also been employed as an acronym in other yeast prion papers (Cox, B.S. et al. 2007; Toombs, T. et al. 2011).

M. F., Tuite, Yeast prions and their prion forming domain. Cell 27, 397-407 (2005).

B. S. Cox, L. Byrne, M. F., Tuite, Protein Stability. Prion 1, 170-178 (2007).

J. A. Toombs, N. M. Liss, K. R. Cobble, Z. Ben-Musa, E. D. Ross, [PSI+] maintenance is dependent on the composition, not primary sequence, of the oligopeptide repeat domain. PLoS One 6, e21953 (2011).

(2) SCD is already an acronym in the IDP field (meaning sequence charge decoration) - the authors should avoid this as their chosen acronym for Serine(S) / threonine (T)-glutamine (Q) cluster domains. Moreover, do we really need another acronym here (we do not).

SCD was first used in 2005 as an acronym for the Serine (S)/threonine (T)-glutamine (Q) cluster domain in the DNA damage checkpoint field (Traven, A. and Heierhorst, J. 2005). Almost a decade later, SCD became an acronym for “sequence charge decoration” (Sawle, L. et al. 2015; Firman, T. et al. 2018).

A. Traven and J, Heierhorst, SQ/TQ cluster domains: concentrated ATM/ATR kinase phosphorylation site regions in DNA-damage-response proteins. Bioessays. 27, 397-407 (2005).

L. Sawle and K, Ghosh, A theoretical method to compute sequence dependent configurational properties in charged polymers and proteins. J. Chem Phys. 143, 085101(2015).

T. Firman and Ghosh, K. Sequence charge decoration dictates coil-globule transition in intrinsically disordered proteins. J. Chem Phys. 148, 123305 (2018).

(3) Protein expression-enhancing (PEE) - just say expression-enhancing, there is no need for an acronym here.

Thank you. Since we have shown that addition of Q-rich motifs to LacZ affects protein expression rather than transcription, we think it is better to use the “PEE” acronym.

The results suggest autonomous protein expression-enhancing activities of regions of multiple proteins containing Q-rich and SCD motifs. Their definition of expression-enhancing activities is vague and the evidence they provide to support the claim is weak. While their previous work may support their claim with more evidence, it should be explained in more detail. The assay they choose is a fusion reporter measuring beta-galactosidase activity and tracking expression levels. Given the presented data they have shown that they can drive the expression of their reporters and that beta gal remains active, in addition to the increase in expression of fusion reporter during the stress response. They have not detailed what their control and mock treatment is, which makes complete understanding of their experimental approach difficult. Furthermore, their nuclear localization signal on the tag could be influencing the degradation kinetics or sequestering the reporter, leading to its accumulation and the appearance of enhanced expression. Their evidence refuting ubiquitin-mediated degradation does not have a convincing control.

Based on the experimental results, the authors then go on to perform bioinformatic analysis of SCD proteins and polyX proteins. Unfortunately, there is no clear hypothesis for what is being tested; there is a vague sense of investigating polyX/SCD regions, but I did not find the connection between the first and section compelling (especially given polar-rich regions have been shown to engage in many different functions). As such, this bioinformatic analysis largely presents as many lists of percentages without any meaningful interpretation. The bioinformatics analysis lacks any kind of rigorous statistical tests, making it difficult to evaluate the conclusions drawn. The methods section is severely lacking. Specifically, many of the methods require the reader to read many other papers. While referencing prior work is of course, important, the authors should ensure the methods in this paper provide the details needed to allow a reader to evaluate the work being presented. As it stands, this is not the case.

Thank you. As described in detail below, we have now performed rigorous statistical testing using the GofuncR package.

Overall, my major concern with this work is that the authors make two central claims in this paper (as per the Discussion). The authors claim that Q-rich motifs enhance protein expression. The implication here is that Q-rich motif IDRs are special, but this is not tested. As such, they cannot exclude the competing hypothesis ("N-terminal disordered regions enhance expression").

In fact, “N-terminal disordered regions enhance expression” exactly summarizes our hypothesis.

On pages 12-13 and Figure 4 of our preprint manuscript, we explained our hypothesis in the paragraph entitled “The relationship between PEE function, amino acid contents, and structural flexibility”.

The authors also do not explore the possibility that this effect is in part/entirely driven by mRNA-level effects (see Verma Na Comms 2019).

As pointed out by the first reviewer, we show evidence that the increase in protein abundance and enzymatic activity is not due to changes in plasmid copy number or mRNA abundance (Figure 2), and that this phenomenon is not affected by translational quality control mutants (Figure 3).

As such, while these observations are interesting, they feel preliminary and, in my opinion, cannot be used to draw hard conclusions on how N-terminal IDR sequence features influence protein expression. This does not mean the authors are necessarily wrong, but from the data presented here, I do not believe strong conclusions can be drawn. That re-assignment of stop codons to Q increases proteome-wide Q usage. I was unable to understand what result led the authors to this conclusion.

My reading of the results is that a subset of ciliates has re-assigned UAA and UAG from the stop codon to Q. Those ciliates have more polyQ-containing proteins. However, they also have more polyN-containing proteins and proteins enriched in S/T-Q clusters. Surely if this were a stop-codon-dependent effect, we'd ONLY see an enhancement in Q-richness, not a corresponding enhancement in all polar-rich IDR frequencies? It seems the better working hypothesis is that free-floating climate proteomes are enriched in polar amino acids compared to sessile ciliates.

Thank you. These comments are not supported by the results in Figure 1.

Regardless, the absence of any kind of statistical analysis makes it hard to draw strong conclusions here.

We apologize for not explaining more clearly the results of Tables 5-7 in our preprint manuscript.

To address the concerns about our GO enrichment analysis by both reviewers, we have now performed rigorous statistical testing for SCD and polyQ protein overrepresentation using the GOfuncR package (https://bioconductor.org/packages/release/bioc/html/GOfuncR.html). GOfuncR is an R package program that conducts standard candidate vs. background enrichment analysis by means of the hypergeometric test. We then adjusted the raw p-values according to the Family-wise error rate (FWER). The same method had been applied to GO enrichment analysis of human genomes (Huttenhower, C., et al. 2009).

Curtis Huttenhower, C., Haley, E. M., Hibbs, M., A., Dumeaux, V., Barrett, D. R., Hilary A. Coller, H. A., and Olga G. Troyanskaya, O., G. Exploring the human genome with functional maps, Genome Research 19, 1093-1106 (2009).

The results presented in Author response image 5 and Author response image 6 support our hypothesis that Q-rich motifs prevail in proteins involved in specialized biological processes, including Saccharomyces cerevisiae RNA-mediated transposition, Candida albicans filamentous growth, peptidyl-glutamic acid modification in ciliates with reassigned stop codons (TAAQ and TAGQ), Tetrahymena thermophila xylan catabolism, Dictyostelium discoideum sexual reproduction, Plasmodium falciparum infection, as well as the nervous systems of Drosophila melanogaster, Mus musculus, and Homo sapiens (74). In contrast, peptidyl-glutamic acid modification and microtubule-based movement are not overrepresented with Q-rich proteins in Stentor coeruleus, a ciliate with standard stop codons.

1. Cara L, Baitemirova M, Follis J, Larios-Sanz M, Ribes-Zamora A. The ATM- and ATR-related SCD domain is over-represented in proteins involved in nervous system development. Sci Rep. 2016;6:19050.

Author response image 5.

Selection of biological processes with overrepresented SCD-containing proteins in different eukaryotes. The percentages and number of SCD-containing proteins in our search that belong to each indicated Gene Ontology (GO) group are shown. GOfuncR (Huttenhower, C., et al. 2009) was applied for GO enrichment and statistical analysis. The p values adjusted according to the Family-wise error rate (FWER) are shown. The five ciliates with reassigned stop codons (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author response image 6.

Selection of biological processes with overrepresented polyQ-containing proteins in different eukaryotes. The percentages and numbers of polyQ-containing proteins in our search that belong to each indicated Gene Ontology (GO) group are shown. GOfuncR (Huttenhower, C., et al. 2009) was applied for GO enrichment and statistical analysis. The p values adjusted according to the Family-wise error rate (FWER) are shown. The five ciliates with reassigned stops codons (TAAQ and TAGQ) are indicated in red. Stentor coeruleus, a ciliate with standard stop codons, is indicated in green.

Author Response

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

eLife assessment

The study provides valuable insights into allosteric regulation of BTK, a non-receptor protein kinase, challenging previous models. Using a variety of biophysical and functional techniques, the paper presents evidence that the N-terminal PH-TH domain of BTK exists in a conformational ensemble surrounding a compact SH3-SH2-kinase core, that the BTK kinase domain can form partially active dimers, and that the PH domain can form a novel inhibitory interface after SH2/SH3 disengagement. Overall the presented evidence is solid, but the EM results may be over-interpreted and the work would benefit from additional functional validation.

We made every effort in our descriptions of the cryoEM data presented for full-length BTK to not overinterpret the results. In essence this is not an ideal EM target but given the failure by us and others to capture the full-length multi-domain protein crystallographically, we decided that the albeit low resolution cryoEM data are useful to the field.

Reviewer #1 (Public Review):

The manuscript by Lin et al describes a wide biophysical survey of the molecular mechanisms underlying full-length BTK regulation. This is a continuation of this lab's excellent work on deciphering the myriad levels of regulation of BTKs downstream of their activation by plasma membrane localised receptors.

The manuscript uses a synergy of cryo EM, HDX-MS and mutational analysis to delve into the role of how the accessory domains modify the activity of the kinase domain. The manuscript essentially has three main novel insights into BTK regulation.

1) Cryo EM and SAXS show that the PHTH region is dynamic compared to the conserved Src module.

2) A 2nd generation tethered PH-kinase construct crystal of BTK reveals a unique orientation of the PH domain relative to the kinase domain, that is different from previous structures.

3) A new structure of the kinase domain dimer shows how trans-phosphorylation can be achieved.

Excitingly these structural works allow for the generation of a model of how BTK can act as a strict coincidence sensor for both activated BCR complex as well as PIP3 before it obtains full activity. To my eye the most exciting result of this work is describing how the PH domain can inhibit activity once the SH3/SH2 domain is disengaged, allowing for an additional level of regulatory control.

I have very few experimental concerns as the methods and figures are well-described and clear. As the authors are potentially saying that the previously solved PH domain-kinase interface is artefactual, additional evidence strengthening their model would be helpful to resolve any possible controversies.

We do not argue that the previously solved PH domain-kinase interface is artefactual. Instead we point out that the PH/kinase interface identified in the prior structure is incompatible with the contacts between the SH3 and kinase domains in autoinhibited BTK. This then leads us to the suggestion that a PH/kinase inhibitory interaction may instead occur upon dissociation of the SH3-SH2 cassette from the kinase domain. Our data support that model. Moreover, our data suggest the PHTH domain is dynamic, likely not settling in to one particular autoinhibitory state. Thus, it is possible the previously solved PH/kinase structure exists within the conformational ensemble of a range PH/kinase domain interactions. In an effort to clarify our think we added two sentences to the Discussion (pg. 19).

Reviewer #2 (Public Review):

In this study, multiple biophysical techniques were employed to investigate the activation mechanism of BTK, a multi-domain non-receptor protein kinase. Previous studies have elucidated the inhibitory effects of the SH3 and SH2 domains on the kinase and the potential activation mechanism involving the membranebound PIP3 inducing transient dimerization of the PH-TH domain, which binds to lipids.

The primary focus of the present study was on three new constructs: a full-length BTK construct, a construct where the PH-TH domain is connected to the kinase domain, and a construct featuring a kinase domain with a phosphomimetic at the autophosphorylation site Y551. The authors aimed to provide new insights into the autoinhibition and allosteric control of BTK.

The study reports that SAXS analysis of the full-length BTK protein construct, along with cryoEM visualization of the PH-TH domain, supports a model in which the N-terminal PH-TH domain exists in a conformational ensemble surrounding a compact/autoinhibited SH3-SH2-kinase core. This finding is interesting because it contradicts previous models proposing that each globular domain is tightly packed within the core.

Furthermore, the authors present a model for an inhibitory interaction between the N-lobe of the kinase and the PH-TH domain. This model is based on a study using a tethered complex with a longer tether than a previously reported construct where the PH-TH domain was tightly attached to the kinase domain (ref 5). The authors argue that the new structure is relevant. However, this assertion requires further explanation and discussion, particularly considering that the functional assays used to assess the impact of mutating residues within the PH-TH/kinase domain contradict the results of the previous study (ref 5).

In our hands BTK activity is not significantly affected by mutation of just two residues, R133 and Y134. It is somewhat difficult to compare the previously reported activity assay for the same BTK mutant (Wang et al. ref 5, Figure 4D) with the data we report here. For unexplained reasons, the time scale for the quantitative assay in the previous work is truncated to 50 munutes for the R133/Y134 mutant data compared to 120 minutes for all of the other activity data reported in that figure. In our data, if we qualitatively examine the differences in a representative progress curve at 50 minutes between WT and the double R133/Y134 mutant (see Figure 6a, dark blue and pink traces) one might conclude that the R133/Y134 mutation is activating BTK. However, when we calculate the average kinase activity rate ± standard error for three independent experiments we find that the difference between WT and the double R133/Y134 mutant is not significant (see Figure 6b and c). Thus, instead of making any assertions about the previously published data we are trying to be as rigoruous as possible in presentation and interpretation of our own data.

In addition, throughout the manuscript we tried to be very careful in our discussion of our data and that published previously, to avoid conclusive statements about the previously described interface. Afterall, one of our overriding conclusions is that the N-terminal region of BTK is highly dynamic. See response to reviewer 1 above.

Additionally, the study presents the structure of the kinase domain with swapped activation loops in a dimeric form, representing a previously unseen structure along the trans-phosphorylation pathway. This structure holds potential relevance. To better understand its significance, employing a structure/function approach like the one described for the PH-TH/kinase domain interface would be beneficial.

We completely agree with this comment and are pursuing such studies now.

Overall, this study contributes to our understanding of the activation mechanism of BTK and sheds light on the autoinhibition and allosteric control of this protein kinase. It presents new structural insights and proposes novel models that challenge previous understandings. However, further investigation and discussion would significantly strengthen the study.

As indicated we are pursuing further investigation and felt that the body of work presented here is sufficient for a single manuscript.

Reviewer #3 (Public Review):

Yin-wei Lin et al set out to visualize the inactive conformation of full-length Bruton's Tyrosine Kinase (BTK), a molecule that has evaded high-resolution structural studies in its full-length form to this date. An open question in the field is how the Pleckstrin Homology-Tec Homology (PHTH) domain inhibits BTK activity, with multiple competing models in the field. The authors used a complimentary set of biophysical techniques combined with well-thought-out stabilizing mutations to obtain structural insights into BTK regulation in its full-length form. They were able to crystallize the full-length construct of BTK but unfortunately, the PHTH was not resolved yielding a structure similar to that previously obtained in the field. The investigation of the same construct by SAXS yielded an elongated structural model, consistent with previous SAXS studies. Using cryo-EM the authors obtained a low-resolution model for the FL BTK with a loosely connected density assigned to the dynamic PHTH around the compact SH2-SH3-Kinase Domain (KD) core. To gain further molecular insights into PHTH-KD interactions the authors followed a previously reported strategy and generated a fusion of PHTH-KD with a longer linker, yielding a crystal structure with a novel PHTH-KD interface which they tested in biochemical assays. Lastly, Yin-wei Lin et al crystallized the BTK KD in a novel partially active state in a "face-to-face" dimer with kinases exchanging the activation loops, although partially disordered, being theoretically perfectly positioned for transphosphorylation. Overall this presents a valiant effort to gain molecular insights into what clearly is a dynamic regulatory motif on BTK and is a valuable addition to the field.

However, this work can be improved by considering these points:

1) The cryo-EM reconstructions are potentially over-interpreted. The reported resolution for all of the analyzed reconstructions is better than 8Å, at which point helices should be recognized as well-resolved structural elements. In the current view/depiction of the cryo-EM maps/models it is hard to see such structural features and it would be great if the authors could include a panel showing maps at higher thresholds to show correspondence between the helices in the kinase C lobe and the cryo-EM maps. Otherwise, the overall positioning of the models within the cryo-EM maps is hard to evaluate and may very well be wrong. (Fig 4, S2).

First, we fully recognize the model is low-resolution and we are careful in our discussion of the cryo-EM data to use language that acknowledges the limitations of the model. Nevertheless, this is the model we have (specific data processing points are discussed below).

The resolution numbers are from the Fourier Shell Correlation (FSC) curve given by Cryosaprc at the end of refinement. We do acknowledge the reviewer’s comments that the resolution could be over estimated in that calculation, but our main focus is to show that the overall domain arrangement of the autoinhibited BTK core (Src-module) fits into the reconstructions.

We tested visualizing the maps at higher threshold, but the secondary structures of the reconstructions were still not well resolved. We do realize that with the current reconstructions, we do not have the structural details to correctly orientate and fit individual domains; this is why we chose to simply fit the available crystal structure of the autoinhibited BTK SH3-SH2-kinase core into the maps.

2) With the above in mind, if the maps are not at the point where helices are well resolved, it may be beneficial to low-pass filter the maps to a more conservative resolution for fitting, analysis, and representation. (Fig 4, S2).

Using low-pass filtered maps at 10Å or unsharpened maps, the fitting of the BTK model and map do not change significantly.

3) It would be valuable to get a quantitative metric on the model/map fitting for the cryo-EM work. One good package for this is Situs which provides cross-correlation values for the top orthogonal fits, without user input for initial fitting. This would again increase confidence in the correctness of model positioning on the map. (Fig 4, S2).

Thank you for this suggestion. We tested the colores feature (Exhaustive One-At-A-Time 6D Search) in Situs to perform model to map fitting without user input as the reviewer suggested. The highest ranked fitting is identical to what we presented in the manuscript. Following are the cross-corelation numbers calculated from “Fit-in-map” tool in chimera and from “collage” function in Situs. We now indicate this step in the caption to Figure 4.

Author response table 1.

4) It would be great to see 2D class averages from the particles contributing to each of the 3D classes. Theoretically, a clear bright "blob" (hypothesized to be the PHTH domain) should be observable in the 2D class averages. In the current 2D class averages that region is unconvincingly weak. (Fig 4, S2).

We attempted to improve both 2D and 3D reconstructitions by feeding the particles from each 3D class through many cycles of 2D classification and selection to exclude ‘bad’ paritcles, but neither the 2D class averages nor 3D reconstructions could be improved.

We agree the feature that appears in the 2D class averages is weak. The BTK protein is only 77kD in size and is highly dynamic and flexible. Thus, in reality this is not an ideal system for cryo-EM. As well, the PHTH domain itself is quite small and NMR data, acquired in the context of a different project, provides evidence that the isolated PHTH domain is dynamic in solution (NMR linewidths vary throughout the protein suggesting intermediate exchange). Nevertheless, given the inability to capture the PHTH domain in crystal structures of full-llength BTK we reasoned that cryo-EM could provide some insight. In the future we anticipate building on these data to include inhibitory binding partners of BTK; however such an effort is beyond the scope of the current work.

5) It seems like there was quite a large circular mask applied during 2D classification. Are authors confident that the weak density attributed to the PHTH domain is not neighboring particles making their way into the extraction box? It would be great if the authors would trim their particle stack with a very stringent interparticle distance cutoff (or report the cutoff in the manuscript if already done so) to minimize this possibility.

We initially picked particles using a small radius (100 Å), and stringently selected 2D classes with particles that contained only density aligning to the core SH3-SH2-kinase domains. We found, however, that 3D ab initio reconstruction always resulted in an additional density located at different positions around the larger core density. The structure of a single BTK PHTH domain fits into that additional remote density. Given the additional density that consistently appeared in 3D reconstructions, we went back and picked particles using a larger circular mask (200 A). Subsequent 2D classification and 3D reconstruction from this analysis gave similar results and are presented in the manuscript.

Regardless of the mask radius, we used stringent conditions for particle picking and checked for the presence of duplicates. An interparticle distance cutoff of 0.1 to 0.5 times the particle diameter was used and resulted in fewer number of particles, but the presence of the extended density remains. We also made use of template picking (2D class averages) to repick the particles and found no significant difference in the number of particles or quality of 2D classifications.

6) The cryo-EM processing may benefit from more stringent particle picking. The authors picked over 2M particles from 750 micrographs which likely represents very heavy overpicking. I would encourage the authors to re-pick the micrographs with 2D class averages and use more stringent metrics to reduce the overpicking. This may result in higher-resolution reconstructions. (Fig 4, S2).

This was an effort to maximize the number of particles extracted. After multiple rounds of 2D classification and selection to exclude empty and junk particles, the final number of particles selected for 3D ab-initio reconstructions were only 68,788, and only ~20K particles for each 3D reconstruction. Thus, we are not concerned that we overpicked particles. This approach is described in Supp Figure S2.

7) The Dmax from SAXS for the Full Length BTK is at 190Å. It would be great if the authors could make a cartoon of what domain arrangement may satisfy this distance, as it is quite extended for such a small particle. Can the authors rule out dimerization at SAXS concentrations? (Fig 1).

SAXS data for full-length, wild-type BTK has been previously published (Márquez et al, 2003 EMBO J. (2003) 22:4616-4624). Our data for WT BTK are consistent with that published previously (and we have cited this previous work). In that work, the authors attribute the ~200 Å Dmax value to an elongated BTK conformation where the domains of BTK are arranged in a linear fashion (a figure showing this domain arragement is provided by Marquez et al. precluding the need for such a cartoon here).

In the present work we take advantage of targeted mutations to stabilize the autoinhibted SH2-SH2-kinase core and the Dmax value that we report for this more autoinhibited version of full-length BTK (FL 4P1F) is ~150Å. Notwithstanding low resolution in both SAXS and cryoEM, it is notable that superposition of the cryoEM models in Figure 4c & d gives a distance of ~150Å between the PHTH domains from the two models.

Finally, we cannot completely rule out that a small fraction of full length BTK is forming dimers. However, in our experience purifying and working with this protein, we find that purified and concentrated monomeric fulllength Btk proteins (as high as 15mg/ml) are quite stable and remain monomeric and free of aggregation even after sitting at 4°C for more than a week. Here the BTK SAXS data were collected within 24 hours after the samples were thawed.

8) In Figure S1 (C) it seems that the curves are just scattering curves with Guinier plots in the inserts, but are labeled as Guinier plots in the legend. The Guinier plots for some samples (FL 4P1F) show signs of aggregation, which may complicate the analysis, it could be beneficial to redo.

We thank the reviewer for pointing out our mistake in presention of the SAXS data. We have now replaced plots in Figure S1c with the correct scattering profiles for each construct with the Guinier insets shown. We revised the label of this panel to “Scattering profile and Guinier plots (insets)”.

In addition, we re-processed the FL 4P1F data by performing buffer subtraction (using a different buffer alone scattering dataset (also collected during original data acquisition)). The data quality after reprocessing were significantly improved (see new scattering profiles and Guinier plots for full-length BTK in Supplementary Figure S1). Protein stability (see above) and the current data quality therefore suggest that aggregation is not complicating the SAXS analysis.

9) Have the authors verified that the activation loop mutations that they introduce do not disrupt the PHTH binding as they previously reported an activation loop on BTK to interact with PHTH, an interaction they do not see here? If so, a citation would be helpful in the text. If not, testing this would strengthen the paper.

The same activation loop mutations were included in the constructs used in the previous solution studies of the PHTH/kinase domain interaction by NMR and HDX (see ref [11]). We clarify this point in the methods section. As well, all but one of the sequence changes introduced into the activation loop are at positions at the ‘base’ of the activation loop and therefore are not surface exposed. Only one amino acid change is on the exposed part of the activation loop (V555T).

10) Can the authors comment on the surfaces which are accessible and inaccessible to the PHTH in the crystal (Fig 3E)? The fact that PHTH doesn't adopt a stable conformation in the solvent channel to some degree indicates that the accessible interaction surfaces are not suitable for PHTH interactions, as the "effective concentration" of the PHTH would be quite high. Are these surfaces consistent with the cryo-EM analysis?

This is an excellent point and we did state the following in describing the crystallization results:

“the crystallography results are consistent with a flexible N-terminal PHTH domain with the caveat that the domain swapped dimer organization might limit native autoinhibitory contacts between the PHTH and SH3SH2-kinase regions.”

In the domain swapped dimer seen in the crystal, a symmetry related molecule does partially block the Ghelix region of the kinase domain while the activation loop and C-helix in the N-lobe remain accessible. Our previous solution studies (ref [11]) pointed to the G helix as part of the interaction interface in addition to the activation loop and part of the N-lobe. We have now modified the sentence above to more clearly describe which parts of the kinase domain are inaccessible in the crystal and the possible ramifications of the steric environment on PHTH domain mobility in the crystal (see pg. 10). That said, all of our previous HDX data shows little protection in the PHTH domain in full-length BTK (mapping of the PHTH/kinase interaction was only possible in trans using excess PHTH domain) and so our data can be best summarized by concluding that the PHTH domain visits a number of conformational states and makes transient contacts with various regions of the kinase domain (dependent upon whether the SH3-SH2 region is engaged or not). This is similar to the ‘fuzzy’ intramolecular contacts described for the N-terminal region of the SRC family. Like the SRC family, BTK (and other TEC kinases) contain a long disordered linker between the N-terminal region and the compact SH3-SH2-kinase core.

11) For the novel active state dimer of the Kinase Domain it would be great to see some functional validation of the dimerization interface. It is structurally certainly quite suggestive, but without such experiments the functional significance is unclear. If appropriate mutations have been published previously a citation would be helpful.

We completely agree. We scoured the literature and our own facuntional assay results over many years but the appropriate mutations to test the functional significance of the kinase domain dimer have not been reported or previously studied in our lab. We are therefore actively pursuing this line of investigation now.

Reviewer #1 (Recommendations For The Authors):

I have the following proposed experiments/analysis that should help.

1) To better validate the putative PH-kinase interface seen, the authors should try some alphafold multimer / rosettaTTFold modelling of just the PHTH module with the kinase domain. The advantage of this is that it will test how conserved over evolution the potential interface is, and will help to decipher discrepancies between the two structures. This may end up being similar to what is seen in Akt (in this case the alphafold prediction does not match the allosteric inhibitor structure, or the nanobody bound structure), but this could help provide additional insight into how the PH domain interacts.

We have applied alphafold to this system. The PHTH-kinase fusion sequence was fed to Alphafold and the separate PHTH and kinase domains to Aphafold multimer. The results provide a range of ‘complexes’ none of which recapitulate the PHTH/kinase interface reported here or that reported by Wang et al in previous work. Three of five results from Alphafold Multimer place the PHTH domain on the activation loop face of the kinase domain consistent with the previous solution data pointing to a similar regulatory interface. This is interesting but our experience in applying alphafold to dynamic confromationally heterogeneous systems is that the results need to be considered with caution. For that reason we did not include any of the alphafold predictions in the manuscript.

Evolutionary conservation is discussed further in the next section:

2) Could the authors provide a detailed evolutionarily analysis of the binding surface between the PHTH and kinase domains and include this in Fig5, this also would help interpret the likelihood of this interface.

This is an excellent question and we have in fact previously published a detailed evolutionary analysis of the BTK kinase domain in collaboration with Kannan Natarajan (see Amatya et al., PNAS, 2019, [ref 11]). In that work we found that evolutionarily conserved residues on the kinase domain map to the activation loop face, supporting the solution data that the PHTH interacts with the kinase domain across the activation loop face. That work predated alphafold but it is interesting that, to the exent that alphafold predicts anything, it seems to converge on the PHTH domain containg the activation loop face.

In the context of our current work, and this question from the reviewer, we re-examined the evolutionary anlysis carried out previously and find that BTK (or TEC family) specific residues on the kinase domain do not appear at the newly identified PHTH/kinase interface we report here. We could speculate that since the ‘back’ of the kinase domain N-lobe interacts with multiple binding partners (SH3, SH2-linker and PHTH) evolutionary pressures may have resulted in a certain degree of plasticity to allow recognition of multiple binding partners.

Evolutionary analysis of the BTK PH domain was also carried out previously and shows that the conserved sites map to the phospholipid binding pocket of the PH domain. The analysis did not include TH domain residues. Since we find the TH domain contributes to the PHTH/kinase interface in our crystal structure, we do not have the data at this time to do a thourough anaylsis but we appreciate this comment and can address this in furture work with collaborators.

Reviewer #1 (Public Review):

Ps observed 24 objects and were asked which afforded particular actions (14 action types). Affordances for each object were represented by a 14-item vector, values reflecting the percentage of Ps who agreed on a particular action being afforded by the object. An affordance similarity matrix was generated which reflected similarity in affordances between pairs of objects. Two clusters emerged, reflecting correlations between affordance ratings in objects smaller than body size and larger than body size. These clusters did not correlate themselves. There was a trough in similarity ratings between objects ~105 cm and ~130 cm, arguably reflecting the body size boundary. The authors subsequently provide some evidence that this clear demarcation is not simply an incidental reflection of body size, but likely causally related. This evidence comes in the flavour of requiring Ps to imagine themselves as small as a cat or as large as an elephant and showing a predicted shift in the affordance boundary. The manuscript further demonstrates that ChatGPT (theoretically interesting because it's trained on language alone without sensorimotor information; trained now on words rather than images) showed a similar boundary.

The authors also conducted a small MRI study task where Ps decided whether a probe action was affordable (graspable?) and created a congruency factor according to the answer (yes/no). There was an effect of congruency in the posterior fusiform and superior parietal lobule for objects within body size range, but not outside. No effects in LOC or M1.

The major strength of this manuscript in my opinion is the methodological novelty. I felt the correlation matrices were a clever method for demonstrating these demarcations, the imagination manipulation was also exciting, and the ChatGPT analysis provided excellent food for thought. These findings are important for our understanding of the interactions between action and perception, and hence for researchers from a range of domains of cognitive neuroscience.

The major elements that limit conclusions and I'd recommend to be addressed in a revision include justification of the 80% of Ps removed for the imagination analysis, and consideration that an MRI study with 12 P in this context can really only provide pilot data. I'd also encourage the authors to consider theoretically how else this study could really have turned out and therefore the nature of the theoretical progress.

Specifics:<br /> 1. The main behavioural work appears well-powered (>500 Ps). This sample reduces to 100 for the imagination study, after removing Ps whose imagined heights fell within the human range (100-200 cm). Why 100-200 cm? 100 cm is pretty short for an adult. Removing 80% of data feels like conclusions from the imagination study should be made with caution.

2. There are only 12 Ps in the MRI study, which I think should mean the null effects are not interpreted. I would not interpret these data as demonstrating a difference between SPL and LOC/M1, but rather that some analyses happened to fall over the significance threshold and others did not.

3. I found the MRI ROI selection and definition a little arbitrary and not really justified, which rendered me even more cautious of the results. Why these particular sensory and motor regions? Why M1 and not PMC or SMA? Why SPL and not other parietal regions? Relatedly, ROIs were defined by thresholding pF and LOC at "around 70%" and SPL and M1 "around 80%", and it is unclear how and why these (different) thresholds were determined.

4. Discussion and theoretical implications. The authors discuss that the MRI results are consistent with the idea we only represent affordances within body size range. But the interpretation of the behavioural correlation matrices was that there was this similarity also for objects larger than body size, but forming a distinct cluster. I therefore found the interpretation of the MRI data inconsistent with the behavioural findings.

5. In the discussion, the authors outline how this work is consistent with the idea that conceptual and linguistic knowledge is grounded in sensorimotor systems. But then reference Barsalou. My understanding of Barsalou is the proposition of a connectionist architecture for conceptual representation. I did not think sensorimotor representation was privileged, but rather that all information communicates with all other to constitute a concept.

6. More generally, I believe that the impact and implications of this study would be clearer for the reader if the authors could properly entertain an alternative concerning how objects may be represented. Of course, the authors were going to demonstrate that objects more similar in size afforded more similar actions. It was impossible that Ps would ever have responded that aeroplanes afford grasping and balls afford sitting, for instance. What do the authors now believe about object representation that they did not believe before they conducted the study? Which accounts of object representation are now less likely?

Reviewer #3 (Public Review):

Summary:<br /> Feng et al. test the hypothesis that human body size constrains the perception of object affordances, whereby only objects that are smaller than the body size will be perceived as useful and manipulable parts of the environment, whereas larger objects will be perceived as "less interesting components."

To test this idea, the study employs a multi-method approach consisting of three parts:

In the first part, human observers classify a set of 24 objects that vary systematically in size (e.g., ball, piano, airplane) based on 14 different affordances (e.g., sit, throw, grasp). Based on the average agreement of ratings across participants, the authors compute the similarity of affordance profiles between all object pairs. They report evidence for two homogenous object clusters that are separated based on their size with the boundary between clusters roughly coinciding with the average human body size. In follow-up experiments, the authors show that this boundary is larger/smaller in separate groups of participants who are instructed to imagine themselves as an elephant/cat.

In the second part, the authors ask different large language models (LLMs) to provide ratings for the same set of objects and affordances and conduct equivalent analyses on the obtained data. Some, but not all, of the models produce patterns of ratings that appear to show similar boundary effects, though less pronounced and at a different boundary size than in humans.

In the third part, the authors conduct an fMRI experiment. Human observers are presented with four different objects of different sizes and asked if these objects afford a small set of specific actions. Affordances are either congruent or incongruent with objects. Contrasting brain activity on incongruent trials against brain activity on congruent trials yields significant effects in regions within the ventral and dorsal visual stream, but only for small objects and not for large objects.

The authors interpret their findings as support for their hypothesis that human body size constrains object perception. They further conclude that this effect is cognitively penetrable, and only partly relies on sensorimotor interaction with the environment (and partly on linguistic abilities).

Strengths:<br /> The authors examine an interesting and relevant question and articulate a plausible (though somewhat underspecified) hypothesis that certainly seems worth testing. Providing more detailed insights into how object affordances shape perception would be highly desirable. Their method of analyzing similarity ratings between sets of objects seems useful and the multi-method approach is quite original and interesting.

Weaknesses:<br /> The study presents several shortcomings that clearly weaken the link between the obtained evidence and the drawn conclusions. Below I outline my concerns in no particular order:

1) Even after several readings, it is not entirely clear to me what the authors are proposing and to what extent the conducted work actually speaks to this. In the introduction, the authors write that they seek to test if body size serves not merely as a reference for object manipulation but also "plays a pivotal role in shaping the representation of objects." This motivation seems rather vague motivation and it is not clear to me how it could be falsified.<br /> Similarly, in the discussion, the authors write that large objects do not receive "proper affordance representation," and are "not the range of objects with which the animal is intrinsically inclined to interact, but probably considered a less interesting component of the environment." This statement seems similarly vague and completely beyond the collected data, which did not assess object discriminability or motivational values.<br /> Overall, the lack of theoretical precision makes it difficult to judge the appropriateness of the approaches and the persuasiveness of the obtained results. This is partly due to the fact that the authors do not spell out all of their theoretical assumptions in the introduction but insert new "speculations" to motivate the corresponding parts of the results section. I would strongly suggest clarifying the theoretical rationale and explaining in more detail how the chosen experiments allow them to test falsifiable predictions.

2) The authors used only a very small set of objects and affordances in their study and they do not describe in sufficient detail how these stimuli were selected. This renders the results rather exploratory and clearly limits their potential to discover general principles of human perception. Much larger sets of objects and affordances and explicit data-driven approaches for their selection would provide a far more convincing approach and allow the authors to rule out that their results are just a consequence of the selected set of objects and actions.

3) Relatedly, the authors could be more thorough in ruling out potential alternative explanations. Object size likely correlates with other variables that could shape human similarity judgments and the estimated boundary is quite broad (depending on the method, either between 80 and 150 cm or between 105 to 130 cm). More precise estimates of the boundary and more rigorous tests of alternative explanations would add a lot to strengthen the authors' interpretation.

4) Even though the division of the set of objects into two homogenous clusters appears defensible, based on visual inspection of the results, the authors should consider using more formal analysis to justify their interpretation of the data. A variety of metrics exist for cluster analysis (e.g., variation of information, silhouette values) and solutions are typically justified by convergent evidence across different metrics. I would recommend the authors consider using a more formal approach to their cluster definition using some of those metrics.

5) While I appreciate the manipulation of imagined body size, as a way to solidify the link between body size and affordance perception, I find it unfortunate that this is implemented in a between-subjects design, as this clearly leaves open the possibility of pre-existing differences between groups. I certainly disagree with the authors' statement that their findings suggest "a causal link between body size and affordance perception."

6) The use of LLMs in the current study is not clearly motivated and I find it hard to understand what exactly the authors are trying to test through their inclusion. As noted above, I think that the authors should discuss the putative roles of conceptual knowledge, language, and sensorimotor experience already in the introduction to avoid ambiguity about the derived predictions and the chosen methodology. As it currently stands, I find it hard to discern how the presence of perceptual boundaries in LLMs could constitute evidence for affordance-based perception.

7) Along the same lines, the fMRI study also provides very limited evidence to support the authors' claims. The use of congruency effects as a way of probing affordance perception is not well motivated. What exactly can we infer from the fact a region may be more active when an object is paired with an activity that the object doesn't afford? The claim that "only the affordances of objects within the range of body size were represented in the brain" certainly seems far beyond the data.

Importantly (related to my comments under 2) above), the very small set of objects and affordances in this experiment heavily complicates any conclusions about object size being the crucial variable determining the occurrence of congruency effects.

I would also suggest providing a more comprehensive illustration of the results (including the effects of CONGRUENCY, OBJECT SIZE, and their interaction at the whole-brain level).

Overall, I consider the main conclusions of the paper to be far beyond the reported data. Articulating a clearer theoretical framework with more specific hypotheses as well as conducting more principled analyses on more comprehensive data sets could help the authors obtain stronger tests of their ideas.

Author Response

Reviewer #1 (Public Review):

I believe it is important for the authors to clarify how the time frames to test for group differences of ERP components were defined. Were the components defined based on a grand average across lesions and controls or based or on the maximum range for both groups? As the paper is written currently this is unclear to me. It is also unclear why the group comparisons between controls and lateral PFC group were based only on the control group. To ensure no inadvertent biases towards the larger control group were introduced and ensure the studies findings were reliable, it would be appreciated if the authors could clarify this.

We thank the reviewer for the helpful comment. We recognize the need for a clearer definition of time frames for testing group differences in the ERP components and apologize for any ambiguity in the previous version of the manuscript.

Regarding the time frames to test for group differences of ERP components for the OFC and control groups, they were determined based on the combined maximum range for both groups. The time range for each group and each ERP component was derived from the statistical analysis of the condition contrasts run for each group. For instance, for the Local Deviance MMN, the condition contrast (i.e., Control condition versus Local Deviance condition) for the CTR group revealed a MMN component from 67 to128 ms, while the same condition contrast for the OFC group revealed a MMN from 73 to131 ms. The time frame used for the group comparison on the MMN time window was 50 to 150 ms to capture component activity for both groups. In the same way, for the Local Deviance P3a, the condition contrast (i.e., Control condition versus Local Deviance condition) for the CTR group revealed a P3a component ranging from 141 to 313 ms, while the same condition contrast for the OFC group revealed a P3a from 145 to 344 ms. The time frame used for the group comparison on the P3a time window encompassed 140 to 350 ms to capture component activity for both groups.

In the “Results” section of the main manuscript, together with the results from the cluster-based permutation independent samples t-tests, we provide the time frames in which the latter were computed for each ERP component. These segments have been highlighted with yellow in the revised manuscript. Moreover, in the section “Materials and methods - Statistical analysis of event-related potentials” of the main manuscript [page 37, paragraph 2], we provide a revised description of how the time frames for group differences of ERPs were defined. The revised description states: “In a second step, to check for differences in the ERPs between the two main study groups, we ran the same cluster-based permutation approach contrasting each of the four conditions of interest between the two groups using independent samples t-tests. The cluster-based permutation independent samples t-tests were computed in the latency range of each component, which was determined based on the maximum range for both groups combined. The latency range for each group and component was based on the time frames derived from the statistical analysis of task condition contrasts.”

Regarding the comparisons between the lateral PFC and control groups, they were not based solely on the control group condition contrast. This was miswritten. The approach to define time frames to test for ERP differences between the CTR and the lateral PFC group was the same as the one used to test differences between CTR and OFC groups. We apologize for any confusion this may have caused. We have revised the erroneous statements in the Supplementary File 1 [highlighted text, page 9-10].

An additional potential weakness of the paper, and one that if addressed would increase our confidence that neural differences arise because of the specific lesion effect, is the lack of evidence that the lesion and control groups do not differ on measures that could inadvertently bias the neural data. For example, while the groups did not differ on demographics and a range of broad cognitive functions, were there any differences between the number or distribution of bad/noisy channels in each subject between the two groups? Were there differences in the number of blinks/saccades or distribution of blinks or saccades across the conditions in each subject across the two groups.

We thank the reviewer for this suggestion. We have completed a number of measurements and tests to ensure that the OFC lesion group and the control group did not differ on measures that could affect the neural data. First, we computed the number of bad/noisy channels for each subject and group, and found that the two groups did not differ significantly. Second, we computed the number of trials remaining after removing the noisy segments across conditions for each subject and group, and found no significant differences between the groups. Third, the number of blinks/saccades across conditions for each subject and group showed no significant group differences. Altogether, the results indicate that the neural differences observed in our study arose because of the specific lesion effect.

These additional EEG measures and the statistical test results are included in the Supplementary File 1 [page 15-16] and Supplementary File 1g. We have also added text in the section “Materials and methods - EEG acquisition and pre-processing” of the main manuscript [page 35, paragraph 3], which states: “To ensure the validity of the neural data analysis, potential sources of bias were assessed between the healthy control participants and the OFC lesion patients. Specifically, no significant differences were observed between the two groups in terms of the number of noisy channels, the number of noisy trials, or the number of blinks across the task blocks and the experimental conditions.”

On a similar note, while I appreciate this is a well established task could the authors clarify whether task difficulty is balanced across the different conditions? The authors appear to have used the counting task to ensure equal attention is paid across conditions although presumably the blocks differ in the number of deviant tones and therefore in the task difficulty. Typically, tasks to maintain attention are orthogonal to the main task and equally challenging across the different blocks. Is there a way to reassure readers that this has not affected the neural results?

Thank you for pointing this out. Indeed, the experimental blocks differ in the number of deviant tones and therefore in the task difficulty. Thus, it is a very good suggestion to look for behavioral performance differences across the different blocks. In the present set of analyses, two block types were used: Regular (xX) and Irregular (xY). In regular blocks, where the repeated sequence is xxxxx, participants were required to count the rare/uncommon sequences, i.e., xxxxy and xxxxo. In irregular blocks, where the repeated sequence is xxxxy, participants were required to count the rare/uncommon sequences, i.e., xxxxx and xxxxo. We have now updated the behavioral analysis. First, by excluding the omission block’s counting performance, and second, by calculating the counting performance separately for the two blocks. The new behavioral analysis revealed that participants from both groups performed better in the irregular block compared to the regular block. However, there was no statistically significant difference between the counting performances of the two groups.

The new results are reported on page 5 of the main manuscript, section “Results - Behavioral performance”, paragraph 1: “Participants from both groups performed the task properly with an average error rate of 9.54% (SD 8.97) for the healthy control participants (CTR) and 10.55% (SD 6.18) for the OFC lesion patients (OFC). There was no statistically significant difference between the counting performance of the two groups [F(24) = 0.11, P = 0.75]. Participants from both groups performed better in the irregular block (CTR: 8.39 ± 8.24%; OFC: 7.50 ± 7.34%) compared to the regular block (CTR: 10.69 ± 11.36%; OFC: 13.60 ± 10.97%) [F(24) = 3.55, P = 0.07]. There was no block X group interaction effect [F(24) = 0.73, P = 0.40].”

As with many patient lesion studies, while the comparison directly against the healthy age matched controls is critical it would have strengthened the authors claims if they could show differences between the brain damaged control group. Given the previous literature that also links lateral PFC with prediction error detection, I understand that this region is potentially not the clearest brain damaged control group and therefore another lesion group might have strengthened claims of specificity. Furthermore, the authors do not offer an explanation for why no differences between lateral PFC and control groups were found when others have previously reported them. Identifying those differences would strengthen our understanding of the involvement of different structures in this task/function.

We thank the reviewer for raising this crucial issue. We recognize the importance of addressing the lack of neurophysiological differences between the lateral PFC lesion group and the control group. First, it is important to clarify that the lateral PFC lesion control group was initially included not as a control for specific lateral PFC lesions but rather a broader control group to account for potentially general effects of frontal brain damage. However, considering that previous studies have implicated specific areas of the lateral PFC (e.g., inferior frontal gyrus; IFG) in predictive processing, we also think that a more thorough justification of these null findings is needed.

Intracranial EEG studies examining local and global level prediction error detection pointed to the role of inferior frontal gyrus (IFG) as a frontal source supporting top-down predictions in MMN generation (Dürschmid et al., 2016; Nourski et al., 2018; Phillips et al., 2016; Rosburg et al., 2005). However, other intracranial studies reported unclear (Bekinschtein et al., 2009) or weak (Dürschmid et al., 2016) frontal MMN effects. El Karoui et al. (2015) observed late ERP responses in the lateral PFC related to global deviants but no MMN to local deviants, and it was not clear where in the PFC these responses occurred, not showing responses in the IFG. Additionally, studies employing dynamic causal modeling of MMN consistently modeled frontal sources in the IFG region (Garrido et al., 2008; Garrido et al., 2009; Phillips et al., 2015). A review by Deouell (2007) highlighted the potential contributions of both IFG and middle frontal gyrus to MMN generation, suggesting that the specific source might vary depending on characteristics of the deviant stimuli, such as pitch or duration.

In Alho et al. (1994) lesion study, diminished MMN to local-level deviants was found after lesion to the lateral PFC, with the lesion cohort exhibiting a hemisphere ratio of 7/3 for left and right hemispheres, respectively, which is different from our cohort's ratio of 4/6. Furthermore, all individuals in that study had infarcts in the middle cerebral artery, resulting in a more uniform lesion location compared to our cohort. Notably, the lesions observed in our lateral PFC group appeared to be situated in more superior brain regions and towards the MFG compared to the predominantly reported involvement of the IFG in previous studies. Another factor that might contribute to the lack of significant effects is the heterogeneity of the lesions in our lateral PFC group (see Supplementary Figures 2, 3 and 4). Especially for the left hemisphere cohort, the individual lesions did not share a consistent anatomical location. The right hemisphere cohort had a greater lesion overlap, but overall, the lesions were not centered in the IFG area with highest overlap being in the MFG area. This distinction in lesion location might contribute to the absence of effects observed in our study.

Regarding the global effect, often reflected in the P300 component, it appears that the neural sources responsible for processing global deviance exhibit a more distributed pattern. This means that the brain regions involved in detecting and processing global deviations may not be as localized or concentrated as those implicated in local deviance processing. Given that the neural mechanisms underlying global deviance detection and processing are likely to involve a wider network of brain regions, they may be less susceptible to disruptions caused by focal lesions in the lateral PFC.

In response to your comment, we have expanded the “Discussion” to address this point by adding a new section titled “Lack of findings in the lateral PFC lesion group” [page 21]. In this section, we first present some of the findings implicating specific areas of the lateral PFC in the generation of MMN and in predictive processing, and then offer an account of the potential reasons behind the lack of neurophysiological differences between the lateral PFC and control groups.

Finally, while the authors have already cited widely across multiple fields, again speaking to the likely large impact the study will make, there does appear to be an unexplored conceptual link between the conclusions here that the OFC supports "the formation of predictions that define the current task by using context and temporal structure to allow old rules to be disregarded so that new ones can be rapidly acquired" and that lesions of the lateral portions of the OFC disrupt the assignment of credit or value to a stimuli that occurred temporally close to the outcome (Walton et al 2010, Noonan et al 2010, PNAS, Rudebeck et al 2017 Neuron, Noonan et al 2017, JON, Wittmann et al 2023 PlosB, note the wider imaging literature in line with this work Jocham et al 2014 Neuron and Wang et al bioRxiv). Without the OFC monkeys and humans appear to rely on an alternative, global learning mechanism that spreads the reinforcing properties of the outcome to stimuli that occurred further back in time. Could the authors speculate on how these two strains of evidence might converge? For example, does the OFC only assign credit in the event of a prediction error or does one mechanism subsume another?

We thank the reviewer for this comment regarding the unexplored conceptual link between our study’s conclusion, which suggests that the OFC facilitates the detection of prediction errors, and the findings of other research that delves into the OFC’s role in assignment of credit to stimuli. We find this comment very interesting and appreciate the opportunity to speculate on the potential functional convergence of these two processes within the OFC.

The OFC is a critical neural hub implicated in learning, decision-making, and adaptive behavior. The detection of prediction errors and the assignment of credit to stimuli are mechanisms linked with the OFC, which play an important role in all these functions (Noonan et al., 2012; Schultz & Dickinson, 2000; Sul et al., 2010; Tobler et al., 2006; Walton et al., 2010; Walton et al., 2011). Prediction errors involve recognizing discrepancies between expected and actual outcomes, which engages the OFC in rapidly updating stimulus valuations to align with newfound information (Holroyd & Coles, 2002; Kakade & Dayan, 2002). Signaling of errors provides a powerful mechanism whereby OFC facilitates adaptive learning and enables the brain to adjust its expectations based on novel experiences (Schultz, 2015; Seymour et al., 2004). Credit assignment, on the other hand, refers to properly identifying the causes of prediction errors. Without proper credit assignment, one might have intact error signaling mechanisms, but lose the ability to learn appropriately. This is especially true when multiple possible antecedents may be related to the error or when past choices have been unpredictable. In such situations, it is important to assign credit to the most recent choice and not get distracted by previous alternatives (Stalnaker et al., 2015).

These mechanisms within the OFC appear interrelated yet distinct. While prediction errors could trigger credit assignment, the OFC's ability to continually assess stimuli's values extends beyond instances of prediction errors. The OFC is involved in continuously evaluating and updating the values of stimuli based on ongoing experiences (Padoa-Schioppa & Assad, 2006; Tremblay & Schultz, 1999). This process enables the brain to learn from both unexpected outcomes and regular, predictable interactions with the environment. In situations where outcomes are not solely determined by prediction errors, the assignment of credit remains important. Complex decision-making involves considering a variety of factors beyond just prediction errors, such as contextual information and long-term consequences. Clarifying the convergence of these mechanisms within the OFC holds profound implications for understanding the intricacies of learning dynamics and the orchestration of adaptive responses to the environment.

While we recognize the value of this discussion, we believe it extends beyond the primary focus of our study. Consequently, we have made the decision not to incorporate it into the current manuscript.

One remaining weakness, which plagues all patient studies, is that of anatomical specificity. The authors have analysed what is, for the field, a large group of patients, and while the lesions appear to be relatively focused on the OFC the individuals vary in the degree to which different subregions within the OFC are damaged. This is increasingly important as evidence over the last 10 years has identified functional roles of these specific structures (Rushworth et al 2011, Neuron, Rudebeck et al 2017 Neuron). It would be important to ultimately know whether the detection of prediction errors was specific to a particular OFC subregion, a general mechanism across this area of cortex, or whether different subregions were more involved during different contexts or types of stimuli/contexts/tasks etc. Some comments on this would be appreciated.

The reviewer raised an important point here. It would have been interesting to explore this aspect. However, one challenge with focal lesion studies is to establish large patient cohorts. The group size of our study, which is relatively large compared to other studies of focal PFC lesions, does not allow us to perform any exploratory lesion-symptom mapping analyses. A larger patient sample will provide a stronger basis for drawing conclusions about the critical role of a particular OFC subregion to the detection of prediction errors and allow statistical approaches to lesion subclassification and brain-behavior analysis (e.g., voxel-based lesion-symptom mapping (Bates et al., 2003; Lorca-Puls et al., 2018)).

Considering the average percentage of damaged tissue in our study, the medial part of OFC or Brodmann area 11 is affected more by the lesion (approx. 33%), followed by the anterior-most region of the prefrontal cortex or Brodmann area 10 (approx. 25%), and the lateral portions of the OFC or Brodmann area 47 (approx. 12%). From our analysis, it is difficult to conclude whether the detection of prediction errors in our study was specific to a certain OFC area, or whether different subregions were involved more than others during different types of stimuli/contexts processing.

To provide a more balanced interpretation of our findings, we incorporated a section in the “Discussion”, titled “Limitations and future directions” [page 24-25], which delves into the limitations of our study and lesion studies generally with respect to anatomical specificity and the challenge to establish large patient cohorts.

Reviewer #2 (Public Review):

The current version of the manuscript is overall very long and verbose, for example, the introduction is 5 pages long and includes up to 102 references. In my view this is way too much. I suppose authors wish to be very detailed, but somehow they get an opposite effect, the main message of the introduction and aims get diluted.

We thank the reviewer for the feedback on our manuscript's length and content. This prompted us to carefully reconsider the balance between providing necessary context and ensuring the clarity of our main message. Our intention was to establish a strong foundation for our research by presenting relevant literature and setting the stage for our aims. In our revised manuscript, we have condensed the Introduction while retaining the key elements necessary to understand the context and motivations behind our research. Specifically, the current version of the “Introduction” is three pages long and includes 83 references.

I wonder if the presentation rate used, SOA; 150 is too fast and the stimuli too short 50 ms. Please prove a rationale for this.

We appreciate the reviewer's thoughtful consideration of the stimulus duration and presentation rate (SOA) used in our study. We understand the importance of providing a rationale for our choices to ensure the validity of our experimental design. The decision to use a SOA of 150 ms and stimuli of 50 ms duration was grounded in established practices and relevant literature in the field. Similar presentation rates and stimulus durations were employed in previous studies using similar auditory oddball paradigms, investigating rapid cognitive processes in combination with event-related potentials (ERPs). For instance, Bekinschtein et al. (2009) first introduced the task by using a SOA of 150 ms and stimulus duration of 50 ms, demonstrating that this combination is sensitive to detecting auditory deviations and eliciting early and late ERP components. Additionally, Wacongne et al. (2011), Chennu et al. (2013), Uhrig et al. (2014), and El Karoui et al. (2015) employed similar task designs with the same SOA and stimulus duration in combination with scalp EEG, fMRI and intracranial recordings, further supporting the validity of this approach. Other studies, employing the same paradigm, such as Chao et al. (2018) and Doricchi et al. (2021), used a SOA of 200 ms but kept the same stimulus duration of 50 ms.

One of the conditions is 'omissions', but results are not reported, so either authors do not mention this at all, or they report these data, which would be probably interesting.

We thank the reviewer for the nice reminder. The “omissions” condition is indeed an integral part of our study, and we acknowledge its potential significance. However, we have decided to publish the detailed analysis of the 'omissions' condition in a separate paper, because we think that such analysis and discussion would make the current paper quite dense and complicated. We apologize for any confusion that might arise from the absence of the 'omissions' results in this manuscript. On page 33 of the main manuscript, we state the reason for not including the “omissions” condition in the current analysis: “In the present set of analyses, the Omission blocks were not further examined, because such analysis and discussion would make the current paper overly dense and complicated.”

The Discussion is very long and in some aspect even too speculative. For example, in the conclusions authors claim that the OFC contributes to a top-down predictive process that modulates the deviance detection system in the primary auditory cortices and may be involved in connecting PEs at lower hierarchical areas with predictions at higher areas. I am not sure the current data support this. This would-be probably more appropriate if they could compare results from OFC and AC etc. so it is a more dynamic study.

We thank the reviewer for this observation. We have made revisions to shorten and refine the discussion, with a primary focus on presenting and interpreting the key results in a more concise and straightforward manner (See tracked changes in the revised manuscript).

However, the overall length of the Discussion has not been reduced significantly because we have introduced two additional sections within the Discussion (i.e., “Lack of findings in the lateral PFC lesion group” and “Limitations and future directions”) in response to reviewers’ request to address the lack of finding in the lateral PFC lesion group and certain limitations associated with the employed lesion method.

We also agree that the claim mentioned by the reviewer is overly too speculative and therefore revised the sentence as follows [page 38, “Conclusion”]: “We suggest that the OFC likely contributes to a top-down predictive process that modulates the deviance detection system in lower sensory areas.”

At the beginning of Discussion, the authors mention that overall, these findings provide novel information about the role of the OFC in detecting violation of auditory prediction at two levels of stimuli abstraction/time scale. I think this needs to be detailed more specifically rather than mention they provide novel results.

We understand the importance of providing readers with precise descriptions about the novelty of our study. Therefore, we have revised the statement to provide more detailed information about the novel contributions offered by our study. The revised text states as follows [“Discussion”, page 18,]: “These findings indicate that the OFC is causally involved in the detection of local and local + global auditory PEs, thus providing a novel perspective on the role of OFC in predictive processing.”

I am not sure I like to have a section as a general discussion within the discussion itself, probably this heading should be reformatted to be more specific to what is discussed.

As suggested by the reviewer, we reformatted the heading to “OFC and hierarchical predictive processing” [page 22-24] to better capture the essence of the content covered in this section of the “Discussion”. Here, we discuss the functional relevance of our EEG findings under the umbrella of the predictive coding framework and the potential role of OFC in predictive processes (See tracked changes in the revised manuscript).

Reviewer #3 (Public Review):

The central claim of the study is that hierarchical predictive processing is altered in OFC patients. However, OFC patients were able to identify global deviants as well as controls. Thus, hierarchical predictive processing itself seems to be unaltered, even though its neural correlates were different. This begs the question of what exactly the functional meaning of the EEG findings is. From the evidence presented this is difficult to determine for three reasons (See comments below).

We thank the reviewer for the detailed observations and valuable comments. The reviewer points out that hierarchical predictive processing is unaltered even though the neural correlates were altered, because OFC patients were able to identify global deviants as accurately as control participants. We respectfully disagree with the reviewer’s claim for two reasons: 1) The primary purpose of the behavioral data in this study was not to measure the participants’ deviant detection performance, but to confirm that they were paying attention to the global rule of each block. However, we agree that an effect of lesion on behavioral performance would strengthen the claim of altered high-level predictive processing. Your point highlights the importance of looking more carefully at our behavioral results. In a follow up study, which we are currently running, we explore the behavioral nuances of our task by measuring reaction times of correct deviant detections. 2) Earlier lesion studies reported typical performance on simple oddball tasks for patients with focal frontal lesions that did not significantly differ from control participants. However, despite normal task execution and neuropsychological profiles, patients with LPFC and OFC lesions present distinct neurophysiological evidence of alterations in novelty processing (Knight, 1984, 1997; Knight & Scabini, 1998; Løvstad et al., 2012; Yamaguchi & Knight, 1991).

Regarding the central claim of our study being that hierarchical predictive processing is altered in OFC patients, we have tried not to make strong claims about our results showing altered hierarchical predictive processing. For example, the conclusion of the abstract states: “the altered magnitudes and time courses of MMN/P3a responses after lesions to the OFC indicate that the neural correlates of detection of auditory regularity violation is impacted at two hierarchical levels of stimuli abstraction.” Thus, we do not claim that detection of regularity violation is directly impaired (e.g., OFC patients were able to identify global deviants as well as healthy controls) but that the neural correlates of deviants’ detection are altered, and therefore impaired.

Finally, we have gone through all the comments/reasons, which the reviewer believes are difficult to determine the functional meaning of our EEG findings, and addressed them one by one (see comments below). We hope that the revised manuscript has been improved accordingly and provides a more critical view on the extent to which the findings support hierarchical predictive coding.

It is possible that the shifts in scalp potentials are due to volume conduction differences linked to post-lesion changes in neural tissue and anatomy rather than differences in information processing per se.

We appreciate your comment regarding the potential influence of volume conduction differences on the observed shifts in scalp potentials in our study. We acknowledge that there are special challenges in interpreting ERP findings in brain lesion populations (Kutas et al., 2012; Rugg, 1995). To reliably interpret changes in the ERPs in lesion patients as reflecting impairments in certain cognitive processes, it is necessary to identify factors that might possibly affect the results and to apply the appropriate control measures. As noted by the reviewer, structural pathology, and the replacement of neural tissue by cerebrospinal fluid following tumor resection, likely causes inhomogeneities in the volume conduction of electrical activity and resulting changes in current flow patterns. Moreover, post-craniotomy skull defects can cause local inhomogeneities in the resistive properties of the skull (Løvstad & Cawley, 2011; Rugg, 1995). Both types of biophysical changes might alter the amplitude levels and/or topography (by altering the configuration of the generators) of surface-recorded ERPs (e.g., Swick (2005)). Consequently, caution is warranted when comparing the ERPs and their scalp distributions of intact and brain-lesioned groups. It is difficult to directly quantify the consequences of brain lesions on tissue conductivity. To conclude that ERP differences between patients and controls reflect functional abnormalities in particular cognitive processes, and not primarily nonspecific effects of structural brain damage, it is helpful to demonstrate that they are specific to certain ERP components/stages of information processing and task conditions. Changes confined to one or a subset of ERP components, that additionally may not manifest across all task conditions, can give some indication concerning the specificity of ERP changes (Kutas et al., 2012; Swaab, 1998). In our study, group differences pertaining to ERP amplitudes were limited to specific task conditions and not across all data. This condition-dependent pattern suggests that the observed shifts are related to the specific cognitive processes engaged during those task conditions rather than being a global artifact of volume conduction. If volume conduction was the main driver, we would expect these group differences to be more uniformly present across task conditions. Another piece of evidence against volume conduction effects is the scalp potentials’ latency differences between the two groups observed for the Local + Global deviance detection. Group differences in the latencies of ERPs, such as the MMN and P3a, cannot be attributed to volume conduction alone (Hämäläinen et al., 1993). These differences in the timing of neural responses strongly indicate genuine variations in cognitive processing.

To provide a more balanced interpretation of our findings, we have incorporated a section in the “Discussion” that delves into the limitations of our study and lesion studies generally with respect to volume conduction and amplitude changes, titled “Limitations and future directions” [page 24-25].

It is unclear from the analyses whether the P3a amplitude differences are true amplitude differences or a byproduct of latency differences. The reason is that the statistical method used (cluster based permutations) might yield significant effects when the latency of a component is shifted, even if peak amplitudes are the same. Complementary analyses on mean or peak amplitudes could resolve this issue.

We thank the reviewer for raising an important concern about the use of cluster-based permutation tests and their potential to yield significant effects when the latency of a component is shifted. We acknowledge this concern and recognize the need for complementary analyses to address this issue. To provide a clearer understanding of the nature of the observed ERP amplitude differences, we conducted complementary analyses on mean amplitudes of the MMN and P3a components on the midline sensors for the conditions where significant group differences were observed. For the MMN component elicited by the Local Deviance, we found group amplitude differences on the electrodes AFz (p = 0.021), Fz (p = 0.008), CPz (p = 0.015), and Pz (p < 0.001). Surprisingly, we also found amplitude differences for the P3a component elicited by the Local Deviance on the electrodes AFz (p < 0.001), Fz (p < 0.001), FCz (p < 0.001), and Cz (p = 0.002) that were not observed previously with the cluster-based permutation analysis. For the MMN component elicited by the Local+Global Deviance, our analysis showed group amplitude differences on the electrodes AFz (p = 0.007), FCz (p = 0.051), Cz (p = 0.004), CPz (p = 0.002), and Pz (p < 0.001). However, as the reviewer rightly pointed out, the group differences for the P3a elicited by the Local + Global Deviance seem to be a byproduct of latency differences, as we did not find amplitude differences on any of the midline electrodes. Overall, this complementary analysis shows that the OFC patients had an attenuated MMN/P3a to local level prediction violation, and an attenuated and delayed MMN followed by a delayed P3a to the combined local and global level prediction violation. The new analysis is added in the Supplementary File 1 [page 5-7] and Supplementary File 1c and 1d.

The MMN, P3a and P3b components are difficult to map to the hierarchical PC theory. Traditionally, the MMN is ascribed to lower level processing while P3a and P3b are ascribed to higher level processing. However, the picture is more complicated. For example, the current results show that the MMN is enhanced in local + global surprise while the P3a is elicited by local surprise. Furthermore, the P3a is classically interpreted as reflecting attention reorientation and the P3b as reflecting the conscious detection of task-relevant targets. How attention and conscious awareness fit in hierarchical PC is not entirely clear.

Indeed, the relationships between MMN, P3a and P3b components and the predictive coding (PC) framework can be intricate. However, numerous studies employed the PC theory to interpret these common electrophysiological signatures as prediction error (PE) signals (Garrido et al., 2007, 2009; Lieder et al., 2013) and dissociations between these ERPs supported that there are successive levels of predictive processing (Chennu et al., 2013; El Karoui et al., 2015; Wacongne et al., 2011).

In terms of hierarchical PC (Friston, 2005), the temporally constrained MMN has been traditionally linked with first-level predictive processing, known as the local effect of short-term stimulus deviance. PE signals at this level feed forward to a temporally extended, attention-dependent system that extracts longer-term patterns. PE signals at the higher level are usually indexed by the P300, identified as the global effect of longer-term stimulus deviance. The P300 reflects a more attention-driven process, emerging in response to novel or low-probability “target” stimuli that violate broader contextual expectations (Polich, 2007), such as those that form over multiple trials. Because the MMN, P3a and P3b also appear to exhibit varying degrees of sensitivity to preconscious and conscious perceptual predictions (Sculthorpe et al., 2009), they could serve as measures for examining the concept of a predictive neural hierarchy.

Indeed, the MMN has been viewed as sensitive to local violation and essentially blind to higher-order regularities. However, this is a simplified view. For example, Wacongne et al. (2011) showed that violating a low-level perceptual expectation triggers the MMN, violating contextual expectations triggers the higher-level P3, and when both expectations are simultaneously violated, a larger response is evoked compared to either one alone. These findings, which are consistent with the results of our study, show that the local and global effects are not fully independent but interact in an early time window, indexed by enhanced and temporally extended MMN responses. They provide support not just for a hierarchical model, but for a predictive rather than a feedforward one. Moreover, the MMN has been found to be relatively insensitive to attention, because it is elicited in situations in which the subjects’ attention is directed away from the stimuli and there are no task demands (Chennu et al., 2013). Given that early MMN is a pre-attentive automatic ERP component (Näätänen et al., 2001; Pegado et al., 2010; Tiitinen et al., 1994), and given that it has been observed in comatose and vegetative state patients (Bekinschtein et al., 2009; Fischer et al., 2004; Naccache et al., 2004), the finding that even early MMN is impaired in OFC patients indicate that patients may suffer from a deficit in sensory predictive processing that is independent of attention and conscious awareness.

The picture is more complicated when it comes to the predictive roles of P3a and P3b components. Following the MMN, a positive polarity P300 complex, sensitive to the detection of unpredicted auditory events, has been reported (Chennu et al., 2013; Doricchi et al., 2021; Kompus et al., 2020; Liaukovich et al., 2022). However, the two types of P300 (P3a and P3b) have not been clearly fitted into the hierarchical PC theory. The P3a is considered to be part of the brain's mechanism for detecting PEs (Wessel et al., 2012; Wessel et al., 2014) and may indicate that the brain is reallocating attentional resources to process and learn from these unexpected events. The P3a is typically interpreted as reflecting an involuntary attentional reorienting process (Escera & Corral, 2007; Ungan et al., 2019), which may relate to the operations of the ventral attention network (Corbetta et al., 2008; Corbetta & Shulman, 2002; Nieuwenhuis et al., 2005). Predictive coding emphasizes the role of contextual information in generating predictions with P3a being influenced by the context in which an unexpected event occurs (Schomaker et al., 2014). In the hierarchy of predictive processing, the P3a may reflect PEs at different hierarchical levels, depending on the complexity of the prediction and the degree to which it deviates from the sensory input. On the other hand, the P3b is linked to higher-level cognitive processes that involve updating long-term predictions based on incoming sensory information. It is highly dependent on attention, conscious awareness and active engagement with the task (Bekinschtein et al., 2009; Del Cul et al., 2007; Sergent et al., 2005; Strauss et al., 2015). It is thought to play a role in integrating the unexpected sensory input into the current context, potentially leading to updates of predictions in working memory (Chao et al., 1995; Donchin & Coles, 1988; Polich, 2007).

Hierarchical PC theory is continually evolving, and the relationship between these ERP components and attention or conscious awareness remains an active area of research. We acknowledge the need for further investigation to better understand how attention and conscious awareness fit within this framework. In light of your comment, we provide a more comprehensive discussion about the functional meaning of the EEG findings in our “Discussion - OFC and hierarchical predictive processing” [page 22-24].

The fact that lateral PFC patients show unaltered neural responses contradicts prominent views from PC identifying this region as a generator of the MMN and a source of predictions sent to temporal auditory areas.

We appreciate the reviewer's comment and want to acknowledge that another reviewer raised this concern previously. We have provided a detailed response to this issue in our previous response (see Response to Reviewer #1 Comment 4). We have expanded the “Discussion” to address this point by adding a new section titled “Lack of findings in the lateral PFC lesion group” [page 21]. In this section, we first present some of the findings implicating specific areas of the lateral PFC in the generation of MMN and in predictive processing, and then offer an account of the potential reasons behind the lack of neurophysiological differences between the lateral PFC and control groups.

For these reasons, a more critical view on the extent to which the findings support hierarchical predictive coding is needed.

By responding to the reviewer’s previous comments (i.e., the reasons why the reviewer thinks it is difficult to determine the functional meaning of the EEG findings), we believe that we have offered a more critical view on this matter.

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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):

The work by Yijun Zhang and Zhimin He at al. analyzes the role of HDAC3 within DC subsets. Using an inducible ERT2-cre mouse model they observe the dependency of pDCs but not cDCs on HDAC3. The requirement of this histone modifier appears to be early during development around the CLP stage. Tamoxifen treated mice lack almost all pDCs besides lymphoid progenitors. Through bulk RNA seq experiment the authors identify multiple DC specific target gens within the remaining pDCs and further using Cut and Tag technology they validate some of the identified targets of HDAC3. Collectively the study is well executed and shows the requirement of HDAC3 on pDCs but not cDCs, in line with the recent findings of a lymphoid origin of pDC.

1) While the authors provide extensive data on the requirement of HDAC3 within progenitors, the high expression of HDAC3 in mature pDCs may underly a functional requirement. Have you tested INF production in CD11c cre pDCs? Are there transcriptional differences between pDCs from HDAC CD11c cre and WT mice?

We greatly appreciate the reviewer’s point. We have confirmed that Hdac3 can be efficiently deleted in pDCs of Hdac3fl/fl-CD11c Cre mice (Figure 5-figure supplement 1 in revised manuscript). Furthermore, in those Hdac3fl/fl-CD11c Cre mice, we have observed significantly decreased expression of key cytokines (Ifna, Ifnb, and Ifnl) by pDCs upon activation by CpG ODN (shown in Author response image 1). Therefore, HDAC3 is also required for proper pDC function. However, we have yet to conduct RNA-seq analysis comparing pDCs from HDAC CD11c cre and WT mice.

Author response image 1.

Cytokine expression in Hdac3 deficient pDCs upon activation

2) A more detailed characterization of the progenitor compartment that is compromised following depletion would be important, as also suggested in the specific points.

We thank the reviewer for this constructive suggestion. We have performed thorough analysis of the phenotype of hematopoietic stem cells and progenitor cells at various developmental stages in the bone marrow of Hdac3 deficient mice, based on the gating strategy from the recommended reference. Briefly, we analyzed the subpopulations of progenitors based on the description in the published report by "Pietras et al. 2015", namely MPP2, MPP3 and MPP4, using the same gating strategy for hematopoietic stem/progenitor cells. As shown in Author response image 2 and Author response image 3, we found that the number of LSK cells was increased in Hdac3 deficient mice, especially the subpopulations of MPP2 and MPP3, whereas no significant changes in MPP4. In contrast, the numbers of LT-HSC, ST-HSC and CLP were all dramatically decreased. This result has been optimized and added as Figure 3A in revised manuscript. The relevant description has been added and underlined in the revised manuscript Page 6 Line 164-168.

Author response image 2.

Gating strategy for hematopoietic stem/progenitor cells in bone marrow.

Author response image 3.

Hematopoietic stem/progenitor cells in Hdac3 deficient mice

Reviewer #2 (Public Review):

In this article Zhang et al. report that the Histone Deacetylase-3 (HDAC3) is highly expressed in mouse pDC and that pDC development is severely affected both in vivo and in vitro when using mice harbouring conditional deletion of HDAC3. However, pDC numbers are not affected in Hdac3fl/fl Itgax-Cre mice, indicating that HDCA3 is dispensable in CD11c+ late stages of pDC differentiation. Indeed, the authors provide wide experimental evidence for a role of HDAC3 in early precursors of pDC development, by combining adoptive transfer, gene expression profiling and in vitro differentiation experiments. Mechanistically, the authors have demonstrated that HDAC3 activity represses the expression of several transcription factors promoting cDC1 development, thus allowing the expression of genes involved in pDC development. In conclusion, these findings reveals HDAC3 as a key epigenetic regulator of the expression of the transcription factors required for pDC vs cDC1 developmental fate.

These results are novel and very promising. However, supplementary information and eventual further investigations are required to improve the clarity and the robustness of this article.

Major points

1) The gating strategy adopted to identify pDC in the BM and in the spleen should be entirely described and shown, at least as a Supplementary Figure. For the BM the authors indicate in the M & M section that they negatively selected cells for CD8a and B220, but both markers are actually expressed by differentiated pDC. However, in the Figures 1 and 2 pDC has been shown to be gated on CD19- CD11b- CD11c+. What is the precise protocol followed for pDC gating in the different organs and experiments?

We apologize for not clearly describing the protocols used in this study. Please see the detailed gating strategy for pDC in bone marrow, and for pDC and cDC in spleen (Figure 4 and Figure 5). These information are now added to Figure1−figure supplement 3, The relevant description has been underlined in Page 5 Line 113-116, in revised manuscript.

We would like to clarify that in our study, we used two different panels of antibody cocktails, one for bone marrow Lin- cells, including mAbs to CD2/CD3/TER-119/Ly6G/B220/CD11b/CD8/CD19; the other for DC enrichment, including mAbs to CD3/CD90/TER-119/Ly6G/CD19. We included B220 in the Lineage cocktails to deplete B cells and pDCs, in order to enrich for the progenitor cells from bone marrow. However, when enriching for the pDC and cDC, B220 or CD8a were not included in the cocktail to avoid depletion of pDC and cDC1 subsets . For the flow cytometry analysis of pDCs, we gated pDCs as the CD19−CD11b−CD11c+B220+SiglecH+ population in both bone marrow and spleen. The relevant description has been underlined in the revised manuscript Page 16 Line 431-434.

2) pDC identified in the BM as SiglecH+ B220+ can actually contain DC precursors, that can express these markers, too. This could explain why the impact of HDAC3 deletion appears stronger in the spleen than in the BM (Figures 1A and 2A). Along the same line, I think that it would important to show the phenotype of pDC in control vs HDAC3-deleted mice for the different pDC markers used (SiglecH, B220, Bst2) and I would suggest to include also Ly6D, taking also in account the results obtained in Figures 4 and 7. Finally, as HDCA3 deletion induces downregulation of CD8a in cDC1 and pDC express CD8a, it would important to analyse the expression of this marker on control vs HDAC3-deleted pDC.

We agree with the reviewer’s points. In the revised manuscript, we incorporated major surface markers, including Siglec H, B220, Ly6D, and PDCA-1, all of which consistently demonstrated a substantial decrease in the pDC population in Hdac3 deficient mice. Moreover, we did notice that Ly6D+ pDCs showed higher degree of decrease in Hdac3 deficient mice. Additionally, percentage and number of both CD8+ pDC and CD8- pDC were decreased in Hdac3 deficient mice (Author response image 4). These results are shown in Figure1−figure supplement 4 of the revised manuscript. The relevant description has been added and underlined in the revised manuscript Page 5 Line 121-125.

Author response image 4.

Bone marrow pDCs in Hdac3 deficient mice revealed by multiple surface markers

3) How do the authors explain that in the absence of HDAC3 cDC2 development increased in vivo in chimeric mice, but reduced in vitro (Figures 2B and 2E)?

As shown in the response to the Minor point 5 of Reviewer#1. Briefly, we suggested that the variabilities maybe explained by the timing of anaysis after HDAC3 deletion. In Figure 2C, we analyzed cells from the recipients one week after the final tamoxifen treatment and observed no significant change in the percentage of cDC2 when further pooled all the experiment data. In Figure 2E, where tamoxifen was administered at Day 0 in Flt3L-mediated DC differentiation in vitro, the DC subsets generated were then analyzed at different time points. We observed no significant changes in cDCs and cDC2 at Day 5, but decreases in the percentage of cDC2 were observed at Day 7 and Day 9. This suggested that the cDC subsets at Day 5 might have originated from progenitors at a later stage, while those at Day 7 and Day 9 might originate form the earlier progenitors. Therefore, based on these in vitro and in vivo experiments, we believe that the variation in the cDC2 phenotype might be attributed to the progenitors at different stages that generated these cDCs.

4) More generally, as reported also by authors (line 207), the reconstitution with HDAC3-deleted cells is poorly efficient. Although cDC seem not to be impacted, are other lymphoid or myeloid cells affected? This should be expected as HDAC3 regulates T and B development, as well as macrophage function. This should be important to know, although this does not call into question the results shown, as obtained in a competitive context.

In this study, we found no significant influence on T cells, mature B cells or NK cells, but immature B cells were significantly decreased, in Hdac3-ERT2-Cre mice after tamoxifen treatment (Figure 6). However, in the bone marrow chimera experiments, the numbers of major lymphoid cells were decreased due to the impaired reconstitution capacity of Hdac3 deficient progenitors. Consistent with our finding, it has been reported that HDAC3 was required for T cell and B cell generation, in HDAC3-VavCre mice (Summers et al., 2013), and was necessary for T cell maturation (Hsu et al., 2015). Moreover, HDAC3 is also required for the expression of inflammatory genes in macrophages upon activation (Chen et al., 2012; Nguyen et al., 2020).

5) What are the precise gating strategies used to identify the different hematopoietic precursors in the Figure 4 ? In particular, is there any lineage exclusion performed?

We apologize for not describing the experimental procedures clearly. In this study we enriched the lineage negative (Lin−) cells from the bone marrow using a Lineage-depleting antibody cocktail including mAbs to CD2/CD3/TER-119/Ly6G/B220/CD11b/CD8/CD19. We also provide the gating strategy implemented for sorting LSK and CDP populations from the Lin− cells in the bone marrow (Author response image 5), shown in the Figure 3A and Figure4−figure supplement 1 of revised manuscript.

Author response image 5.

Gating strategy for LSK, CD115+ CDP and CD115− CDP in bone marrow

6) Moreover, what is the SiglecH+ CD11c- population appearing in the spleen of mice reconstituted with HDAC3-deleted CDP, in Fig 4D?

We also noticed the appearance of a SiglecH+CD11c− cell population in the spleen of recipient mice reconstituted with HDAC3-deficient CD115−CDPs, while the presence of this population was not as significant in the HDAC3-Ctrl group, as shown in Figure 4D. We speculate that this SiglecH+CD11c− cell population might represent some cells at a differentiation stage earlier than pre-DCs. Alternatively, the relatively increased percentage of this population derived from HDAC3-deficient CD115−CDP might be due to the substantially decreased total numbers of DCs. This could be clarified by further analysis using additional cell surface markers.

7) Finally, in Fig 4H, how do the authors explain that Hdac3fl/fl express Il7r, while they are supposed to be sorted CD127- cells?

This is indeed an interesting question. In this study, we confirmed that CD115−CDPs were isolated from the surface CD127− cell population for RNA-seq analysis, and the purity of the sorted cells were checked (Author response image 6), as shown in Figure4−figure supplement 1 in revised manuscript.

The possible explanation for the expression of Il7r mRNA in some HDAC3fl/fl CD115−CDPs, as revealed in Figure 4H by RNA-seq analysis, could be due to a very low level of cell surface expression of CD127, these cells therefore could not be efficiently excluded by sorting for surface CD127- cells.

Author response image 6.

CD115−CDPs sorting from Hdac3-Ctrl and Hdac3-KO mice

8) What is known about the expression of HDAC3 in the different hematopoietic precursors analysed in this study? This information is available only for a few of them in Supplementary Figure 1. If not yet studied, they should be addressed.

We conducted additional analysis to address the expression of Hdac3 in various hematopoietic progenitor cells at different stages, based on the RNA-seq analyis. The data revealed a relatively consistent level of Hdac3 expression in progenitor populations, including HSC, MMP4, CLP, CDP and BM pDCs (Author response image 7). That suggests that HDAC3 may play an important role in the regulation of hematopoiesis at multiple stages. This information is now added in Figure1−figure supplement 1B of revised manuscript.

Author response image 7.

Hdac3 expression in hematopoietic progenitor cells

9) It would be highly informative to extend CUT and Tag studies to Irf8 and Tcf4, if this is technically feasible.

We totally agree with the reviewer. We have indeed attempted using CUT and Tag study to compare the binding sites of IRF8 and TCF4 in wild-type and Hdac3-deficient pDCs. However, it proved that this is technically unfeasible to get reliable results due to the limited number of cells we could obtain from the HDAC3 deficient mice. We are committed to explore alternative approaches or technologies in future studies to address this issue.

reply to u/IamOkei at https://www.reddit.com/r/Zettelkasten/comments/17beucn/comment/k5s6aek/?utm_source=reddit&utm_medium=web2x&context=3

u/IamOkei, I know you've got a significant enough practice that not much of what I might suggest may be helpful beyond your own extension of what you've got and how it is or isn't working for you. Perhaps chatting with a zettelkasten therapist may be helpful? Does anyone have "Zettelkasten Whisperer" on a business card yet?! More seriously, I occasionally dump some of my problems and issues into a notebook, unpublished on my blog, or even into a section of my own zettelkasten, which I never index or reconsult, as a helpful practice. Others like Henry David Thoreau have done something like this and there's a common related practice of writing "Morning Pages" that you can explore. My own version is somewhat similar to the idea of rubber duck debugging but focuses on my own work. You might try doing something like this in one of Bob Doto's cohorts or by way of private consulting sessions. Another free version of this could be found by participating in Will's regular weekly posts/threads "Share with us what is happening in your ZK this week" at https://forum.zettelkasten.de/. It's always a welcoming and constructive space. There are also some public and private (I won't out them) Discords where some of the practiced hands chat and commiserate with each other. Even the Obsidian PKM/Zettelkasten Discord channels aren't very Obsidian/digital-focused that you couldn't participate as an analog practitioner. I've even found that participating in book clubs related to some of my interests can be quite helpful in talking out ideas before writing them down. There are certainly options for working out and extending your own practice.

Beyond this, and without knowing more of your specific issues, I can only offer some broad thoughts which expand on some of the earlier discussion above.

I recommend stripping away Scheper's religious fervor, some of which he seems to have thrown over lately along with the idea of a permanent note or "main card" (something I think is a grave mistake), and trying something closer to Luhmann's idea of ZKII.

An alternate method, especially if you like a nice notebook or a particular fountain pen, might be to take all of your basic literature/fleeting notes along with the bibliographic data in a notebook and then just use your analog index cards/slips to make your permanent notes and your index.

Ultimately it's all a lot of the same process, though it may come down to what you want to call it and your broad philosophy. If you're anti-antinet, definitely quit using the verbiage for the framing there and lean toward the words used by Ahrens, Dan Allosso, Gerald Weinberg, Mark Bernstein, Umberto Eco, Beatrice Webb, Jacques Barzun & Henry Graff, or any of the dozens of others or even make up your own. Goodness knows we need a lot more names and categories for types of notes—just like we all need another one page blog post about how the Zettelkasten method works by someone who's been at it for a week. Maybe someone will bring all these authors to terms one day?

Generally once you know what sorts of ideas you're most interested in, you take fewer big notes on administrivia and focus more of your note taking towards your own personal goals and desires. (Taking notes to learn a subject are certainly game, but often they serve little purpose after-the-fact.) You can also focus less on note taking within your entertainment reading (usually a waste) and focusing more heavily on richer material (books and journal articles) that is "above you" in Adler's framing. You might make hundreds of highlights and annotations in a particular book, but only get two or three serious ideas and notes out of it ultimately. Focus on this and leave the rest. If you're aware of the Pareto principle or the 80/20 rule, then spend the majority of your time on the grander permanent notes (10-20%), and a lot less time worrying about the all the rest (the 80-90%).

In the example above relating to Marx, you can breeze through some low level introductory material for context, but nothing is going to beat reading Marx himself a few times. The notes you make on his text will have tremendously more value than the ones you took on the low level context. A corollary to this is that you're highly unlikely to earn a Ph.D. or discover massive insight by reading and taking note posts on Twitter, Medium, or Substack (except possibly unless your work is on the cultural anthropology of those platforms).

A lot of the zettelkasten spaces focus heavily on the note taking part of the process and not enough on the quality of what you're reading and how you're reading it. This portion is possibly more valuable than the note taking piece, but the two should be hand-in-glove and work toward something.

I suspect that most people who have 1000 notes know which five or ten are the most important to where they're going and how they're growing. Focus on those and your "conversations with texts" relating to those. The rest is either low level context for where you're headed or either pure noise/digital exhaust.

If you think of ideas as incunables, which notes will be worth of putting on your tombstone? In other words: What are your "tombstone notes"? (See what I did there? I came up with another name for a type of note, a sin for which I'm certainly going to spend a lot of time in zettelkasten purgatory.)

This can be a whole range of both external and internal stimuli. For example, our pain can be blocked out when we are focused on someone or something else that we feel is more important. We can block out our hunger when we are about to give a public presentation or performance. When we truly believe that something is the most important thing at that moment, we can have almost superhuman like abilities to drown out anything that could be keeping us from that one singular thing. First responders and military would be a great example of this.

Author Response

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

We sincerely thank the editor and reviewers for their constructive feedback on our manuscript. Based on their recommendations, we've conducted additional experiments, made revisions to the text and figures, and provide a point-by-point response below.

Reviewer #1 (Recommendations for the authors):

1) The lack of behavioral/physiological measures of the depth of anesthesia (ventilation, heart rate, blood pressure, temperature, O2, pain reflexes, etc...) combined with the lack of dose-response and the use of different routes of administration makes the data difficult to interpret. Sure, there is a clear difference in network activation between KET and ISO, but are those effects due to the depth of the anesthesia, the route of administration, and the dose used? The lack of behavioral/physiological measures prevents the identification of brain regions responsible for some of the physiological effects and different effects of anesthetics.

We greatly appreciate the insightful feedback you have provided.

In response to the concerns about anesthesia depth:

a. We recorded EEG and EMG data both before and after drug administration. Supplementary Figure 1 showcases the changes in EEG and EMG power observed 30 minutes post-drug administration, normalized to a 5-minute baseline taken prior to the drug's administration. Notably, no significant differences were detected in the normalized EEG and EMG power between the ISO and KET groups. Given the marked statistical differences observed between the EEG power in the KET and saline groups, and the EMG power in the home cage and ISO groups, we infer that both anesthetics effectively induced a loss of consciousness.

b. We used standard methods and doses for inducing c-Fos expression with anesthetics, as documented in prior studies (Hua, T, et al., Nat Neurosci, 2020; 23(7): 854-868; Jiang-Xie, L F, et al., Neuron, 2019; 102(5): 1053-1065.e4; Lu, J, et al., J Comp Neurol, 2008; 508(4): 648-62). In future research, it might be more optimal to adopt continuous intraperitoneal or intravenous administration of ketamine.

c. Within the scope of our study, while disparities in anesthesia duration might potentially influence the direct statistical comparison of ISO and KET, such disparities wouldn't compromise the identification of brain regions activated by KET or ISO when assessed as distinct stimuli (ISO vs. home cage; KET vs. saline) or in relation to their individual functional network hub node results.

We hope these additions and clarifications adequately address your concerns and enhance the comprehensibility of our data.

2) Under anesthesia there should be an overall reduction of activity, is that the case? There is no mention of significantly downregulated regions. The authors use multiple transformations of the data to interpret the results (%, PC1 values, logarithm) without much explanation or showing the full raw data in Fig 1. It would be helpful to interpret the data to compare the average fos+ neurons in each region between treatment and control for each drug.

Absence of Significantly Downregulated Regions Under Anesthesia: There are two primary reasons for this observation:

a. Our study's sampling time for the home cage, ISO, saline, and KET groups was during Zeitgeber Time (ZT) 6-7.5. During this period, mice in both the home cage and saline groups typically showed reduced spontaneous activity or were in a sleep state. Our Supplementary Figure 1 EEG and EMG data corroborate this, revealing no significant statistical variations in EEG power between the home cage and ISO groups, nor in EMG power between the saline and KET groups.

b. Our immunohistochemical data showed that the total number of c-Fos positive cells in the two control groups was notably lower than in the experimental groups (Saline group vs KET group: 11808±2386 versus 308705±106131, P = 0.006; Home cage vs ISO group: 3371±840 vs 12326±1879, P = 0.001). This is in line with previous studies, like the one by Cirelli C and team, which found minimal c-Fos expression throughout the mouse brain during physiological sleep (Cirelli, C, and G Tononi, Sleep, 2000; 23(4): 453-69). Thus, in our analysis, we did not detect regions with significant downregulation when comparing anesthetized mice with controls.

Interpreting Raw Data from Figure 1: Regarding the average Fos+ neurons:

In Figures 4 and 5, we utilized raw data (c-Fos cell count) to assess cell expression differences across 201 brain regions within each group. Only brain regions that had significant statistical differences after multiple comparison corrections are shown in the figures.

3) I do not understand their interpretation of the PCA analyses. For instance, in Fig 2 they claim that KET is associated with PC1 while ISO is associated with PC2. Looking at the distribution of points it's clear that the KET animals are all grouped at around +2.5 on PC1 and -2.0 on PC2, this means that KET is associated with both PC1 and PC2 to a similar degree (2 to 2.5). Moreover, I'm confused about why they use PCA to represent the animals/group. PCA is a powerful technique to reduce dimensionality and identify groups of variables that may represent the same underlying construct; however, it is not the best way to identify clusters of individuals or groups.

Clarification on PCA Analyses in Figure 2: Thank you for pointing out the ambiguities in our initial presentation of the PCA analyses. We are grateful for the opportunity to address these concerns.

KET and ISO Associations with PC1 and PC2: You rightly observed that KET samples manifest both a positive value on PC1 (around +2.5) and a negative one on PC2 (around -2.0), suggesting that KET has a substantial influence on both principal components. In PCA, a positive score implies a positive association with that component, whereas a negative score suggests a negative association. Contrarily, ISO samples predominantly exhibit values around +2.5 on PC2, with nearly neutral values for PC1, underlining its stronger association with PC2 and lack of significant correlation with PC1. To ensure transparency and clarity, we've adjusted the corresponding descriptions in our manuscript, which can be found on Line 100.

Rationale Behind Using PCA to Represent Animals/Groups: Our initial step was to conduct PCA clustering analysis on the 201 brain regions within both the ISO and KET groups. In the accompanying chart, varying colors denote different brain regions, while distinct shapes represent separate clusters. There wasn't a pronounced distribution pattern within the ISO and KET groups, which led us to adopt the current computational method presented in the paper. This approach was chosen to directly contrast the relative differential expressions between ISO and KET.

We deeply value your feedback, which has steered us toward a clearer and more accurate presentation of our data. We genuinely appreciate your meticulous review.

Author response image 1.

4) The actual metric used for the first PCA is unclear, is it the FOS density in each of the regions (some of those regions are large and consist of many subregions, how does that affect the analysis) is it the %-fos, or normalized cells? The wording describing this is variable causing some confusion. How would looking at these different metrics influence the analysis?

Thank you for raising concerns about the metrics used in our PCA analysis. We recognize the need for clearer exposition and appreciate the opportunity to clarify.

PCA Metrics: The metric for our PCA is calculated by obtaining the ratio of the Fos density within a specific brain region to the global Fos density across the brain. Briefly, this entails dividing the number of Fos-positive cells in a given region by its volume, and then comparing this to the Fos density of the whole brain. The logarithm of this ratio provides our PCA metric. We've elaborated on this in the Materials and Methods section (Lines 401) and enhanced clarity in our revised manuscript, particularly at Line 96.

In Figure 2A, we employed 53 larger, mutually exclusive brain regions based on the reference from the study by Do et al. (eLife, 2016;5:e13214). However, in Figure 3A, we used a more detailed segmentation, incorporating 201 distinct brain areas that are more granular than those in Figure 2A. Notably, the PCA results from both representations were consistent. The rationale behind selecting either the 53 or 201 brain regions can be found in our response to Question 10.

Rationale for Metric Choice: The log ratio of regional c-Fos densities relative to the global brain density was chosen due to:

a. Notable disparities in c-Fos cell expression across the groups.

b. A significant non-normal distribution of density values across animals within the group. Employing the log ratio effectively mitigates the impact of extreme values and outliers, achieving a more standardized data distribution.

We've added PCA plots based on c-Fos densities, depicted in Author response image 2. However, the data dispersion has resulted in a significantly spread-out horizontal scale for these visuals.

Author response image 2.

5) Based on Fig 3 the authors concludes that ISO activates the hypothalamic regions and inhibits the cortex, however, Fig 1 shows neither an activation of the hypothalamus in the ISO nor an inhibition of the cortex when compared to home cage control. If anything it suggests the opposite.

Thank you for your insightful observations regarding the discrepancies between Figures 2 and 3. We believe that when you refer to Figure 1, you are actually referencing Figure 2C.

ISO activation in Hypothalamus: In Figure 2C, we regret the oversight where we inadvertently interchanged the positions of ISO and Saline. When accurately represented, Figure 2C indeed shows that ISO notably activates the periventricular zone (PVZ) and the lateral zone (LZ) of the hypothalamus compared to the home cage group. Moreover, there's a discernible difference in the hypothalamic response between ISO and KET.

ISO's Effect on the Cortex: The main aim of Figure 3 was to highlight the differing responses between ISO and KET in the cortex. Notably, KET demonstrates a positive correlation with PC1 (+7 on PC1), whereas ISO shows a negative association (-3 on PC1). Given that the coefficient of PC1 for the cortical region is positive, it suggests that the cortical areas activated by KET are inhibited by ISO (with KET's distribution around 0 on PC2). However, the divergence between ISO and the home cage is most apparent in PC2, with ISO clusters at +4 and the home cage approximately at -2, suggesting that ISO activates a different set of cortical nuclei. In alignment with this, Figure 2C also illustrates that ISO activates specific cortical areas, such as ILA and PIR, in contrast to the home cage.

Thus, Figure 3 primarily employs PCA to delineate the contrasts between ISO and KET, whereas Figure 2C emphasizes the comparison of each against their respective controls.

6) Control for isoflurane should be air in the induction chamber rather than home cage. It is possible that Fos activation reflects handling/stress pre-anesthesia in the animals, which would increase Fos expression in the stress-related regions such as the BST, striatum (CeA), hypothalamus (PVH) and potentially the LC.

Thank you for emphasizing the importance of an appropriate control for Isoflurane.

In our efforts to minimize the potential impact of stress-induced c-Fos expression, we implemented several precautionary measures. Prior to the experiment, both groups of mice were subjected to handling and acclimatization within the induction chamber over four days. By the day of the experiment, for the mice in the experimental group, we ensured they were comfortable and exhibited no signs of distress or fear—such as cowering or evading. With care, we slowly relocated them to the nearby anesthesia induction chamber. Using 5% ISO, anesthesia was induced promptly, following a meticulously devised protocol to reduce stress impacts on c-Fos expression.

Moreover, existing studies have shown Isoflurane's activation of BST/CeA (Hua, T, et al., Nat Neurosci, 2020, 23: 854-868), PVH (Xu, Z, et al., British Journal of Anaesthesia, 2023, 130: 446-458), and LC (Lu, J, et al., J Comp Neurol, 2008, 508: 648-62), even when using oxygen controls. Such literature supports our findings, indicating that the activation we observed was indeed due to Isoflurane and not purely stress-related.

7) In the Ket network there are a few anticorrelated regions, most of which are amongst the list of the most activated regions, does this mean that the strong correlation results from an overall decreased activation? And if so, is it possible that the ketamine anesthesia was stronger than the isoflurane, causing a more general reduction in activity?

The pronounced correlations observed within the ketamine (KET) network do not signify a generalized decrease in activation. Instead, these correlations reflect significantly enhanced activity in specific regions under KET anesthesia. This amplified correlation is an indication of a more widespread increase in activity, rather than a decrease. These findings are consistent with previous research, which showed that anesthetic doses of ketamine produce patterns of Fos expression in the CNS similar to wakefulness (Lu, J, et al., J Comp Neurol, 2008; 508(4): 648-62).

Regarding the comparative strength of KET versus ISO anesthesia, our electroencephalographic evidence confirms that both agents induce a loss of consciousness. No significant differences were observed in EEG and EMG readings within the first 30 minutes post-administration. In future research, a continuous intravenous or intraperitoneal administration of KET might be a preferable method.

8) Since they have established networks it would be easy and useful to look at how the different regions identified (sleep, pain, neuroendocrine, motor-related, ...) work together to maintain analgesia, are they within the same module? Do they become functionally connected and is this core network of functional connections similar for KET and ISO?

Thank you for your suggestion. In response to your inquiry, we undertook analysis of the core functional networks for KET and ISO, using a set threshold at r>0.82 and P<0.05. For evaluating the modularity of each network, we utilized Newman's spectral community detection algorithm.

(A) The ISO’s core functional network (56 nodes, 372 edges) predominantly divides into two modules with a modularity quotient of 0.345. ISO-active regions include arousal-associated regions (PL, ILA, PVT), analgesia-related (CeA, LC, PB), neuroendocrine function nuclei (TU, PVi, ARH, PVH, SON) as detailed in Figure 5. Notably, ARH and SON weren't incorporated into the core network. Analgesia-associated regions, such as CeA, LC, and PB, reside within module 1, while neuroendocrine nuclei are spread between modules 1 and 2.

(B) In contrast, KET's core functional network (61 nodes, 1820 edges) splits into three distinct modules, but its low modularity quotient (0.06) indicates a lack of clear functional modularization, suggesting denser interconnections among brain regions. Furthermore, functionally-related regions such as arousal (PL, ILA, PVT, DR), analgesia-related (ACA, APN, PAG, LC), and neuroendocrine regulation (PVH, SON),etc., as seen in Figure 4, are distributed across different modules. This distribution may implies that functions like analgesia and neuroendocrine regulation are not governed by simple, linear processes, but arise from complex, overlapping pathways spanning various modules and functional zones.

In summary, the core functional networks of ISO and KET differ, with functionally-related regions spanning multiple modules, reflecting their diverse roles in varied physiological regulations.

Author response image 3.

9) The naming of the function of some of the regions is very much debatable. For instance, PL/ILA are named "sleep-wakefulness regulation" regions in the paper. I can think of many more important functions of the PL/IL including executive functions, behavioral flexibility, and emotional control. It is unclear how the functions of all the regions were attributed. I am not sure that this biased labeling of structure-function is useful to the reports, it may instead suggest wrong conclusions.

Thank you for your thoughtful feedback regarding our classification of the functions of the PL/ILA regions in our manuscript.

We recognize the challenge in accurately defining the functions of brain regions. While there is evidence highlighting the role of PL/ILA in arousal pathways, we also acknowledge their documented roles in executive functions, behavioral flexibility, and emotional control. In response to your comments, we have refined our description, changing "sleep-wakefulness regulation" to "wake-promoting pathways" (see Line: 159, 164).

It's worth noting that many brain regions, including the PL/ILA, have multiple functions. We agree that a single label might not capture the entirety of their roles. To provide a broader perspective, we will add a section in our manuscript that sheds light on the varied functions of these regions (Line: 181).

10) A point of concern and confusion is the number of brain regions analyzed. In the introduction, it is mentioned that 987 brain regions are considered, but this is reduced to 53 selected brain regions in Figure 2, then 201 brain regions in Figure 3, and reduced again to 63 for the network analysis. The rationale for selecting different brain regions is not clear.

For the 987 brain regions: Using the standard mouse atlas available at http://atlas.brain-map.org/, the mouse brain is organized into nine levels. The broadest category is the grey matter, which then progresses to more specific subdivisions, totaling 987 unique regions.

For the 53 brain regions: To effectively understand the activation patterns of ISO and KET, we started with a broad approach, looking at larger brain areas like the thalamus and hypothalamus. This broad view, presented in Figure 2, focuses on the 5th-level brain regions, encompassing 53 primary areas. This methodology is also employed in the study by Do et al. (Elife, 2016; 5: e13214). We have added the rationale for selecting these brain regions in the main text (Line: 92).

Regarding the 201 brain regions in Figures 3, 4, and 5: We delved deeper, examining the 6th-level brain regions, a common granularity in neuroscience research. This detailed view allowed us to highlight specific areas, like the CeA and PVH (Line:129).

Finally, for Figures 6 and 7, we selected 63 regions that were activated by both ISO and KET, as well as regions previously reported to be related to the mechanism of general anesthesia(Leung, L, et al., Progress in neurobiology, 2014; 122: 24-44) (Line: 220). Using these regions, we analyzed the correlation of c-Fos expression, aiming to construct a functional brain network with strong positive connections.

We hope this clarifies our approach and the rationale behind our region selection at each stage of the study. Thank you for your attention to this detail.

11) The statistical analysis does not seem appropriate considering the high number of comparisons. They use simple t-tests without correction for multiple comparisons.

Thank you for pointing out the concern regarding our statistical analysis. In the revised manuscript, we addressed the issue of multiple comparisons correction in our t-tests. We adopted the statistical methods detailed in the papers by Renier, N, et al., Cell, 2016; and Benjamini, Y, and Y Hochberg, 1995. P-values were adjusted for multiple comparisons using the two-stage linear step-up procedure of Benjamini, Krieger, and Yekutieli, with a false discovery rate (FDR) threshold (Q) of 0.05. This approach is now explained in the Materials and Methods section (Line: 434). After this adjustment, the brain regions we initially identified remained statistically significant. Furthermore, we revisited the original immunohistochemical images to confirm the differences in c-Fos cell expression between the experimental and control groups, reinforcing our conclusions.

12) There is no statistical analysis in Fig 2C。

Thank you for bringing to our attention the lack of statistical analysis in Fig 2C. We have now added the relevant statistical data in Supplementary Table 1 and provided annotations in Fig 2C to reflect this.

Reviewer #2

1) The authors report 987 brain regions in the introduction, but I cannot find any analysis that incorporates these or even which regions they are. Very little rationale is provided for the regions included in any of the analyses and numbers range from 53 in Figure 1, to 201 in Figure 3, to 63 in Figure 6. It would help if the authors could first survey Fos+ counts across all regions to identify a subset that is of interest (significantly changed by either condition compared to control) for follow up analysis.

Thank you for your insightful comments on the number of brain regions analyzed in our study.

987 Brain Regions: The reference to 987 brain regions from the standard mouse atlas (http://atlas.brain-map.org/) represents the entire categorization of the mouse brain across nine levels. We recognize that a comprehensive analysis of all these regions would be valuable, but to ensure clarity and depth, we took a focused approach.

Region Selection Rationale:

Figure 2: Concentrated on 5th-level brain regions (53 areas), inspired by methods from Do et al. (eLife, 2016;5:e13214). This provided a broad overview of c-Fos expression differences. Figures 4 and 5: Delved into 6th-level brain regions (201 areas), a common practice in neuroscience for more detailed study. Figure 6: We focused on 63 regions, which encompass not only the regions activated by both ISO and KET but also those previously reported to be associated with the mechanisms of general anesthesia. Methodological Approach: Our region selection was rooted in identifying areas with significant changes under anesthetic conditions compared to controls. This staged approach allowed a targeted analysis of the most affected regions, ensuring robust conclusions.

Enhancements: We've incorporated comparative analyses of activated brain regions at different hierarchical levels in Figures 4 and 5. For clearer comprehension, we’ve added clarifications in the manuscript at Lines: 92, 130, and 220.

2) Different data transformations are used for each analysis. One that is especially confusing is the 'normalization' of brain regions by % of total brain activation for each animal prior to PCA analysis in Figures 2 and 3. This would obscure any global differences in activation and make it unlikely to observe decreases in activation (which I think is likely here) that could be identified using the Fos+ counts after normalizing for region size (ie. Fos+ count / mm3) which is standard practice in such Fos-based activity mapping studies. While PCA can be powerful approach to identify global patterns, the purpose of the analysis in its current form is unclear. It would be more meaningful to show that regional activation patterns (measured as counts/mm3) are on separate PCs by group.

Thank you for your thoughtful comments. We regret any confusion caused by our initial presentation. For the PCA analysis in Figures 2A and 3A, we calculated the ratio of cell density in each brain region to the overall brain density, and then applied a logarithmic transformation to this ratio. Our approach in Figure 2C was to use the proportion of c-Fos cell counts in individual brain regions to the total cell counts throughout the brain. This methodology considers variations in overall c-Fos cell counts across animals, effectively mitigating potential biases due to differential global activation levels across subjects.

Furthermore, our direct comparison of differences in c-Fos cell counts between ISO, KET, and their respective control groups in Figures 4 and 5 addresses your concerns about potential decreases in activation. Notably, we did not identify any brain regions with significant suppression in these figures, which is consistent with the trends observed post-normalization in Figure 2C.

Given your feedback, we conducted another PCA using cell densities for each region (counts/mm3). However, we found significant variability and non-normal distribution of c-Fos density across the groups, leading to extensive data dispersion. Consequently, normalizing the cell counts across regions and then applying a logarithmic transformation before PCA might be more appropriate.

Author response image 4.

Additionally, our exploration of regional activation patterns using PCA analysis for ISO and KET separately, based on the logarithm ratio of the c-Fos density, revealed that there was no distinct clustering feature among the different brain regions (as illustrated in Author response image 5: colors represented distinct brain regions, while the shapes were indicative of different clusters). This observation further suggests that our original statistical approach might be more suitable.

Author response image 5.

3) Critical problem: The authors include a control group for each anesthetic (ketamine vs. saline, isofluorane vs. homecage) but most analyses do not make use of the control groups or directly compare Fos+ counts across the groups. Strictly speaking, they should have compared relative levels of induction by ketamine versus induction by isoflurane using ANOVAs. Instead, each type of induction was separate from the other. This does not account for increased variability in the ketamine versus isoflurane groups. There is no mention in the Statistics section or in Results section that any multiple comparison corrections were used. It appears that the authors only used Students t-test for each region and did not perform any corrections.

We appreciate the reviewer's insights and have addressed your concerns:

Given the pronounced difference in c-Fos cell count expression between the KET and ISO groups, a direct comparison of Fos+ counts may not effectively capture their inherent disparities. To better highlight these distinctions, we used the logarithm ratio of c-Fos density in our PCA analysis (Figure 3), mitigating potential disparities in overall cell counts between samples and emphasizing relative variations. However, in response to your feedback, we've included additional analyses. Author response image 6 depicts the c-Fos density (cells/mm^3) across different brain regions for the home cage, ISO, saline, and KET groups, with regions like the cerebral cortex, cerebral nuclei, thalamus, and others differentiated by shaded backgrounds. Data are represented as mean ± SEM. We performed a one-way ANOVA followed by Tukey’s post hoc test, marking significant differences between ISO and KET with asterisks: P < 0.001, P < 0.01, P < 0.05.

Regarding multiple comparison corrections, we've conducted thorough analyses on the data in Figure 2C and Figures 4, 5, and 6, implementing multiple comparison corrections. The detailed methodology is provided in the “Statistical analysis” section.

Author response image 6.

4) Figures 4 and 5 show brain regions 'significantly activated' following KET or ISO respectively, but again a subset of regions are shown and the stats seem to be t-tests with no multiple comparisons correction. It would help to show these two figures side by side, include the same regions, and keep the y axis ranges similar so the reader can easily compare the 'activation patterns' across the two treatments. Indeed, it looks like KET/Saline induced activation is an order or magnitude or two higher than ISO/Homecage. I would also recommend that this be the first data figure before any other analyses and maybe further analysis could be restricted to regions that are significantly changed in following KET or ISO here.

Thank you for your constructive feedback regarding Figures 4 and 5.

Comparison and Presentation of Figures 4 and 5: We acknowledge your suggestion to present these figures side by side for easier comparison. In the supplementary figure provided in the previous question, we've placed Figures 4 and 5 adjacent to each other, with consistent y-axis ranges, ensuring that readers can make direct comparisons between the activation patterns elicited by KET and ISO.

Statistical Concerns and Region Selection: As mentioned in our previous response, we have conducted multiple comparison corrections on the data presented in Figures 4 and 5. Detailed procedures are elaborated in the “Statistical analysis” section. We believe this approach addresses your concerns regarding the use of t-tests without corrections for multiple comparisons.

Difference in Activation Levels: We observed that the c-Fos activation due to KET is significantly higher than that from ISO. When presented side-by-side using the same scale, ISO activations appear less prominent, potentially mask subtle differences in the activation patterns of ISO, particularly if both KET and ISO showed changes in the same direction in certain brain regions but differed in magnitude. To address this, we used the proportion of c-Fos cell counts in Figure 2C, the logarithm ratio of c-Fos density in Figure 2A and Figure 3. This method emphasizes the relative changes, rather than absolute values, giving a more balanced view of the effects of each treatment.

5) Analyses in Figure 6 and 7 are interesting but again the choice of regions to include is unclear and makes interpreting the results impossible. For example, in Figure 7 it is unclear why the list of regions in bar graphs showing Degree and Betweenness Centrality are not the same even within a single row?

Thank you for your pertinent observation. The choice of brain regions in Figures 6 and 7 was carefully determined based on two main criteria: regions that were significantly activated by ISO or KET within the scope of our study, and those previously reported to be associated with anesthesia mechanisms and sleep-wake regulation.

Regarding your second concern on Figure 7, the discrepancies observed in the x-axes of the bar graphs arise from our methodological approach. We prioritized presenting the top 20% of regions based on their Degree or Betweenness Centrality values. By separately ranking these regions from highest to lowest, the regions presented for each metric inherently differ. This approach was taken to elucidate nodes that consistently emerge as significant across both metrics, thereby highlighting core nodes in the functional network. Were we to use a consistent x-axis without this ranking, it would not only necessitate a more extensive presentation but might also dilute the emphasis on key information. To clarify this methodology and its rationale for our readers, we have expanded upon this in the manuscript at Line 243.

We hope these clarifications address your concerns and facilitate a clearer understanding of our findings.

Reviewer #1 (Recommendations For The Authors):

Minor points

1) In Table 1: the separation of which substructures belong to which brain structure is not clear

2) Line 132 on page 3 seems to repeat the sentence earlier in the paragraph "KET predominantly affects brain regions within the cerebral cortex (CTX), while significantly inhibiting the hypothalamus, midbrain, and hindbrain."

3) Typos

a) Line 99/100 and 130 Central nucleus (CNU) should be cerebral nucleus

b) Comma on line 166

c) Fig. 4D: KET instead of Keta

d) Line 263 "ep"

e) Line 332: 35" "ml (add space)

4) Will data and code be made available?

Thank you for your detailed feedback.

1. We have revised Table 1 to clarify which substructures belong to which brain structures.

2. We acknowledge the redundancy and have now edited line 139 on page 3 to remove the repeated sentence regarding the effects of KET on brain regions.

3. We have addressed the typos you pointed out:

a. The terms "Central nucleus (CNU)" have been corrected to "cerebral nucleus."

b. The comma issue on line 166 has been rectified.

c. In Fig. 4D, we have corrected "Keta" to "KET."

d. We have corrected the typo "ep" on line 263.

e. A space has been added between "35" and "ml" on line 332 as you indicated.

1. Regarding the availability of data and code, we are currently conducting additional analyses related to this study. Once these analyses are completed, we will be more than happy to make the data and code available.

Thank you for assisting us in improving our manuscript.

Reviewer #2 (Recommendations For The Authors):

Minor comments:

6) The term 'whole-brain mapping' in the title suggests that the mapping was performed on 'intact brains' where in fact serial sections were used here. Maybe the authors could change to 'brain-wide mapping' to align better with the study.

Thank you for your insightful comments.

We have revised the title as suggested, changing "whole-brain mapping" to "brain-wide mapping".

7) It is unclear if the mice were kept under anesthesia for the 90-min duration and how the authors monitored the level of sedation. Additionally, if the KET mice were already sedated why were they further sedated with ISO before perfusions and tissue extraction? The methods should be clarified and any potential confounds discussed.

To maintain consistency in the experimental protocol and to reduce stress reactions in the mice, ISO was used before perfusion in all cases. However, this does not affect c-Fos expression as the expression of c-Fos protein starts 20-30 minutes after stimulation (Lara Aparicio, S Y, et al., NeuroSci, 2022; 3(4): 687-702).

We appreciate your guidance in enhancing the clarity of our manuscript.

Reviewer #3 (Recommendations For The Authors):

Recommendation: Minor corrections.

1) The authors should delve deeper into the molecular mechanisms underlying the observed effects, particularly the changes associated with NMDA and GABA receptors. Exploring these mechanisms would provide a more comprehensive understanding of how Ketamine and Isoflurane modulate neural activity and induce anesthesia.

2) The clinical relevance of these findings has not been sufficiently addressed. It would be valuable to elaborate on how the current research outcomes could potentially lead to changes in current anesthesia practices. For instance, identifying the distinct pathways of action for Ketamine and Isoflurane could aid anesthesiologists in selecting the most appropriate anesthetic based on the specific needs of individual patients or surgical procedures.

3) Both Ketamine and Isoflurane have been associated with neurotoxicity. It is important to discuss how the c-Fos activation induced by these anesthetics could contribute, at least partially, to anesthesia-related neurotoxicity. Examining the potential neurotoxic effects would provide a more comprehensive understanding of the risks associated with these anesthetics and aid in the development of safer anesthesia protocols.

Thank you for your valuable suggestions.

Regarding the three points (1, 2, and 3) you've raised, we fully recognize their significance. In the current study, our primary focus was on the differential impacts of Isoflurane and Ketamine on widespread c-Fos expression in the brain. However, we indeed acknowledge the importance of delving deeper into these mechanisms and their clinical relevance. Therefore, we intend to explore these critical issues in greater detail in our future research endeavors.

We appreciate your feedback, which provides constructive guidance for our subsequent research directions.

Author Response

eLife assessment

This study uses a multi-pronged empirical and theoretical approach to advance our understanding of how differences in learning relate to differences in the ways that male versus female animals cope with urban environments, and more generally how reversal learning may benefit animals in urban habitats. The work makes an important contribution and parts of the data and analyses are solid, although several of the main claims are only partially supported or overstated and require additional support.

We thank the Editor and both Reviewers for their time and for their constructive evaluation of our manuscript. We will work to address each comment and suggestion offered by the Reviewers in a revision.

Reviewer #1 (Public Review):

Summary:

In this highly ambitious paper, Breen and Deffner used a multi-pronged approach to generate novel insights on how differences between male and female birds in their learning strategies might relate to patterns of invasion and spread into new geographic and urban areas.

The empirical results, drawn from data available in online archives, showed that while males and females are similar in their initial efficiency of learning a standard color-food association (e.g., color X = food; color Y = no food) scenario when the associations are switched (now, color Y = food, X= no food), males are more efficient than females at adjusting to the new situation (i.e., faster at 'reversal learning'). Clearly, if animals live in an unstable world, where associations between cues (e.g., color) and what is good versus bad might change unpredictably, it is important to be good at reversal learning. In these grackles, males tend to disperse into new areas before females. It is thus fascinating that males appear to be better than females at reversal learning. Importantly, to gain a better understanding of underlying learning mechanisms, the authors use a Bayesian learning model to assess the relative role of two mechanisms (each governed by a single parameter) that might contribute to differences in learning. They find that what they term 'risk sensitive' learning is the key to explaining the differences in reversal learning. Males tend to exhibit higher risk sensitivity which explains their faster reversal learning. The authors then tested the validity of their empirical results by running agent-based simulations where 10,000 computer-simulated 'birds' were asked to make feeding choices using the learning parameters estimated from real birds. Perhaps not surprisingly, the computer birds exhibited learning patterns that were strikingly similar to the real birds. Finally, the authors ran evolutionary algorithms that simulate evolution by natural selection where the key traits that can evolve are the two learning parameters. They find that under conditions that might be common in urban environments, high-risk sensitivity is indeed favored.

Strengths:

The paper addresses a critically important issue in the modern world. Clearly, some organisms (some species, some individuals) are adjusting well and thriving in the modern, human-altered world, while others are doing poorly. Understanding how organisms cope with human-induced environmental change, and why some are particularly good at adjusting to change is thus an important question.

The comparison of male versus female reversal learning across three populations that differ in years since they were first invaded by grackles is one of few, perhaps the first in any species, to address this important issue experimentally.

Using a combination of experimental results, statistical simulations, and evolutionary modeling is a powerful method for elucidating novel insights.

Thank you—we are delighted to receive this positive feedback, especially regarding the inferential power of our analytical approach.

Weaknesses:

The match between the broader conceptual background involving range expansion, urbanization, and sex-biased dispersal and learning, and the actual comparison of three urban populations along a range expansion gradient was somewhat confusing. The fact that three populations were compared along a range expansion gradient implies an expectation that they might differ because they are at very different points in a range expansion. Indeed, the predicted differences between males and females are largely couched in terms of population differences based on their 'location' along the range-expansion gradient. However, the fact that they are all urban areas suggests that one might not expect the populations to differ. In addition, the evolutionary model suggests that all animals, male or female, living in urban environments (that the authors suggest are stable but unpredictable) should exhibit high-risk sensitivity. Given that all grackles, male and female, in all populations, are both living in urban environments and likely come from an urban background, should males and females differ in their learning behavior? Clarification would be useful.

Thank you for highlighting a gap in clarity in our conceptual framework. To answer the Reviewer’s question—yes, even with this shared urban ‘history’, it seems plausible that males and females could differ in their learning. For example, irrespective of population membership, such sex differences could come about via differential reliance on learning strategies mediated by an interaction between grackles’ polygynous mating system and male-biased dispersal system, as we discuss in L254–265. Population membership might, in turn, differentially moderate the magnitude of any such sex-effect since an edge population, even though urban, could still pose novel challenges—for example, by requiring grackles to learn novel daily temporal foraging patterns such as when and where garbage is collected (grackles appear to track this food resource: Rodrigo et al. 2021 [DOI: 10.1101/2021.06.14.448443]). We will make sure to better introduce this important conceptual information in our revision.

Reinforcement learning mechanisms:

Although the authors' title, abstract, and conclusions emphasize the importance of variation in 'risk sensitivity', most readers in this field will very possibly misunderstand what this means biologically. Both the authors' use of the term 'risk sensitivity' and their statistical methods for measuring this concept have potential problems.

Please see our below responses concerning our risk-sensitivity term

First, most behavioral ecologists think of risk as predation risk which is not considered in this paper. Secondarily, some might think of risk as uncertainty. Here, as discussed in more detail below, the 'risk sensitivity' parameter basically influences how strongly an option's attractiveness affects the animal's choice of that option. They say that this is in line with foraging theory (Stephens and Krebs 2019) where sensitivity means seeking higher expected payoffs based on prior experience. To me, this sounds like 'reward sensitivity', but not what most think of as 'risk sensitivity'. This problem can be easily fixed by changing the name of the term.

We apologise for not clearly introducing the field of risk-sensitive foraging, which focuses on how animals evaluate and choose between distinct food options, and how such foraging decisions are influenced by pay-off variance i.e., risk associated with alternative foraging options (seminal reviews: Bateson 2002 [DOI: 10.1079/PNS2002181]; Kacelnik & Bateson 1996 [DOI: 10.1093/ICB/36.4.402]). We further apologise for not clearly explaining how our lambda parameter estimates such risk-sensitive foraging. To do so here, we need to consider our Bayesian reinforcement learning model in full. This model uses observed choice-behaviour during reinforcement learning to infer our phi (informationupdating) and lambda (risk-sensitivity) learning parameters. Thus, payoffs incurred through choice simultaneously influence estimation of each learning parameter—that is, in a sense, they are both sensitive to rewards. But phi and lambda differentially direct any reward sensitivity back on choicebehaviour due to their distinct definitions (we note this does not imply that the two cannot influence one another i.e., co-vary on the latent scale). Glossing over the mathematics, for phi, stronger reward sensitivity (bigger phi values) means faster internal updating about stimulus-reward pairings, which translates behaviourally into faster learning about ‘what to choose’. For lambda, stronger reward sensitivity (bigger lambda values) means stronger internal determinism about seeking the non-risk foraging option (i.e., the one with the higher expected payoffs based on prior experience), which translates behaviourally into less choice-option switching i.e., ‘playing it safe’. We hope this information, which we will incorporate into our revision, clarifies the rationale and mechanics of our reinforcement learning model, and why lamba measures risk-sensitivity.

In addition, however, the parameter does not measure sensitivity to rewards per se - rewards are not in equation 2. As noted above, instead, equation 2 addresses the sensitivity of choice to the attraction score which can be sensitive to rewards, though in complex ways depending on the updating parameter. Second, equations 1 and 2 involve one specific assumption about how sensitivity to rewards vs. to attraction influences the probability of choosing an option. In essence, the authors split the translation from rewards to behavioral choices into 2 steps. Step 1 is how strongly rewards influence an option's attractiveness and step 2 is how strongly attractiveness influences the actual choice to use that option. The equation for step 1 is linear whereas the equation for step 2 has an exponential component. Whether a relationship is linear or exponential can clearly have a major effect on how parameter values influence outcomes. Is there a justification for the form of these equations? The analyses suggest that the exponential component provides a better explanation than the linear component for the difference between males and females in the sequence of choices made by birds, but translating that to the concepts of information updating versus reward sensitivity is unclear. As noted above, the authors' equation for reward sensitivity does not actually include rewards explicitly, but instead only responds to rewards if the rewards influence attraction scores. The more strongly recent rewards drive an update of attraction scores, the more strongly they also influence food choices. While this is intuitively reasonable, I am skeptical about the authors' biological/cognitive conclusions that are couched in terms of words (updating rate and risk sensitivity) that readers will likely interpret as concepts that, in my view, do not actually concur with what the models and analyses address.

To answer the Reviewer’s question—yes, these equations are very much standard and the canonical way of analysing individual reinforcement learning (see: Ch. 15.2 in Computational Modeling of Cognition and Behavior by Farrell & Lewandowsky 2018 [DOI: 10.1017/CBO9781316272503]; McElreath et al. 2008 [DOI: 10.1098/rstb/2008/0131]; Reinforcement Learning by Sutton & Barto 2018). To provide a “justification for the form of these equations'', equation 1 describes a convex combination of previous values and recent payoffs. Latent values are updated as a linear combination of both factors, there is no simple linear mapping between payoffs and behaviour as suggested by the reviewer. Equation 2 describes the standard softmax link function. It converts a vector of real numbers (here latent values) into a simplex vector (i.e., a vector summing to 1) which represents the probabilities of different outcomes. Similar to the logit link in logistic regression, the softmax simply maps the model space of latent values onto the outcome space of choice probabilities which enter the categorial likelihood distribution. We can appreciate how we did not make this clear in our manuscript by not highlighting the standard nature of our analytical approach. We will do better in our revision. As far as what our reinforcement learning model measures, and how it relates cognition and behaviour, please see our previous response.

To emphasize, while the authors imply that their analyses separate the updating rate from 'risk sensitivity', both the 'updating parameter' and the 'risk sensitivity' parameter influence both the strength of updating and the sensitivity to reward payoffs in the sense of altering the tendency to prefer an option based on recent experience with payoffs. As noted in the previous paragraph, the main difference between the two parameters is whether they relate to behaviour linearly versus with an exponential component.

Please see our two earlier responses on the mechanics of our reinforcement learning model.

Overall, while the statistical analyses based on equations (1) and (2) seem to have identified something interesting about two steps underlying learning patterns, to maximize the valuable conceptual impact that these analyses have for the field, more thinking is required to better understand the biological meaning of how these two parameters relate to observed behaviours, and the 'risk sensitivity' parameter needs to be re-named.

Please see our earlier response to these suggestions.

Agent-based simulations:

The authors estimated two learning parameters based on the behaviour of real birds, and then ran simulations to see whether computer 'birds' that base their choices on those learning parameters return behaviours that, on average, mirror the behaviour of the real birds. This exercise is clearly circular. In old-style, statistical terms, I suppose this means that the R-square of the statistical model is good. A more insightful use of the simulations would be to identify situations where the simulation does not do as well in mirroring behaviour that it is designed to mirror.

Based on the Reviewer’s summary of agent-based forward simulation, we can see we did a poor job explaining the inferential value of this method—we apologise. Agent-based forward simulations are posterior predictions, and they provide insight into the implied model dynamics and overall usefulness of our reinforcement learning model. R-squared calculations are retrodictive, and they say nothing about the causal dynamics of a model. Specifically, agent-based forward simulation allows us to ask—what would a ‘new’ grackle ‘do’, given our reinforcement learning model parameter estimates? It is important to ask this question because, in parameterising our model, we may have overlooked a critical contributing mechanism to grackles’ reinforcement learning. Such an omission is invisible in the raw parameter estimates; it is only betrayed by the parameters in actu. Agent-based forward simulation is ‘designed’ to facilitate this call to action—not to mirror behavioural results. The simulation has no apriori ‘opinion’ about computer ‘birds’ behavioural outcomes; rather, it simply assigns these agents random phi and lambda draws (whilst maintaining their correlation structure), and tracks their reinforcement learning. The exercise only appears circular if no critical contributing mechanism(s) went overlooked—in this case computer ‘birds’ should behave similar to real birds. A disparate mapping between computer ‘birds’ and real birds, however, would mean more work is needed with respect to model parameterisation that captures the causal, mechanistic dynamics behind real birds’ reinforcement learning (for an example of this happening in the human reinforcement learning literature, see Deffner et al. 2020 [DOI: 10.1098/rsos.200734]). In sum, agent-based forward simulation does not access goodness-of-fit—we assessed the fit of our model apriori in our preregistration (https://osf.io/v3wxb)—but it does assess whether one did a comprehensive job of uncovering the mechanistic basis of target behaviour(s). We will work to make the above points on the insight afforded by agent-based forward simulation explicitly clear in our revision.

Reviewer #2 (Public Review):

Summary:

The study is titled "Leading an urban invasion: risk-sensitive learning is a winning strategy", and consists of three different parts. First, the authors analyse data on initial and reversal learning in Grackles confronted with a foraging task, derived from three populations labeled as "core", "middle" and "edge" in relation to the invasion front. The suggested difference between study populations does not surface, but the authors do find moderate support for a difference between male and female individuals. Secondly, the authors confirm that the proposed mechanism can actually generate patterns such as those observed in the Grackle data. In the third part, the authors present an evolutionary model, in which they show that learning strategies as observed in male Grackles do evolve in what they regard as conditions present in urban environments.

Strengths:

The manuscript's strength is that it combines real learning data collected across different populations of the Great-tailed grackle (Quiscalus mexicanus) with theoretical approaches to better understand the processes with which grackles learn and how such learning processes might be advantageous during range expansion. Furthermore, the authors also take sex into account revealing that males, the dispersing sex, show moderately better reversal learning through higher reward-payoff sensitivity. I also find it refreshing to see that the authors took the time to preregister their study to improve transparency, especially regarding data analysis.

Thank you—we are pleased to receive this positive evaluation, particularly concerning our efforts to improve scientific transparency via our study’s preregistration (https://osf.io/v3wxb).

Weaknesses:

One major weakness of this manuscript is the fact that the authors are working with quite low sample sizes when we look at the different populations of edge (11 males & 8 females), middle (4 males & 4 females), and core (17 males & 5 females) expansion range. Although I think that when all populations are pooled together, the sample size is sufficient to answer the questions regarding sex differences in learning performance and which learning processes might be used by grackles but insufficient when taking the different populations into account.

In Bayesian statistics, there is no strict lower limit of required sample size as the inferences do not rely on asymptotic assumptions. With inferences remaining valid in principle, low sample size will of course be reflected in rather uncertain posterior estimates. We note all of our multilevel models use partial pooling on individuals (the random-effects structure), which is a regularisation technique that generally reduces the inference constraint imposed by a low sample size (see Ch. 13 in Statistical Rethinking by Richard McElreath [PDF: https://bit.ly/3RXCy8c]). We further note that, in our study preregistration (https://osf.io/v3wxb), we formally tested our reinforcement learning model for different effect sizes of sex on learning for both target parameters (phi and lambda) across populations, using a similarly modest N (edge: 10 M, 5 F; middle: 22 M, 5 F ; core: 3 M, 4 F) to our actual final N, that we anticipated to be our final N at that time. This apriori analysis shows our reinforcement learning model: (i) detects sex differences in phi values >= 0.03 and lambda values >= 1; and (ii) infers a null effect for phi values < 0.03 and lambda values < 1 i.e., very weak simulated sex differences (see Figure 4 in https://osf.io/v3wxb). Thus, both of these points together highlight how our reinforcement learning model allows us to say that across-population null results are not just due to small sample size. Nevertheless the Reviewer is not wrong to wonder whether a bigger N might change our population-level results (it might; so might much-needed population replicates—see L270), but our Bayesian models still allow us to learn a lot from our current data.

Another weakness of this manuscript is that it does not set up the background well in the introduction. Firstly, are grackles urban dwellers in their natural range and expand by colonising urban habitats because they are adapted to it? The introduction also fails to mention why urban habitats are special and why we expect them to be more challenging for animals to inhabit. If we consider that one of their main questions is related to how learning processes might help individuals deal with a challenging urban habitat, then this should be properly introduced.

In L53–56 we introduce that the estimated historical niche of grackles is urban environments, and that shifts in habitat breadth—e.g., moving into more arid, agricultural environments—is the estimated driver of their rapid North American colonisation. We will work towards flushing out how urban-imposed challenges faced by grackles, such as the wildlife management efforts introduced in L64–65, may apply to animals inhabiting urban environments more broadly.

Also, the authors provide a single example of how learning can differ between populations from more urban and more natural habitats. The authors also label the urban dwellers as the invaders, which might be the case for grackles but is not necessarily true for other species, such as the Indian rock agama in the example which are native to the area of study. Also, the authors need to be aware that only male lizards were tested in this study. I suggest being a bit more clear about what has been found across different studies looking at: (1) differences across individuals from invasive and native populations of invasive species and (2) differences across individuals from natural and urban populations.

We apologise for not specifying that the review we cite in L42 by Lee & Thornton (2021) covers additional studies on cognition in both urban invasive species as well as urban-dwellers versus nonurban counterparts—we will remedy this omission in our revision. We will also revise our labelling of the lizard species. We are aware only male lizards were tested but this information is not relevant to substantiating our use of this study; that is, to highlight that learning can differ between urban-dwelling and non-urban counterparts. Finally, the Reviewer’s general suggestion is a good one—we will work to add this biological clarity to our revision.

Finally, the introduction is very much written with regard to the interaction between learning and dispersal, i.e. the 'invasion front' theme. The authors lay out four predictions, the most important of which is No. 4: "Such sex-mediated differences in learning to be more pronounced in grackles living at the edge, rather than the intermediate and/or core region of their range." The authors, however, never return to this prediction, at least not in a transparent way that clearly pronounces this pattern not being found. The model looking at the evolution of risk-sensitive learning in urban environments is based on the assumption that urban and natural environments "differ along two key ecological axes: environmental stability 𝑢 (How often does optimal behaviour change?) and environmental stochasticity 𝑠 (How often does optimal behaviour fail to pay off?). Urban environments are generally characterised as both stable (lower 𝑢) and stochastic (higher 𝑠)". Even though it is generally assumed that urban environments differ from natural environments the authors' assumption is just one way of looking at the differences which have generally not been confirmed and are highly debated. Additionally, it is not clear how this result relates to the rest of the paper: The three populations are distinguished according to their relation to the invasion front, not with respect to a gradient of urbanization, and further do not show a meaningful difference in learning behaviour possibly due to low sample sizes as mentioned above.

Thank you for highlighting a gap in our reporting clarity. We will take care in our revision to transparently report our null result regarding our fourth prediction; more specifically, that we did not detect meaningful behavioural or mechanistic population-level differences in grackles’ learning. Regarding our evolutionary model, we agree with the Reviewer that this analysis is only one way of looking at the interaction between learning phenotype and apparent urban environmental characteristics. Indeed, in L282–288 we state: “Admittedly, our evolutionary model is not a complete representation of urban ecology dynamics. Relevant factors—e.g., spatial dynamics and realistic life histories—are missed out. These omissions are tactical ones. Our evolutionary model solely focuses on the response of reinforcement learning parameters to two core urban-like (or not) environmental statistics, providing a baseline for future study to build on”. But we can see now that ‘core’ is too strong a word, and instead ‘supposed’, ‘purported’ or ‘theorised’ would be more accurate—we will revise our wording. As far as how our evolutionary results relate to the rest of the paper, these results suggest successful urban living should favour risk-sensitive learning, and our other analyses in our paper reveal male grackles—the dispersing sex in this historically urban-dwelling and currently urban-invading species—show pronounced risk-sensitive learning, so it appears risk-sensitive learning is a winning strategy for urban-invading male grackles and urban-invasion leaders more generally (we note, of course, other factors undoubtedly contribute to grackles’ urban invasion success, as discussed in ‘Ideas and speculation’; see also our first response to R1). We will work to make these links clearer in our revision. Finally, please see our above response on the inferential sufficiency of our sample size.

In conclusion, the manuscript was well written and for the most part easy to follow. The format of eLife having the results before the methods makes it a bit harder to follow because the reader is not fully aware of the methods at the time the results are presented. It would, therefore, be important to more clearly delineate the different parts and purposes. Is this article about the interaction between urban invasion, dispersal, and learning? Or about the correct identification of learning mechanisms? Or about how learning mechanisms evolve in urban and natural environments? Maybe this article can harbor all three, but the borders need to be clear. The authors need to be transparent about what has and especially what has not been found, and be careful to not overstate their case.

Thank you, we are pleased to read that the Reviewer found our manuscript to be generally digestible. In our revision, we will work to add further clarity, and to temper our tone.

Author Response

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

Reviewer #1 (Public Review):

This manuscript tried to answer a long-standing question in an important research topic. I read it with great interest. The quality of the science is high, and the text is clearly written. The conclusion is exciting. However, I feel that the phenotype of the transgenic line may be explained by an alternative idea. At least, the results should be more carefully discussed.

We thank the reviewer #1 for his/her comments that helped to improve the manuscript. We have incorporated changes to reflect the suggestions provided by the reviewer. Here is a point-by-point response to the reviewer's specific and other minor comments.

Specific comments:

1) Stability or activity (Fv/Fm) was not affected in PSII with the W14F mutation in D1. If W14F really represents the status of PSII with oxidized D1, what is the reason for the degradation of almost normal D1?

In this study, we used W14F mutation to mimic Trp-14 oxidation. The W14F mutant did not affect the stability and photosynthetic activity under normal growth conditions. However, the W14F mutant showed increased D1 degradation and reduced Fv/Fm values under high light. These results suggested that the W14F mutant has almost normal D1 protein stability under growth light conditions, as pointed out by the reviewer.

However, it should be noted that D1 protein in the W14F strain rapidly degraded under high light. In the discussion part, we mentioned the possibility that other OPTMs may have additive effects on D1 degradation. Synergistic effects such as different amino acid oxidations may cause D1 degradation, and among those oxidative damages, W14 oxidation would be a key signal for D1 degradation by FtsH.

2) To focus on the PSII in which W14 is oxidized, this research depends on the W14F mutant lines. It is critical how exactly the W-to-F substitution mimics the oxidized W. The authors tried to show it in Figure 5. Because of the technical difficulty, it may be unfair to request more evidence. But the paper would be more convincing with the results directly monitoring the oxidized D1 to be recognized by FtsH.

We agree that confirming the direct interaction of oxidized D1 protein with FtsH provides more robust evidence. However, since FtsH progressively degrades the trapped substrate, it would be quite a challenging attempt to capture that moment. There are also technical limitations to obtaining sufficient substrate using Co-IP to compare its oxidation state. We included your suggested point in the discussion part. Thank you for your valuable suggestion.

3) Figure 3. If the F14 mimics the oxidized W14 and is sensed by FtsH, I would expect the degradation of D1 even under the growth light. The actual result suggests that W14F mutation partially modifies the structure of D1 under high light and this structural modification of D1 is sensed by FtsH. Namely, high light may induce another event which is recognized by FtsH. The W14F is just an enhancer.

Our results indicated that W14 oxidation is one of the keys to D1 degradation. On the other hand, we agree with the possibility that the reviewer points out. There is the possibility that factors other than W14 may act synergistically to promote D1 degradation. High light triggered more D1 degradation in W14F, suggesting that unknown factor(s) may be required for D1 degradation, e.g., oxidative modification at other sites and/or conformational changes of PSII under the high light. However, the current data that we have cannot reveal. We have incorporated the reviewer's comment and discussed it in the discussion part.

Reviewer #2 (Public Review):

In their manuscript, Kato et al investigate a key aspect of membrane protein quality control in plant photosynthesis. They study the turnover of plant photosystem II (PSII), a hetero-oligomeric membrane protein complex that undertakes the crucial light-driven water oxidation reaction in photosynthesis. The formidable water oxidation reaction makes PSII prone to photooxidative damage. PSII repair cycle is a protein repair pathway that replaces the photodamaged reaction center protein D1 with a new copy. The manuscript addresses an important question in PSII repair cycle - how is the damaged D1 protein recognized and selectively degraded by the membrane-bound ATP-dependent zinc metalloprotease FtsH in a processive manner? The authors show that oxidative post-translational modification (OPTM) of the D1 N-terminus is likely critical for the proper recognition and degradation of the damaged D1 by FtsH. Authors use a wide range of approaches and techniques to test their hypothesis that the singlet oxygen (1O2)-mediated oxidation of tryptophan 14 (W14) residue of D1 to N-formylkynurenine (NFK) facilitates the selective degradation of damaged D1. Overall, the authors propose an interesting new hypothesis for D1 degradation and their hypothesis is supported by most of the experimental data provided. The study certainly addresses an elusive aspect of PSII turnover and the data provided go some way in explaining the light-induced D1 turnover. However, some of the data are correlative and do not provide mechanistic insight. A rigorous demonstration of OPTM as a marker for D1 degradation is yet to be made in my opinion. Some strengths and weaknesses of the study are summarized below:

We thank reviewer #2 for his/her comments that helped to improve the manuscript. We have incorporated changes to reflect the suggestions pointed out as weaknesses by reviewer #2. Other minor comments were also answered in a point-by-point response.

Strengths:

1) In support of their hypothesis, the authors find that FtsH mutants of Arabidopsis have increased OPTM, especially the formation of NFK at multiple Trp residues of D1 including the W14; a site-directed mutation of W14 to phenylalanine (W14F), mimicking NFK, results in accelerated D1 degradation in Chlamydomonas; accelerated D1 degradation of W14F mutant is mitigated in an ftsH1 mutant background of Chlamydomonas; and that the W14F mutation augmented the interaction between FtsH and the D1 substrate.

2) Authors raise an intriguing possibility that the OPTM disrupts the hydrogen bonding between W14 residue of D1 and the serine 25 (S25) of PsbI. According to the authors, this leads to an increased fluctuation of the D1 N-terminal tail, and as a consequence, recognition and binding of the photodamaged D1 by the protease. This is an interesting hypothesis and the authors provide some molecular dynamics simulation data in support of this. If this hypothesis is further supported, it represents a significant advancement.

3) The interdisciplinary experimental approach is certainly a strength of the study. The authors have successfully combined mass spectrometric analysis with several biochemical assays and molecular dynamics simulation. These, together with the generation of transplastomic algal cell lines, have enabled a clear test of the role of Trp oxidation in selective D1 degradation.

4) Trp oxidative modification as a degradation signal has precedent in chloroplasts. The authors cite the case of 1O2 sensor protein EXECUTER 1 (EX1), whose degradation by FtsH2, the same protease that degrades D1, requires prior oxidation of a Trp residue. The earlier observation of an attenuated degradation of a truncated D1 protein lacking the N-terminal tail is also consistent with authors' suggestion of the importance of the D1 N-terminus recognition by FtsH. It is also noteworthy that in light of the current study, D1 phosphorylation is unlikely to be a marker for degradation as posited by earlier studies.

Weaknesses:

1) The study lacks some data that would have made the conclusions more rigorous and convincing. It is unclear why the level of Trp oxidation was not analyzed in the Chlamydomonas ftsH 1-1 mutant as done for the var 2 mutant. Increased oxidation of W14 OPTM in Chlamydomonas ftsH 1-1 is a key prediction of the hypothesis.

We thank the reviewer for this valuable comment. We agree with the reviewer that the analysis of oxidized Trp level will reinforce the importance of Trp oxidation in the N-terminal of D1. In our preliminary experiment, we observed a trend toward increase of the kynurenine in Trp-14 in Chlamydomonas ftsH1-1 strain. However, we found large errors, and we could not conclude that this trend is significant. A possible reason for the large error was that the signal intensity of oxidized Trp was insufficient for quantification in a series of Chlamydomonas experiment. In addition, the fact that the amount of D1 in each culture was not stable also might be one reason. On the other hand, we keep note of a previous result that more fragmentation of D1 protein was observed in the Chlamydomonas ftsH1-1 mutant compared to that in Arabidopsis (Malnoë et al., Plant Cell 2014). This result suggests that an alternative D1 degradation pathway involving other proteases is more active in the Chlamydomonas ftsH1-1 mutant than in Arabidopsis var2 mutant. Furthermore, the Chlamydomonas ftsH1-1 mutant, caused by an amino acid substitution, still has a significant FtsH1/FtsH2 heterohexamer, and the level of FtsH1 and FtsH2 proteins increases significantly under high light irradiation. This is a significant difference from the Arabidopsis var2 mutant lacking FtsH2 subunit and showed reduced protein accumulation. These factors may explain to the lower detection levels of oxidized Trp in Chlamydomonas. We believe that improved sensitivity for detection of oxidized Trp peptides and more sophisticated experimental systems could solve this issue in the future.

It is also unclear to me what is the rationale for showing D1-FtsH interaction data only for the double mutant but not for the single mutant (W14F).

We thank the reviewer for the comment. As suggested by the reviewer, the analysis of the mutant crossing ftsH and W14F single mutation will provide more convincing evidence. Fig.3 showed that the photosensitivity in both W14F and W14FW317F was caused by the enhanced D1 degradation observed, which was due to the W14F mutation. Therefore, we crossed the ftsH mutant with W14FW317F, which has a more severe phenotype, to confirm whether FtsH is involved in this D1 degradation.

Why is the FtsH pulldown of D2 not statistically significant (p value = {less than or equal to}0.1). Wouldn't one expect FtsH pulls down the RC47 complex containing D1, D2, and RC47. Probing the RC47 level would have been useful in settling this.

For the immunoblot result of D2 and its statistical analysis, we answered in the following comment; No.2 in the reviewer's comment in Recommendations For The Authors.

We agree with the reviewer's suggestion that further immunoblot analysis for CP47 protein would help our understanding of FtsH and RC47 interaction. Indeed, we attempted the immunoblot analysis of CP47 after the FtsH Co-IP experiment. However, the detection of CP43 protein was not sensitive enough. This reason may be due to the lower titer of the CP47 antibody compared to the D1 and D2 antibodies.

A key proposition of the authors' is that the hydrogen bonding between D1 W14 and S25 of PsbI is disrupted by the oxidative modification of W14. Can this hypothesis be further tested by replacing the S25 of PsbI with Ala, for example?

It is an interesting question whether amino acid substitution in PsbI-S25 affects the stability of D1-N-term and its degradation by FtsH. We would like to analyze the possibility in the future. We thank the reviewer for this helpful suggestion.

2) Although most of the work described is in vivo analysis, which is desirable, some in vitro degradation assays would have strengthened the conclusions. An in vitro degradation assay using the recombinant FtsH and a synthetic peptide encompassing D1 N-terminus with and without OPTM will test the enhanced D1 degradation that the authors predict. This will also help to discern the possibility that whether CP43 detachment alone is sufficient for D1 degradation as suggested for cyanobacteria.

In vitro experimental systems are interesting. However, FtsH is known to function as a hexamer, which has not yet been successfully reconstituted in vitro. Therefore, it would not be easy to perform an in vitro experimental system using the N-terminal synthetic peptide of D1 as a substrate. Thank you for your valuable suggestions.

3) The rationale for analyzing a single oxidative modification (W14) as a D1 degradation signal is unclear. D1 N-terminus is modified at multiple sites. Please see Mckenzie and Puthiyaveetil, bioRxiv May 04 2023. Also, why is modification by only 1O2 considered while superoxide and hydroxide radicals can equally damage D1?

We agree with the possibility that oxidative modifications in other amino acids are also involved in the D1 degradation, as pointed out by the reviewer. We also thank the reviewer for pointing us to the interesting article of Mckenzie and Puthiyaveetil et al. that showed additional oxidations occurred in the D1-Nterminus, which we had yet to be aware of when we submitted our manuscript. It will be interesting to see how these amino acid oxidations work with W14 oxidation on D1 degradation in the future. The oxidation of Trp by 1O2 can serve as a substrate for FtsH, as in the case of EX1, so we focused on the analysis of Trp oxidation. Single oxygen is believed to be the potential reactive species of Trp oxidation. However, the detected oxidative modifications in this study were not exactly sure depended on singlet oxygen. Thus, we changed several sentences that mention tryptophan oxidation by single oxygen.

4) The D1 degradation assay seems not repeatable for the W14F mutant. High light minus CAM results in Fig. 3 shows a statistically significant decrease in D1 levels for W14F at multiple time points but the same assay in Fig. 4a does not produce a statistically significant decrease at 90 min of incubation. Why is this? Accelerated D1 degradation in the Phe mutant under high light is key evidence that the authors cite in support of their hypothesis.

In Fig. 4a, the p-value comparing the D1 level at 90 min between control and W14F was 0.1075. This value is slightly larger than 0.1. The result that one of the control experiments showed a decrease in D1 level relative to 0 h might cause this value. Given that the D1 level of the remaining three of the four replicates was unchanged in the control experiments, it can be considered an outlier. We believe the results do not affect our hypothesis that the earlier D1 degradation is occurred in W14F.

5) The description of results at times is not nuanced enough, for e.g. lines 116-117 state "The oxidation levels in Trp-14 and Trp-314 increased 1.8-fold and 1.4-fold in var2 compared to the wild type, respectively (Fig. 1c)" while an inspection of the figure reveals that modification at W314 is significant only for NFK and not for KYN and OIA.

In this sentence, we described the result that is compared with the oxidized peptide levels calculated from all Trp-oxidized derivatives. However, as pointed out by the reviewer, it was not correct to explain the result of Fig.1C. We corrected the sentence following the reviewer's suggestion as below;“The levels of Trp-oxidized derivatives, OIA, NFK, and KYN in Trp-14 and the level of KYN in Trp-314 were significantly increased in var2 compared to the wild type, respectively (Fig. 1c). "

Likewise, the authors write that CP43 mutant W353F has no growth phenotype under high light but Figure S6 reveals otherwise. The slow growth of this mutant is in line with the earlier observation made by Anderson et al., 2002.

As pointed out by the reviewer, the growth of W353F seems to be a little slow under HL. We have changed our description of the result part. However, we still conclude that CP43 had little impact on the PSII repair, because the impaired growth in W353F is not as severe as those in W14F and W14F/W317F under HL

In lines 162-163, the authors talk about unchanged electron transport in some site-directed mutants and cite Fig. 2c but this figure only shows chl fluorescence trace and nothing else.

We agreed with the reviewer's suggestion and changed the sentence. In this study, we did not perform detailed photosynthetic analysis. Based on the analysis of phototrophic growth, oxygen-evolving activity, and Chl fluorescence, we concluded that overall photosynthetic activity was not a significant difference in the mutants.

6) The authors rightly discuss an alternate hypothesis that the simple disassembly of the monomeric core into RC47 and CP43 alone may be sufficient for selective D1 degradation as in cyanobacteria. This hypothesis cannot yet be ruled out completely given the lack of some in vitro degradation data as mentioned in point 2. Oxidative protein modification indeed drives the disassembly of the monomeric core (Mckenzie and Puthiyaveetil, bioRxiv May 04 2023).

Thanks for your suggestion. We added a discussion of PSII disassembly by ROS-induced oxidation to the discussion part, and the reference is added.

Reviewer #3 (Public Review):

Light energy drives photosynthesis. However, excessive light can damage (i.e., photo-damage) and thus inactivate the photosynthetic process. A major target site of photo-damage is photosystem II (PSII). In particular, one component of PSII, the reaction center protein, D1, is very suspectable to photo-damage, however, this protein is maintained efficiently by an elaborate multi-step PSII-D1 turnover/repair cycle. Two proteases, FtsH and Deg, are known to contribute to this process, respectively, by efficient degradation of photo-damaged D1 protein processively and endoproteolytically. In this manuscript, Kato et al., propose an additional step (an early step) in the D1 degradation/repair pathway. They propose that "Tryptophan oxidation" at the N-terminus of D1 may be one of the key oxidations in the PSII repair, leading to processive degradation of D1 by FtsH. Both, their data and arguments are very compelling.

The D1 protein repair/degradation pathway in its simplest form can be defined essentially by five steps: (1) migration of damaged PSII core complex to the stroma thylakoid, (2) partial PSII disassembly of the PSII core monomer, (3) access of protease degrading damaged D1, (4) concomitant D1 synthesis, and (5) reassembly of PSII into grana thylakoid. An enormous amount of work has already been done to define and characterize these various steps. Kato et al., in this manuscript, are proposing a very early yet novel critical step in D1 protein turnover in which Tryptophan(Trp) oxidation in PSII core proteins influences D1 degradation mediated by FtsH.

Using a variety of approaches, such as mass-spectrometry (Table 1), site-directed mutagenesis (Figures 2-4), D1 degradation assays (Figures 3, and 4), and simulation modeling (Figure 5), Kato et al., provide both strong evidence and reasonable arguments that an N-terminal Trp oxidation may be likely to be a 'key' oxidative post-translational modification (OPTM) that is involved in triggering D1 degradation and thus activating the PSII repair pathway. Consequently, from their accumulated data, the authors propose a scenario in which the unraveling of the N-terminal of the D1 protein facilitated by Trp oxidation plays a critical 'recognition' role in alerting the plant that the D1 protein is photo-damaged and thus to kick start the processive degradation pathway initiated possibly by FtsH. Coincidently, Forsman and Eaton-Rye (Biochemistry 2021, 60, 1, 53-63), while working with the thermophilic cyanobacterium, Thermosynechococcus vulcanus, showed that when the N-terminal DE-loop of the D1 protein is photo-damaged that occurs which may serve as a signal for PSII to undergo repair following photodamage. While the activation of the processive degradation pathways in Chlamydomonas versus Thermosynechococcus vulcanus have significant mechanistic differences, it's interesting to note and speculate that the stability of the N-terminal of their respective D1 proteins seems to play a critical role in 'signaling' the PSII repair system to be activated and initiate repair. But it's complicated. For instance, significant Trp oxidation also occurs on the lumen side of other PSII subunits which may also play a significant role in activating the repair processes as well. Indeed, Kato et al.,( Photosynthesis Research volume 126, pages 409-416 (2015)) proposed a two-step model whereby the primary event is disruption of a Mn-cluster in PSII on the lumen side.

A secondary event is damage to D1 caused by energy that is absorbed by chlorophyll. But models adapt, change, and get updated. And the data provided by Kato et al., in this manuscript, gives us a unique glimpse/snapshot into the importance of the stability of the N-terminal during photo-damage and its role in D1-turnover. For instance, the author's use site-directed mutagenesis of Trp residues undergoing OPTM in the D1 protein coupled with their D1 degradation assays (Figure 3 and 4), provides evidence that Trp oxidation (in particular the oxidation of Trp14) in coordination with FtsH results in the degradation of D1 protein. Indeed, their D1 degradation assays coupled with the use of a ftsh mutant provide further significant support that Trp14 oxidation and FtsH activity are strongly linked. But for FstH to degrade D1 protein it needs to gain access to photo-damaged D1. FtsH access to D1 is achieved by having CP43 partially dissociate from the PSII complex. Hence, the authors also addressed the possibility that Trp oxidation may also play a role in CP43 disassembly from the PSII complex thereby giving FtsH access to D1. Using a site-directed mutagenesis approach, they showed that Trp oxidation in CP43 appeared to have little impact on the PSII repair (Supplemental Figure S6). This result shows that D1-Trp14 oxidation appears to be playing a role in D1 turnover that occurs after CP43 disassembly from the PSII complex. Alternatively, the authors cannot exclude the possibility that D1-Trp14 oxidation in some way facilitates CP43 dissociation. Further investigation is needed on this point. However, D1-Trp14 oxidation is causing an internal disruption of the D1 protein possibly at the N-terminus of the protein. Consequently, the role of Trp14 oxidation in disrupting the stability of the N-terminal domain of the D1 protein was analyzed computationally. Using a molecular dynamics approach (Figure 5), the authors attempted to create a mechanistic model to explain why when D1 protein Trp14 undergoes oxidation the N-terminal domain of D1protein becomes unraveled. Specifically, the authors propose that the interaction between D1 protein Trp14 with PsbI Ser25 becomes disrupted upon oxidation of Trp14. Consequently, the authors concluded from their molecular dynamics simulation analysis that " the increased fluctuation of the first α-helix of D1 would give a chance to recognize the photo-damaged D1 by FtsH protease". Hence, the author's experimental and computational approaches employed here develop a compelling early-stage repair model that integrates 1) Trp14 oxidation, 2) FtsH activation and 3) D1- turnover being initiated at its N-terminal domain. However, a word of caution should be emphasized here. This model is just a snapshot of the very early stages of the D1 protein turnover process. The data presented here gives us just a small glimpse into the unique relationship between Trp oxidation of the D1 protein which may trigger significant N-terminal structural changes of the D1 protein that both signals and provides an opportunity for FstH to begin protease digestion of the D1 protein.

However, the authors go to great lengths in their discussion section to not overstate solely the role of Trp14 oxidation in the complicated process of D1 turnover. The authors certainly recognize that there are a lot of moving parts involved in D1 turnover. And while Trp14 oxidation is the major focus of this paper, the authors show in Supplemental Fig S4 the structural positions of various additional oxidized Trp residues in the Thermosynecoccocus vulcans PSII core proteins. Indeed, this figure shows that the majority of oxidized Trps are located on the luminal side of PSII complex clustered around the oxygen-evolving complex. So, while oxidized Trp14 may be involved in the early stages of D1 turnover certainly oxidized Trps on the lumen side are also more than likely playing a role in D1 turnover as well. To untangle this complex process will require additional research.

Nevertheless, identifying and characterizing the role of oxidative modification of tryptophan (Trp) residues, in particular, Trp14, in the PSII core provides another critical step in an already intricate multi-step process of D1 protein turnover during photo-damage.

We thank reviewer #3 for all the helpful comments and their supportive review of the manuscript.

We thank the reviewer for raising this interesting study that ROS might disrupt the interaction between the PsbT and D1 in Thermosynechococcus vulcanus. The stroma-exposed DE-loop of D1 is one of the possible cleavage sites by Deg protease. Because the D1 cleavage by Deg facilitates the effective D1 degradation by FtsH under high-light conditions, it is interesting to elucidate Deg and FtsH cooperative D1 degradation further. We added this discussion in the manuscript. Other minor comments were also answered in a point-by-point response.

Reviewer #1 (Recommendations For The Authors):

Other minor points

4) L227. How do you eliminate the possibility of reduced stability under high light?

D1 synthesis under HL as pointed out by the reviewer was not tested in this study. Therefore, we can not rule out the possibility of a reduced D1 synthesis rate under HL in the mutant. However, the rate of D1 turnover(coordinated degradation and synthesis) is increased under HL. Since the pulse-labeling experiment is affected D1 degradation as well as D1 synthesis, even if there is a difference in the rate of D1 synthesis under HL, we can not clearly distinguish whether the cause of reduced labeling is the increased D1 degradation seen in the W14F mutant or the delay in D1 synthesis. We thank the reviewer for this valuable comment.

5) Ls25-26. It would be quite rare that P680 directly absorbs light energy.

We changed the sentence.

6) L28. intrinsic antenna? Is this commonly used? core antenna?

Corrected to “core antenna”

7) Ls4143. Because the process is described as step iii), it is curious to mention it again as other critical steps.

We removed the sentence.

8) L75. Is it correct? Do you mean damage is caused by inhibition?

We changed the sentence to “…the disorder of photosynthesis…”

9) Figure 1c. +4, +16 and +32 should be explained in the legend.

We added the explanation in the legend.

10) Supplementary Figures S1 and S2. Title. Is it true that oxidation depends on singlet oxygen? This is a question. If it is not experimentally proved, modify the expression.

In general, singlet oxygen (1O2) is believed to contribute in vivo oxidation of Trp. However, as suggested, these detected oxidative modifications were not exactly sure depends on singlet oxygen. Thus, we changed the title of Fig S1 and S2.

11) Figure 3. Correct errors in + or - in the Figure.

Corrected

12) L328. Cyc > Cys.

Corrected

Reviewer #2 (Recommendations For The Authors):

1) A few suggestions on typos and style:

• Lines 2-3, please rephrase the sentence. The meaning is unclear.

rephased the sentence to “Photosynthesis is one of the most …”

• Lines 28-29, "Despite its orchestrated coordination...". Tautology.

We changed the sentence.

• Line 31, "...one, known as the PSII repair...". Please rewrite.

We followed the reviewer suggestion and changed the sentence to “…synthesized one in the PSII repair.”

• Line 49, "Their family proteins...". Rephrase.

Rephrased the words.

• Lines 64-66, please rewrite. I am not sure what the authors imply here. Are they talking about FtsH turnover or regulation of FtsH at the protein or gene level?

FtsH itself is also degraded under high-light stress. To compensate for this, ftsH gene expression is upregulated and contributes to the proper FtsH level in thylakoid membranes. We rewrote the sentence as follows “increased turnover of FtsH is crucial for their function under high-light stress. That is compensated by upregulated FtsH gene expression”.

• Line 68, "...to dislocate their substrates..."

We changed the sentence to “to pull their substrates and push them into the protease chamber by ATPase activity”

• Line 86, N-formylkymurenine => N-formylkynurenine

Corrected

• Lines 111-112, "Consistent with previous results...". Please specify which studies are being referred to and cite them if relevant.

We added references.

• Line 114, "...in extracts Arabidopsis..." => "...in extracts of Arabidopsis...".

Corrected

• Line 171, "influences in high-light sensitivity." Please rephrase.

We rephrased the sentence.

• Line 192, Fv/Fm. "v" and "m" should be subscripts.

Corrected

• Line 210, "...encounters...". Unclear meaning.

We rephrased the sentence.

• Line 358, hyphen usage. "fine-tuned". This sentence should be rewritten to make the role of phosphorylation clear. "Fine-tuning" is vague.

We changed the sentence to “…spatiotemporal regulation of D1 degradation”

• Fig. 6 legend, luminal => lumenal

Changed to luminal

2) The statistical notation used for some results is confusing. In Fig. 6b, "*" stands for p = {less than or equal to}0.1 while in fig. 4 it denotes p = {less than or equal to}0.05. If this is not a typo, this usage deviates from the standard one. How is a D2 change in Fig. 6b significant given its p value of {less than or equal to}0.1? The Fig. 6b key for D2 does not correspond with the histogram pattern.

Thank you for your comments and suggestions. The asterisk in the Figure 6b is not a typo. We revised p value sign for less than 0.05 with a single asterisk to avoid confusion. While the case of p value in less than 0.1, we applied section sign “§” instead of the single asterisk sign to avoid confusion. Generally accepted p value to indicate statistically difference is less than 0.05. We found that D1 was p = 0.03322 and D2 was p = 0.07418. As we suspect these p value differences, the results for D2 protein detection were somewhat fluctuating while not in D1 protein detection as you commented. Still the reason of the fluctuating result of D2 signal intensity is not clear yet, we found the p value was between 0.05 and 0.10. We also rewrite the description in the corresponding result part.

3) There are no error bars in Fig. 5d while the error bars in Fig. 5e show that there are no significant differences between Cβ distances of W14F and W14ox with WT contrary to the authors' assertion in the text (lines 254-255).

The reason that there are no error bars in Fig. 5d. is because the fluctuation value in Fig. 5d was calculated from the entire trajectory (i.e., all snapshots) of the MD simulation. In contrast, the Cβ-Cβ distance value can be obtained at each individual snapshot of the simulation. Thus, Fig. 5e shows the averaged distances with the standard deviations (the error bars) over all these snapshots. To prevent any confusion for the reader, we have explicitly described “averaged Cβ-Cβ distance” and added an explanation of the error bars in the caption of Fig. 5e. It is important to note that our focus in the text (lines 254-255) was not on comparing the Cβ-Cβ distance of W14F with that of W14ox but the distance of W14F or W14ox with that of WT.

4) Figure 3 legends and figure labels do not correspond. Fig. 3b should be labeled as High light - Chloramphenicol and likewise, fig 3c should read growth light + Chloramphenicol to be consistent with the legend.

Corrected

5) How are OPTM levels of D1 Trp residues normalized? Is it against unmodified peptides or total proteins?

Oxidation levels of three oxidative variants of Trp in Trp14 and Trp317 containing peptides were obtained by label-free MS analysis. Fig.1 shows the intensity values of oxidized variants of Trp14 and Trp317. In this analysis, the levels of unoxidized peptides were not significantly changed between var2 and WT.

6) Fig. 1a cartoon might need work. It looks like the oxygen atom in OIA is misplaced.

Corrected

Reviewer #3 (Recommendations For The Authors):

In regard to Table 1, the sequence of the mass spectra fragment listed for Trp14 (i.e., ENSSL(W)AR ) in Table 1 is different from the sequence of the mass spectra fragment of Trp14 shown in Supplemental Figure S1 (i.e., ESESLWGR). Likewise, the sequence of the mass spectra fragment listed for Trp317 (i.e., VLNT(W)ADIINR ) in Table 1 is different from the sequence of the mass spectra fragment of Trp14 shown in Supplemental Figure S2 (i.e., VINTWADIINR). This discrepancy, I think can be simply explained.

Table 1 shows the newly detected peptide of Trp oxidation in PSII core protein in Chlamydomonas. On the other hand, Figures S1 and S2 are the results of MS analysis used for the level of Trp oxidation analysis in Arabidopsis var2 mutant, as shown in Fig. 1C. To avoid confusion, we added in the supplemental figure title that it was detected in Arabidopsis.

Labeling: In Figure 3, the figure legend states that b, high-light in the absence of CAM; but panel b, shows +CAM conditions. I think this labeling is incorrect and needs to be -CAM. Likewise, the figure legend states that c, growth-light in the presence of CAM. I think this labeling is incorrect and needs to be +CAM.

Corrected

This reviewer has a few comments/suggestions on the presentation of the sequence alignments showing the various positions of oxidized Trps within the D1(Figure 1), D2 and CP43 (Supplemental Figure S3) and CP47 (Supplemental Figure S3):

The authors should consider highlighting in red all the various Trps shown in Table 1 with the corresponding alignments shown in Figure 1 for D1 protein and corresponding alignments in Supplemental Figure S3 (for D2 and CP43) and Supplemental Figure S3 continued (For CP47). Highlighting the locations of oxidized Trps across various species is very informative but as presented here the red labeling somewhat is haphazard, confusing and thus these figures lose some of their impact factor. For instance, in Supplementary Fig. S4, the reader can visualize the structural positions of oxidized Trp residues in the Thermosynecoccocus vulcanus PSII core proteins. When one then looks at the various alignments presented by the authors, one can see that other species have a similar arrangement of oxidized Trp residues as well. Consequently, when you now collectively look at the data presented in Table 1, Figure 1, Supplemental Figure S3 and Supplemental Figure S4, a picture emerges that illustrates how common the phenomenon of overall Trp oxidation is and more specifically how oxidized Trp14 across species is playing a similar role in possibly activating D1 turnover. I think these Figures, if presented in a more comprehensive and unified fashion, will really add to the paper.

Thank you for your suggestion. In this study, we tried to show the identified oxidized Trp by the MS-MS analysis, the residue conservation in the sequences, and its position in the structure. Since we have to show a lot of information, combining them into one figure is difficult. We hope you understand the reason for this.

Author Response

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

We are grateful for the helpful comments of both reviewers and have revised our manuscript with them in mind.

One of the main issues raised was that readers may by default assume that our models are correct. We in fact made it very clear in our discussion that the models are merely hypotheses that will need testing by “wet” experiments and we do not therefore agree that even readers unfamiliar with AF would assume that the models must be correct. It was also suggested that readers could be reassured by including extensive confidence estimates such as PAE plots. As it happens, every single model described in the manuscript had reasonably high PAE scores and more crucially the entire collection of output files, including PAE data, are readily accessible on Figshare at https://doi.org/10.6084/m9.figshare.22567318.v2, a fact that the reviewers appear to have overlooked. The Figshare link is mentioned three times in the manuscript. Embedding these data within the manuscript itself would in our view add even more details and we have therefore not included them in our revised manuscript. Likewise, it is rather simple for any reader to work out which part of a PAE matrix corresponds to an interaction observed in the corresponding pdb prediction. Besides which, it is our view that the biological plausibility and explanatory power of models is just as important as AF metrics in judging whether they may be correct, as is indeed also the case for most experimental work.

Another important point was that the manuscript was too long and not readable. Yes, it is long and it could well be argued that we could have written a different type of manuscript, focusing entirely on what is possibly the simplest and most important finding, namely that our AF models suggest that in animal cells Wapl appears to form a quarternary complex with SA, Pds5, and Scc1 in a manner suggesting that a key function of Wapl’s conserved CTD is to sequester Scc1’s Nterminal domain after it has dissociated from Smc3. For right or for wrong, we decided that this story could not be presented on its own but also required 1) an explanation for how Scc1 is induced to dissociate from Smc3 in the first place and 2) how to explain that the quarternary complex predicted for animal cells was not initially predicted for fungi such as yeast. The yeast situation was an exception that clearly needed explaining if the theory was to have any generality and it turned out that delving into the intricate details of the genetics of releasing activity in yeast was eventually required and yielded valuable new insights. We also believe that our work on the recruitment of Eco/Esco acetyl transferases to cohesin and the finding that sororin binds to the Smc3/Scc1 interface also provided important insight into how releasing activity is regulated. We acknowledge that the paper is indeed long but do not think that it is badly written. It is above all a long and complex story that in our view reveals numerous novel insights into how cohesin’s association with chromosomes is regulated and have endeavoured to eliminate any excessive speculation. We feel it is not our fault that cohesin uses complex mechanisms.

Notwithstanding these considerations, we have in fact simplified a few sections and removed one or two others but acknowledge that we have not made substantial cuts.

It was pointed out that a key feature of our modelling, namely the predicted association of Wapl’s C-terminal domain with SA/Scc3’s CES is inconsistent with published biochemical data. The AF predictions for this interface are universally robust in all eukaryotic lineages and crucially fully consistent with published and unimpeachable genetic data. We note that any model that explains all findings is bound to be wrong for the very simple reason that some of these findings will prove to be incorrect. There is therefore an art in Science of judging which data must be explained and accommodated and which should be ignored. In this particular case, we chose to ignore the biochemistry. Time will tell whether our judgement proves correct.

Last but not least, it was suggested that we might provide some experimental support for our proposed SA/Scc3-Pds5-Scc1-WaplC quaternary complex. We are in fact working on this by introducing cysteine pairs (that can be crosslinked in cells) into the proposed interfaces but decided that such studies should be the topic of a subsequent publication. It would be impossible with the resources available to our labs to follow up all of the potential interactions and we therefore decided to exclude all such experiments.

We are grateful for the detailed comments provided by both reviewers, many of which were very helpful, and in many but not all cases have amended the manuscript accordingly.

With regard to the more specific comments:

Reviewer #1 (Recommendations For The Authors):

1) One concern is that observed interfaces/complexes arise because AF-multimer will aim to pack exposed, conserved and hydrophobic surfaces or regions that contain charge complementarity. The risk is that pairwise interaction screens can result in false positive & non-physiological interactions. It is therefore important to report the level of model confidence obtained for such AF calculations:

A) The authors should color the key models according to pLDDT scores obtained as reported by AF. This would allow the reader to judge the estimated accuracy of the backbone and side chain rotamers obtained. At least for the key models and interactions it would be important to know if the pLDDT score is >90 (Correct backbone and most rotamers) or >70 (only backbone is correct).

B) It would also be important to report the PAE plots to allow estimation of the expected position error for most of the important interactions. pLDDT coloring and PEA plots can be shown side-by-side as shown in other published data (e.g. https://pubmed.ncbi.nlm.nih.gov/35679397/ (Supplementary data)

C) The authors should include a Table showing the confidence of template modeling scores for the predicted protein interfaces as ipTM, ipTM+pTM as reported by AlphaFold-multimer. Ideally, they would also include DockQ scores but this may not be essential. Addition of such scores would help classification into Incorrect, Acceptable or of high quality. For example, line 1073 et seq the authors show a model of a SCC1SA and ESCO1 complex (Fig. 37). Are the modeling scores for these interfaces high? It does not help that the authors show cartoons without side chains? Can the authors provide a close-up view of the two interfaces? Are the amino acids are indeed packed in a manner expected for a protein interface? Can we exclude the possibility that the prediction is obtained merely because the sequence segments (e.g. in ESCO1 & ESCO2) are hydrophobic and conserved?

We do not agree that including this level of detail to the text/figures of the manuscript would be suitable. All the relevant data for those who may be sceptical about the models are readily available at https://doi.org/10.6084/m9.figshare.22567318.v2. In our view, the cartoon versions of the models are easier for a reader to navigate. Anyone interested in the molecular details can look at the models directly.

Importantly, no amount of statistical analysis can completely validate these models. What is required are further experiments, which will be the topic of further work from our and I dare from other laboratories.

D) When they predict an interaction between the SA2:SCC1 complex and Sororin's FGF motif, they find that only 1/5 models show an interaction and that the interaction is dissimilar to that seen of CTCF. Again, it would be helpful to know about modeling scores. Can they show a close-up view of the SORORIN FGF binding interface to see if a realistic binding mode is obtained? Can they indicate the relevant region on the PAE plot?

Given that AF greatly favours other interactions of Sororin’s FGF motif over its interaction with SA2-Scc1, we do not agree that dwelling on the latter would serve any purpose.

2) Line 996: AF predicts with high confidence an interaction between Eco1 & SMC3hd. What are the ipTM (& DockQ if available) scores. Would the interface score High, Medium or Acceptable?

As mentioned, see https://doi.org/10.6084/m9.figshare.22567318.v2.

3) Line 1034 et seq: Eco1/ESCO1/ESCO2 interaction with PDS5. Interface scores need to be shown to determine that the models shown are indeed likely to occur. If these interactions have low model confidence, Fig. 36 and discussion around potential relevance to PDS5-Eco1 orientation relative to the SMC3 head remains highly speculative and could be expunged.

See https://doi.org/10.6084/m9.figshare.22567318.v2. It should be clear that the predictions are very similar in fungi and animals. Crucially, we know that Pds5 is essential for acetylation in vivo, so the models appear plausible from a biological point of view.

4) Considering the relatively large interface between ECO1 and SMC3, would the author consider the possibility that in addition to acetylating SMC3's ATPase domain, ECO1 remains bound to cohesin-DNA complex, as proposed for ESCO1 by Rahman et al (10.1073/pnas.1505323112)?

This is certainly possible but we would not want to indulge in such speculation.

5) E.g. Line 875 but also throughout the text: As there is no labeling of the N- and C-termini in the Figures, is frequently unclear what the authors are referring to when they mention that AF models orient chains in a certain manner.

Good point. This has been amended. However, the positions of N- and C- is all available at https://doi.org/10.6084/m9.figshare.22567318.v2.

6) Fig19B: PAE plots: authors should indicate which chains correspond to A, B, C. Which segment corresponds to the TYxxxR[T/S]L motif? Can they highlight this section on the PAE plot?

Good point and amended in the revised manuscript.

Minor comments:

1) Line 440: the WAPL YSR motif is not shown in Fig. 14A

2) Line 691: Scc3 spelling error.

3) Line 931: Sentence ending '... SCC3 (SCC3N).' requires citation.

4) Line 1008: Figure reference seems wrong. It should read: Fig. 34A left and right. Fig. 34B does not contain SCC1.

Many thanks for spotting these. Hopefully, all corrected.

5) Fig. 41 can be removed as it shows the absence of the interaction of Sororin with SMC1:SCC1. Sufficient to mention in the text that Sororin does not appear to interact with SMC1:SCC1.

This is possible but we decided to leave this as is.

Reviewer #2 (Recommendations For The Authors):

Minor points

(1) Are there any predicted models in which one of the two dimer interfaces of the hinge is open when the coiled coils are folded back, as seen in the cryo-EM structure of human cohesin-NIPBL complex in the clamped state?

No AF runs ever predicted half opened hinges. It is possible that the introduction of mutations in one of the two interfaces might reveal a half-opened state and we ought to try this. However, it would not be appropriate for this manuscript, we believe.

(2) Structures of the SA-Scc1 CES bound to [Y/F]xF motifs from Sgo1 and CTCF have been reported, suggesting that a similar motif could interact with SA/Scc3. Surprisingly, AF did not predict an interaction between Scc3/SA and Wapl FGF motifs, which only bind to the Pds5 WEST region. On the other hand, AF predicted interactions of the Sororin FGF motif with both Pds5 WEST and SA CES. Can the authors comment on this Wapl FGF binding specificity? What will happen if a Wapl fragment lacking the CTD is used in the prediction?

This seems to be an academic point as the CTD is always present.

Author Response

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

Reviewer #1 (Public Review):

The study as a concept is well designed, although there are two issues I see in the methodology (these may be just needing further explanation or if I am correct in my interpretation of what was done, may need reanalysis to take into account). Both issues relate to the data that was extracted from the published literature on zoonotic malaria prevalence in the study area.

1) No limit was set on the temporal range

With no temporal limit on the range of studies, the landscape in many cases will have changes between the study being conducted and the spatial data. This will be particularly marked in areas where there has been clearing since the zoonotic malaria prevalence study. Also, population changes (either through population growth, decline or movement) will have occurred. All research is limited in what it can do with the available data, so I realise that there may not be much the authors can do to correct this. One possible solution would be to look at the land use change at each site between the prevalence study and the remote sensing data. I'm not sure if this is feasible, but if it is I would recommend the authors attempt this as it will make their results stronger.

Thank you for the comments. We agree that matching the date of remote sensing data to samples is particularly important for environmental variables that change rapidly (such as forest loss). To clarify, no limit was set on the date range of the studies identified from the literature to ensure no articles were excluded due to arbitrary date restrictions. We have edited the manuscript to clarify this (line 422). Regarding landscape and environmental features, remote sensing data was extracted annually for every year for the full date range of the data (see Table 1 and S11, annual temporal resolution from 2006 to 2020). Forest was then matched contemporaneously (see lines 467–473) meaning that, insofar as it was possible, forest data was extracted for the same year as the data was collected. Where a date range was given for the primate data, the mean year was used. For human population density, covariate data were extracted for multiple years but were found to be relatively stable over the time period for the sites covered, so median year was used (see Supplementary Information, Appendix E and Table S11). Elevation is stable and typically only one time point is used as reference (in this instance the SRTM 90m Digital Elevation model, 2003).

2) Most studies only gave a geographic area or descriptive location.

The spatial analysis was based on a 5km and 20km radius of the 'study site' location, but for many of the studies the exact site is not known. Therefore the 'study site' was artificially generated using a polygon centroid. Considering that the polygon could be an administrative boundary (i.e., district/state/country), this is an extremely large area for which a 5km radius circle in the middle of the polygon is being taken as representative of the 'study site'. This doesn't make sense as it assumes that the landscape is uniform across the district, which in most cases it will not be (in rural areas it is going to be a mixture of villages, forest, plantation, crops etc which will vary across the landscape). This might just be a case of misunderstanding what was done (in which case the text needs rewording to make it clearer) or if I have interpreted it correctly the selection of the centroid to represent the study area does not make sense. I am not sure how to overcome this as it probably not possible to get exact locations for the study sites. One possibility could be to make the remote sensing data the same scale as the prevalence data ie if the study site is only identifiable at the polygon level, then the remote sensing data (fragmentation, cover and population) is used at the polygon level.

Both these issues could have an impact on the study's findings. I would think that in both cases it might make the relationship between the environmental variables and prevalence even clearer.

We would like to thank the reviewer for their concerns and provide some clarification on the methods used to extract environmental variables:

• Centroid was initially explored, but not pursued for the same concerns raised by the reviewer. Taking the centroid would be arbitrary and the central point of a large polygon is not likely to be representative of habitat across the entire sampling area and introduces error so this was not pursued(Cheng et al., 2021). We have clarified the wording in the manuscript with reference to centroids to avoid confusion on this point (line 491).

• We demonstrate a method to account for the lack of precise geolocation by taking 10 ‘pseudo-sampling’ points instead of a single random location, with environmental variables extracted at 5, 10 and 20km for each site (lines 487-500). By including 10 environmental realisations, surveys conducted in smaller or more uniform landscapes will have more consistent covariates and this will lend more weight to the model. Conversely, samples taken from large administrative polygons are likely to be highly variable, and these associations will have less representation in the final model. This approach was used to demonstrate an alternative to using a single arbitrary site to represent the area.

To further support the validity of this technique:

• Figures illustrating the variance of the environmental variables across the 10 sampling sites at 5, 10 and 15km for GADM administrative classifications at country level (GID0), state (GID1), district (GID2) and exact coordinates (GPS) are now included in the SI (Figure S12).

• Sensitivity analyses were conducted, in which final GLMM models were fit again but using only acceptable levels of variance in environmental variables and/or acceptable size of administrative boundary (Table S15 and S16). In sensitivity analyses, forest cover and fragmentation retained a significant effect on prevalence of P. knowlesi in macaques, suggesting this effect is robust to spatial uncertainty.

We would also like to highlight that the main finding of this research is the novel synthesis of regional prevalence of P. knowlesi in simian reservoirs across Southeast Asia, which was formerly assumed to be ubiquitous high prevalence, and which can now be used to inform regionally specific transmission modelling, better estimate spatial risk and parameterise early warning systems for P. knowlesi malaria in countries approaching elimination of human malarias. The risk factor analysis here is provided to begin to understand what may be driving this geographic heterogeneity in P. knowlesi prevalence at finer scales and demonstrate methods that could be used to accommodate spatial uncertainty in secondary data. We appreciate that this may not have been clear and have edited the manuscript accordingly.

Reviewer #2 (Public Review):

This is the first comprehensive study aimed at assessing the impact of landscape modification on the prevalence of P. knowlesi malaria in non-human primates in Southeast Asia. This is a very important and timely topic both in terms of developing a better understanding of zoonotic disease spillover and the impact of human modification of landscape on disease prevalence.

This study uses the meta-analysis approach to incorporate the existing data sources into a new and completely independent study that answers novel research questions linked to geospatial data analysis. The challenge, however, is that neither the sampling design of previous studies nor their geospatial accuracy are intended for spatially-explicit assessments of landscape impact. On the one hand, the data collection scheme in existing studies was intentionally opportunistic and does not represent a full range of landscape conditions that would allow for inferring the linkages between landscape parameters and P. knowlesi prevalence in NHP across the region as a whole. On the other hand, the absolute majority of existing studies did not have locational precision in reporting results and thus sweeping assumptions about the landscape representation had to be made for the modeling experiment. Finally, the landscape characterization was oversimplified in this study, making it difficult to extract meaningful relationships between the NHP/human intersection on the landscape and the consequences for P. knowlesi malaria transmission and prevalence.

Thank you for the feedback on the manuscript. We agree that the data was not originally intended for spatial assessment of landscape impact nor represents a full range of landscape conditions across the region. However, we would like to highlight the first set of results from the meta-analysis. Here, the synthesis of all available data allows for the detection of regional disparities and geographic heterogeneity of prevalence in host species, which individual small-scale opportunistic studies are not powered to do, and which had not been identified before this investigation.

In this context, the risk factor analysis is an exploratory analysis to understand what may be driving the observed geographic variation at broad scales as well as provide a framework for dealing with spatial uncertainty. Landscape data was extracted at a level deemed appropriate given the limitations of the data. The majority were geolocated to district level and sensitivity analysis showed a reasonable consistency of landscape features at our chosen scales (Table S8, Figure S12A). To address some of these concerns, we conducted further analysis to explore the deviation of environmental covariates in each sampling area and ran sensitivity analysis by removing extremely variable datapoints (Table S15 and Table S16). When removing highly uncertain data and/or countrylevel data, effects of canopy cover on non-human primate malaria prevalence is retained, supporting the original findings.

Despite many study limitations, the authors point to the critical importance of understanding vector dynamics in fragmented forested landscapes as the likely primary driver in enhanced malaria transmission. This is an important conclusion particularly when taken together with the emerging evidence of substantially different mosquito biting behaviors than previously reported across various geographic regions.

Another important component of this study is its recognition and focus on the value of geospatial analysis and the availability of geospatial data for understanding complex human/environment interactions to enable monitoring and forecasting potential for zoonotic disease spillover into human populations. More multi-disciplinary focus on disease modeling is of crucial importance for current and future goals of eliminating existing and preventing novel disease outbreaks.

Reviewer #1 (Recommendations For The Authors):

A couple of minor points

1) Was the human density and forest cover correlated? If so was this taken into account

Human density and forest cover at selected scales were not found to be strongly correlated (Spearman’s rank values -0.38 and -0.45 within 5km and 20km buffer radii for human population density respectively).

In selecting variables for inclusion in the final model, we examined variance inflation factors (VIF) to detect and minimise multicollinearity in the model. VIF measures the correlation and strength of correlation between independent predictors. VIF of each predictor variable was examined starting with a saturated model and sequentially excluding the variable with the highest VIF score from the model. Stepwise selection continued until the entire subset of explanatory variables in the global model satisfied a conservative threshold of VIF ≤6 (Rogerson, 2001), which ensures that the remaining variables included in the final model have minimal correlation. Spearman’s correlation matrices for all variables at all scales and final selected variables (below VIF threshold) are included in the Supplementary Information (Figure S13 and Figure S14).

2) Reference (Speldewinde et al., 2019) is down as Davidson et al. in the reference list

Thank you for the thoroughness in this review. There are two similar but separate references, both published in 2019 with the same co-authors, and the (Speldewinde et al, 2019) was incorrectly referenced. They should be (Davidson et al., 2019a) and Davidson et al., 2019b) respectively. This has now been corrected in the manuscript.

Davidson, G., Chua, T.H., Cook, A. et al. Defining the ecological and evolutionary drivers of Plasmodium knowlesi transmission within a multi-scale framework. Malar J 18, 66 (2019). https://doi.org/10.1186/s12936-019-2693-2

Davidson G, Chua TH, Cook A, Speldewinde P, Weinstein P. The Role of Ecological Linkage Mechanisms in Plasmodium knowlesi Transmission and Spread. Ecohealth. 2019;16(4):594-610. https://doi:10.1007/s10393-019-01395-6

Reviewer #2 (Recommendations For The Authors):

Line 143: "We hypothesise that higher prevalence of P. knowlesi in primate host species is driven by landscape change..." without specifying here the kind of landscape change (e.g. "forest degradation and fragmentation") it is virtually impossible to confirm or reject this hypothesis.

We agree that the wording of the hypotheses needed to be more specific. We have edited lines 142 – 145 to specify forest fragmentation as our landscape variable of interest, and to more explicitly include the regional meta-analysis of P. knowlesi prevalence.

Table 1 vs Table S11 discrepancy regarding spatial resolution of Forest cover and fragmentation variables. The original dataset resolution is 30m but I don't think one can compute a PARA index at 30 m since it really requires a polygon that is larger than the single value pixel. Table S11 indicates a 30 km gridcell with some postprocessing of the original datasets.

We appreciate this being identified. The resolution refers to the input layer (tree canopy cover, 30m). PARA was calculated from the binary forest cover layer (30m resolution) within each buffer radii 5, 10 and 20km. We have edited both Table 1 and Table S11 to help clarify this.

It would be very helpful if you provided justification for selecting specific metrics to represent the key landscape variables. How are these particular landscape variables relevant? Why not other land cover/land use components?

We have now included a paragraph in the Supplementary Information (Appendix D) to explain the choice of environmental covariates. Elevation was chosen as an important proxy for vector distribution (but was not retained in model selection). Human population density was chosen as a measure of proximity to human settlement, rather than relying on qualitative assessment of rural/peri-urban/urban. Tree canopy cover and fragmentation indices are key determinants of primate habitat selection and of vector breeding habitat, and justification for the use of perimeter: area ratio is included in the methods section (section beginning line 462).

I think the other issues present substantial weaknesses that you cannot address without redoing the study. I will list those below just for reference.

1) If the forest is so dominant (which I would agree with based on my understanding of macaque ecology), how does it make sense to select completely random points (especially at the country or even state level) to represent landscape covariates? At a minimum, I would suggest getting random points within the forest or better yet forest edge habitat. But even then, I doubt that these points would be at all representative of the conditions of a specific study. The geospatial uncertainty is just too large. The dataset simply doesn't support the analysis that is attempted here.

On the point of selecting from only within forest: forest is a dominant habitat, but Long-tailed macaques are anthropophilic and not exclusively found in forest (Stark et al., 2019), and a proportion of the more opportunistic and nuisance samples caught were found in areas more associated with human activity (Li et al., 2021). As such, random points only within forested areas is also unlikely to capture the true habitat of the primates sampled and selecting only from forested areas would bias the results.

Whilst fully georeferenced samples would be the ideal scenario, the idea behind selecting random points from the sampling polygon is that for smaller areas (with higher spatial certainty), habitat would be more consistent between random points and lend more weight to the final model, whereas large polygons with high uncertainty are likely to vary and lend less weight to the final model. In response to these comments, we have further supported this by running regression models only on samples within a reasonable administrative boundary size and on samples within reasonable threshold of uncertainty (i.e., data points are removed if the deviation of environmental covariates across the 10 random points is so high that the sample is uninformative, or if datapoints can only be geolocated to country-level). In these sensitivity analyses, forest cover and species are retained as factors associated with higher malarial prevalence in non-human primates (Table S15S16).

2) Hansen et al. dataset reflects "tree cover" - which is not the same as "forest cover" since it would also include plantations that are very widely distributed across Southeast Asia. If the animal use of plantations differs from that of natural forests, it will present a large issue for the study.

In this analysis the feature of interest was habitat configuration (fragmentation) and deforestation (forest loss) rather than specific land class. We have defined forest as >50% canopy cover, which considers canopy density given historical forest loss and has precedence in other work (Fornace et al.,, 2016). In addition to importance to macaque ecology, forest (canopy) cover, forest loss and forest edge are noted to be key determinants of vector breeding and vector habitat (Byrne et al., 2021, Chua et al., 2019). For this reason, these are important variables to include in analyses. More specific landscape variables were explored, but the temporal and spatial range of the data precluded fine-scale land classification data. To investigate preliminary links to landscape configuration and habitat fragmentation at broad scales this is felt to be sufficient. We have also amended the manuscript to be more discerning with the use of ‘forest’ to avoid confusion throughout.

3) Tree regrowth in the ecosystems of monsoonal Asia is very rapid. Based on the study description, tree regrowth was not accounted for in the study which could potentially lead to a very large underestimation of tree cover if only tree loss since 2000 was monitored. Again unless there is a reason to assume that macaques do not use young successional forests or use it at a highly reduced rate. Both of these points are acknowledged as limitations at the end of the discussion section but in my opinion they have a very strong impact on the study, making the results non-significant.

This is an interesting suggestion. Macaques do forage in plantations and cultivated landscapes to supplement food, but preferentially roost and range in forest edges and interior forest, though ranging behaviour will be complex and vary across Southeast Asia. In this study the primary interest was in deforestation (forest loss) and fragmentation of old growth forested landscapes, which are key variables both for macaque ecology and for vector breeding sites. Therefore, it was felt that forest loss (transition from >50% canopy cover to <50% canopy cover since 2000) was sufficient to capture this. Ranging behaviour of individual animals and macaque troops would not be captured at this scale, and higher spatial and temporal resolution would be required to characterise relationships with tree regrowth and young plantations which is outside the scope of this study. In all regions, purposeful fine scale follow-up studies would be required to unpick fine scale relationships across a habitat gradient.

I am not 100% sure I understand the geospatial design fully. The pieces are distributed between different subsections and it was challenging to string together the processing chain between subsections of the manuscript and the supplemental information. I would help to add a figure (a flowchart, perhaps?) to the supplemental section that walks through the entire geospatial covariates assembly. E.g.

• GPS location create 5, 10, and 20 km buffers mean elevation, mean population, %(?) Forest, PARA(?) for each buffer - I still don't understand the 30m or 30 km spatial resolution reference for forest and PARA in this context.

This was an error in the table in the Supplementary Information and has been corrected – the forest cover raster has a resolution of 30m, and the perimeter: area ratio is calculated within 5, 10 and 20km buffers.

• landscape covariates receive the full weight (1) in the model. - This is defensible even though not ideal

This is equivalent, but we felt more intuitive, to sampling GPS points x10 and inputting with equal weights to the areal data.

• No GPS location assign to the best identifiable administrative unit (country, state, or district) generate 10 random points within the administrative unit create 5, 10, and 20 km buffers mean elevation, mean population, %(?) Forest, PARA(?) for each buffer landscape covariates from each point receive the proportional weight (0.1) in the model. I do not believe that this approach is representative of macaque habitat/macaque human interaction characterization.

In other examples dealing with spatial uncertainty, the centroid is taken to be representative of an area. This method generates considerable bias and uncertainty – particularly if the uncertainty is not then accounted for by weighting subsequent models (Cheng, 2021). In this exploratory analysis, pseudo-sampling from 10 random sites generates a more realistic generalised environmental realisation than taking a centroid/random point. This was used as an exploratory analysis to explain broad regional trends in prevalence between, which can be used to guide further investigation on fine scale studies which are required to completely describe disease dynamics in specific macaque habitats.

Thank you for this useful suggestion – we have taken this advise and added a flowchart of data processing to the Supplementary Information (Appendix D, Figure S8).

Discussion:

Based on information in Table S4, sampled NHPs were predominantly from human-dominated (peridomestic, agricultural, and urban) landscapes. In forested landscapes, only macaques that live in forest edge habitats were likely sampled in the first place just simply due to extreme challenges in getting to macaques in remote inaccessible areas. There is a very substantial spatial bias in sampling will undoubtedly reflect that fragmented habitat is a key landscape component impacting the prevalence of Pk in NHP, especially as the authors point out in the later part of the discussion, the critical vectors for transmission are also associated with forest edge habitats. High forest fragmentation is also linked to the presence/ increase in migrant human workers (logging or plantation activities) - a population also strongly associated with higher malaria prevalence for a variety of P spp (although I am not aware of studies that are specific to Pk malaria). However, the living conditions for migrant workers have frequently been implicated in higher rates of malaria transmission and thus those could, hypothetically, also contribute to Pk infection rates in NHP. Ultimately, the discussion appears to suggest that the biggest gap in our understanding is within vector ecology and understanding the NHP-vector-human dynamics within local landscape settings. It is an interesting finding. However, my overall conclusion would be that the sampling strategy (both for NHP and geospatial covariates) renders this study as "exploratory" at maximum and that all findings would need to be tested and verified through independent and more rigorously designed studies.

Thank you to the reviewer for a comprehensive assessment. We would first like to highlight the regional meta-analysis, which was one of the main findings. This is a novel result for P. knowlesi literature; being the first demonstration of regional differences in prevalence that correlate to regional hotspots of human incidence, the force of infection from NHP may drive hotspots of P. knowlesi in human populations.

We include a risk factor analysis that suggests a method for dealing with high spatial uncertainty, and an exploratory analysis that finds landscape complexity may be a contributory factor to broad regional heterogeneity. These associations are robust to sensitivity analysis where data with extreme variability in environmental variables is removed (Table S15-S16).

Habitat descriptions in original studies are qualitative, likely subjective, and whilst there is likely to be an important sampling bias there was also evident differences in prevalence between the NHP sampled in different environments from the available data that we have further characterised. Risk factors for human P. knowlesi do include forest loss (reduction in canopy cover) within 5 years and within 2km, as well as contact with macaques and occupations in plantations (Fornace et al., 2014; Fornace et al., 2016). Reverse spillover from humans to NHP is an interesting suggestion, but outside the scope and scale of the study. Given known links of deforestation (forest loss) with human incidence of P. knowlesi and also with increased vector breeding sites (Byrne et al., 2021), this analysis explores whether deforestation is linked to prevalence in reservoir species thus contributing to the force of infection at broad scales.

Reviewer #1 (Public Review):

Summary:<br /> The work of Muller and colleagues concerns the question of where we place our feet when passing uneven terrain, in particular how we trade-off path length against the steepness of each single step. The authors find that paths are chosen that are consistently less steep and deviate from the straight line more than an average random path, suggesting that participants indeed trade-off steepness for path length. They show that this might be related to biomechanical properties, specifically the leg length of the walkers. In addition, they show using a neural network model that participants could choose the footholds based on their sensory (visual) information about depth.

Strengths:<br /> The work is a natural continuation of some of the researchers' earlier work that related the immediately following steps to gaze [17]. Methodologically, the work is very impressive and presents a further step forward towards understanding real-world locomotion and its interaction with sampling visual information. While some of the results may seem somewhat trivial in hindsight (as always in this kind of study), I still think this is a very important approach to understanding locomotion in the wild better.

Weaknesses:<br /> The manuscript as it stands has several issues with the reporting of the results and the statistics. In particular, it is hard to assess the inter-individual variability, as some of the data are aggregated across individuals, while in other cases only central tendencies (means or medians) are reported without providing measures of variability; this is critical, in particular as N=9 is a rather small sample size. It would also be helpful to see the actual data for some of the information merely described in the text (e.g., the dependence of \Delta H on path length). When reporting statistical analyses, test statistics and degrees of freedom should be given (or other variants that unambiguously describe the analysis). The CNN analysis chosen to link the step data to visual sampling (gaze and depth features) should be motivated more clearly, and it should describe how training and test sets were generated and separated for this analysis. There are also some parts of figures, where it is unclear what is shown or where units are missing. The details are listed in the private review section, as I believe that all of these issues can be fixed in principle without additional experiments.

Reviewer #1 (Public Review):

Overall, the experiments are well-designed and the results of the study are exciting. We have one major concern, as well as a few minor comments that are detailed in the following.

Major:<br /> 1. The authors suggest that "Visuomotor experience induces functional and structural plasticity of chandelier cells". One puzzling thing here, however, is that mice constantly experience visuomotor coupling throughout life which is not different from experience in the virtual tunnel. Why do the authors think that the coupled experience in the VR induces stronger experience-dependent changes than the coupled experience in the home cage? Could this be a time-dependent effect (e.g. arousal levels could systematically decrease with the number of head-fixed VR sessions)? The control experiment here would be to have a group of mice that experience similar visual flow without coupling between movement and visual flow feedback. Either change would be experience-dependent of course, but having the "visuomotor experience dependent" in the title might be a bit strong given the lack of control for that. We would suggest changing the pitch of the manuscript to one of the conclusions the authors can make cleanly (e.g. Figure 4).

Minor:<br /> 2. "ChCs shape the communication hierarchy of cortical networks providing visual and contextual information." We are not sure what this means.

3. "respond to locomotion and visuomotor mismatch, indicating arousal-related activity" This is not clear. We think we understand what the authors mean but would suggest rephrasing.

4. 'based on morphological properties revealed that 87% (287/329) of labeled neurons were ChCs" Please specify the morphological properties used for the classification somewhere in the methods.

5. We may have missed this - in the patch clamp experiment (Fig.1 H-K), please add information about how many mice/slices these experiments were performed in.

6. "These findings suggest that the rabies-labeled L1-4 neurons providing monosynaptic input to ChCs are predominantly inhibitory neurons". We are not sure this conclusion is warranted given the sparse set of neurons labelled and the low number of cells recorded in the paired patch experiment. We would suggest properly testing (e.g. stain for GABA on the rabies data) or rephrasing.

7. Figure 2E. A direct comparison of dF/F across different cell types can be subject to a problematic interpretation. The transfer function from spikes to calcium can be different from cell type to cell type. Additionally, the two cell populations have been marked with different constructs (despite the fact that it's the same GECI) further reducing the reliability of dF/F comparisons. We would recommend using a different representation here that does not rely on a direct comparison of dF/F responses (e.g. like the "response strength" used in Figure 3B). Assuming calcium dynamics are different in ChCs and PyCs - this similarity in calcium response is likely a coincidence.

8. If ChCs are more strongly driven by locomotion and arousal, then it's a bit counterintuitive that at the beginning of the visual corridor when locomotion speed consistently increases, the activity of ChCs consistently decreases. This does not appear to be driven by suppression by visual stimuli as it is present also in the first and last 20cm of the tunnel where there are no visual stimuli. How do the authors explain this?

9. The authors mention that "ChC responses underwent sensory-evoked plasticity during the repeated visual exposure, even though the visual stimuli were different from those encountered during training in the virtual tunnel". How would this work? And would this mean all visual responses are reduced? What is special about the visual experience in the virtual tunnel? It does not inherently differ from visual experience in the home cage, given that the test stimuli (full field gratings) are different from both.

10. Just as a point to consider for future experiments: For the open-loop control experiments, the visual flow is constant (20cm/s) - ideally, this would be a replay of the running speed the mouse previously generated to match statistics.

11. We would recommend specifying the parameters used for neuropil correction in the methods section.

12. If we understand correctly, the F0 used for the dF/F calculation is different from that used for division. Why is this?

13. Authors compare neuronal responses using "baseline-corrected average". Please specify the parameters of the baseline correction (i.e. what is used as baseline here).

This idea of 'trolling' as a signifier of an in-group identity raises questions regarding the ethics of the action as it relates to socio-economic status. If a privileged group in society behaves in these way, it is arguably far more reprehensible than if an oppressed group behaved similarly as a means of protest due to the innate power one group may hold.

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

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Reply to the reviewers

Please see below for the detailed description of the changes made in response to the reviewers’ comments.

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

The manuscript investigated the composition of the plastid proteomes of seven distantly-related kareniacean dinoflagellates, including newly-sequenced members of three genera (Karenia, Karlodinium, and Takayama). Using a custom plastid-targeting predictor, automatic single-gene tree building and phylogenetic sorting of plastid-targeted proteins for plastid proteome construction, the authors suggest that the haptophyte order Chrysochromulinales is the closest living relative of the fucoxanthin plastid donor. Interestingly, the N-terminal targeting sequences of kareniacean plastid signal peptides, reveal a high sequence conservation. Moreover, ecological and mechanistic factors are suggested that may have driven the endosymbiotic acquisition of the fucoxanthin plastid. Overall, this is a comprehensive and interesting analysis.

Other comments.

1. For analyses of N-terminal targeting sequences, why did the authors not consider to employ Predalgo as an additional tool? Author response: We thank the reviewer for their suggestion. To our understanding, PredAlgo is a targeting predictor trained on primary green algae, which have two-membrane bound plastids and purely hydrophilic N-terminal plastid targeting sequences. It thus would be expected to perform poorly for the prediction of N-terminal targeting sequences in complex plastids such as those of the Kareniaceae bound by three or more membranes, who are located within endomembrane-derived compartments and which utilise plastid-targeting sequences based on an N-terminal hydrophobic signal peptide for ER import.

We considered the application of PredAlgo for the identification of downstream hydrophilic transit peptide regions in Kareniacean presequences, but note that the specific residue positioned after the signal peptidase cleavage site is typically a much better predictor than transit peptide hydrophobicity for identifying plastid-targeting sequences (Gruber et al., Plant J 2015, and citing references). We found that other targeting prediction tools based primarily on hydrophobicity (e.g., HECTAR) performed poorly in identifying probable plastid-targeting sequences in our control Kareniacean dataset, and therefore chose to prioritise a modified version of ASAFind that takes into account the residue context of Kareniacean signal peptidase cleavage site for our targeting predictor, which works with high sensitivity and specificity on our control dataset. We summarise these observations in Fig. S15.

Given the fact that peridinin or fucoxanthin pigment binding is in the focus of the paper, a more detailed introduction of the peridinin and fucoxanthin light-harvesting systems should be given.

Author response: A brief introduction to the pigment-binding proteins in dinoflagellates was added, “These include a unique carotenoid pigment… massively paralogized and synthesized as polyproteins” (lines 86-89).

The authors state "It is also possible that there has been a direct niche competition between the peridinin and fucoxanthin plastid that may have coexisted in the same host for a period of time with possibly different selective pressure on retention of their respective proteins based on their interaction with plastid-encoded components, e.g., extrinsic photosystem subunits not assembling correctly with their intrinsic haptophyte-like counterparts." It is tempting to ask, whether peridinin light-harvesting systems have left traces in the fucoxanthin plastid, possibly due to mistargeting of peridinin light-harvesting systems into the fucoxanthin plastid? Are some photosynthetic subunits "in-between" peridinin and fucoxanthin plastids?

Author response: We did not identify any other peridinin-like photosystem subunits than the ones visualized in the map schematic (i.e., ferredoxin/PetF in both Karenia and Karlodinium and PsaD of Karlodinium micrum) and discussed in the supplementary text. PetF is the only consistently retained peridinin-like photosystem protein, likely due to the fact that it is not strictly linked to photosynthesis: it is expressed in plant leucoplasts, and plastid-encoded in some non-photosynthetic chrysophytes. We have added a sentence in Supporting Text 6.4 that “we detect no possible homologues of peridinin-chlorophyll binding proteins (PCP) in any kareniacean transcriptome” (line 91).

Figure 3 is difficult to understand, e.g. for PSI and PSII which subunits are shown, why has PSI "more" contribution from dinoflagellates as compared to PSII?

Author response: The photosystem subunits are ordered numerically in the schematic, and detailed information on each protein and the corresponding sequences with their origin are included in the supplementary table S3. A single subunit of photosystem I (PsaD) was determined to be of plastid-early (peridinin-like) origin in Karlodinium (while the same protein is plastid-encoded in Karenia and undetermined in Takayama). We believe this may be simply due to an evolutionarily neutral differential loss / non-adaptive retention of photosynthesis-related proteins in a secondarily non-photosynthetic host before the acquisition of a replacement plastid. We note that there are only two (incomplete) kareniacean plastid genomes available so we cannot rule out the possibility of this subunit being plastid-encoded in Karlodinium as well (which would mean that both plastid-late and plastid-early homologs co-occur in this genus).

Fig. 3 is necessarily complex due to the size and multiplicity of the dataset considered. To facilitate reader navigation, we have added the following text to the figure legend (lines 1128-1140) text “Plastid proteins are arranged by major metabolic pathway or biological process, with each protein shown as rosettes … Proteins of plastid-late (haptophyte) origin, such as are concentrated in photosystem and ribosomal processes, are coloured red; and proteins of plastid-early (dinoflagellate) origin, such as are concentrated in carbon and amino acid metabolism are coloured blue. … In certain cases (shown as rosettes with multiple colours), homologues from different species have different evolutionary origins, e.g. Karenia possessing plastid-late and Karlodinium/ Takayama plastid-early”.

Data shown in figure 4, is there experimental evidence for signal peptide cleavage site(s). Could these data been used to predict mature plastid targeted protein sequence?

Author response: We were able to determine the conserved motives in signal peptide, including its cleavage site (GRR) which we exploited in the design of kareniaceae-specific matrix for ASAFind. We show these residues in Fig. 4. We note that these motifs were identified based on homology to known signal processing peptidase recognition sites, as opposed to experimentally determined protein N-termini.

Consistent with previous studies (e.g. Yokoyama et al., J Phycol 2011) we see limited evidence for consensus plastid transit peptide cleavage motifs in kareniacean presequences, and do not discuss this further as a result.

The authors state "Partial Least Square (PLS) analysis shows a set of environmental variables (salinity, silicate, iron) positively correlated with abundances of both Karenia and Takayma and also haptophytes as a whole, but at the same time negatively correlated to Karlodinium (Figure S8), further illustrating that the latter genus is quite distant from the rest in its biogeographical pattern." How could this be interpreted in the light of the plastid proteomes

Author response: We believe that this may be due to the more cosmopolitan distribution of Karlodinium, and possibly also a result of bias stemming from our strategy of grouping the organisms at the genus level (as not enough data was available at species level) which may obscure the potential outlier status of only some species/ subpopulations. This is particularly true for the haptophytes, where in the absence of specific ancestry for individual kareniacean plastids we are only able to consider distributions at the levels of entire orders. We now acknowledge this in the Discussion: “specific ecological interactions between the progenitors … via ancestral niche reconstruction for each lineage” (lines 473-475).

Please note, that the results might have changed slightly from the previous version due to the re-calculation following additional normalization of the data (see below).

Reviewer #1 (Significance (Required)):

The current manuscript gives insights into the endosymbiotic acquisition of the fucoxanthin plastids.

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

This is a well done, detailed bioinformatic analysis of genomic and transcriptomic data from an important lineage of dinoflagellates that have undergone serial substitution of their plastid. On the whole I am enthusiastic about the paper; it presents valuable new insights, and is rigorously performed. However, I have to object to the way the term "proteome" is used in the paper; the manuscript is talking about the predicted proteome, not a measured proteome. This is something of a technical distinction, but it is an important one because the transcriptome and the proteome don't necessarily track each other, and there is little or no actual proteomic data available from dinoflagellates. We assume that transcript abundance has something to do with proteome abundance, but this is often violated. What this paper is really addressing is the potential proteome, because if a given gene is completely absent from the genome and the transcriptome we can be confident it will not be present in the proteome. The converse is not true. For this reason I feel it is important to be clear on the distinction. I would be satisfied in this regard by minor modifications, using the term "predicted proteome" in the title, and being more direct in the introduction about the distinction.

Author response: We agree that the usage of the word proteome for in silico predictions is not entirely correct, and have used the term “predicted proteome” where possible in the text to clarify this.

We have also, as described in our response to Reviewer 1 above, included a statement in the Discussion that our largely bioinformatic results will be transformed by an experimentally realised kareniacean plastid proteome, which we nonetheless feel goes beyond the scope of our manuscript.

Overall the analyses are impressive. I do have to squirm a little when I see automated analyses generating alignments where the threshold is less than 75% gaps and at least 100 nucleotides aligned. I looked at the supplementary data and the figshare files and could not find the alignments themselves, so I don't know what fraction of the sequences are in that territory. Because phylogenetic analysis (as performed here) treats the alignments as an observation, and because the alignments include sequences with more than 50% gaps, it is entirely possible that some taxa, or even whole segments of the tree, are based on non-overlapping data.

Author response: We thank the reviewer for their comment and have added in three new supplementary figures (S16-S18) providing statistics on alignment size, length, and average gap percentage distribution. We report that most of the alignments contained relatively little gaps: 90% of the alignments contained between 1.1 and 24.5% of gaps with median value of 6.6%.

Mind you, we have done similar analyses, and I don't think this invalidates the results, but it does open up the possibility of some dramatic artifacts. Consequently, I would recommend a) making the alignments available (or more obvious where to find them), and b) providing more detail on the alignments, including, if possible, to add a figure (probably in the supplementary data) that visualizes them. It is not given in the text itself, but according to the figure 2 caption there are 22 sequences thought to be "plastid late", and 241 in the pan-eukaryotic dataset. This is a scale that is feasible to put in a figure showing, for example, each aligned residue as a color and indels as grey. Such a figure is readable even when the individual residues are only a few pixels in size (less than a millimeter when printed). I also recommend describing the final alignments more fully in the text. Most of the summary statistics are presented in normalized form, and that can obscure patterns that come from poorly sampled taxa. Better clarify on the characteristics of the alignments will make it easier to interpret the findings overall. Although this is critical to interpreting the results, gappy alignments are not uncommon in analyses of this sort, and setting that aside the analyses presented are comprehensive and thorough. The discussion does a good job of addressing the significance of the work, and potential causes of error are addressed adequately (aside from the matter of the alignments).

Author response: We thank the reviewer for their comment and have provided alignments for all single-gene trees, in a dedicated online supporting repository (https://figshare.com/articles/dataset/all-automatically-generated-alignments_rar/24347032). The datasets and alignments used for PhyloFisher and plastid-encoded gene trees are included directly in the supplementary files (phylofisher_files.tar, plastid_genome_phylogeny_files.tar and plastid_protein_phylogeny_files.tar).

We have additionally included three new supporting figures (S16-S18) showing the distributions of lengths, gaps and homologues in each single-gene tree. These data project largely completion of individual alignments, with only 5% containing > 20% gapped positions (see Fig. S18), for example. We have additionally clarified in the Methods that “The trimmed alignments were then filtered by a custom python script that discarded sequences comprising of more than 75% gaps and then rejected alignments shorter than 100 positions or containing fewer than 10 taxa.” (lines 571-573).

For the two concatenated trees presented, we have clarified in the Methods the alignment lengths (PhyloFisher: 72, 162 positions; plastid genes: 2,404 positions), and that we removed sequences containing >66% of gaps from the final alignment. Reflecting on the congruency assumptions required to concatenated alignments, we have chosen to replace the plastid-late concatenated tree (which may group proteins with multiple phylogenetic signals) with a new main text figure 2 providing an overview of the plastid signals we observe across the entire dataset (see comments below to Reviewer 3).

Reviewer #2 (Significance (Required)):

I find the paper to be exciting and important. These organisms are economically important, particularly as potential nuisance organisms, but also because of their role in primary productivity. They also have extremely complex evolutionary histories and similarly complex genomes. performing any bioinformatic analysis of these organisms is a substantial challenge because almost every gene exists in high copy number and with complex and often obscure patterns of homology. The manuscript brings forward these challenges, and makes a substantial step forward in elucidating the evolution of a group that is fascinating and important, but remarkably difficult to work with. I feel that it is an important analysis, and should be of interest to a broad audience.

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

Summary

This manuscript entitled "Divergent and diversified proteome content across a serially acquired plastid lineage" by Novak Vanclova et al. proposes the origin and evolution of plastids in kareniacean dinoflagellates. The authors generated new transcriptome data from Karenia mikimotoi, Karenia papilionacea, Karlodinium micrum, Karlodinium armiger, and Takayama helix. Combining them to the previously published transcriptome data from kareniacean dinoflagellates, they constructed the pan-kareniacean transcriptome library. They surveyed plastid-targeted protein-coding transcripts in the dataset, and consequently they estimated ~14.5% of the transcriptome data were of plastid-targeted ones. Of them, 65-80% were derived from a peridinin-containing dinoflagellate ancestor while ~15% were derived from EGTs from a haptophyte endosymbiont of the current plastid origin. By using the plastid-targeted transcript dataset, they investigated 1) origins of the plastid-targeted protein-coding transcripts by single gene-trees, 2) the plastid origin and evolution by the multigene dataset of 22 conserved plastid-targeted protein-coding transcripts and of 3) plastid genome-derived transcripts, 4) plastid functions, 5) diversity of plastid-targeted signals in kareniacean dinoflagellates, and 6) the distributions of kareniacean species by using the Tara Oceans database. On the basis of their results, they proposed many hypotheses regarding kareniacean dinoflagellate evolution, such as i) the chrysochromulinales-origin of the plastids, ii) more recent acquisition of the plastid than previously thought, iii) a plastid replacement within kareniaceae evolution, iv) the strict selection of signal peptides but non-conserved transit peptides in the kareniacean plastid-targeted proteins, and v) correlated or non-correlated distribution patterns of kareniaceaen dinoflagellates to specific haptophyte lineages.

Although their proposals are interesting, I have many concerns to be addressed. Especially, their analyses on which the above proposals are based seem to be still preliminary and inconclusive. To support their proposals more confidently, I also suggest some additional analyses.

Major comments

1. seemingly inconsistency between the authors' claims The most striking is inconsistency of the authors' claims proposed in this manuscript. Their proposals include a) the common ancestor of kareniaceans has not possessed a fucoxanthin plastid but the plastid has been acquired more recently, b) an ancestor of Takayama and Karlodinium has gained a fucoxanthin plastid from a (chrysochlomulinales) haptophyte, c) an ancestor of Karenia has gained a fucoxanthin plastid from Karlodinium. However, they also demonstrate a higher proportion of plastid-late proteins in Karenia than Karlodinium and Takayama. If I understand correctly, "a higher proportion of plastid-late proteins in Karenia than Karlodinium and Takayama" would seemingly be inconsistent to and challenge two of the authors' claims: no haptophyte-derived plastid in the common ancestor of kareniacean dinoflagellates and a Karlodinium-to-Karenia plastid transfer (Fig. 7). If the Karenia plastid is derived from Karlodinium, I have no idea why haptophyte-derived plastid proteome of Karenia is larger than that of Karlodinium. After the plastid acquisition in Karenia, Karenia might have gained more genes for plastid-targeted proteins from haptophytes by LGTs. If this is true, many single gene trees would suggest different origins of plastid-targeted proteins between Karenia and Karlodinium/Takayama. Can we see it in the single gene analyses? I would like authors to rationalize the inconsistency in the main text.

Author response: We agree with the reviewer that the evolutionary origins and dynamics of the kareniacean plastid proteome are complex, and thank them for their suggestion.

First, to take into account the different evolutionary scenarios that could explain the present-day distribution of the kareniacean plastids, including the new plastid genome sequences identified in response to the reviewer’s suggestions, we have made a revised version of Fig. 8 evaluating three different hypotheses (see below). Nonetheless, we feel that the Karlodinium-to-Karenia model we propose is plausible, based on the following observations:

• We identify 1,418 plastid protein gene trees in which at least two of the three studied genera (Karenia, Karlodinium, Takayama), and 748 in which all three resolve as monophyletic, and with a haptophyte sister-group (i.e., a common plastid-late origin; Fig. S2). This points to a common haptophyte ancestry in all three groups, as opposed to independent endosymbiotic consumptions of free-living haptophytes in Karenia and Karlodinium micrum.

• We see no such shared signal with the RSD, which shares only 42 proteins with at least two other kareniacean genera (Fig. S4). Thus, and consistent with previous studies (Hehenberger et al., PNAS 2019) we cannot invoke an ancestral presence of a fucoxanthin plastid shared with the RSD in the last common kareniacean ancestor. This discrepancy thus likely points to a serial transfer of the kareniacean plastid from either Karlodinium into Karenia or vice versa (Fig. 8).

• Concerning the direction of this transfer, among 1,059 gene trees of plastid-late origin found in both Takayama, Karenia and Karlodinium, 873 place Takayama as basal to a monophyletic clade of Karenia and Karlodinium, i.e. support a specific plastid transfer between the latter two genera. The most parsimonious explanation for this is the origin of the fucoxanthin plastid in the common Takayama/ Karlodinium ancestor, which was subsequently transferred into Karenia. It is true that Karenia contains both a greater absolute proportion of predicted plastid-targeted proteins (Fig. 1) and greater number of unique KO number annotations (Table S4) of plastid-late origin than either Karlodinium or Takayama. That said, this signal may be influenced by multiple other factors beyond how old the given endosymbiosis is (i.e., longer coexistence implies more EGT). For example, the number of plastid-late gene in a host genome may depend on the frequency of duplication of plastid-late genes and the receptiveness of the host nuclear genome to incoming horizontally derived genes. It may further be influenced by the presence and relative selective advantage or disadvantage of competing genes of host nuclear origin (i.e. plastid-early genes) that may be differentially selected over plastid-late genes, which might vary between Karenia and Karlodinium due to differential retention of the ancestral peridinin-type plastid in each lineage.

We have elaborated on this point in the Discussion, noting that there may have been “a direct niche competition between the peridinin and fucoxanthin plastid … with possibly different selective pressure on retention of individual imported proteins” (lines 370-372), “relatively recent origin and spread throughout the kareniacean genome, e.g., via gene duplications” (line 459), and finally that precedent for divergent evolutionary trajectories in different Kareniaceae exists from the Karenia and Karlodinium plastid genomes that “contain partially non-overlapping sets of genes that suggest independent post-endosymbiotic plastid genome reduction” (lines 403-404). Nonetheless, we acknowledge that the evolutionary model we propose is not definitive, and that alternative explanations may find more favour with increased genome data.

Signal peptide prediction I think the modified ASAFind would be greatly helpful for future studies on automatic prediction of plastid proteomes in kareniacean dinoflagellates. However, I found no data on selection criteria for the signal peptide prediction program SignalP5.0 used. I believe such data would be very important to interpret the previously published paper by Gruber et al. in which prediction methods for plastid-targeting sequences are compared to each other to see how sensitively and specifically they can capture the plastid proteomes.

Gruber et al. 2020. Comparison of different versions of SignalP and TargetP for diatom plastid protein predictions with ASAFind.

According to Gruber et al. (2020), signalP5.0 is not suitable for prediction of signal peptides for diatoms, in consistent with the authors' claim for kareniacean dinoflagellates. This inconsistency would be difference of the nature in signal peptides between diatoms and kareniacean dinoflagellates. Even if so, it would be useful to see quantitatively how much different their signal peptides are in terms of their suitable prediction programs.

Author response: In our preliminary benchmarking using only the previously published transcriptomes (see additional sheet in Supplementary tables), SignalP 5.0 performed substantially better in terms of specificity than SignalP 3.0 (i.e., 22 versus 34/ 728 retrieved positive hits of proteins with uniquely non-plastidial functions), with comparable sensitivity in the correct prediction of positive control proteins. Given the size of our dataset, and the substantial risk of false positive detection in the highly expanded and redundant dinoflagellate transcriptomes we have used, we feel that the greater specificity of SignalP 5.0 is important to integrate in our model selection. We have clarified this position in the Methods, stating “First, the relative effectiveness of two SignalP versions … SignalP 5.0 was used for all subsequent analysis.” (lines 525-529).

I also have a concern about use of the combination of PrediSI and ChloroP, combination which is suitable for the plastid proteome prediction in Euglena gracilis. The authors should rationalize why the method for Euglena plastids can be applicable without any modification to the plastid proteome prediction in kareniacean dinoflagellates. Although Euglena plastids are enclosed by three membranes, kareniacean plastids are by four. Therefore, from the side of molecular mechanisms in protein import, the method suitable for Euglena plastids is not necessarily suitable for kareniacean dinoflagellate plastids.

By using PrediSI and ChloroP, they detected additional "candidate plastid proteomes" including several proteins not detectable by SignalP5.0 and the modified ASAFind. That seems great. However, they did not seem to consider false positives since there is no mention on it. Although the additional candidates predicted by PrediSI and ChloroP included true plastid proteins of kareniacean dinoflagellates, many might not be. Nevertheless, the authors suggest 7.5 to 14.5% in K. micrum and K. brevis, respectively, are of plastid-targeted ones. I am so afraid if the proportions would be highly overestimated due to false positives by PrediSI and ChloroP. To rationalize the use of PrediSI and ChloroP, the authors should show sensitivity and specificity by quantitative analyses with a benchmark dataset.

Author response: We thank the author for this comment. The reasoning behind using the parallel PrediSI+ChloroP strategy was the previously reported similarity of the plastid signal structure between euglenids and peridinin dinoflagellates (c.f., Lukes et al., PNAS, 2009) and the previous observation that some kareniaceae posses plastid-targeting sequences resembling those of peridinin dinoflagellates (c.f., Hehenberger et al., PNAS, 2019). Per the reviewers’ suggestion, we present a modified sensitivity/ specificity testing PrediSI+ChloroP, alongside other alternative targeting predictors in Figure S15. While the PrediSI+ChloroP sensitivity is very low, its specificity is comparable with the modified ASAFind, and in this regard outperforms other targeting predictor tools, thus rationalising the use of both targeting prediction tools together.

Origin and evolution of kareniacean plastids The authors suggest the chrysochromulinales origin of the kareniacean dinoflagellate plastids and the Karlodinium-to-Karenia plastid transfer, on the basis of phylogenetic analyses using the concatenated datasets with the 22 conserved plastid-targeted proteins and with plastid-genome derived transcripts. It is very interesting that those plastid-targeted proteins in kareniacean dinoflagellates might be phylogenetically closely related to chrysochromulinales haptophyte I have suggestions on the analyses and interpretation

As the 22 analyzed genes are nuclear-encoded plastid targeted genes, they are a quite small portion of entire plastid proteins. I am not convinced by that evolution of the small number of genes reflects evolution of fucoxanthin plastids of which proteomes are comprised of >1000 proteins. How many genes for haptophyte-derived plastid-targeted proteins suggest the monophyly of kareniaceaen dinoflagellates and chrysochromulinales haptophytes should be investigated by, for example, a coalescence-based analysis such as Astral for all the detected haptophyte-derived plastid-targeted proteins including the 22 genes. This is because the monophyly could be reconstructed only by one or few, limited number of proteins even if the concatenated dataset is analyzed.

Relevant to this, plastid-targeted proteins derived from a peridinin-containing ancestor might still have phylogenetic signals of host evolution. I am interested in whether such analyses with peridinin plastid-derived plastid-targeted proteins reconstruct Takayama and Karlodinium as monophyletic but separate Karenia from them, as suggested in the phylogenomics with non-plastid proteins.

Author response: We agree with the reviewer concerning the problematic nature of concatenations with small numbers of genes, particularly if the underlying gene trees are not phylogenetically congruent to one another, and have chosen to replace the concatenation with a more global evaluation of the different plastid protein origins across our entire dataset. Using automated sorting approaches, we have evaluated the support for our evolutionary model across hundreds of gene trees. We feel that this approach supercedes coalescence-based techniques, as it enables us to treat each gene topology as an independent event, and to consider multiplicity in the origin of the kareniacean plastid proteome. We present these data in a new Fig. 2 and S2.

As stated above, these data strongly support monophyly of all three Kareniacean genera. Concerning the potential Chrysochromulinalean plastid signal in our dataset, we have reanalysed our data and quantify a substantial number of trees (220/ 1,418 of plastid-late origin) that specifically place multiple kareniacean genera within the Chrysochromulinales. This figure is more than twice the number (91) that place the kareniaceae with the next most occurrent haptophyte group in our dataset, Isochrysidales. We nonetheless have chosen to no longer present this as a cryptic plastid endosymbiosis, in the absence of clear examples of extant kareniaceae still possessing this plastid, saying purely in the Discussion that “a common ancestor of the studied organisms either possessed a stable plastid or had a long-term symbiotic relationship (e.g., kleptoplastidic) with a haptophyte lineage related to the extant Chrysochromulinaceae” (lines 363-365).

Concerning the phylogenetic placement of each karenicean genus, the majority of our plastid-late trees specifically recover the monophyly of Karenia and Karlodinium. Remarkably, we find that Takayama and Karlodinium only resolve together in 69/ 1,039 plastid-late gene trees in which all three genera are represented, strongly refuting a vertical origin of the haptophyte-derived components of their plastid proteome. This is not due to the Phaeocystales origin of the current Takayama plastid genome, which is found in only 21 of our plastid protein trees. Nonetheless, as the reviewer suggests, the opposite trend (1,505/ 2,804 gene trees grouping Takayama and Karlodinium as monophyletic) was observed amongst plastid-early gene trees, which might reflect a cryptic peridinin plastid shared between these groups. We expand on these results in the Discussion, stating “Many of the plastid-early gene trees copy the organismal topology …this awaits structural confirmation via microscopy” (lines 383-386).

Finally, to enable reviewer comprehension of the relationships shown, we have presented some exemplar topologies of some of the trees previously displayed in the concatenation, provided in a new Fig. S5.2.

For the phylogenetic analysis of plastid genome-derived transcripts, I might be wrong, but I could not find any information on dataset sizes (i.e., the numbers of sites) and evolutionary models for the analyses in the main text nor supplementary document. Although one may see the dataset sizes when looking at the original datasets in the supplementary files, such information is substantial and thus is to be described in the materials and methods section. I am afraid if this analysis was performed with a small dataset size. I would like to know total lengths of the concatenated sequences and especially that for Takayama. The phylogenetic position of Takayama, distantly related to the other kareniaceans, in this tree might be caused by a larger portion of gaps in the Takayama sequences than in the other kareniaceans.

Author response: As noted in our response to Reviewer 2, we have included three new supplementary figures (S16-S18) with statistics on alignment size, length, and average gap percentage distribution. The average and median values of these three measurements do not differ significantly when calculated separately for different organisms. We have clarified in the Methods that the concatenated alignments retained (PhyloFisher, and plastid-encoded genes) were “constructed by IQ-TREE with the LG+C60+F model for the plastid matrices and posterior mean site frequency (PMSF) model (LG+C60+F+G with a guide tree constructed with C20) for PhyloFisher matrix” (lines 630-632).

Moreover, due to lack of the plastid genome sequence of Takayama, no one could confidently identify plastid genome-derived transcripts: some of those could be derived from second, nuclear copies that might be pseudogenes. Otherwise, even if they are plastid-derived, no one can evaluate whether they are transcripts after or prior to RNA editing. I am afraid if the dataset used is comprised of a mixture of edited and non-edited sequences in kareniacean sequences. Either of sequences after or prior to RNA editing, latter of which are identical with DNA sequences, should be consistently used for the phylogenetic analysis. In any case, the plastid genomes are necessary for this analysis, and the authors can easily obtain them by DNAseq as they have the cultures.

Author response: We thank the Reviewer for their insightful response. We agree that understanding the evolution of kareniacean plastid genomes are crucial to understanding their evolutionary history.

We have accordingly, as described above, integrated a new main text Fig. 5 building a concatenated tree of plastid marker genes (psbA, psych, psbD, psaA, rbcL, and 16S rDNA) historically and commonly used to assess the evolutionary origins of fucoxanthin plastids (e.g., Takishita et al., Phycol Res 1999; Dorrell and Howe, PNAS 2012). These sequences were amplified cryopreserved stocks of total RNA and specific primers, amplified by RT-PCR. We have chosen here to use RNA sequences, to account for the presence of plastid RNA editing, which has been shown to play an important role in maintaining sequence identity between kareniaceaen plastids and haptophyte relatives despite a high DNA mutation rate in the former (Jackson et al., MBE 2013; Klinger et al., GBE 2018), rather than DNA sequences for this analysis.

Additionally, we would like to note that while plastid genomes are generally relatively simple to sequence and assemble, this is not the case in Kareniaceae. The existing plastid genome assemblies are partially incomplete and suggest more complex and possibly unstable structures (e.g., involving at least some minicircles in Karlodinium micrum, Espelund et al., PLoS One 2012; Richardson et al., MBE 2014). From personal communication with our colleagues, we are aware of some efforts to sequence additional kareniacean plastid genomes that unfortunately have not yielded satisfactory results and publications to this day. This strongly invites a separate project focused on kareniacean plastid genomes but is vastly out of scope of this study.

As described above, we have obtained striking new results which we are happy to report in the revised manuscript and which suggest even more, so far unnoticed, plastid replacements in the kareniacean lineage. In light of these finding, parts of the Results and Discussion sections have been extensively rewritten, and the schematic models presented in Fig. 8 has been updated to account for the distinct evolutionary origins of the Karlodinium armiger and Takayama helix plastids.

In addition, although I might be wrong, the phylogenomic analysis for plastid-encoded transcripts might be performed with their nucleotide sequences according to the figure title and legend of Figure S4 mentioning "nucleotide phylogenetic matrix" and the file name "plastid_coded_nt_concatenation_files.tar". If so, translated amino acid sequences should be subjected to phylogenetic analysis, to avoid a well-known artifact that is caused by saturation of substitutions at the 3rd codon.

Author response: With the exception of our 16S rDNA trees (in supporting data), all of our trees were generated with conceptual amino acid translations using a standard codon translation table, in accordance with previous studies (e.g., Klinger et al. GBE 2018). We have revised the file and figure names accordingly.

Duplication of an ATP synthase subunit Duplication and relocation of ATP synthase subunit delta seems interesting. In figure S6.4.1, could you clarify why the possible extensions containing signal peptides lack the initiation methionine at N-termini? I wonder they are 5′ UTRs but artifactually detected as signal peptides, if they all indeed lack Met. To evaluate this point, I recommend 5′ RACE followed by transformation into a model organism as performed in previous studies by some of the authors.

Author response: We reinvestigated these sequences more thoroughly using raw nucleotide data and conclude that the evidence for their retargeting to plastids is very weak and the reported extensions more likely represent untranslated regions some of which were falsely predicted as signal peptides. This section was removed from the new version of the manuscript, although we have noted in Supplementary Text 6.4 that: “A targeted HMMER search for possible distant homologs revealed that the distantly related functional analog of this protein in mitochondrial F-type ATP synthase (ATP5D, K02134) is duplicated in all species except Takayama. The additional copies, however, do not possess a detectable plastid-targeting signal and the specific functions of this duplicated subunit remain to be determined” (lines 107-111).

Comparison of transit peptides Amino acid compositions in transit peptides would vary when targeted compartments are different. In complex plastids, there are functionally distinct compartments: lumen, stroma, periplastidal compartment (PPC). Comparison should therefore be conducted separately for lumen-targeted, stroma-targeted and PPC-targeted proteins in order to claim their transit peptides are not conserved.

Author response: We acknowledge that this question was not explored in our analysis. We therefore re-analyzed our datasets taking the inferred sub-plastidial (thylakoid vs other, based on function) localization of the proteins into account. Our results showed no notable differences between these subsets and are reported in supplementary figure S10.

RDS never possessed a stable fucoxanthin plastid Although the authors cite Hehenberger et al. 2019 for that RDS never possessed a stable fucoxanthin plastid, as far as I know, that paper seems not to mention it. Could you let me know where that is mentioned in the paper? Hehenberger et al. instead proposed the retention of non-photosynthetic peridinin plastid.

Author response: We have modified the Results text, noting that we only identify 42 plastid-late proteins shared between RSD and other Kareniaceae, and in the Discussion that these data provide only limited support for a shared fucoxanthin plastid. We further clarify in the Introduction that “In some cases, the co-existence of a new organelle or endosymbiont with a remnant of the ancestral plastid has been proposed” (lines 106-108) and “It has previously been suggested that the RSD retains a non-photosynthetic form of peridinin plastid” (lines 378-379) with regard to the Hehenberger paper.

Regardless of whether Hehenberger et al. mentioned or not, Novák Vanclová et al. propose that RDS never possessed a stable fucoxanthin plastid because, if I understand correctly, they detected no or few haptophyte-derived RDS genes for plastid-targeted proteins of which origins are shared with those of Karlodinium, Karenia, and Takayama. What about the possibility that the last common ancestor of kareniacean dinoflagellates possessed a fucoxanthin plastid in addition to peridinin plastid followed by almost complete losses of those haptophyte-derived genes after loss of a fucoxanthin plastid in evolution leading to RSD? Free living eukaryotes were appeared to have lost a plastid in recent studies and they have only a few or no genes showing evidence of a plastid previously retained. We cannot rule out that an ancestor of kareniacean dinoflagellates possessed both of peridinin and fucoxanthin plastids, as the authors mention in the main text, and either plastid was inherited to each lineage by differential losses. Accordingly, I would say Fig. 7 is a too much strong proposal as alternative hypotheses are still present. They should be introduced equally.

Author response: We thank the reviewer for this comment. As discussed above, we evaluate the possibility of a cryptic peridinin plastid shared in different kareniaceae, which is suggested at a genetic level by our data but awaits structural confirmation.

We agree that alternative hypotheses may be invoked for the origins of the current kareniacean plastids, and have modified our Fig. 8 to present three alternative possibilities: serial transfer, independent acquisition, and coexistence of an ancestral peridinin and fucoxanthin plastid, as the reviewer suggests. The presence of an ancestral fucoxanthin plastid that was subsequently replaced in Takayama and Karlodinium armiger is strongly suggested by the monophyly of the plastid-late signal across all kareniacean species studied, except RSD. We nonetheless feel that the frequent monophyletic placement of the Karenia and Karlodinium micrum plastids to the exclusion of Takayama in our plastid-late gene trees strongly argues against a vertical inheritance of this plastid from the common kareniacean ancestor, and more likely reflects a serial transfer between the Karenia and Karlodinium / Takayama branches. We have evaluated the evidence for and against each hypothesis in the Discussion and in the Fig. 8 legend.

rRNA copy numbers in dinoflagellates It is known that the rRNA gene copy number varies among populations or strains in dinoflagellates; some possess several dozens of times as many rRNA gene copies as others (Galluzzi et al. 2010). Is it informative to see the ocean wide rRNA gene amplicon data for the kareniacean dinoflagellates? The numbers of rRNA gene-derived reads would not necessarily reflect the cell abundance of dinoflagellates.

Galluzzi et al. 2010. Analysis of rRNA gene content in the Mediterranean dinoflagellate Alexandrium catenella and Alexandrium taylori: implications for the quantitative real-time PCR-based monitoring methods. J Appl Phycol 22:1-9

Author response: We thank the reviewer for raising this point. The exploration of Kareniaceae distribution was intended primarily to investigate their respective ecological relevance in terms of niche diversity, in particular compared with the well-known cosmopolitan patterns of haptophytes, rather than comparing their abundance patterns. We feel that our approach, treating each Kareniacean genus independently, is sufficient for this, but have now clarified in the Results that the different abundances observed “may be biased by the different ribosomal DNA copy numbers in different genera” (lines 330-331) and have cited the reference the reviewer has kindly supplied.

We further note in the Discussion that “It will therefore be worthwhile in the future to assess the distributions of other more recently developed marker genes (Penot et al., 2022; Pierella Karlusich et al., 2023)” (lines 371-372).

Minor points

1. the dataset size for the 241 protein-based host phylogeny should also be described in the main text. Author response: The information (72,162 positions241 genes, removal of sequences with >66% gaps) has been included in the Materials and Methods.

The authors mention in Discussion "Thus, our results illuminate the mechanistics of a fundamental process that may under pin vast tracts of chloroplast evolution". If I understand correctly, I think this is based on "shopping bag model" when considering plastid replacements in dinoflagellates. It is helpful to add more details to clarify why the authors would like to claim so. "Chloroplast" should be replaced with "plastid".

Author response: We agree that the term plastid is more appropriate in this context, and have used it globally throughout the manuscript. We have mentioned once in the Introduction “primary plastids, i.e. chloroplasts” to orient the non-specialist reader.

We have elaborated on our definition of the Shopping Bag model, and the specific importance of the Kareniaceae, in the Discussion: “The idea that individual genes encoding plastid-targeted proteins may exhibit evolutionary affiliation with other groups than the plastid donor, typifying the “shopping bag” model (Larkum et al., 2007), is well-established in many plastid lineages” (lines 350-352).

Nonetheless, we feel that our data are in many ways different to those previously observed in other plastid lineages. This may reflect that the kareniacean plastid has undergone one, and potentially multiple, recent replacement events. Nonetheless, the predominant contribution of the host to the plastid proteome is striking, which we elaborate in the Discussion: “Our data show that the dinoflagellate host was the principal contributor of nucleus-encoded proteins supporting the kareniacean plastid proteome” (lines 352-353).

Supplementary document S6.6 I found the term nitrogen fixation, but should this be replaced with "nitrogen assimilation"?

Author response: We have corrected the text as requested.

Figure S5 For those LGTs, all the trees should be shown in supplementary text as they are only 11 or 12 trees. Especially, please add the chlorophyllide b reductase and chlorophyllase in the figure.

Author response: Trees for all laterally transferred genes mentioned in the text have been provided among supplementary figures (S7.1-10).

References I am not picky about a format of the reference list, but I think it should be consistent throughout the list. I recommend adding journals, volumes, and pages precisely for cited papers. I found lack of them at least in Novak Vanclova et al. and Pierella Karlusich et al.

Author response: We corrected the incomplete citations and will perform a complete reformatting of the references to comply with the requirements of a concrete affiliate journal.

Figures In figure 3, I strongly recommend adding RDS data, while distinguishing them by another color if they are derived from different origins from those of Karenia, Karlodinium, and Takayama. This would make the authors claim clearer that there are few haptophyte-derived genes for plastid targeted proteins of which origins are shared with those of the other kareniacean dinoflagellates.

Author response: We believe the comparison to RSD is not among the main stories of our study and adding this dimension to the already complex discussion and metabolic map schematic would compromise the overall clarity. This point is already noted by Reviewer 1 (above). However, this question may indeed be asked by some readers, therefore we decided to include the results for RSD as an additional column in the supplementary table S3 and as an additional graphical element in the supplementary version of the map schematic (figure S8). Per the reviewer’s comments above, we have further stated the number of plastid-late trees shared (42) between the RSD and other kareniaceae in the Results text.

In figures S5.1-2 showing LGTs, I found two paralogs of kareniacean dinoflagellates. What does "CP" mean? If "CP" means ChloroPlast-targeted, both paralogs of K. brevis in HARS and those of K. micrum are of plastid-targeted in TARS and they do not have cytosolic ones. I am afraid if these cases are caused by false positives of detection for plastid-targeted proteins by PredSI and ChloroP. Similarly, in figure S5.4, I found two distant paralogs of heam oxygenase in the tree and the taxon names for both types in kareniaceans include "CP." Are both targeted to the plastids or of false positives?

Author response: The annotation with “CP” and darker colour denotes proteins that were predicted as plastid-targeted by our pipeline. We have clarified in supporting text 6.8 that we investigated our aminoacyl-tRNA synthetases for possible dual targeting to both plastid and mitochondria but found no evidence for it.

We have searched the K. brevis SP3 HARS sequence (CAMPEP-0189291366) by CD-search and note that the conserved domain (underlined) starts at residue 24 after the first predicted methionine (bold), which is inconsistent with the probable length a plastid-targeting sequence, and we have noted in the figure legend that this is likely to represent a false positive.

CAMPEP_0189291366_Karenia-brevis-SP3-20130916

SWLVLLAFALTTPGPVVAVSATILRGLLVGLQRPCAAALRLSCCAATRALPLPGASELGSRFAAAAASSAR__M__GKEGKKKEDGKKKKDETKTEKLIGLEPPSGTRDFFPAEMRQQRYIFNKFRETANLYGFQEYDAPVLEHQELYIRKQGEEITDQMYSFDDKEGAKVTLRPEMTPTLARMVLNLMRVETGEMAAQLPLKWFSIPQCWRFETTQRGRKREHYQWNMDIVGVTSIYAEAELLSAICNFFESVGITSKDVGLRVNSRKVLNAVTKLAGVPDDRFAETCVIIDKLDKIGAEAVKTEMREKIGLPEEVGERIVKATGAKSLEEFADLAGVGQNNPEVLELKHLFELAEDYGYGDWLIFDASVVRGLGYYTGVVFEGFDRAGVLRAICGGGRYDRLLTKFGSPKEIPCVGFGFGDCVIAELLKEKGVTPSLPEHIDFVVAAFNSEMMGKAMNAARRLRLGGKSVDIFTEPGKKVGKAFNYADRVGADMVAFIAPDEWAKGLVRIKALRMGQDVPDDQKQKDVPLEDLANVDSYFGLAPAAAPVMSAAPAASTVKSTAPALAVPAAAKASAPKAAAPSGTGADVEAFLVDHPYVGGFRPCARDRTLFDELRLTSGRPSTPALGRWYDHIDSFPAVVRASWC

The green HARS sequences (including that of Karenia brevis SP1) in contrast typically have conserved domains starting after residues 50-60, and are likely to be genuinely plastid-targeted. Reflecting that the automated prediction approach used within our dataset may contain other such false positive results (c.f., Fig. S18), we have chosen for tree-sorting and pathway reconstruction analyses to only consider genes in which we can identify plastid-targeted homologues of the same inferred phylogenetic origin in at least two distinct Kareniacean genera (Figs. 2, 3).

For the Karlodinium micrum TARS sequence we have identified a second TARS sequence (CAMPEP_0200847158) that is of apparent dinoflagellate origin and lacks a credible targeting sequence, and have updated the tree accordingly.

In the case of heme oxygenases, we are convinced that (at least) two paralogs of distinct origins are indeed plastid targeted. The presence of multiple copies of this enzyme has been noticed in other organisms including some plants (e.g., Dammeyer and Frankenberg-Dinkel, Photochemical & Photobiological Sciences, 2008) and may be reflective of functional specialization or regulation / expression under different conditions. We have discussed this in the supporting text 6.1: “Two evolutionarily distinct versions of the biliverdin-producing haem oxygenase seem to be present …the specific metabolic functions of the green- and haptophyte-like haem oxygenases in the fucoxanthin plastid await experimental characterisation.” (lines 52-58).

Reviewer #3 (Significance (Required)):

Significance

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

This study by Novak Vanclova et al. provide new transcriptome datasets from multiple species in kareniacean dinoflagellates including harmful and toxic species. Their transcriptome datasets would help understand their biology, evolution, and ecology. The authors also provide a program that predicts plastid proteomes in those dinoflagellates, which would be useful for future studies to focus on kareniacean dinoflagellate plastids, after further refinement. The most important aspect of this study is that many plastid-targeted proteins might be derived from a particular haptophyte lineage, although it is still not sure whether they are derived from LGTs or EGTs. Phylogenetic analyses performed in this study should be improved by adding some plastid genomes, in order to gain more conclusive results. In addition to methods, interpretation of the current results and proposals on plastid evolution should be toned-down.

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

Although there are technical issues, this study improves our conceptual understanding the plastid proteome evolution in Kareniacean dinoflagellates. The plastid proteomes are comprised of proteins with more various origins in those dinoflagellates, suggesting more complex plastid proteome evolution than previously thought.

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

This study seems to be "basic research".

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

algal evolution, eukaryotic evolution, mitochondrial metabolisms, plastid metabolisms, phylogenomics

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Referee #3

Evidence, reproducibility and clarity

Summary

This manuscript entitled "Divergent and diversified proteome content across a serially acquired plastid lineage" by Novak Vanclova et al. proposes the origin and evolution of plastids in kareniacean dinoflagellates. The authors generated new transcriptome data from Karenia mikimotoi, Karenia papilionacea, Karlodinium micrum, Karlodinium armiger, and Takayama helix. Combining them to the previously published transcriptome data from kareniacean dinoflagellates, they constructed the pan-kareniacean transcriptome library. They surveyed plastid-targeted protein-coding transcripts in the dataset, and consequently they estimated ~14.5% of the transcriptome data were of plastid-targeted ones. Of them, 65-80% were derived from a peridinin-containing dinoflagellate ancestor while ~15% were derived from EGTs from a haptophyte endosymbiont of the current plastid origin. By using the plastid-targeted transcript dataset, they investigated 1) origins of the plastid-targeted protein-coding transcripts by single gene-trees, 2) the plastid origin and evolution by the multigene dataset of 22 conserved plastid-targeted protein-coding transcripts and of 3) plastid genome-derived transcripts, 4) plastid functions, 5) diversity of plastid-targeted signals in kareniacean dinoflagellates, and 6) the distributions of kareniacean species by using the Tara Oceans database. On the basis of their results, they proposed many hypotheses regarding kareniacean dinoflagellate evolution, such as i) the chrysochromulinales-origin of the plastids, ii) more recent acquisition of the plastid than previously thought, iii) a plastid replacement within kareniaceae evolution, iv) the strict selection of signal peptides but non-conserved transit peptides in the kareniacean plastid-targeted proteins, and v) correlated or non-correlated distribution patterns of kareniaceaen dinoflagellates to specific haptophyte lineages.

Although their proposals are interesting, I have many concerns to be addressed. Especially, their analyses on which the above proposals are based seem to be still preliminary and inconclusive. To support their proposals more confidently, I also suggest some additional analyses.

Major comments

1. seemingly inconsistency between the authors' claims The most striking is inconsistency of the authors' claims proposed in this manuscript. Their proposals include a) the common ancestor of kareniaceans has not possessed a fucoxanthin plastid but the plastid has been acquired more recently, b) an ancestor of Takayama and Karlodinium has gained a fucoxanthin plastid from a (chrysochlomulinales) haptophyte, c) an ancestor of Karenia has gained a fucoxanthin plastid from Karlodinium.

However, they also demonstrate a higher proportion of plastid-late proteins in Karenia than Karlodinium and Takayama. If I understand correctly, "a higher proportion of plastid-late proteins in Karenia than Karlodinium and Takayama" would seemingly be inconsistent to and challenge two of the authors' claims: no haptophyte-derived plastid in the common ancestor of kareniacean dinoflagellates and a Karlodinium-to-Karenia plastid transfer (Fig. 7). If the Karenia plastid is derived from Karlodinium, I have no idea why haptophyte-derived plastid proteome of Karenia is larger than that of Karlodinium. After the plastid acquisition in Karenia, Karenia might have gained more genes for plastid-targeted proteins from haptophytes by LGTs. If this is true, many single gene trees would suggest different origins of plastid-targeted proteins between Karenia and Karlodinium/Takayama. Can we see it in the single gene analyses? I would like authors to rationalize the inconsistency in the main text. 2. Signal peptide prediction I think the modified ASAFind would be greatly helpful for future studies on automatic prediction of plastid proteomes in kareniacean dinoflagellates. However, I found no data on selection criteria for the signal peptide prediction program SignalP5.0 used. I believe such data would be very important to interpret the previously published paper by Gruber et al. in which prediction methods for plastid-targeting sequences are compared to each other to see how sensitively and specifically they can capture the plastid proteomes.

Gruber et al. 2020. Comparison of different versions of SignalP and TargetP for diatom plastid protein predictions with ASAFind.

According to Gruber et al. (2020), signalP5.0 is not suitable for prediction of signal peptides for diatoms, in consistent with the authors' claim for kareniacean dinoflagellates. This inconsistency would be difference of the nature in signal peptides between diatoms and kareniacean dinoflagellates. Even if so, it would be useful to see quantitatively how much different their signal peptides are in terms of their suitable prediction programs.

I also have a concern about use of the combination of PrediSI and ChloroP, combination which is suitable for the plastid proteome prediction in Euglena gracilis. The authors should rationalize why the method for Euglena plastids can be applicable without any modification to the plastid proteome prediction in kareniacean dinoflagellates. Although Euglena plastids are enclosed by three membranes, kareniacean plastids are by four. Therefore, from the side of molecular mechanisms in protein import, the method suitable for Euglena plastids is not necessarily suitable for kareniacean dinoflagellate plastids. By using PrediSI and ChloroP, they detected additional "candidate plastid proteomes" including several proteins not detectable by SignalP5.0 and the modified ASAFind. That seems great. However, they did not seem to consider false positives since there is no mention on it. Although the additional candidates predicted by PrediSI and ChloroP included true plastid proteins of kareniacean dinoflagellates, many might not be. Nevertheless, the authors suggest 7.5 to 14.5% in K. micrum and K. brevis, respectively, are of plastid-targeted ones. I am so afraid if the proportions would be highly overestimated due to false positives by PrediSI and ChloroP. To rationalize the use of PrediSI and ChloroP, the authors should show sensitivity and specificity by quantitative analyses with a benchmark dataset. 3. Origin and evolution of kareniacean plastids The authors suggest the chrysochromulinales origin of the kareniacean dinoflagellate plastids and the Karlodinium-to-Karenia plastid transfer, on the basis of phylogenetic analyses using the concatenated datasets with the 22 conserved plastid-targeted proteins and with plastid-genome derived transcripts. It is very interesting that those plastid-targeted proteins in kareniacean dinoflagellates might be phylogenetically closely related to chrysochromulinales haptophyte I have suggestions on the analyses and interpretation

As the 22 analyzed genes are nuclear-encoded plastid targeted genes, they are a quite small portion of entire plastid proteins. I am not convinced by that evolution of the small number of genes reflects evolution of fucoxanthin plastids of which proteomes are comprised of >1000 proteins. How many genes for haptophyte-derived plastid-targeted proteins suggest the monophyly of kareniaceaen dinoflagellates and chrysochromulinales haptophytes should be investigated by, for example, a coalescence-based analysis such as Astral for all the detected haptophyte-derived plastid-targeted proteins including the 22 genes. This is because the monophyly could be reconstructed only by one or few, limited number of proteins even if the concatenated dataset is analyzed.

Relevant to this, plastid-targeted proteins derived from a peridinin-containing ancestor might still have phylogenetic signals of host evolution. I am interested in whether such analyses with peridinin plastid-derived plastid-targeted proteins reconstruct Takayama and Karlodinium as monophyletic but separate Karenia from them, as suggested in the phylogenomics with non-plastid proteins.

For the phylogenetic analysis of plastid genome-derived transcripts, I might be wrong, but I could not find any information on dataset sizes (i.e., the numbers of sites) and evolutionary models for the analyses in the main text nor supplementary document. Although one may see the dataset sizes when looking at the original datasets in the supplementary files, such information is substantial and thus is to be described in the materials and methods section. I am afraid if this analysis was performed with a small dataset size. I would like to know total lengths of the concatenated sequences and especially that for Takayama. The phylogenetic position of Takayama, distantly related to the other kareniaceans, in this tree might be caused by a larger portion of gaps in the Takayama sequences than in the other kareniaceans. Moreover, due to lack of the plastid genome sequence of Takayama, no one could confidently identify plastid genome-derived transcripts: some of those could be derived from second, nuclear copies that might be pseudogenes. Otherwise, even if they are plastid-derived, no one can evaluate whether they are transcripts after or prior to RNA editing. I am afraid if the dataset used is comprised of a mixture of edited and non-edited sequences in kareniacean sequences. Either of sequences after or prior to RNA editing, latter of which are identical with DNA sequences, should be consistently used for the phylogenetic analysis. In any case, the plastid genomes are necessary for this analysis, and the authors can easily obtain them by DNAseq as they have the cultures.

In addition, although I might be wrong, the phylogenomic analysis for plastid-encoded transcripts might be performed with their nucleotide sequences according to the figure title and legend of Figure S4 mentioning "nucleotide phylogenetic matrix" and the file name "plastid_coded_nt_concatenation_files.tar". If so, translated amino acid sequences should be subjected to phylogenetic analysis, to avoid a well-known artifact that is caused by saturation of substitutions at the 3rd codon. 4. Duplication of an ATP synthase subunit Duplication and relocation of ATP synthase subunit delta seems interesting. In figure S6.4.1, could you clarify why the possible extensions containing signal peptides lack the initiation methionine at N-termini? I wonder they are 5′ UTRs but artifactually detected as signal peptides, if they all indeed lack Met. To evaluate this point, I recommend 5′ RACE followed by transformation into a model organism as performed in previous studies by some of the authors. 5. Comparison of transit peptides Amino acid compositions in transit peptides would vary when targeted compartments are different. In complex plastids, there are functionally distinct compartments: lumen, stroma, periplastidal compartment (PPC). Comparison should therefore be conducted separately for lumen-targeted, stroma-targeted and PPC-targeted proteins in order to claim their transit peptides are not conserved. 6. RDS never possessed a stable fucoxanthin plastid Although the authors cite Hehenberger et al. 2019 for that RDS never possessed a stable fucoxanthin plastid, as far as I know, that paper seems not to mention it. Could you let me know where that is mentioned in the paper? Hehenberger et al. instead proposed the retention of non-photosynthetic peridinin plastid. Regardless of whether Hehenberger et al. mentioned or not, Novák Vanclová et al. propose that RDS never possessed a stable fucoxanthin plastid because, if I understand correctly, they detected no or few haptophyte-derived RDS genes for plastid-targeted proteins of which origins are shared with those of Karlodinium, Karenia, and Takayama. What about the possibility that the last common ancestor of kareniacean dinoflagellates possessed a fucoxanthin plastid in addition to peridinin plastid followed by almost complete losses of those haptophyte-derived genes after loss of a fucoxanthin plastid in evolution leading to RSD? Free living eukaryotes were appeared to have lost a plastid in recent studies and they have only a few or no genes showing evidence of a plastid previously retained. We cannot rule out that an ancestor of kareniacean dinoflagellates possessed both of peridinin and fucoxanthin plastids, as the authors mention in the main text, and either plastid was inherited to each lineage by differential losses. Accordingly, I would say Fig. 7 is a too much strong proposal as alternative hypotheses are still present. They should be introduced equally. 7. rRNA copy numbers in dinoflagellates It is known that the rRNA gene copy number varies among populations or strains in dinoflagellates; some possess several dozens of times as many rRNA gene copies as others (Galluzzi et al. 2010). Is it informative to see the ocean wide rRNA gene amplicon data for the kareniacean dinoflagellates? The numbers of rRNA gene-derived reads would not necessarily reflect the cell abundance of dinoflagellates.

Galluzzi et al. 2010. Analysis of rRNA gene content in the Mediterranean dinoflagellate Alexandrium catenella and Alexandrium taylori: implications for the quantitative real-time PCR-based monitoring methods. J Appl Phycol 22:1-9

Minor points

1. the dataset size for the 241 protein-based host phylogeny should also be described in the main text.
2. The authors mention in Discussion "Thus, our results illuminate the mechanistics of a fundamental process that may under pin vast tracts of chloroplast evolution". If I understand correctly, I think this is based on "shopping bag model" when considering plastid replacements in dinoflagellates. It is helpful to add more details to clarify why the authors would like to claim so. "Chloroplast" should be replaced with "plastid".
3. Supplementary document S6.6 I found the term nitrogen fixation, but should this be replaced with "nitrogen assimilation"?
4. Figure S5 For those LGTs, all the trees should be shown in supplementary text as they are only 11 or 12 trees. Especially, please add the chlorophyllide b reductase and chlorophyllase in the figure.
5. References I am not picky about a format of the reference list, but I think it should be consistent throughout the list. I recommend adding journals, volumes, and pages precisely for cited papers. I found lack of them at least in Novak Vanclova et al. and Pierella Karlusich et al.
6. Figures In figure 3, I strongly recommend adding RDS data, while distinguishing them by another color if they are derived from different origins from those of Karenia, Karlodinium, and Takayama. This would make the authors claim clearer that there are few haptophyte-derived genes for plastid targeted proteins of which origins are shared with those of the other kareniacean dinoflagellates. In figures S5.1-2 showing LGTs, I found two paralogs of kareniacean dinoflagellates. What does "CP" mean? If "CP" means ChloroPlast-targeted, both paralogs of K. brevis in HARS and those of K. micrum are of plastid-targeted in TARS and they do not have cytosolic ones. I am afraid if these cases are caused by false positives of detection for plastid-targeted proteins by PredSI and ChloroP. Similarly, in figure S5.4, I found two distant paralogs of heam oxygenase in the tree and the taxon names for both types in kareniaceans include "CP." Are both targeted to the plastids or of false positives?

Significance

General assessment: provide a summary of the strengths and limitations of the study. What are the strongest and most important aspects? What aspects of the study should be improved or could be developed?

This study by Novak Vanclova et al. provide new transcriptome datasets from multiple species in kareniacean dinoflagellates including harmful and toxic species. Their transcriptome datasets would help understand their biology, evolution, and ecology. The authors also provide a program that predicts plastid proteomes in those dinoflagellates, which would be useful for future studies to focus on kareniacean dinoflagellate plastids, after further refinement. The most important aspect of this study is that many plastid-targeted proteins might be derived from a particular haptophyte lineage, although it is still not sure whether they are derived from LGTs or EGTs. Phylogenetic analyses performed in this study should be improved by adding some plastid genomes, in order to gain more conclusive results. In addition to methods, interpretation of the current results and proposals on plastid evolution should be toned-down.

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

Although there are technical issues, this study improves our conceptual understanding the plastid proteome evolution in Kareniacean dinoflagellates. The plastid proteomes are comprised of proteins with more various origins in those dinoflagellates, suggesting more complex plastid proteome evolution than previously thought.

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

This study seems to be "basic research".

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

algal evolution, eukaryotic evolution, mitochondrial metabolisms, plastid metabolisms, phylogenomics

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Reply to the reviewers

We would like to thank all reviewers for their careful evaluation of our manuscript and their thoughtful feedback, which we could use to improve its quality significantly.

Reviewer #1 (Evidence, reproducibility and clarity):

Summary: This study addresses the problem of what is the optimal ribosome composition in terms of relative RNA and protein content, to ensure optimal growth rate and minimal energy waste. The RNA-world hypothesis suggests that primitive ribosomes were RNA-only objects, and in fact this would appear to be very advantageous from an energetic point of view, since RNA synthesis requires a much lower energy expenditure than protein synthesis. Yet a large fraction of present-day ribosome mass is protein, ranging from 30% to nearly 70% depending on the organism. The authors hypothesize that one of the main functions of ribosomal proteins is to stabilize the RNA and to protect it against degradation. According to their idea, the fast degradation of a protein-free rRNA would offset the energetic advantage given by its cheaper synthesis. To test the hypothesis, they developed a mathematical model whereby to evaluate the optimal ribosome composition under a number of different conditions.

Major comments: The paper is well-written and very readable. I am not an expert of mathematical modelling, so I cannot go into the details of the model presented. As a biologist, I can say that the conclusion arrived at are reasonable and well-justified.

We thank the reviewer for the positive evaluation.

Perhaps the point of view is rather narrow, since ribosomal proteins are known to be important not only for RNA protection and ribosome stability, but also to ensure the accuracy of decoding and, in certain contexts, to allow the ribosomes to interact with other cellular ligands. The authors make only very slight reference to these questions, so it would be worthwhile to further comment on them.

Thank you for your suggestion. To address it, we expanded the discussion as follows:<br /> "Finally, we need to consider that ribosomal proteins may play other roles in the cells, especially in eukaryotic organisms. Ribosomal proteins participate in translation processes, for example, binding of translation factors, release of tRNA, and translocation. They may also affect the fidelity of translation (Nikolay et al., 2015). Furthermore, they play roles in various cellular processes such as cell proliferation, apoptosis, DNA repair, cell migration and others (Kisly and Tamm, 2023). These additional functions might have conferred evolutionary fitness advantages. Nevertheless, the primary role of ribosomal proteins seems to be stabilization and folding of rRNA (Nikolay et al., 2015; Kisly and Tamm, 2023)."

Furthermore, their explanation of why ribosome composition should be so different in different organisms (e.g. protein-poor bacterial ribosomes versus protein-rich archaeal ones) is not entirely convincing. For instance, they suggest that archaea may have protein-richer ribosomes than bacteria because they live in extreme environments, thus needing a further aid to stabilize the organelle. While this may be a factor, one must point out that non-extremophilic archaea (e.g. methanogens) have protein-rich ribosomes, making it obvious that other factors must be at play.<br />

We appreciate the reviewer's feedback. Ribosome composition is indeed complex and influenced by various factors. While extreme environments (may) contribute to protein-rich ribosomes in archaea, it's important to note that not all archaea share this characteristic. Some, like Halobacteriales, Methanomicrobiales, and Methanobacteriales, have ribosomes with protein content similar to bacteria.

Furthermore, there are species in both archaea and bacteria with low protein content in their ribosomes despite extreme habitats. This suggests that alternative strategies, possibly involving specific sequence variants in the rRNA (Nissley et al., 2023), play a role in stabilizing ribosomes. In our model, these findings would correspond to a decreased kdegmax. However, these sequence variants are not universal.

Amils et al. (1993) suggest that protein-rich ribosomes in archaea are (more) ancient and proteins may have been lost in some species, possibly to favor higher growth rates (and in agreement with our theoretical analysis). An intriguing avenue for further research would be a phylogenetic analysis of archaeal evolution to investigate the emergence of different ribosome compositions.

To address your concerns, we added the following paragraph to the discussion:<br /> "Additionally, some extremophilic organisms, such as the bacteria Chloroflexus aurantiacus or Fervidobacterium islandicum, exhibit ribosomes with lower protein content (approximately 40%) compared to extremophilic archaea (50%). It has been suggested that protein-rich ribosomes can be traced back to the oldest phylogenetic lineages, with some ribosomal proteins being lost over time (Amils et al., 1993; Acca et al., 1993). Organisms with lower protein content in their ribosomes may have evolved alternative strategies to thrive in extreme conditions. Examples of such strategies include the presence of specific rRNA sequence variants or base modifications, as recently discussed by Nissley et al. (2023).

Moreover, certain archaeal species, such as those from Methanobacteriales or Halobacteriales, have transitioned to milder environmental conditions and subsequently shed unnecessary ribosomal proteins (Acca et al., 1993; Amils et al., 1993).

To gain a comprehensive understanding of ribosome evolution in response to changing conditions, a thorough phylogenetic analysis is warranted. This analysis should be complemented by measurements of growth rate, translation rate, RNA degradation rate, among other parameters, to delineate the order of protein loss or gain, and the emergence of sequence variations and base modifications."

Minor comments: none in particular. Referencing is adequate, text is clear and the figures are clear and well-organized.

Thank you.

Reviewer #1 (Significance):

As I stated above, the main weakness of this study may be that it concentrates overwhelmingly on a single problem, i.e. the energetic cost of adding proteins to an RNA-only ancestral ribosome. On the other hand, this is a question seldom addressed when talking about ribosome composition, which indeed makes this paper valuable and interesting. The authors expand and advance a previous study of the same kind (to which they make ample reference).

Although rather specialized, I think this paper, in its general conclusions, may be of interest to most of those working in the field of protein synthesis and ribosome evolution.

Referee's keywords: archaea, ribosome evolution, translation, translation initiation

Reviewer #2 (Evidence, reproducibility and clarity):

The authors explore a mathematical model to rationalize the variable RNA content in ribosomes across species. The mathematical model particularly considers the idea that the protein-to-RNA ratio in ribosomes emerges as a consequence of faster rRNA than r-protein synthesis coupled with a faster degradation of rRNA. This is an interesting analysis. The idea is well explained and the math of the model is overall well explained. Overall, I thus support publication of this analysis.

We thank the reviewer for the positive evaluation.

However, while reading the manuscript I was continuously wondering about two major aspects which, I suggest, should be considered more prominently in the text:

1. How clear is it that rRNA is more unstable than r-protein?
2. Why should the translation rate (the speed with which ribosomes assemble new proteins) not be highly dependent on the ribosome-to-protein ratio (with some intermediate ratio ensuring efficient synthesis and efficient translation?

Currently these points are considered briefly in the discussion part. I suggest that these points should at least be discussed more prominently in the introduction. I further appreciate any more detailed thoughts the authors have on these questions.

Finally, I think the discussion section would benefit strongly from a more detailed consideration of possible future experiments. Which data is needed to probe the idea? What types of experiments could be performed to probe the model.

We added a paragraph to the discussion with suggestions for experiments:<br /> "There are still many open questions about ribosome biogenesis and evolution. Our model could guide future experiments. There are a few studies that assessed the effect of individual rP deletions in E. coli, for example mutation in S10 increased RNA degradation (Kuwano et al., 1977), and mutation in L6 lead to disrupted ribosomal assembly (Shigeno et al., 2016). A systematic knock-out screen of all ribosomal proteins could be done (as in Shoji et al. (2011)), complemented with quantification of RNA degradation and misfolding.

In case of extremophilic organisms with protein-rich ribosomes, temperature sensitivity could also be assessed. We would expect that deletion of the extra proteins would cause growth defects only at high temperatures.

Furthermore, after removal of proteins from archaeal protein-rich ribosomes, laboratory evolution could be performed to see whether growth rate increases beyond wild-type.

Comprehensive datasets, akin to the work of Bremer and Dennis in 2008 for E. coli, should be generated for non-standard organisms by measuring various parameters such as transcription and translation rates, ribosome and RNAP activities, and other relevant factors.

Finally, as mentioned earlier, phylogenetic analysis or ribosome evolution across different species and environments could be done."

More detailed comments:

Regarding i: rRNA is pretty stable compared to other RNA types in the cell. The authors argue it is unstable. The specific question then seems to become how stable rRNA is compared to r-protein? Generally, proteins are also stable, but what data is available to support that r-proteins are more stable than rRNA?

While rRNA that is already integrated into a ribosome is stable, nascent RNA may be susceptible to degradation (Jain, 2018). It has been observed that even during exponential growth, some rRNA is degraded (Gausing, 1997; Jain 2018) and the degradation rate increases if ribosome assembly is delayed (Jain, 2018). This suggests that rRNA that is synthesized in excess cannot be stored and used later. Furthermore, when rRNA is overexpressed in excess of rPs, it is rapidly degraded (half life 15-70 min) (Siehnel and Morgan, 1985).

On the other hand, the turnover of proteins is negligible (Bremer and Dennis 2008), and most ribosomal proteins can exist in a free form without RNA. For example, under starvation/in stationary phase, rRNA is degraded, but most proteins are stable and can be reused later (Reier et al., 2022; Deutscher, 2003).

The precise mechanisms of the rRNA instability are not clear. The simplest explanation is that rRNA that is not protected by rPs is attacked by RNases. Another option is that rRNA without proteins is difficult to fold and can get trapped in misfolded states. These are then degraded as a part of quality control. The model developed in this paper allows for both of these mechanisms.

We added these references to the discussion:<br /> "In order to explain a mixed (RNA+protein) ribosome, we consider rRNA degradation in our extended model, thereby increasing the costs for RNA synthesis. While rRNA that is already integrated into a ribosome is stable, nascent RNA may be susceptible to degradation (Jain, 2018). Indeed, it has been experimentally observed that even at maximum growth rate, 10% of newly synthesized rRNA is degraded (Gausing, 1977), and the degradation rate increases if ribosome assembly is delayed (Jain, 2018). Furthermore, when rRNA is overexpressed in excess of rPs, it is rapidly degraded (Siehnel and Morgan, 1985). Due to the extremely high rates at which rRNA is synthesized, errors become inevitable, necessitating the action of quality control enzymes such as polynucleotide phosphorylase (PNPase) and RNase R to ensure ribosome integrity (Dos Santos et al., 2018). The absence of the RNases results in the accumulation of rRNA fragments, ultimately leading to cell death (Cheng and Deutscher, 2003; Jain, 2018).

In contrast, protein turnover is negligible (Bremer & Dennis, 2008), and most ribosomal proteins can exist without rRNA and can be reused (Reier et al., 2022; Deutscher, 2003). Therefore, we do not consider protein degradation in our model."

Regarding ii: Building on their model results, the authors rationalize the highly varying RNA-to-protein ratio in ribosomes across species. The model considers a non-varying rate with which ribosomes synthesize new proteins. This is briefly discussed in the discussion section. However, this appears to be a major assumption that, I think, should be stated clearly stated earlier in the text, including the abstract and introduction. Second, I wonder how the authors then rationalize variations in translation rate across species. Translation rates and the speeds with which ribosomes are varying strongly across species (indicated for example well by the change in the slope between ribosome content/rRNA and growth rate - slope in Fig. 2A). Why could the rRNA-to-protein ratio not be important in playing a role here?

We decided not to consider the effect of rRNA/protein ratio in ribosomes on translation rate mainly because it is not clear in what way it affects it. Proteins are better catalysts than rRNA. Yet, eukaryotic ribosomes which have higher protein content, have lower translation rates. For archaea and mitochondria, we were not able to find data but it is unlikely that the translation rates are faster because the growth rates are not faster.

We added a paragraph to the introduction that explains our assumption:<br /> "We focus on the primary role of ribosomal proteins, which is stabilizing rRNA (by preventing its degradation or misfolding).

Ribosome protein content might also affect other parameters, such as translation rate. Proteins are generally better catalysts than RNA (Jeffares et al., 1998), but the ribosome's catalytic core is formed by rRNA (Tirumalai et al., 2021) and operates at a relatively slow catalytic rate compared to typical enzymes. This suggests that there is little evolutionary pressure to increase the catalytic rate. Furthermore, ribosomes with the lowest protein content, like the E. coli ribosome, exhibit the highest translation rates (Bonven and Gulløv, 1979; Hartl and Hayer-Hartl, 2009; Bremer and Dennis, 2008). Therefore, we do not consider the impact on translation rate in this study."

And a sentence to the abstract:<br /> "In this study, we develop a (coarse-grained) mechanistic model of a self-fabricating cell and validate it under various growth conditions. Using resource balance analysis (RBA), we examine how the maximum growth rate varies with ribosome composition, assuming that all kinetic parameters remain independent of ribosome composition."

More minor point, but I was also not sure about the justification that ribosome mass is constant (line 111). The mass of an amino acid and a nucleotide is quite different. Why should overall mass matter, and not for example the number of amino acids and proteins. I think it also would be good here to motivate the assumption better early on instead of commenting on it in the discussion section.

Thank you for your suggestion. We agree with the reviewer that we should make our assumption of keeping the ribosome mass constant, which we used for simplicity, clearer from the beginning. Therefore, we have added the following statement to the introduction:<br /> "For simplicity, we assume a constant ribosome mass."

Reviewer #2 (Significance):

Protein synthesis by ribosomes is a major determinant of the rate with which microbes and other fast growing cells accumulate biomass. To better understand cell growth it is thus essential to better understand the makeup of ribosomes. Széliová et al present a mathematical model to entertain the idea that the varying RNA content in ribosomes across species is a consequence of RNA degradation. The model makes clear predictions which can guide future experiments.

Reviewer #4 (Evidence, reproducibility and clarity):

Summary

In this manuscript, Széliová et al. used a simple self-replicating cell model to study why the ribosome consists of both RNA and protein from an economic point of view. Their base model predicts an RNA-only ribosome, which is not surprising since the smaller RNAP has a higher turnover number compared to the larger ribosome. When rRNA instability is included, the model predicts an "RNA+Protein" ribosome. In particular, the predicted ribosome composition is comparable to the measured ribosome composition when strong cooperative binding of ribosomal proteins to rRNA is considered. The authors conclude that the maximal growth rate is achieved by the real ribosome composition when rRNA instability is taken into account.

Major comments:

1. The authors modeled the rRNA degradation rate as a function of the concentration of fully assembled ribosomes (equation 5). However, only partially assembled ribosomes are susceptible to RNase, and they make up only a small fraction of total ribosomes. The majority of ribosomes are fully assembled. In addition, the turnover number obtained from Fazal et al. (2015) and used here is the degradation rate of double-stranded RNA, not the fully assembled ribosomes, which have a stable tertiary structure. In my opinion, the rRNA degradation rate should be modeled as a function of the concentration of partially assembled ribosomes (i.e., pre-R in Figure 7) rather than the concentration of fully assembled ribosomes.

We agree with the reviewer that the way we model the process is not entirely biologically accurate. The problem is that even if we add the assembly intermediates, their concentration would be zero as they do not catalyze any reaction (similarly to the metabolites). Therefore, the degradation rate would also always be zero. Given the current modeling setup, the obvious proxy for the intracellular rRNA concentration is the rRNA concentration in the (assembled) ribosome, c_R*(1-x_rP).

1. Compared to the work by Kostinski and Reuveni (2020), the authors have made an improvement by avoiding the use of constant ribosome allocation to ribosomal protein (Φ_rP^R) and RNAP (Φ_RNAP^R), allowing these parameters to vary with predicted growth rates (by changing 𝑥_rP). This is indeed important, as bacteria are very likely to adjust these parameters in response to different growth conditions. However, certain other growth rate-dependent parameters are still treated as constants (or treated as nutrient-specific parameters) across predicted growth rates under given conditions. For example, experiments have shown that the fraction of active RNAP (f_RNAP^act) and the ribosome elongation rate (k_R^el) are growth rate-dependent (Bremer and Dennis, 1996). In contrast, when the authors predict the maximum growth rate by changing 𝑥_rP, f_RNAP^act and k_R^el are held constant regardless of the predicted growth rates.

The fraction of active RNAP (f_RNAP^act) was growth-rate dependent in all our simulations (see Table 2), only the fraction of active ribosomes (f_R^act) was kept constant according to Bremer and Dennis, 1996 & 2008.

We decided to keep the elongation rate (k_R^el) constant similar to Scott et al. 2010 (their explanation is in the supplementary material “Correlation [1] and the control of ribosome synthesis”).

We reran the simulations with variable k_R^el. It has no impact on the predictions of optimal ribosome composition. However, the linear dependence of RNA/protein ratio is less steep and predicts an offset at zero growth rate.

We added the results to the supplementary material and the following text to the results section (for the base model):<br /> "…the base model correctly recovers the well-known linear dependence of the RNA to protein ratio and growth rate (Scott et al. 2010), see Figure 2a, but not the offset at zero growth rate, since our model does not contain any non-growth associated processes and we assume constant translation elongation rate kelR as in Scott et al. (2010). At low growth rate, kelR decreases, most likely because of the lower availability of the required substrates (Bremer and Dennis, 2008; Dai et al., 2016). Interestingly, when we use variable kelR, we observe a nonzero offset (Appendix 1, Figure 2)."

and in a later section:<br /> "Using variable or constant kelR has no impact on the predicted optimal ribosome composition. As in the base model, variable kelR leads to predicted non-zero offset of RNA/protein ratio at zero growth rate (Appendix 1, Figure 6)."

1. _If amino acids or nucleotides are provided in the media, the cell does not have to synthesize all of them de novo. However, the model assumes that the cell always synthesizes all amino acids or nucleotides de novo for growth on growth on amino acid-supplemented media or on LB. This problem could in principle be solved by assuming very fast kinetics of the metabolic reactions in these media, but that should be discussed in the manuscript. Furthermore, why does the turnover number for EAA depend on the growth rate while that of ENT is constant?<br /> > _

We focused on the “enzyme” EAA because it forms a significant fraction of the proteome. However, for consistency, we now also made ENT turnover number depend on growth rate. It made no significant impact on the simulation results.

We agree with the reviewer that the model is currently very simplified and the enzymes ENT and EAA are used even in the media supplemented with AAs/NTs. However, these enzymes represent lumped pathways that aim to take into account not only AA/NT synthesis but also the different ‘nutrient efficiencies’ of the carbon sources (as in Scott et al. 2010). Therefore, to approximate these effects we increase the kcat of EAA (and now also ENT) with growth rate.

We added a paragraph to the results section to explain these simplifications:<br /> "We used parameters from E. coli grown in six different media. Three of them are rich media (Gly+AA, Glc+AA, LB) where amino acids (and nucleotides) are provided so cells only have to express the corresponding transporters instead of the synthesis pathways. In our model, the enzymes ENT and EAA represent lumped pathways for glycolysis and nucleotide / amino acid synthesis, and we only consider one type of transporter. Therefore, to model the changing `nutrient quality' of the different media (inspired by Scott et al. 2010), we assume that turnover numbers of EAA and ENT increase with growth rate."

1. All parameters related to transcription (RNAP) and translation (ribosome) used in this manuscript are adopted from Kostinski and Reuveni (2020), which are slightly modified based on Bremer and Dennis' research (1996, 2008). However, the authors changed some of the original parameters or data points, but did not provide explanations for these changes:

(a) The original data depicted a growth rate-dependent translation elongation rate, but Table 2 presents it as a constant value.

Please see the reply to point 2 above.

(b) Figure 2b displays five experimental data points, as opposed to the six data points in the original dataset and other figures in this manuscript.

The values for the transcription rate were taken from Bremer and Dennis’s paper from 1996 which only contains five growth rates. We updated the Figure 2b – it now displays data from Bremer and Dennis 2008 for six growth rates.

(c) The model does not consider the fraction of RNAP transcribing rRNA (Φ_rRNA^RNAP), except in Appendix Figure 4. In the original data (Bremer and Dennis 1996), the fraction of RNAP transcribing rRNA increases dramatically with growth rate; however, in this study, it remains constant at 1.

Our goal was to keep the model as simple as possible and keep the number of required parameters to a minimum. We only included the figure in the supplementary material because it does not change the conclusions, even though it makes the predictions quantitatively better. In the future we would like to achieve this improvement by expanding the model (with mRNA, tRNA, non-specific RNAP binding to DNA etc.). We added a sentence to the discussion to point out again how the results are affected if Φ_rRNA^RNAP is included, and how this parameter could be mechanistically included in the model in the future.

"Furthermore, incorporating other types of RNA (mRNA, tRNA) and energy metabolism, or even constructing a genome-scale RBA model (Hu et al., 2020), will likely lead to more quantitative predictions of fluxes and growth rate. A strong indication of this is that including a variable RNAP allocation into the model leads to quantitatively better predictions (see Appendix 1, Figure 5). Therefore, in the future, we aim to model RNAP allocation mechanistically. This will involve for example adding other RNA species (mRNA, tRNA), and considering non-specifically bound RNAP which is a significant fraction of RNAP (Klumpp and Hwa, 2008)."

Furthermore, Φ_rRNA^RNAP was first introduced in line 205 but was not explained until line 337.

We added an explanation to the sentence in line 205:<br /> "If we consider RNAP allocation to rRNA (k_RNAP^el^bar = k_RNAP^el f_act^RNAP Φ_rRNA^RNAP, where Φ_rRNA^RNAP is the fraction of RNAP allocated to the synthesis of rRNA), the results get closer to the experimental data (Appendix 1, Figure 5)."

The value(s) of Φ_rRNA^RNAP for Appendix Figure 4 are also missing from this manuscript.

We added the missing values to the figure caption.

1. How, exactly, is the unit of flux converted to mmol g-1 h-1?

We are not exactly sure what the reviewer means by this question. As an example of unit conversion, we provide an explanation for the conversion of literature RNAP fluxes. The RNAP fluxes predicted by the model are in mmol g^-1 h^-1. The RNAP fluxes in Bremer and Dennis (2008) were in nt min^-1 cell^-1. To convert them to mmol g^-1 h^-1, we used the values of dry mass/cell from Bremer and Dennis (2008) and the number of nucleotides in rRNA (the stoichiometric coefficient n_rRNA). The code for the conversion is available on GitHub (https://github.com/diana-sz/RiboComp) in the script fluxes_vs_growth_rate.py.

1. What is the (dry) mass constraint and how is it defined? In the manuscript, both the second equation in line 101 and the bottom row of Table 1 are dry mass constraint(s). Why are they different? Furthermore, why is the right-hand side of the second equation in line 101 a dimensionless 1, and how does the last row of Table 1 result in the unit of growth rate, time^(-1)?

These are two forms of the same constraint. We added a paragraph to the methods section that explains how to convert the equations (capacity constraints, dry mass constraint) into the form in Table 1.

In the first form of the equation, ⍵Tc = 1, the units of ⍵ are g/mmol, and the units of c are mmol/g, so they cancel out.

The rows in Table 1 are multiplied by the vector of fluxes, so we get ⍵C [g/mmol] * vIC [mmol/gh] = μ [1/h].

1. The concentrations of all components that serve as "substrates" will be zero when growth rate is maximized, as these molecules do not catalyze any reactions, nor do they influence reaction kinetics in the model. These "0" concentration components are C, AA, NT, rP, and rRNA. Why are these concentrations even included in the model?

The reviewer is correct in pointing out that these species have zero concentrations at maximum growth, and it would be possible to simplify the model accordingly. However, we have chosen not to merge these reactions to maintain clarity in distinguishing between metabolic and macromolecular synthesis processes. Additionally, while we currently use the model to predict optimal behavior, it is not inherently limited to this purpose, as it can equally describe sub-optimal states (as in Figure 2b). Finally, if needed, we can easily introduce minimum concentration constraints (e.g. obtained from measurements) for any of these species without affecting our overall arguments.

Minor comments:

1. Questions regarding Figure 2:

(a) The explanation of Figure 2a is unclear. Intuitively, I assumed that it was a comparison between model predictions and experimental data, with the points representing experimental data and the line representing predictions; and the authors wrote in the figure legend "The points represent maximum growth rates in six experimental conditions". However, the growth rates shown in the figure do not match the original experimental data. Are all the data in the figure predictions?

Yes, the points are predictions and the line is a linear fit. We changed the figure caption as follows:<br /> "The model predicts a linear relationship between RNA to protein ratio and growth rate. The points represent the predicted maximum growth rates in six experimental conditions (Table 2). The line is a linear fit."

(b) Figure 2b is difficult to understand. This figure shows the non-optimal solutions of the model. It is unclear how these solutions are achieved and why there are three lines in the figure.

We expanded the figure caption to make it clearer:<br /> "Alternative RNAP fluxes at different non-optimal growth rates in glucose minimal medium. These are obtained by varying the growth rate step by step from zero to maximum and enumerating all solutions (elementary growth vectors as defined in Müller et al. (2022)) for each growth rate. The grey and blue lines are the alternative solutions. The blue line corresponds to solutions, where rRNA and ribosomes do not accumulate (constraints rRNA' andcap R' in Table 1 are limiting)."

1. Table 1 is also difficult to understand. While the stoichiometric constraints can be easily derived, the capacity constraints and the dry mass constraint cannot be easily derived from related equations from the text.

We added a paragraph into the methods section that explains how to convert the equations (capacity constraints, dry mass constraint) into matrix form.

1. As the authors ask a question in the title, they should provide an explicit answer in the abstract.

We added a sentence to the abstract:<br /> "Our model highlights the importance of RNA instability. If we neglect it, RNA synthesis is always ``cheaper' than protein synthesis, leading to an RNA-only ribosome at maximum growth rate. However, when we account for RNA turnover, we find that a mixed ribosome composed of RNA and proteins maximizes growth rate."

1. The authors should cite a seminal modeling paper, which was the first to examine resource allocation in simplified self-replicating cell systems (Molenaar et al. 2009, Molecular Systems Biology 5:323).

The citation was added.

1. The meaning of v is not consistently defined throughout the manuscript. It refers to the fluxes of enzymatic reactions in some instances, but in other contexts, it refers to the fluxes of the entire network of enzymatic reactions and protein synthesis reactions (Figure 1, Equation 1, and Line 386).

We have made the notation more consistent. When we refer to the fluxes of the entire network we now use v_tot instead of v.

1. Line 85, it might be difficult to interpret "RNAP fluxes" as the flux of rRNA synthesis without reading the subsequent text.

_We added the explanation in brackets.<br /> "_We validate the model by predicting RNAP fluxes (rRNA synthesis fluxes)."

1. Typo in line 102-103. "...protein fluxes 𝒘" → "...protein synthesis fluxes 𝒘".

Thank you for spotting that, we added the missing word.

1. Line 104, f_RNAP^act and f_R^act are not explained in the text; and their biological significance cannot be understood from their names in Table 2 ("RNAP activity" and "Ribosome activity").

We added a sentence that explains these parameters:<br /> "f_RNAP^act is the fraction of actively transcribing RNAPs, and f_R^act is the fraction of actively translating ribosomes."

1. Notion "**" in Table 2. The coupling between transcription and translation means the coupling of "mRNA" transcription and translation, not rRNA. At least in E. coli, the transcription rate of rRNA is faster than that of mRNA.

The transcription rate of the archaeal RNAP was determined in vitro. To our knowledge, data for transcription rates of rRNA vs. mRNA in vivo are not available. Therefore, the translation rate is only a very rough estimate.

1. Is the citation correct in line 136? I didn't find related information in Bremer and Dennis' paper after a quick scan.

We corrected the citation. Additionally, we added references that indicate that if rRNA is transcribed in excess of available r-proteins, it gets rapidly degraded:<br /> "In fact, the accumulation of free rRNA in a cell is biologically not realistic as it is bound by rPs already during transcription (Rodgers and Woodson, 2021). Furthermore, if rRNA is expressed in excess of rPs, it is rapidly degraded (Siehnel and Morgan, 1985)."

1. Lines 136-138. The statement is not accurate, as the fraction of inactive ribosomes increases with decreasing growth rate in E. coli (Dai et al. 2016, Nat Microbiol 2, 16231). If the studied growth rates are relatively high, it is acceptable to use a constant active ribosome fraction as an approximation, but this approximation should be made explicit.

We used the fractions of active ribosomes as reported in Bremer and Dennis, 2008 which are constant between growth rates of 0.4-2.1 1/h. In Dai et al. 2016, it was similarly observed that above the growth rate of ~0.5 1/h, the active fraction is quite constant. We rephrase the text to make it more accurate:<br /> "For the growth rates studied here (0.4-2.1 1/h), the fraction of inactive ribosomes stays roughly constant at 15-20% (Bremer and Dennis, 1996, 2008; Dai et al., 2016). In our model, we have already incorporated this fraction using the effective translation elongation rate (k_R^el^bar = k_R^el*f_R^act). However, below the growth rate of ~0.5 1/h, the fraction of active ribosomes rapidly decreases (Dai et al. 2016)."

1. The citation in line 142 is not accurate. It should be (Bremer and Dennis, 1996).

We corrected the citation.

1. Lines 192-193: "six" different growth media, not five.

Thank you for pointing that out, we corrected it.

1. Line 287: The statement "... translation rate does not increase in ribosomes with a higher protein content" could be misinterpreted as discussing translation elongation rate changes with different protein content in ribosomal protein mutant strains in a given species. It should be rephrased to remove ambiguity.

We rephrased the sentence as follows:<br /> "…translation rate does not increase in ribosomes from different species which have higher protein content."

1. Parameters for the three panels in Figure 8 are missing.

The parameters used for mitochondria are the same as for E. coli in glucose minimal media. The only difference is that a fraction of rPs can be imported. We added a sentence to the figure caption to clarify this:<br /> "The model can be adjusted to predict mitochondrial protein-rich ribosome composition. All parameters used for the simulation of mitochondria are the same as for E. coli in glucose minimal media, except a fraction of rPs can be imported for free from the cytoplasm and does not have to be synthesized. For simplicity, we assumed that 1/3 of rPs are imported. (In reality, almost all rPs are imported, but mitochondria make additional proteins to provide energy for the whole cell.)"

Reviewer #4 (Significance):

Strengths: Why the ribosome is composed of RNA and protein parts is a fundamental biological question. This manuscript proposes a very interesting hypothesis, arguing that the mixed ribosome composition results from rRNA instability. To test their hypothesis, the authors parameterize a simplified self-replicating cell model with realistic parameters. The model is first developed/parameterized for E. coli, and it could be easily adapted to other organisms with higher ribosomal protein content.

Limitations: The main limitations of this manuscript lie in the development of the model, especially the modeling of rRNA degradation and the use of constant values for growth rate-dependent parameters.

Advances: (1) This manuscript proposes a new hypothesis that rRNA instability is a universal factor that influences the ribosome composition across living organisms. (2) Compared to Kostinski and Reuveni's work, the authors have made certain improvements by including adjustable ribosome allocation to RNA and ribosomal protein when maximizing growth rate, which may lead to more realistic conclusions.

Audience: This work will be of interest to people in the field of theoretical biology, computational biology, and evolution, as well as to researchers studying ribosome structure and function.

Areas of expertise: Microbial systems biology, computational biology, and prokaryotic genomics.

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

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1. General Statements [optional]

The findings presented in this manuscript are original and have not been previously published, nor is the manuscript under consideration for publication by another journal. The authors of this manuscript declare to have no conflicts of interest.

1. Description of the planned revisions

We believe that incorporating the suggested corrections and conducting the additional experiments recommended by the reviewers will significantly enhance the quality of this study. These revisions will not only bolster the current conclusions but also broaden the relevance and applicability of our work to a wider scientific audience, extending beyond the field of virology.

As outlined in the following sections, we are fully committed to implementing the experiments proposed by the reviewers and making the necessary modifications to the manuscript in line with their suggestions. Our responses to each specific comment are provided below.

Reviewer #1

Evidence, reproducibility and clarity

Summary: Several target cell entry pathways have been described for different viruses, including endocytic/ fusion pathways, some which are dynamin-dependent.

Here the authors exploited cell lines with multiple dynamin gene disruptions and other cell biological tools, as well as a phenotypic range of previously characterized viruses, to evaluate the relative importance of dynamin and actin for entry of viruses, including SARS-CoV-2.

In cells that lack the serine protease TMPRSS2, dynamin depletion blocked uptake and infection by SARS-CoV-2. Increasing the input virus partially rescued SARS-CoV-2 infection in the absence of dynamin, and both dynamin-dependent and dynamin-independent entry pathways were inhibited by drugs that disrupt actin polymerization.

Examination by electron microscopy indicated that the dynamin-independent endocytic process was clathrin-independent, in that, in the absence of dynamin, the majority of Semliki Forrest Virions were detected in bulb-shaped, non-coated pits. When TMPRSS2 was expressed, SARS-CoV-2 infection was rendered dynamin-independent.

Significance

Overall, the experiments are expertly performed, the results and conclusions are convincing, the text is clearly written and accurately describes the data, and the manuscript makes an important contribution to a complex and important topic in the cell biology of virus infection. It would be reasonable for the authors to publish the manuscript with the current data.

That being said, we have two main questions/comments:

1. The authors point out that SFV differs from SARS-CoV-2 in that it required actin only for the dynamin-independent entry. The EM experiments were done with SFV, not with SARS-CoV-2. This raises the question of the relevance for SARS-CoV-2 of the interesting finding that, in the absence of dynamin, SFV associated with non-coated pits.

If the authors had the tools to do similar EM experiments with SARS-CoV-2, it would be nice to include those results. Otherwise, it is fine to discuss/speculate about SARS-CoV-2 regarding this issue.

RESPONSE:As requested by the reviewer, we are currently perform the suggested EM analysis of SARS-CoV-2 entry in the presence and absence of dynamins.

1. The authors show that TMPRSS2 allows the original Wuhan strain and Delta Variant of SARS-CoV-2 to bypass the need for dynamin. This is presumably because TMPRSS2 allows SARS-CoV-2 to fuse at the plasma membrane, precluding need for endocytosis altogether. The authors also mention literature claiming that Omicron is more dependent upon endocytosis than the Wuhan and Delta variants. If the authors had data with Omicron it would be really nice to include it.

RESPONSE: We have already conducted this experiment and have incorporated the quantitative results into the updated version of the manuscript, now presented as Figure 8.

There were some minor typos/grammar/other quoted here:

• Ultrastructural analysis by electron microscopy showed that this dynamin-independent endocytic processes - cell injests particles and nutrients by encoulfing them - some viruses have been show

RESPONSE: Thank you for noticing the error. We have modified the text as: “Ultrastructural analysis by electron microscopy showed that this dynamin-independent endocytic processes appeared as 150-200 nm non-coated invaginations that have been shown to be efficiently used by numerous mammalian viruses, including alphaviruses, influenza, vesicular stomatitis, bunya, adeno, vaccinia, and rhinovirus.”.

• The final step of an endocytic vesicle formation culminates with the pinching of vesicle off from the PM into the cytoplasm

RESPONSE: We have modified the sentence as: “The concluding stage of endocytic vesicle formation is marked by the vesicle being pinched off from the plasma membrane and released into the cytoplasm.”

• For other viruses, such as respiratory viruses (This word is a little strange here since influenza was mentioned in the last sentence.)

RESPONSE: Thank you for noticing the error, we have removed the mention to respiratory viruses: “ For other viruses (including coronaviruses), the fusion is triggered by proteolytic cleavage of the spike proteins that, once cleaved, undergo conformational changes leading first to the insertion of the viral spike into the host membrane and, upon retraction, the fusion of viral and cellular membranes9,10.”.

• Viruses that use a receptor that is internalized by dynamin-dependent endocytosis (e.g. CPV and the TfR) (just reminding that TfR is not a virus)

RESPONSE: We have amended the sentence to avoid misunderstandings: “Viruses (e.g. CPV) that use a receptor (e.g. TfR) that are internalized by dynamin-dependent endocytosis cannot efficiently infect cells in the absence of dynamins.”.

• that appeared surrounded by an electron dense coated

RESPONSE: We have corrected the typo: “In MEFDNM1,2 DKO cells treated with vehicle control, TEM analysis revealed numerous viruses at the outer surface of the cells (Figure 4 A), as well as inside endocytic invaginations that were surrounded by an electron dense coat, consistent with the appearance of clathrin coated pits47,48 (CCP) (Figure 4 B).”

• The main virial receptor could be internalized using two endocytic

RESPONSE: We have corrected the typo: “The main viral receptor could be internalized using two endocytic mechanisms, one mainly available in unperturbed cells (e.g. dynamin-dependent), the other activated upon dynamin depletion (i.e. dynamin independent).”

• Virus infection was determined by FACS analysis of virial induced EGFP

RESPONSE: We have corrected the typo: ‘Virus infection was determined by FACS analysis of EGFP (VAVC and VSV), mCherry (SINV) or after immunofluorescence of viral antigens using virus-specific antibodies (IAV X31 and UUKV).”.

Reviewer #2

Evidence, reproducibility and clarity

Summary: Ohja et al. present an interesting study investigating dynamin independent endocytic entry mechanism of viral infection. Using a genetic KO of 2 dynamin isoforms they show impacts on the infection of a range of large and small DNA and RNA viruses.

They go onto show that SARS-CoV-2 may utilise a dynamin independent mechanism of infection that requires an intact actin cytoskeleton.

Significance

This work is of interest to the field of virology and has the potential to answer previously understudied entry mechanisms important for a wide range of viruses. It is a well presented piece of work overall.

Major Comments:

• The abstract does not in my opinion reflect the content of the paper and is too 'SARS-CoV-2' centric. The work involves the use of a range of viruses to first define a mechanism that is applicable to SARS-CoV-2 and I think the abstract and title should reflect this.

RESPONSE: As per the reviewer's request, we will make revisions to the Title and Abstract. As a ‘non SARS-CoV-2-centric’ title we have amended the title to: Multiple animal viruses, including SARS-CoV-2, can infect cells using alternative entry mechanisms.

• In figure 1H the authors postulate that the reduced impact of dyn1,2 KO on SFV infection may be due to the interaction with heparin sulphate proteoglycans. Have the authors considered performing experiments using Heparin to block infection in their KO cells -/+ tamoxifen treatment?

RESPONSE: As per the reviewer's request, we will perform the proposed heparin experiments for SFV.

• In Figure 2 the authors assess infection of a range of viruses in dyn1,2 KO cells showing differential effects in some viruses but not all.

Have the authors confirmed whether tamoxifen treatment and the subsequent KD of dyn1,2 effect surface expression of the entry receptors for the viruses tested?

RESPONSE: Although in general blocking receptor endocytosis results in an increase in its cell surface levels, we agree with the Reviewer that the effect of dynamin depletion on receptors levels should be monitored at least for some of the viruses. To address the question raised by the reviewer, we will monitor the surface expression of SFV receptors VLDLR and ApoER2, and of the CPV receptor TfR in the presence and absence of dynamins.

We have already confirmed that there are no changes in the surface expression of SARS-CoV-2 receptor ACE2 in the absence of dynamin and this new data will be added to Figure 7.

• Additionally in this setting, dyn1,2 KD may impact on post entry steps in the virus life cycle such as the initial establishment of viral replication.

Can the authors either provide evidence as to how they have delineated measurement entry over replication or support their findings with psuedotyped virus-like-particles?

RESPONSE: This is an important point. As suggested by the reviewer, we will perform infection experiments in the presence or absence of Dynamins using VLPs pseudotyped with SFV and VSV spikes.

In addition, several of our experiments already indicate that upon dynamin depletion, the main block in virus infection is at the step of cell entry: 1) Upon DNM-depletion, the decrease in SARS-CoV-2 infection strongly correlates with a proportional block in spike (Figure 5) and virions (Figure 7) endocytosis; 2) exogenous expression of even low levels of the cell surface protease TMPRSS2 rescued SARS-CoV-2 infection in cells devoid of dynamins, indicating that merely by-passing endocytosis restores virus infection; 3) as shown in Figure 1 H for SFV, and in Figure 2 for multiple viruses, increasing the multiplicity of infection increases the number of infected cells, indicating that when virions access the dynamin-independent entry route, cells can be efficiently infected; 4) the infection of both negative strand (i.e. Uukuniemi virus, UUKV, Figure 2 ) and positive strand (i.e. human Rhino virus, HRVA1, Figure S3 D-E) RNA viruses, as well as DNA viruses (i.e. Vaccinia, Figure 2, and Adenovirus-5, Figure S3 B-C) are not affected by dynamin depletion, arguing against a general negative impact of dynamin depletion on cellular protein synthesis or other basic cell functions required for virus replication.

• Figure 3, given the unexpected results with the dynamin inhibitors, could this experiment be repeated with the dyn1-3 triple KD presented in figures 5-8?

RESPONSE: As requested by the reviewer, we will repeat the main inhibitor experiments presented in Figure 3 for SFV also in DNM TKO cells.

• Statistical analysis of imaging data in figure 4 would help with the conclusions.

RESPONSE: We have already performed the requested statistical analysis and modified Figure 4 accordingly.

• Additionally, the authors comment that in the KD cells the viruses were trapped in 'stalled CCPs'. What morphological changes determine this classification?

RESPONSE: As previously reported by Ferguson et al. (Developmental Cell, 2009), who developed the conditional MEF DNM knock out cell models, all CCPs are stalled at 6 days post induction of dynamin depletion. When observed by electron microscopy, stalled CCPs are readily identified by the presence of elongated, membranous narrow neck structures that connects the vesicle to the plasma membrane. We have clarified this description in the manuscript text and indicated the morphological features typical for a ‘stalled’ clathrin coated pit in Figure 4 F (black asterisk and white arrowheads).

• Concerning the SARS-CoV-2 work presented in figures 6-8, the use of exogenous expression of the viral entry receptors ACE2 and TMPRSS2 is a concern.

RESPONSE: While the reviewer appreciates that this is a necessary step to allow entry into their MEF-dyn1-3 KD cells, exogenous receptor expression can result in artificial entry of the virus.

• To support their findings, can the authors perform experiments in either cell lines endogenously expressing ACE-2/TMPRSS2 such as Calu3 or Caco2 and KD dyn1-3 using transient siRNA?

RESPONSE: This experiment poses a challenge due to the inherent difficulty of transfecting Caco2 and Calu3 cells and the potential difficulty of achieving a robust (>80%) simultaneous knockdown of all three dynamin isoforms. This is one of the reasons why we chose the conditional knock out approach. Nevertheless, we are committed to attempting this experiment.

• This approach would also provide more evidence for the role of TMPRSS2 presented in SF5 as the limited expression of this protease limits the robustness of the conclusions one can draw from the data presented.

RESPONSE: We appreciate the reviewer's observation, and to address this concern, we plan to not only perform siRNA knockdown of dynamins in cells with endogenous ACE2 and TMPRSS2 but also endeavor to elevate the expression levels of TMPRSS2 in our MEF DNM1,2,3 TKO ACE2 cells. It's worth noting, however, that this task presents a unique challenge since expression of TMPRSS2, a trypsin-like cell surface protease, leads to cell detachment even when expressed at moderate levels.

Minor comments & typo:

• Introduction paragraph 1 engulfing

RESPONSE: The sentence has been amended: “To gain access into the host cell's cytoplasm where viral protein synthesis and genome replication take place, most animal viruses hijack cell’s endocytic pathways1 by which the cell engulfs particles and nutrients into vesicular compartments. “.

• Pg 13 - typo in 'Figurre 6B'

RESPONSE: The typo has been corrected.

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

• Regarding the Reviewer 1 request on the use of Omicron variants, we have already conducted the requested experiments and have incorporated the quantitative results into the updated version of the manuscript, now presented as Figure 8.
• Regarding the Reviewer 2 request on the EM data, we have already performed the requested statistical analysis and modified Figure 4 accordingly. We have also clarified the EM descriptions in the manuscript text and indicated the morphological features typical for a ‘stalled’ clathrin coated pit in Figure 4 F (black asterisk and white arrowheads).

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

none

I think this plays a big factor how we choose to act in most situations. We learn to talk a certain way to babies because we know that speaking with a certain tone or volume or energy can get the best reaction out of a baby. We do this with adults as well by gauging how much attention we get from certain types of humor, topics, words and expressions we use and so forth. Which can lead people to believe they are "funny", simply because they know how to communicate around certain people in a way that will get the most amused result. This can also be to our disadvantage because we may learn to communicate in social settings in a way that we don't actually enjoy or believe is our own true character.

The purpose of a definition essay may seem self-explanatory: the purpose of the definition essay is to simply define something. But defining terms in writing is often more complicated than just consulting a dictionary. In fact, the way we define terms can have far-reaching consequences for individuals as well as collective groups. Take, for example, a word like alcoholism. The way in which one defines alcoholism depends on its legal, moral, and medical contexts. Lawyers may define alcoholism in terms of its legality; parents may define alcoholism in terms of its morality; and doctors will define alcoholism in terms of symptoms and diagnostic criteria. Think also of terms that people tend to debate in our broader culture. How we define words, such as marriage and climate change, has enormous impact on policy decisions and even on daily decisions. Think about conversations couples may have in which words like commitment, respect, or love need clarification. Defining terms within a relationship, or any other context, can at first be difficult, but once a definition is established between two people or a group of people, it is easier to have productive dialogues. Definitions, then, establish the way in which people communicate ideas. They set parameters for a given discourse, which is why they are so important.

Author Response

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

We appreciate very much the comments and suggestions on our manuscript "Cylicins are a structural component of the sperm calyx being indispensable for male fertility in mice and human". According to the comments, we performed a series of further experiments, re-worded and re-wrote several paragraphs and re-structured the manuscript according to the reviewers’ comment. We think that the manuscript is now improved and are looking forward to the further evaluations. We provide a point by point response to all comments and have prepared a version.

Recommendations for the authors:

Editor’s comment:

1) As pointed out by all three reviewers, it is critical to show the specificity of the antibodies used. The authors should clarify how the specificity of antibodies is tested. Western blot analysis to show the absence of the protein in the knockout is essential.

As suggested by all reviewers, we additionally performed Western Blot analysis on cytoskeletal protein fractions to further verify the specificity of generated antibodies and the generation of functional knockout alleles. Results nicely confirm the results of the IF staining, however, both anti-bodies detected the bands lower than the predicted molecular weight. In addition, Mass Spectrometry was performed to search for the presence of peptides in the cytoskeletal protein fractions. The paragraph reads now as follows:

Line 127-134: Additionally, Western Blot analyses confirmed the absence of CYLC1 and CYLC2 in cytoskeletal protein fractions of the respective knockout (Fig. 1 G), thereby demonstrating i) specificity of the antibodies and ii) validating the gene knockout. Of note, the CYLC1 antibody detects a double band at 40-45 KDa. This is smaller than the predicted size of 74 KDa as, but both bands were absent in Cylc1-/y. Similarly, the CYLC2 Antibody detected a double band at 38-40 KDa instead of 66 KDa. Again, both bands were absent in Cylc2-/-. Next, Mass spectrometry analysis of cytoskeletal protein fraction of mature spermatozoa was performed detecting both proteins in WT but not in the respective knockout samples (Figure 1 – supplement 5; Figure 1 – supplement 6).

Specificity of antibodies was additionally proven by immunohistochemical staining, showing a specific staining only in testis sections but not in any other organ tested. The section reads now as follows:

Line 115-117: Specificity of antibodies was proven by immunohistochemical stainings (IHC), showing a specific signal in testis sections only, but not in any other organ tested (Figure 1 – supplement 2)

2) Re-structuring/streamlining of the figures is recommended. Please consider the flow suggested by reviewer #2 and shorten the evolutionary analysis which takes up more space than it adds to the value of the story.

We thank the reviewers and editor for the valuable suggestion. We re-structured the figures as suggested and rewrote the results section accordingly. The evolutionary analysis was significantly shortened.

3) Provide statistics for the imaging analysis such as TEM as only a single representative image is shown.

We agree that the observed morphological defects require a detailed statistical evaluation. TEM analysis was performed to confirm the results from optical microscopy and representative images with high magnification are shown for a detailed visualization of the defects. For additional quantification, we included statistics for IF stainings against calyx proteins CCIN and CapZa (Fig. 2 I-J). For TEM, we added additional images to the supplement (Figure 3 – supplement 1). Furthermore, we quantified the manchette length of step 10-13 spermatids to prove the increased elongation of the manchette in Cylc2-/- and Cylc1-/y Cylc2-/- spermatids (Fig. 5 A-B).

4) Please consider other points raised by the reviewers below to improve the manuscript and provide responses on how the authors have addressed them.

We thank all reviewers for the detailed review of our manuscript and their valuable suggestions, which helped a lot to improve the manuscript. We considered all points raised by the reviewers to the best of our knowledge and hope that the reviewers will approve the manuscript ready for publication. We added a point-by-point discussion of all comments/suggestions hereafter.

Reviewer #1 (Recommendations For The Authors):

Major comments:

(1) Antibody specificity: Fig 1E - there are some unspecific binding in Cylc2-/- for CYLC2 and in Cylc1/y Cylc2+/- for CYLC1 in the testis (and elongating spermatids in Figure 1 – Supplement 4). Could authors elaborate/comment on this? Western blot analysis would be also helpful to further support the antibody specificity.

The very weak unspecific staining in the testis for CYLC2 (in Cylc2-/-) and CYLC1 (in Cylc1-/y Cylc2+/-) is only present in the lumen of the seminiferous tubules and/or the residual bodies of the testicular sperm cells and can be referred to as background signal. Importantly, the signal is entirely lost in the PT region, proving specificity of the generated antibodies. We added the following paragraph to the results section:

Line 124-127: The generated antibodies did not stain testicular tissue and mature sperm of Cylc1- and Cylc2-deficient males, except for a very weak unspecific background staining in the lumen of seminiferous tubules and the residual bodies of testicular sperm (Fig. 1 F).

Specificity of antibodies was additionally proven by immunohistochemical staining, showing a specific staining only in testis sections but not in any other organ tested.

Line 115-117: Specificity of antibodies was proven by immunohistochemical stainings, showing a specific staining in testis sections only, but not in any other organ tested (Figure 1 – supplement 2)

To further verify the specificity of generated antibodies and the generation of functional knockout alleles, we additionally performed Western Blot analysis on cytoskeletal protein fractions, confirming the results of the IF staining. No unspecific bands were detected in the Western Blot, further supporting the notion that the weak unspecific signals in IF resemble staining artifacts.

The paragraph reads now as follows:

Line 127-132: Additionally, Western Blot analyses confirmed the absence of CYLC1 and CYLC2 in cytoskeletal protein fractions of the respective knockout (Fig. 1 G), thereby demonstrating i) specificity of the antibodies and ii) validating the gene knockout. Of note, the CYLC1 antibody detects a double band at 40-45 KDa. This is smaller than the predicted size of 74 KDa as, but both bands were absent in Cylc1-/y. Similarly, the CYLC2 Antibody detected a double band at 38-40 KDa instead of 66 KDa. Again, both bands were absent in Cylc2-/-.

(2) Please provide more interpretation of the gene dosage effect of Cylicin 2. It is not common to see a gene dosage effect in the sperm phenotype as transcripts and proteins can be shared between haploids due to syncytium formation during spermatogenesis.

We agree and we apologize for the misinterpretation. In Cylc2+/- mice expression of Cylc2 was reduced by half but there was no altered phenotype observed. The sentence now reads as follows:

Line 112: In Cylc2+/- animals expression of Cylc2 was reduced by 50 %.

(3) Line 194-196 - the authors say that the sperm are smaller, with shorter hooks and increased circularity of the nuclei, and reduced elongation. Are these statistically significant? There seems to be a high variation in the graph in S2D and the statistical analysis is not given.

We agree, performed statistical analyses, and highlighted significantly altered values for sperm head elongation and circularity in Figure 2 – Supplement 3.

(4) Line 153-164 It is interesting that the absence of Cylc2 affected many parts of sperm structure. I think some ratios of sperm always have a morphological defect in diverse ways, so it is hard to confirm the finding only with a single sperm image. I think that it will be important to do some statistical analysis or at the minimum show more TEM images from TEM.

We agree that the observed morphological defects require a detailed statistical evaluation. TEM analysis was performed to confirm the results from optical microscopy and representative images with high magnification are shown for a detailed visualization of the defects. For additional quantification, we included statistics for IF stainings against calyx proteins CCIN and CapZa (Fig. 2 I-J). For TEM, we added additional images to the supplement (Figure 3 – Supplement 1).

(5) Line 236-242 - I believe that the phenotype described applies to the sperm from Cylc2-/- and Cylc1/y Cylc2-/- animals; however, I think that the Cylc1-/y Cylc2+/- has a more subtle, intermediate phenotype between the WT and the genotypes missing both Cylc-/- alleles.

We agree and we added a quantification of manchette length at step 10-13 to visualize the differences between the genotypes. The section reads now as follows: Line 268-272: Manchette length was measured starting from step 10 until step 13 spermatids and the mean was obtained, showing that the average manchette length was 76-80 nm in wildtype, Cylc1-/Y and Cylc2+/- while for Cylc2-/- and Cylc1-/Y Cylc2-/- spermatids mean manchette length reached 100 nm (Fig. 5 B). Cylc1-/Y Cylc2+/- spermatids displayed an intermediate phenotype with a mean manchette length of 86 nm.

(6) Since CYLC1 staining is absent in Fig 5B, does that mean that the mutation resulted in protein degradation/instability? Is RNA present? Additional biochemical studies of Cyclins demonstrating the deleterious nature of the mutations would strengthen the molecular pathogenesis of the human mutations.

Thank you for raising these important questions. The CYLC1 variant c.1720G>C is predicted to cause the amino acid substitution p.(Glu574Gln). It is, thus, conceivable that the RNA is present but either the protein is degraded or misfolded and, therefore, not detectable by IF. Unfortunately, for personal reasons of the patient, it is currently not possible to receive additional semen samples, preventing additional analyses of the semen, e.g. analysis of Cylicin transcript level.

(7) Strongly suggest shortening the evolutionary analysis - all the corresponding materials are in supplemental while texts are extensive- or even consider entirely omitting. It does not add a lot to the current study.

We agree that the evolutionary analysis was very detailed. However, we think that the results are important to understand the role of Cylicins for male reproduction in general. The results obtained from the mouse model might be transferable to other species, including humans. Further, the results present a possible explanation for the subfertility of Cylc1-deficient mice, in contrast to infertility of Cylc2-deficient males. We shortened the section, the paragraph reads as follows:

Line 287-302: To address why Cylc2 deficiency causes more severe phenotypic alterations than Cylc1deficiency in mice, we performed evolutionary analysis of both genes. Analysis of the selective constrains on Cylc1 and Cylc2 across rodents and primates revealed that both genes’ coding sequences are conserved in general, although conservation is weaker in Cylc1 trending towards a more relaxed constraint (Fig. 6). A model allowing for separate calculation of the evolutionary rate for primates and rodents, did not detect a significant difference between the clades, neither for Cylc1 nor for Cylc2, indicating that the sequences are equally conserved in both clades.

To analyze the selective pressure across the coding sequence in more detail, we calculated the evolutionary rates for each codon site across the whole tree. According to the analysis, 34% of codon sites were conserved, 51% under relaxed selective constraint, and 15% positively selected. For Cylc2, 47% of codon sites conserved, 44% under neutral/relaxed constraint, and 9% positively selected. Interestingly, codon sites encoding lysine residues, which are proposed to be of functional importance for Cylicins, are mostly conserved. For Cylc1, 17% of lysine residues are significantly conserved and 35% of significantly conserved codons encode for lysine. For Cylc2, this pattern is even more pronounced with 27.9% of lysine codons being significantly conserved and 24.3% of all conserved sites encoding for lysine (Fig. 6).

Minor comments:

(1) Line 114, 115, 118 à Figure 1D is already well-described in the previous paragraph and thus redundant. Ref Fig 1D, E; but only figure E shows IF. Maybe supposed to be E and F or just 1E?

We apologize for the mix-up with the subfigures. The mentioned paragraph refers to Fig. 1 E-F, which was corrected accordingly.

Line 117-123: Immunofluorescence staining of wildtype testicular tissue showed presence of both, CYLC1 and CYLC2 from the round spermatid stage onward (Fig. 1 E). The signal was first detectable in the subacrosomal region as a cap-like structure, lining the developing acrosome (Fig. 1 E-F, Figure 1 – supplement 3). As the spermatids elongate, CYLC1 and CYLC2 move across the PT towards the caudal part of the cell (Figure 1 – supplement 4). At later steps of spermiogenesis, the localization in the subacrosomal part of the PT faded, while it intensified in the postacrosomal calyx region (Fig. 1 E-F).

(2) Figure 1F - Arguably, IF images show expression of both CYLC1 and CYLC2 to reach/include the acrosome/hook portion of the sperm head, but the diagram does not reflect that. Why is that?

We agree and apologize for the inconsistency. The illustration was adjusted according to the experimental data showing localization of Cylicins in the whole ventral part of the sperm.

(3) Line 124 - PAS staining mentioned on line 124, is not explained (Periodic acid Schiff staining) until line 605

We agree and introduced the abbreviation accordingly. The PAS staining was moved to Fig. 4. The paragraph reads now as follows:

Line 220-222: To study the origin of observed structural sperm defects, spermiogenesis of Cylicin deficient males was analyzed in detail. PNA lectin staining and Periodic Acid Schiff (PAS) staining of testicular tissue sections were performed to investigate acrosome biogenesis.

(4) Some figures are hard to read due to being very small (S1B, 3F).

We agree and we increased the figure size. For former Figure 3F (now figure 4A), insets with higher magnification of representative sperm were added. Insets are additionally shown in Figure 4 – Supplement 1 in higher resolution.

(5) Line 139 Please specify whether the sperm was capacitated or not.

Analysis of the flagellar beat was performed with non-capacitated sperm. We clarified this in the main text:

Line 203: The SpermQ software was used to analyze the flagellar beat of non-capacitated Cylc2-/- sperm in detail 22.

As described in the Material and Methods section, sperm were only activated in TYH medium, prior to analysis:

Line 732-733: Sperm samples were diluted in TYH buffer shortly before insertion of the suspension into the observation chamber.

(6) Line 142-145; The sentence is interrupted strangely, perhaps the authors meant to write: "Interestingly, we observed that the flagellar beat of Cylc2-/- sperm cells was similar to wildtype cells, however, with interruptions during which midpiece and initial principal piece appeared stiff whereas high-frequency beating occurs at the flagellar tip"

We corrected the sentence accordingly.

Line 206-208: Interestingly, we observed that the flagellar beat of Cylc2-/- sperm cells was similar to wildtype cells, however, with interruptions during which midpiece and initial principal piece appeared stiff whereas high frequency beating occurs at the flagellar tip (Fig. 3 C, Video 1, Video 2).

(7) Line 142 -Wrong Figure number. Figure S4A is a phylogenic analysis.

We regret the mix up and corrected the Figure reference accordingly. Line 204-205: Cylc2-/- sperm showed stiffness in the neck and a reduced amplitude of the initial flagellar beat, as well as reduced average curvature of the flagellum during a single beat (Figure 3 – supplement 2).

(8) L146-147 Better placed in Discussion.

We agree, and we omitted this sentence from the results part.

(9) Line 154-156 - The white arrowheads are present in both WT and KO sperm, thus it appears they denote the basal plate, not necessarily the dislocation/parallel position as the current text seems to suggest. Furthermore, the position of the WT and KO sperm is somewhat different with the tail coiling differently, so it is hard to see whether the two are comparable.

We agree and we removed the white arrowhead in the WT sperm picture, and it now depicts only the dislocation of the basal plate in the Cylc2-/- sperm. Due to the morphological anomalies of Cylc2-/- sperm cells, it’s difficult to determine the exact angle of the depicted cell. However, we added more TEM pictures of the sperm cells (3 for WT and 6 for Cylc2-/-) in Figure 3 – Supplement 1.

(10) Line 164 Please describe in detail what mitochondrial damage the readers expect to see from the TEM image.

We evaluated the observed mitochondrial damage in more detail. Unfortunately, the defects described initially seem to be an artifact of apoptotic sperm cells and could not be identified in vital sperm cells in either of the knockout mouse models. We apologize for this misinterpretation, and we deleted this section in the manuscript.

(12) Figure S2A - no WT comparison, difficult to compare without it (mitochondria in Cylc2-/-)

See (10). We evaluated the observed mitochondrial damage in more detail and in comparison to WT. Unfortunately, the defects described initially seem to be an artifact of apoptotic sperm cells and could not be identified in vital sperm cells in either of the knockout mouse models. We apologize for this misinterpretation and we deleted this section in the manuscript.

(13) Line 172-173 - Fig 3C denotes quantification of abnormal acrosome only, however, the text mentions sperm coiled tail being quantified within this graph - which is it? Is it both of them? Or only one of them?

Figure 3 C (now Figure 2G) showed the percentage of abnormal sperm in general comprising acrosomal as well as flagellar defects. We modified the figure and evaluated acrosomal defects and tail defects separately. The results section was changed accordingly and reads now as follows:

Line 152-159: Loss of Cylc1 alone caused malformations of the acrosome in around 38% of mature sperm, while their flagellum appeared unaltered and properly connected to the head. Cylc2+/- males showed normal sperm tail morphology with around 30% of acrosome malformations. Cylc2-/- mature sperm cells displayed morphological alterations of head and mid-piece (Fig. 2 F-G). 76% of Cylc2-/- sperm cells showed acrosome malformations, bending of the neck region, and/or coiling of the flagellum, occasionally resulting in its wrapping around the sperm head in 80% of sperm (Fig. 2 F). While 70% of Cylc1-/Y Cylc2+/- sperm showed these morphological alterations, around 92% of Cylc1-/YCylc2-/- sperm presented with coiled tail and abnormal acrosome (Fig. 2 F-G).

(14) Fig 3D - CCIN in the text, cylicin in the figure - this should be consistent. Furthermore, since only the head is being shown, is CCIN ever detected in the WT sperm tail?

We apologize for the inconsistency, and we added the abbreviation “CCIN” to the figure. CCIN is solely detectable in the sperm head of wildtype sperm as published previously. Irregular staining patterns showing signals in the tail region are only observed upon Cylicin deficiency.

(15) Line 199-200 - To say that head of Cylc2-deficient sperm appears less concave seems redundant, likely the observed increased circularity is contributed to by sperm head being less concave in this region; unless there is an extra point that the authors are trying to make and if so, this needs to be elaborated on

We agree and we deleted the sentence from the manuscript.

(16) Figure legend of Fig S3 is wrong. Only S3A and S3B are present, and in the figure legend S3C corresponds to figure S3B.

We agree and corrected the Figure legends accordingly. Due to the re-structuring of the manuscript, Figures and Supplementary figures were re-ordered as well.

(17) Figure 4B - figure legend and/or text should specify that lectin is green and HOOK1 is in red

We specified the figure legend as well as the main text accordingly: Line: 279-281: Co-staining of the spermatids with antibodies against PNA lectin (green) and HOOK1 (red) revealed that abnormal manchette elongation and acrosome anomalies simultaneously occurred in elongating spermatids of Cylc2-/- male mice (Fig. 5 C).

Line: 560-562: Co-staining of the manchette with HOOK1 (red) and acrosome with PNA-lectin (green) is shown in round, elongating and elongated spermatids of WT (upper panel) and Cylc2-/- mice (lower panel).

(18) Line 261-263 - It is difficult to see what is going on with microtubules in these images, as the resolution is low

We increased the pictures and improved their quality. Microtubules are also depicted with letter ‘m’

(19) Line 265-266 - It seems that there is a persistence of manchette, rather than elongation. From these images, I cannot see gaps, and I am not sure where to look for them. This needs to be labelled further and higher-resolution images could be included for clarity.

We agree, although we observed both excessive elongation and persistence of the manchette. The average length of the manchette is now shown in figure 5B.

The paragraph now reads as follows:

Line 235-239: Microtubules appeared longer on one side of the nucleus than on the other, displacing the acrosome to the side and creating a gap in the PT (Fig. 4 C). Whereas elongated spermatids at step 14-15 in wildtype sperm already disassembled their manchette and the PT appeared as a unique structure that compactly surrounds nucleus, in Cylc2-/- spermatids, remaining microtubules failed to disassemble.

The gaps in the perinuclear theca are better visible in TEM micrographs and the description is now in the paragraph describing TEM.

(20) Line 269 Please include the information of "White arrowhead".

We added the information accordingly.

Line 240-242: In addition, at step 16, the calyx was absent, and an excess of cytoplasm surrounded the nucleus and flagellum (Fig. 4 C, white arrowhead).

(21) Line 276-280 This should be placed in the Discussion.

We agree, and we deleted this concluding remark from the results section.

(22) Is Cylc1 and/or Cylc2 conserved/expressed amongst species other than rodents and primates?

Yes, Cylc1 and Cylc2 homologs were identified in C. elegans for example. We added a schematic to the introduction showing the protein structure of human, mouse and C. elegans CYLC1 and CYLC2 (Figure 1 – supplement 1).

The section reads now as follows:

Line 73-78: In most species, two Cylicin genes, Cylc1 and Cylc2, have been identified (Figure 1- supplement 1). They are characterized by repetitive lysine-lysine-aspartic acid (KKD) and lysine-lysine-glutamic acid (KKE) peptide motifs, resulting in an isoelectric point (IEP) > pH 10 14, 15. Repeating units of up to 41 amino acids in the central part of the molecules stand out by a predicted tendency to form individual short α-helices 14. Mammalian Cylicins exhibit similar protein and domain characteristics, but CYLC2 has a much shorter amino-terminal portion than CYLC1 (Figure 1-supplement 1).

(23) The whole chapter "Cylc2 coding sequence is slightly more conserved among species than Cylc1" references only supplemental figures/tables. I find this unusual.

We agree, and in order to show the results of the evolutionary analysis more clearly, we moved the panel to main Figure 6.

Line 286-302: To address why Cylc2 deficiency causes more severe phenotypic alterations than Cylc1deficiency in mice, we performed evolutionary analysis of both genes. Analysis of the selective constrains on Cylc1 and Cylc2 across rodents and primates revealed that both genes’ coding sequences are conserved in general, although conservation is weaker in Cylc1 trending towards a more relaxed constraint (Fig. 6 A). A model allowing for separate calculation of the evolutionary rate for primates and rodents, did not detect a significant difference between the clades, neither for Cylc1 nor for Cylc2, indicating that the sequences are equally conserved in both clades.

To analyze the selective pressure across the coding sequence in more detail, we calculated the evolutionary rates for each codon site across the whole tree. According to the analysis, 34% of codon sites were conserved, 51% under relaxed selective constraint, and 15% positively selected. For Cylc2, 47% of codon sites conserved, 44% under neutral/relaxed constraint, and 9% positively selected. Interestingly, codon sites encoding lysine residues, which are proposed to be of functional importance for Cylicins, are mostly conserved. For Cylc1, 17% of lysine residues are significantly conserved and 35% of significantly conserved codons encode for lysine. For Cylc2, this pattern is even more pronounced with 27.9% of lysine codons being significantly conserved and 24.3% of all conserved sites encoding for lysine (Fig. 6 B).

(24) Line 332 - CYCL2 should be CYLC2

We corrected the typo accordingly.

(25) Line 340 The ratio of head defects is different from Table 1 (98% here and 99 % in the table). Please check this information.

We apologize for the inconsistency. We checked the raw data and corrected the table accordingly.

(26) Line 344-345 From figure 5C it is difficult to determine whether the sperm are "headless" or whether the heads are attached to the highly coiled tails next to them

We agree and we quantified the percentage of sperm showing abnormal flagella and a headless phenotype. Furthermore, we added an arrowhead to figure 6C to highlight headless sperm. The paragraph reads now as follows:

Line 335-339: Bright field microscopy demonstrated that M2270’s sperm flagella coiled in a similar manner compared to flagella of sperm from Cylicin deficient mice. Quantification revealed 57% of M2270 sperm displaying abnormal flagella compared to 6% in the healthy donor (Fig. 7 D). Interestingly, DAPI staining revealed that 27% of M2270 flagella carry cytoplasmatic bodies without nuclei and could be defined as headless spermatozoa (Fig. 7 C, white arrowhead; Fig. 7 E).

(27) L367-368 I agree with the authors' logic of this sentence. Although, it is better to show the co-localization of proteins using multi-channel immunocytochemistry. As you mentioned on L369 this will make your finding more obvious. If it is available, please include the colocalization images of the proteins.

We performed the multi-channel staining against Cylicin1 and Calicin, as well as Cylicin2 and Calicin on mouse epipidymal sperm and it’s shown in Figure 2 – supplement 4. Unfortunately, we did not manage to obtain stainings of tissue sections since antibodies against Cylicins and Calicin require different sample processing.

The sentence was added in the section describing calyx integrity:

Line 168-169: In epididymal sperm, CCIN co-localizes with both CYLC1 and CYLC2 in the calyx (Figure 2 – supplement 4).

(28) Line 376 Please keep the abbreviation. "Calicin" "CCIN".

We included the abbreviation accordingly.

Line 377-378: CCIN is shown to be necessary for the IAM-PT-NE complex by establishing bidirectional connections with other PT proteins.

(29) Line 377-378 "Based on ~". The authors did not prove the interaction between CCIN and Cylicins in this article. The mislocalization of CCIN might be resulted in the loss of Cylicins, without any "interaction". To reach this conclusion, a more direct result should be provided.

We agree that we overinterpreted this as we and others did not prove the interaction between CCIN and Cylicins so far. We therefore weakened this statement and formulated it as a hypothesis.

Line 377-381: CCIN is shown to be necessary for the IAM-PT-NE complex by establishing bidirectional connections with other PT proteins. Zhang et al. found CYLC1 to be among proteins enriched in PT fraction 7. Based on their speculation that CCIN is the main organizer of the PT, we hypothesize that both CCIN and Cylicins might interact, either directly or in a complex with other proteins, in order to provide the ‘molecular glue’ necessary for the acrosome anchoring.

(30) Line 499 Please specify which is the target of the immunostaining on the Figure legend. (Tubulin à acetylated α-tubulin)

We specified that α-Tubulin was stained. The figure legend reads now as follow: Line 555-557: Immunofluorescence staining of α-Tubulin to visualize manchette structure in squash testis samples of WT, Cylc1-/y, Cylc2+/-, Cylc2-/-, Cylc1 -/y Cylc2+/- and Cylc1-/y Cylc2-/- mice.

(31) Line 502 Please specify which color indicates which target protein (not only cellular structure).

Line 560-562: Co-staining of the manchette with HOOK1 (red) and acrosome with PNA-lectin (green) is shown in round, elongating and elongated spermatids of WT (upper panel) and Cylc2-/- mice (lower panel).

(32) Line 509 Please include scale bar information in the figure legend like Figure 4 (The magnifications of Figure 5 B, C, and D seem different).

We included the scale bar information accordingly (now Figure 6).

Line 575-588: Figure 6: Cylicins are required for human male fertility

(A) Pedigree of patient M2270. His father (M2270_F) is carrier of the heterozygous CYLC2 variant c.551G>A and his mother (M2270_M) carries the X-linked CYLC1 variant c.1720G>C in a heterozygous state. Asterisks (*) indicate the location of the variants in CYLC1 and CYLC2 within the electropherograms.

(B) Immunofluorescence staining of CYLC1 in spermatozoa from healthy donor and patient M2270. In donor’s sperm cells CYLC1 localizes in the calyx, while patient’s sperm cells are completely missing the signal. Scale bar: 5 µm.

(C) Bright field images of the spermatozoa from healthy donor and M2270 show visible head and tail anomalies, coiling of the flagellum as well as headless spermatozoa who carry cytoplasmatic residues without nuclei. Heads were counterstained with DAPI. Scale bar: 5 µm.

(D-E) Quantification of flagellum integrity (D) and headless sperm (E) in the semen of patient M2270 and a helathy donor.

(F-G) Immunofluorescence staining of CCIN (F) and PLCz (G) in sperm cells of patient M2270 and a healthy donor. Nuclei were counterstained with DAPI. Scale bar: 3 µm.

(33) S2A is not clear. Please describe specifically what the left panel and right panel are about to show with a clear indication of what is PM, mitochondria, etc. On the right, in only one cross-section that shows both mitochondria and the 9+2 axoneme, they look both unaltered whereas on the left, there are unpacked, not aligned mitochondria but the tail boundary is not clear to grasp at first sight.

We apologize for the bad quality of the TEM pictures showing the axonemes and the missing labeling. We recorded and included new images showing an intact 9+2 microtubular structure in Cylc2-/-. Furthermore, we added an image for the wildtype control.

(34) S2D: colors of the last three plots of each graph are too close to tell apart

We agree and changed the color scheme for better visualization.

Reviewer #2 (Recommendations For The Authors):

However, I find the manuscript a bit messy, and I will propose to reorganize the figures: following figure 1, showing the reproductive phenotype, I would continue with a figure showing the morphology of sperm in optical microscopy and showing the morphological defect of the nucleus (Fig 3B and 3E), followed with one figure focusing on the flagellum, with images obtained with optical and electronic microscopies, allowing to present the abnormalities of the flagellum and finally the impact on sperm motility and flagellum beating (mix of figure 2FG/3A); next, one figure focusing on acrosome. After that, I would present all data concerning spermiogenesis, starting with figure 2C.

We thank the reviewer for the valuable suggestion, which helps a lot to improve the structure and comprehensibility of the manuscript. We re-organized the figures and the results section accordingly.

Major remarks

1) Line 111. The specificity of raised Ab is not clear. Please specify if antibodies are specific: what immune-decorates anti-CYLC1: only CYLC1 or CYLC1 and CYLC2. Same question for anti-CYLC2

Both antibodies were raised against specific peptides of the CYLC1 or CYLC2 protein, respectively. The antigen peptides used for immunization are depicted in the Material and Methods section (AESRKSKNDERRKTLKIKFRGK and KDAKKEGKKKGKRESRKKR peptides for CYLC1; KSVGTHKSLASEKTKKEVK and ESGGEKAGSKKEAKDDKKDA for CYLC2). The peptides used for immunization are specific as they do not resemble the highly conserved and repetitive KKD/KKE motives present in both, Cylc1 and Cylc2.

The specificity of raised antibodies was validated by IF staining of wildype and Cylicin-deficient testis sections. The results clearly show, that CYLC1 signal is absent in Cylc1-deficient spermatids and CYLC2 signal being absent in Cylc2 deficient spermatids.

Specificity of antibodies was additionally proven by immunohistochemical stainings, showing a specific staining only in testis sections but not in any other organ tested.

Line 115-117: Specificity of antibodies was proven by immunohistochemical stainings, showing a specific staining only in testis sections but not in any other organ tested (Figure 1 - supplement 2)

To further verify the specificity of generated antibodies and the generation of functional knockout alleles, we additionally performed Western Blot analysis on cytoskeletal protein fractions, confirming the results of the IF staining.

The paragraph reads now as follows:

Line 127-134: Additionally, Western Blot analyses confirmed the absence of CYLC1 and CYLC2 in cytoskeletal protein fractions of the respective knockout (Fig. 1 G), thereby demonstrating i) specificity of the antibodies and ii) validating the gene knockout. Of note, the CYLC1 antibody detects a double band at 40-45 KDa. This is smaller than the predicted size of 74 KDa as, but both bands were absent in Cylc1-/y. Similarly, the CYLC2 Antibody detected a double band at 38-40 KDa instead of 66 KDa. Again, both bands were absent in Cylc2-/-. Next, Mass spectrometry analysis of cytoskeletal protein fraction of mature spermatozoa was performed detecting both proteins in WT but not in the respective knockout samples (Figure 1 – supplement 5; Figure 1 – supplement 6).

2) Line 115 and figure 1D. From the images presented in figure 1D, it is not clear where CYLC1 and CYLC2 are localized in the round and in elongated spermatids. Please make double staining using a second Ab to identify the acrosome such as DPY19L2 (best option) or SP56 and the manchette such as acetylated alpha-tubulin.

We agree, and we added a double staining of CYLC1/CYLC2 and SP56 to the supplement (Figure 1 - supplement 3), showing co-localization of the developing acrosome and Cylicins. Manchette staining was not performed due to antibodies being available in same species as those against Cylicins (anti-rabbit).

Line 117-120: Immunofluorescence staining of wildtype testicular tissue showed presence of both, CYLC1 and CYLC2 from the round spermatid stage onward (Fig. 1 E, Figure 1 – supplement 3). The signal was first detectable in the subacrosomal region as a cap like structure, lining the developing acrosome (Fig. 1 E-F, Figure 1 – supplement 3).

3) Line 118 and figure 1. The drawing showing the localization of Cylicin in mature sperm does not fit with the experimental data. Cylicins are located on the whole ventral face of the sperm.

We agree and apologize for the inconsistency. The illustration was adjusted according to the experimental data showing localization of Cylicins in the whole ventral part of the sperm.

4) Figure 1: Change "expression of Cylicin" to "localization of cylicin" (green)

We changed the legend accordingly.

5) Line 124 and figure 2C. In the figure provided, the PAS staining seems defective. The acrosomes do not seem stained (in pink as expected for a PAS staining). It may be due to the low quality of the pdf file, nevertheless, it is important to provide in supplementary data, an enlargement of the spermatid region showing the staining of the acrosome.

We apologize for the bad quality of the PDF file and the low magnification. We restructured the subfigure showing PAS stained spermatids at different steps of spermiogenesis at higher magnification. According to the initial reviewer’s suggestion, the PAS staining was moved to figure 4. The PAS staining in figure 2 was replaced by HE-stained overview testis sections in Figure 3 – supplement 1 showing intact spermatogenesis in all genotypes.

6) Line 130. Please indicate a reference for the lower limit of 58%. If this lower limit corresponds to human sperm, it should be omitted.

Indeed, the given reference limit of 58% is only valid for human sperm samples. Therefore, we omitted the reference limit. The paragraph reads now as follows: Line 144-146: Eosin-Nigrosin staining revealed that the viability of epididymal sperm from all genotypes was not severely affected (Fig. 2 D, Figure 2 – supplement 2).

7) line 152 Sperm morphology. Before showing the ultrastructure of the sperm, it would be important to show sperm morphology observed by optical microscopy. Therefore, I recommend including figure S2 as a principal figure, with a mix of Figures 3B and 3E.

We thank the reviewer for the suggestion. The results section was re-structured accordingly, first showing results of optical microscopy (Fig. 2), followed by an in-depth ultrastructural investigation of morphological defects and their effects on sperm motility. Brightfield images of epididymal sperm were moved from former Figure S2 to main Figure 2.

8) Line 164. figure S2A, showing that the 9+2 pattern is normal in KO sperm, is not convincing. Enlargement is required to conclude that the axoneme structure is normal; from the pictures, it rather seems that some doublets are missing.

We apologize for the bad quality of the TEM pictures showing the axonemes. We recorded and included new images showing an intact 9+2 microtubular structure.

9) Line 196. I would suggest removing the term "mild globozoospermia". Globozoospermia is rather complete (100% of round sperm heads) or incomplete (<90 % of round sperm heads). The anomalies observed on sperm heads, sperm motility, and the decrease in sperm concentration are rather suggestive of an OAT.

We agree and we omitted the term “mild globozoospermia”. Instead, we added a concluding remark to the section, summarizing the described defects as OAT syndrome. The section reads now as follows:

Line 215-217: Taken together, observed anomalies of sperm heads, impaired sperm motility, and the decrease in epididymal sperm concentration show that Cylc deficiency results in a severe OAT phenotype (Oligo-Astheno-Teratozoospermia-syndrome) described in human.

10) Line 248. It is not clear from the data of figure 4B that "the developing acrosome lost its compact adherence to the nuclear envelope". From this figure, only defective morphologies of the acrosome are observed

We agree and we omitted the sentence. Furthermore, it does not add additional information to the manuscript, since defects in the attachment of the acrosome to the nuclear envelope have been described in detail in Figure 4C.

11) line 260-264. Manchette defects appear at stages 9-10. At this stage, the HTCA is already attached to the nucleus of the spermatid. see for instance figure 2 from Shang Y, Zhu F, Wang L, Ouyang YC, Dong MZ, Liu C, Zhao H, Cui X, Ma D, Zhang Z, Yang X, Guo Y, Liu F, Yuan L, Gao F, Guo X, Sun QY, Cao Y, Li W. Essential role for SUN5 in anchoring sperm head to the tail. Elife. 2017 Sep 25;6:e28199. doi: 10.7554/eLife.28199 . Therefore, the hypothesis that "abnormal attachment of the developing flagellum to the basal plate and consequently flipping of the head and coiling of the tail in mature spermatozoa" is unlikely and I suggest modifying this paragraph. In the HOOK paper, the manchette defects occurred earlier.

We read the suggested literature and we agree to this reviewer’s comment. Manchette defects that we observe appear at later stages and are probably not responsible for the morphological anomalies of the mature sperm. We also re-analyzed all the manchette staining pictures and didn’t find any defects at earlier stages, so we decided to delete the sentence from the manuscript.

12) Line 344. Please indicate a percentage of headless spermatozoa. Many sperm is too vague.

We agree and we quantified the percentage of sperm showing abnormal flagella and a headless phenotype. The paragraph reads now as follows:

Line 335-339: Bright field microscopy demonstrated that M2270’s sperm flagella coiled in a similar manner compared to flagella of sperm from Cylicin deficient mice. Quantification revealed 57% of M2270 sperm displaying abnormal flagella compared to 6% in the healthy donor (Fig. 7 D). Interestingly, DAPI staining revealed that 27% of M2270 flagella carry cytoplasmatic bodies without nuclei and could be defined as headless spermatozoa (Fig. 7 C, white arrowhead; Fig. 7 E).

13) Any data concerning the success of ICSI for this patient?

Yes, the outcome of the ICSI were added to the main text. Line 309-311: The couple underwent one ICSI procedure which resulted in 17 fertilized oocytes out of 18 retrieved. Three cryo-single embryo transfers were performed in spontaneous cycles, but no pregnancy was achieved.

14) Finally, it would be interesting to study the localization of PLCzeta in this model, since its localization in the perinuclear theca has been clearly shown (Escoffier et al, 2015 doi:10.1093/molehr/gau098 )

We thank the reviewer for the valuable suggestion and performed PLCzeta staining on human sperm, clearly showing an irregular PT staining pattern in sperm of patient M2270 compared to healthy control sperm. Of note, staining was not possible in the mouse due to the antibody being reactive only for human samples.

The section reads as follows:

Line 343-349: Testis specific phospholipase C zeta 1 (PLCζ1) is localized in the postacrosomal region of PT in mammalian sperm (Yoon and Fissore, 2007) and has a role in generating calcium (Ca²⁺) oscillations that are necessary for oocyte activation (Yoon, 2008). Staining of healthy donor’s spermatozoa showed a previously described localization of PLCζ1 in the calyx, while sperm from M2270 patient presents signal irregularly through the PT surrounding sperm heads (Fig. 7 G). These results suggest that Cylicin deficiency can cause severe disruption of PT in human sperm as well, causing male infertility.

Reviewer #3 (Recommendations For The Authors):

1) Why the Cylc1-/y Cylc2+/- males were infertile? It would be helpful to show the homologue of the two proteins;

To elaborate more on the homology of CYLC1 and CYLC2, we added a more detailed section about the protein and domain structure to the introduction.

Line 73-78: In most species, two Cylicin genes, Cylc1 and Cylc2, have been identified (Figure 1supplement 1). They are characterized by repetitive lysine-lysine-aspartic acid (KKD) and lysine-lysineglutamic acid (KKE) peptide motifs, resulting in an isoelectric point (IEP) > pH 10 14, 15. Repeating units of up to 41 amino acids in the central part of the molecules stand out by a predicted tendency to form individual short α-helices (Hess et al., 1993). Mammalian Cylicins exhibit similar protein and domain characteristics, but CYLC2 has a much shorter amino-terminal portion than CYLC1 (Figure 1supplement 1).

Speculations about the infertility of Cylc1-/y Cylc2+/- males was added to the discussion:

Line 410-413: Interestingly, Cylc1-/Y Cylc2+/- males displayed an “intermediate” phenotype, showing slightly less damaged sperm than Cylc2-/- and Cylc1-/Y Cylc2-/- animals. This further supports our notion, that loss of the less conserved Cylc1 gene might be at least partially compensated by the remaining Cylc2 allele.

2) Western blot is important to show the absence of the two proteins in the mouse models;

To further verify the specificity of generated antibodies and the generation of functional knockout alleles, we additionally performed Western Blot analysis on cytoskeletal protein fractions, confirming the results of the IF staining.

A paragraph was added to the manuscript and reads as follows:

Line 127-134: Additionally, Western Blot analyses confirmed the absence of CYLC1 and CYLC2 in cytoskeletal protein fractions of the respective knockout (Fig. 1 G), thereby demonstrating i) specificity of the antibodies and ii) validating the gene knockout. Of note, the CYLC1 antibody detects a double band at 40-45 KDa. This is smaller than the predicted size of 74 KDa as, but both bands were absent in Cylc1-/y. Similarly, the CYLC2 Antibody detected a double band at 38-40 KDa instead of 66 KDa. Again, both bands were absent in Cylc2-/-. Next, Mass spectrometry analysis of cytoskeletal protein fraction of mature spermatozoa was performed detecting both proteins in WT but not in the respective knockout samples (Figure 1 – supplement 5; Figure 1 – supplement 6).

3) On Page 7, line 227 and line 243, was the acetylated α-tubulin or α-tubulin antibody used?

For all stainings α-tubulin antibody was used. We corrected this accordingly. Line 257-259: We used immunofluorescence staining of α-tubulin on squash testis samples containing spermatids at different stages of spermiogenesis to investigate whether the altered head shape, calyx structure, and tail-head connection anomalies originate from possible defects of the manchette structure.

4) Fig. 2S: A cartoon showing the elongation and circularity of nuclei for evaluation is helpful; The TEM images from the control and Cylc1 KO mice are needed;

Cylc1-/Y TEM picture was added in Figure 3A.

5) The discussion should be rewritten. The current version is to repeat the experiments/findings. The authors should discuss more about the potential mechanisms.

We discussed the observed defects of Cylc-deficient animals and discussed this in relation to other published mouse models deficient in Calyx components. Furthermore, we speculated about potential interaction partners of Cylicins and the importance of these protein complexes for male fertility. However, to this point, we think that it is too farfetched to speculate about potential mechanisms without any evidence for Cylc interaction partner or their exact molecular function. This requires further research.

Author Response

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

eLife assessment

This useful manuscript challenges the utility of current paradigms for estimating brain-age with magnetic resonance imaging measures, but presents inadequate evidence to support the suggestion that an alternative approach focused on predicting cognition is more useful. The paper would benefit from a clearer explication of the methods and a more critical evaluation of the conceptual basis of the different models. This work will be of interest to researchers working on brain-age and related models.

Response: Thank you so much for providing high-quality reviews on our manuscript. We revised the manuscript to address all of the reviewers’ comments and provided full responses to each of the comments below.

Briefly, regarding clearer explanations of the methods, we added additional analyses (e.g., commonality analyses on ridge regression and on multiple regressions with a quadratic term for chronological age) to address some of the concerns and additional details in text and figures to ensure that the reader can fully understand our methodological procedures. Regarding the critical evaluation of the conceptual basis of the different models, we added discussions to help with interpretations and the scope of the generalisability of our findings. For instance, as opposed to treating Brain Cognition and Brain Age as separate biomarkers and comparing them in the ability to explain fluid cognition, we now treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. In other words, we now examined the extent to which Brain Age missed the variation in the brain MRI that could explain fluid cognition (for this particular issue, please see our response to Reviewer 3 Public Review #4).

Reviewer 1:

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. I have some comments that I believe the authors ought to address which mostly relate to clarity and interpretation.

Reviewer 1 Public Review #1:

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. I would suggest the authors nuance their discussion to provide broader considerations of the utility of their method and on the limits of interpretation of brain-age models more generally. Further, I think that since brain-age models by construction confound relevant biological variation with the accuracy of the regression models used to estimate them, there may be limits to the interpretation of (e.g.) the brain-age gap is as a dimensionless biomarker. This has also been discussed elsewhere (see e.g. https://academic.oup.com/brain/article/143/7/2312/5863667). I would suggest that the authors consider and comment on these issues.

Response: Thank you Reviewer 1 for pointing out these important issues. We addressed them in our response to Reviewer 1 Recommendations For The Authors #1 (see below).

Reviewer 1 Public Review #2

Second, from a methods perspective, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand how the stacked regression models were constructed. Stacked models can be prone to overfitting when combined with cross-validation. This is because the predictions from the first-level models (i.e. the features that are provided to the second level 'stacked' models) contain information about the training set and the test set. If cross-validation is not done very carefully (e.g. using multiple hold-out sets), information leakage can easily occur at the second level. Unfortunately, there is not a sufficient explanation of the methodological procedures in the current manuscript to fully understand what was actually done. Please provide more information to enable the reader to better understand the stacked regression models. If the authors are not using an approach that fully preserves training and test separability, they need to do so.

Response: Thank you Reviewer 1. We addressed this issue in our response to Reviewer 1 Recommendations For The Authors #2 (see below). Briefly, we now made it clearer that training models for both non-stacked and stacked models did not involve the test set, ensuring that there was no data leakage between training and test sets.

Reviewer 1 Public Review #3

Please also provide an indication of the different regression strengths that were estimated across the different models and cross-validation splits. Also, how stable were the weights across splits?

Response: Thank you Reviewer 1. We addressed this issue in our response to Reviewer 1 Recommendations For The Authors #3 (see below).

Reviewer 1 Public Review #4:

Please provide more details about the task designs, MRI processing procedures that were employed on this sample in addition to the regression methods, and bias-correction methods used. For example, there are several different parameterisations of the elastic net, please provide equations to describe the method used here so that readers can easily determine how the regularisation parameters should be interpreted.

Response: Thank you Reviewer 1. We addressed this issue in our response to Reviewer 1 Recommendations For The Authors #5-#6. Briefly, we followed your advice and add all of the suggested details.

Reviewer 2 (Public Review):

Reviewer 2 Public Review Overall:

In this study, the authors aimed to evaluate the contribution of brain-age indices in capturing variance in cognitive decline and proposed an alternative index, brain-cognition, for consideration. The study employs suitable data and methods, albeit with some limitations, to address the research questions. A more detailed discussion of methodological limitations in relation to the study's aims is required. For instance, the current commonality analysis may not sufficiently address potential multicollinearity issues, which could confound the findings. Importantly, given that the study did not provide external validation for the indices, it is unclear how well the models would perform and generalize to other samples. This is particularly relevant to their novel index, brain-cognition, given that brain-age has been validated extensively elsewhere. In addition, the paper's rationale for using elastic net, which references previous fMRI studies, seemed somewhat unclear. The discussion could be more nuanced and certain conclusions appear speculative.

Response Thank you for your encouragement. We have now added discussion of methodological limitations (see below). Regarding potential multicollinearity issues, we addressed this comment using Ridge regressions (see our response to Reviewer 2 Recommendations For The Authors #2). Regarding external validation, we now added discussions about how consistency between our results and several recent studies that investigated similar issues with Brain Age in different populations (see Reviewer 2 Recommendations For The Authors #1). Regarding Brain Cognition, we also added previous studies showing similarly high prediction for cognition functioning (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We added a discussion about Elastic Net (see Reviewer 1 Recommendations For The Authors #6)

Discussion

“There are several potential limitations of this study. First, we conducted an investigation relying only on one dataset, the Human Connectome Project in Aging (HCP-A) (Bookheimer et al., 2019). While HCP-A used state-of-the-art MRI methodologies, covered a wide age range from 36 to 100 years old and used several task-fMRI from different tasks that are harder to find in other bigger databases (e.g., UK Biobank from Sudlow et al., 2015), several characteristics of HCP-A might limit the generalisability of our findings. For instance, the tasks used in task-based fMRI in HCP-A are not used widely in clinical settings (Horien et al., 2020). This might make it challenging to translate the approaches used here. Similarly, HCP-A also excluded participants with neurological conditions, possibly making their participants not representative of the general population. Next, while HCP-A’s sample size is not small (n=725 and 504 people, before and after exclusion, respectively), other datasets provide a much larger sample size (Horien et al., 2020). Similarly, HCP-A does not include younger populations. But as mentioned above, a study with a larger sample in older adults (Cole, 2020) and studies in younger populations (8-22 years old) (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023) also found small effects of the adjusted Brain Age Gap in explaining cognitive functioning. And the disagreement between the predictive performance of age-prediction models and the utility of Brain Age found here is largely in line with the findings across different phenotypes seen in a recent systematic review (Jirsaraie, Gorelik, et al., 2023).”

Reviewer 2 Public Review #1:

The authors aimed to evaluate how brain-age and brain-cognition indices capture cognitive decline (as mentioned in their title) but did not employ longitudinal data, essential for calculating 'decline'. As a result, 'cognition-fluid' should not be used interchangeably with 'cognitive decline,' which is inappropriate in this context.

Response Thank you for raising this issue. We now no longer used the word ‘cognitive decline’.

Reviewer 2 Public Review #2:

In their first aim, the authors compared the contributions of brain-age and chronological age in explaining variance in cognition-fluid. Results revealed much smaller effect sizes for brain-age indices compared to the large effects for chronological age. While this comparison is noteworthy, it highlights a well-known fact: chronological age is a strong predictor of disease and mortality. Has the brain-age literature systematically overlooked this effect? If so, please provide relevant examples. They conclude that due to the smaller effect size, brain-age may lack clinical significance, for instance, in associations with neurodegenerative disorders. However, caution is required when speculating on what brain-age may fail to predict in the absence of direct empirical testing. This conclusion also overlooks extant brain-age literature: although effect sizes vary across psychiatric and neurological disorders, brain-age has demonstrated significant effects beyond those driven by chronological age, supporting its utility.

Response For aim 1, we focused our claims on cognitive functioning and not on any clinical significance for neurodegenerative disorders. We now made it clearer that the small effects of the Corrected Brain Age Gap in explaining fluid cognition of aging individuals found here are consistent with a study with a larger sample in older adults (Cole, 2020) and studies in younger populations (8-22 years old) (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023).

We believe this issue of the utility of brain age on cognitive functioning vs neurological/psychological disorders requires another consideration, namely the discrepancy in the training and test samples typically used for studies focusing on neurological/psychological disorders. We made this point in the discussion now (see below).

Discussion

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). That is, those Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. This means that age-prediction models from Brain Age studies focusing on neurological/psychological disorders might be under-fitted when applied to participants with neurological/psychological disorders because they were built from largely healthy participants. And thus the difference in Brain Age indices between participants without vs. with neurological/psychological disorders might be confounded by the under-fitted age-prediction models (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other Brain Age studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning do not suffer from being under-fitted. We consider this as a strength, not a weakness of our study.”

Reviewer 2 Public Review #3:

The second aim's results reveal a discrepancy between the accuracy of their brain-age models in estimating age and the brain-age's capacity to explain variance in cognition-fluid. The authors suggest that if the ultimate goal is to capture cognitive variance, brain-age predictive models should be optimized to predict this target variable rather than age. While this finding is important and noteworthy, additional analyses are needed to eliminate potential confounding factors, such as correlated noise between the data and cognitive outcome, overfitting, or the inclusion of non-healthy participants in the sample. Optimizing brain-age models to predict the target variable instead of age could ultimately shift the focus away from the brain-age paradigm, as it might optimize for a factor differing from age.

Response We discussed the issue regarding the discrepancy between the accuracy of their brain-age models in estimating age and the brain-age's capacity to explain variance in fluid cognition in our response to Reviewer 3 Public Review #9 (see below). This issue is found to be widespread in a recent systematic review (Jirsaraie, Gorelik, et al., 2023). We now provided several strategies to mitigate this issue to improve the utility of Brain Age in explaining other phenotypes based on our current work and others, using different MRI modalities as well as modelling techniques (Bashyam et al., 2020; Jirsaraie, Kaufmann, et al., 2023; Rokicki et al., 2021).

Regarding potential confounding factors, we are not sure what the reviewer meant by “correlated noise between the data and cognitive outcome”. The current study, for instance, used ICA-FIX (Glasser et al., 2016) to remove noise in functional MRI. It is unclear how much ‘noise’ is still left and might confound our findings. More importantly, we are not sure how to define ‘noise’ as referred to by Reviewer 2 here. As for overfitting, we used nested cross-validation to ensure that training and test sets were separate from each other (see Reviewer 1 Recommendations For The Authors #2). If overfitting happened as suggested, we should see a ‘lower’ predictive performance of age-prediction and cognitive-prediction models since the models would fit well with the training set but would not generalise well to the test set. This is not what we found. The predictive performance of our age-prediction and cognitive-prediction models was high and consistent with the literature. Regarding the inclusion of non-healthy participants in the sample, we discussed this above in our response to Reviewer 2 Public Review #2).

Reviewer 2 Public Review #4:

While a primary goal in biomarker research is to obtain indices that effectively explain variance in the outcome variable of interest, thus favouring models optimized for this purpose, the authors' conclusion overlooks the potential value of 'generic/indirect' models, despite sacrificing some additional explained variance provided by ad-hoc or 'specific/direct' models. In this context, we could consider brain-age as a 'generic' index due to its robust out-of-sample validity and significant associations across various health outcome variables reported in the literature. In contrast, the brain-cognition index proposed in this study is presumed to be 'specific' as, without out-of-sample performance metrics and testing with different outcome variables (e.g., neurodegenerative disease), it remains uncertain whether the reported effect would generalize beyond predicting cognition-fluid, the same variable used to condition the brain-cognition model in this study. A 'generic' index like brain-age enables comparability across different applications based on a common benchmark (rather than numerous specific models) and can support explanatory hypotheses (e.g., "accelerated ageing") since it is grounded in its own biological hypothesis. Generic and specific indices are not mutually exclusive; instead, they may offer complementary information. Their respective utility may depend heavily on the context and research or clinical question.

Response Thank you Reviewer 2 for pointing out this important issue. Reviewer 1 (Recommendations For The Authors #4) and Reviewer 3 (Public Review #4) bought up a similar issue. We agreed with Reviewer 2 that both 'specific/direct' index and Brain Age as a 'generic/indirect' index have merit in their own right. We made a discussion about this issue in our response to Reviewer 3 Public Review #4 (please see this response below).

Briefly, in the revision, as opposed to treating Brain Cognition and Brain Age as separate biomarkers and comparing them, we treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. In other words, we now examined the extent to which Brain Age missed the variation in the brain MRI that could explain fluid cognition. We also made a discussion about using our commonality approach to test for this missing variation in future work:

Discussion

“Finally, researchers should test how much Brain Age miss the variation in the brain MRI that could explain fluid cognition or other phenotypes of interest. As demonstrated here, one straightforward method is to build a prediction model using a phenotype of interest as the target (e.g., fluid cognition) and incorporate the predicted value of this model (e.g., Brain Cognition), along with Brain Age and chronological age, into a multiple regression for commonality analyses. The unique effect of this predicted value will inform the missing variation in the brain MRI from Brain Age. If this unique effect is large, then researchers might need to reconsider whether using Brain Age is appropriate for a particular phenotype of interest.”

Reviewer 2 Public Review #5:

The study's third aim was to evaluate the authors' new index, brain-cognition. The results and conclusions drawn appear similar: compared to brain-age, brain-cognition captures more variance in the outcome variable, cognition-fluid. However, greater context and discussion of limitations is required here. Given the nature of the input variables (a large proportion of models in the study were based on fMRI data using cognitive tasks), it is perhaps unsurprising that optimizing these features for cognition-fluid generates an index better at explaining variance in cognition-fluid than the same features used to predict age. In other words, it is expected that brain-cognition would outperform brain-age in explaining variance in cognition-fluid since the former was optimized for the same variable in the same sample, while brain-age was optimized for age. Consequently, it is unclear if potential overfitting issues may inflate the brain-cognition's performance. This may be more evident when the model's input features are the ones closely related to cognition, e.g., fMRI tasks. When features were less directly related to cognitive tasks, e.g., structural MRI, the effect sizes for brain-cognition were notably smaller (see 'Total Brain Volume' and 'Subcortical Volume' models in Figure 6). This observation raises an important feasibility issue that the authors do not consider. Given the low likelihood of having task-based fMRI data available in clinical settings (such as hospitals), estimating a brain-cognition index that yields the large effects discussed in the study may be challenged by data scarcity.

Response Given the use of nested cross-validation, we do not consider the good predictive performance of Brain Cognition found here as overfitting. In fact, we found a similar level of predictive performance of Brain Cognition on another database with younger participants in the past (Tetereva et al., 2022). However, we agreed with Reviewer 2 that the prediction of fluid cognition might be driven by MRI modalities that are different from those that drive the prediction of chronological age. In our own work with other age groups, including young adults (Tetereva et al., 2022) and children (Pat, Wang, Anney, et al., 2022), cognitive functioning seems to be predicted well from task-based functional MRI. And Reviewer 2 is right that task-based fMRI is not commonly used in clinics, making it harder to translate our results. However, given our results, clinicians should be encouraged to use task-based fMRI if their goal is to predict cognitive functioning. Nevertheless, as suggested, we listed data scarcity as one of the limitations of our approach.

Discussion “For instance, the tasks used in task-based fMRI in HCP-A are not used widely in clinical settings (Horien et al., 2020). This might make it challenging to translate the approaches used here.”

Reviewer 2 Public Review #6:

This study is valuable and likely to be useful in two main ways. First, it can spur further research aimed at disentangling the lack of correspondence reported between the accuracy of the brain-age model and the brain-age's capacity to explain variance in fluid cognitive ability. Second, the study may serve, at least in part, as an illustration of the potential pros and cons of using indices that are specific and directly related to the outcome variable versus those that are generic and only indirectly related.

Response We are thankful for the encouragement. For the discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker for fluid cognition, we made a detailed discussion in our response to Reviewer 3 Public Review #9. More specifically, to ensure that readers can benefit from our findings, we made suggestions on how to ensure the utility of Brain Age indices as a biomarker for other phenotypes by drawing from our own strategy, as well as strategies used by Rokicki and colleagues (2021), Jirsaraie and colleagues (2023) and Bashyam and colleagues (2020).

As for the pros and cons between generic vs specific biomarkers, we made a detailed discussion in our response to Reviewer 3 Public Review #4. We also made some suggestions on how to make use of the difference in the ability between generic vs specific biomarkers (see Reviewer 2 Public Review #4, above).

Reviewer 2 Public Review #7:

Overall, the authors effectively present a clear design and well-structured procedure; however, their work could have been enhanced by providing more context for both the brain-age and brain-cognition indices, including a discussion of key concepts in the brain-age paradigm, which acknowledges that chronological age strongly predicts negative health outcomes, but crucially, recognizes that ageing does not affect everyone uniformly. Capturing this deviation from a healthy norm of ageing is the key brain-age index. This lack of context was mirrored in the presentation of the four brain-age indices provided, as it does not refer to how these indices are used in practice. In fact, there is no mention of a more common way in which brain-age is implemented in statistical analyses, which involves the use of brain-age delta as the variable of interest, along with linear and non-linear terms of age as covariates. The latter is used to account for the regression-to-the-mean effect. The 'corrected brain-age delta' the authors use does not include a non-linear term, which perhaps is an additional reason (besides the one provided by the authors) as to why there may be small, but non-zero, common effects of both age and brain-age in the 'corrected brain-age delta' index commonality analysis. The context for brain-cognition was even more limited, with no reference to any existing literature that has explored direct brain-cognitive markers, such as brain-cognition.

Response Regarding Brain Age and negative health outcomes, we addressed this in our response to Reviewer 1 Recommendations For The Authors #1 (see below). Briefly, we now discussed (1) the consistency between our findings on fluid cognition and other recent works on negative health outcomes, (2) the differences between Brain Age studies focusing on negative health outcomes vs. cognitive functioning and (3) suggested solutions to optimise the utility of brain age for both cognitive functioning and negative health outcomes.

Regarding how Brain Age was used in practice, we addressed this in our response to Reviewer 3 Public Review #2 (see below). Our argument resonates Butler and colleagues’ (2021) suggestion that the common practice for Brain Age analysis should be re-evaluated: “The MBAG and performance on the complex cognition tasks were not associated (r =  .01, p = 0.71). These results indicate that the association between cognition and the BAG are driven by the association between age and cognitive performance. As such, it is critical that readers of past literature note whether or not age was controlled for when testing for effects on the BAG, as this has not always been common practice (e.g., Beheshti et al., 2018; Cole, Underwood, et al., 2017; Franke et al., 2015; Gaser et al., 2013; Liem et al., 2017; Nenadi c et al., 2017; Steffener et al., 2016). (p. 4097).”

Importantly, we also implemented “brain-age delta as the variable of interest, along with linear and non-linear terms of age as covariates” in our additional analyses along with other implementations (see Reviewer 2 Recommendations For The Authors #3). Of particular note, we found that adding a non-linear term (i.e., a quadratic term for chronological age) barely changed the results of commonality analyses.

We now wrote this paragraph to recommend how future research should implement Brain Age:

Discussion

“First, they have to be aware of the overlap in variation between Brain Age and chronological age and should focus on the contribution of Brain Age over and above chronological age. Using Brain Age Gap will not fix this. Butler and colleagues (2021) recently highlighted this point, “These results indicate that the association between cognition and the BAG are driven by the association between age and cognitive performance. As such, it is critical that readers of past literature note whether or not age was controlled for when testing for effects on the BAG, as this has not always been common practice (p. 4097).” Similar to their recommendation (Butler et al., 2021), we suggest future work focus on Corrected Brain Age Gap or, better, unique effects of Brain Age indices after controlling for chronological age in multiple regressions. In the case of fluid cognition, the unique effects might be too small to be clinically meaningful as shown here and previously (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023). “

Regarding brain cognition, we now expanded our explanation about Brain Cognition on how it might be relevant to Brain Age and on Brain Cognition’s predictive performance found previously.

Introduction

“Third and finally, certain variation in the brain MRI is related to fluid cognition, but to what extent does Brain Age not capture this variation? To estimate the variation in the brain MRI that is related to fluid cognition, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in the brain MRI that is related to fluid cognition and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. Consequently, the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age indicate what is missing from Brain Age -- the amount of co-variation between brain MRI and fluid cognition that cannot be captured by Brain Age.”

Discussion

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation of brain MRI that is related to fluid cognition. Brain Cognition, from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022).”

Reviewer 2 Public Review #8:

While this paper delivers intriguing and thought-provoking results, it would benefit from recognizing the value that both approaches--brain-age indices and more direct, specific markers like brain-cognition--can contribute to the field.

Response Thank you so much for recognising the value of our work. As we mentioned above in our response to Reviewer 2 Public Review #4 and #6, we made some suggestions on how to make use of the difference in the ability between generic vs specific biomarkers.

Reviewer 3 (Public Review):

Reviewer 3 Public Review Overall:

The main question of this article is as follows: "To what extent does having information on brain-age improve our ability to capture declines in fluid cognition beyond knowing a person's chronological age?" While this question is worthwhile, considering that there is considerable confusion in the field about the nature of brain-age, the authors are currently missing an opportunity to convey the inevitability of their results, given how brain-age and the brain-age gap are calculated. They also argue that brain-cognition is somehow superior to brain-age, but insufficient evidence is provided in support of this claim.

Response We addressed the concerns below. The inevitability of our results is not obvious to many researchers who might be interested in Brain Age. We hope our findings might make many issues surrounding Brain Age more obvious, and we now make many suggestions on how to address some of these issues. We no longer argue that Brain Cognition is superior to Brain Age (Reviewer 3 Public Review #4). Rather, we treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. We used the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age to indicate how much Brain Age misses the variation in the brain MRI that could explain fluid cognition.

Specific comments follow:

Reviewer 3 Public Review #1:

• "There are many adjustments proposed to correct for this estimation bias" (p3). Regression to the mean is not a sign of bias. Any decent loss function will result in over-predicting the age of younger individuals and under-predicting the age of older individuals. This is a direct result of minimizing an error term (e.g., mean squared error). Therefore, it is inappropriate to refer to regression to the mean as a sign of bias. This misconception has led to a great deal of inappropriate analyses, including "correcting" the brain age gap by regressing out age.

Response: Thank you so much for raising this issue. We used the word ‘bias’ following many articles in the field. For instance,

de Lange and Cole (2020) wrote: “brain-age estimation also involves a frequently observed bias: brain age is overestimated in younger subjects and underestimated in older subjects, while brain age for participants with an age closer to the mean age (of the training dataset) are predicted more accurately (Cole, Le, Kuplicki, McKinney, Yeh, Thompson, Paulus, Investigators, et al., 2018, Liang, Zhang, Niu, 2019, Niu, Zhang, Kounios, Liang, 2019, Smith, Vidaurre, Alfaro-Almagro, Nichols, Miller, 2019).”

Cole (2020) wrote: “As recent research has highlighted a proportional bias in brain-age calculation, whereby the difference between chronological age and brain-predicted age is negatively correlated with chronological age (Le et al., 2018, Liang et al., 2019, Smith et al., 2019), an age-bias correction procedure was used. This entailed calculating the regression line between age (predictor) and brain-predicted age (outcome) in the training set, then using the slope (i.e., coefficient) and intercept of that line to adjust brain-predicted age values in the testing set (by subtracting the intercept and then dividing by the slope). After applying the age-bias correction the brain-predicted age difference (brain-PAD) was calculated; chronological age subtracted from brain-predicted age.”

Beheshiti and colleagues (2019) used bias in their title: “Bias-adjustment in neuroimaging-based brain age frameworks: a robust scheme”

More recently, Cumplido-Mayoral and colleagues (2023) wrote: “As recent research has shown that brain-age estimation involves a proportional bias (de Lange et al., 2020a; Le et al., 2018; Liang et al., 2019; Smith et al., 2019), we applied a well-established age-bias correction procedure to our data (de Lange et al., 2020a; Le et al., 2018).”

Still, we agree with Reviewer 3 that using ‘bias’ might lead to misinterpretation. As Butler and colleagues (Butler et al., 2021) pointed out, ”It is important to note that regression toward the mean is not a failure, but a feature, of regression and related methods.“ We rewrote the paragraph and clarified the “regression towards the mean” issue. We no longer used the word “bias” here:

Introduction

“Note researchers often subtract chronological age from Brain Age, creating an index known as Brain Age Gap (Franke & Gaser, 2019). A higher value of Brain Age Gap is thought to reflect accelerated/premature aging. Yet, given that Brain Age Gap is calculated based on both Brain Age and chronological age, Brain Age Gap still depends on chronological age (Butler et al., 2021). If, for instance, Brain Age was based on prediction models with poor performance and made a prediction that everyone was 50 years old, individual differences in Brain Age Gap would then depend solely on chronological age (i.e., 50 minus chronological age). Moreover, Brain Age is known to demonstrate the “regression towards the mean” phenomenon (Stigler, 1997). More specifically, because Brain Age is a predicted value of a regression model that predicts chronological age, Brain Age is usually shrunk towards the mean age of samples used for training the model (Butler et al., 2021; de Lange & Cole, 2020; Le et al., 2018). Accordingly, Brain Age predicts chronological age more accurately for individuals who are closer to the mean age while overestimating younger individuals’ chronological age and underestimating older individuals’ chronological age. There are many adjustments proposed to correct for the age dependency, but the outcomes tend to be similar to each other (Beheshti et al., 2019; de Lange & Cole, 2020; Liang et al., 2019; Smith et al., 2019). These adjustments can be applied to Brain Age and Brain Age Gap, creating Corrected Brain Age and Corrected Brain Age Gap, respectively. Corrected Brain Age Gap in particular is viewed as being able to control for age dependency (Butler et al., 2021). Here, we tested the utility of different Brain Age calculations in capturing fluid cognition, over and above chronological age.”

Reviewer 3 Public Review #2:

• "Corrected Brain Age Gap in particular is viewed as being able to control for both age dependency and estimation biases (Butler et al., 2021)" (p3). This summary is not accurate as Butler and colleagues did not use the words "corrected" and "biases" in this context. All that authors say in that paper is that regressing out age from the brain age gap - which is referred to as the modified brain age gap (MBAG) - makes it so that the modified brain age gap is not dependent on age, which is true. This metric is meaningless, though, because it is the variance left over after regressing out age from residuals from a model that was predicting age. If it were not for the fact that regression on residuals is not equivalent to multiple regression (and out of sample estimates), MBAG would be a vector of zeros. Upon reading the Methods, I noticed that the authors use a metric from Le et al. (2018) for the "Corrected Brain Age Gap". If they cite the Butler et al. (2021) paper, I highly recommend sticking with the same notation, metrics and terminology throughout. That would greatly help with the interpretability of the present manuscript, and cross-comparisons between the two.

Response: We thank Reviewer 3 for pointing out the issues surrounding our choices of wording: "corrected" and "biases". We share the same frustration with Reviewer 3 in that different brain-age articles use different terminologies, and we tried to make sure our readers understand our calculations of Brain Age indices in order to compare our results with previous work.

We commented on the word “bias” in our response to Reviewer 3 Public Review #1 above and refrained from using this word in the revised manuscript. Here we commented on the use of the word “Corrected Brain Age Gap". And by doing so, we clarified how we calculated it.

Reviewer 3 is right that we cited the work of Butler and colleagues (2021), but wasn’t accurate to say that we used “a metric from Le et al. (2018) for the "Corrected Brain Age Gap". We, instead, used a method described in de Lange and Cole’s (2020) work. We now added equations to explain this method in our Materials and Method section (see below).

It is important to note that Butler and colleagues (2021) did not come up with any adjustment methods. Instead, Butler and colleagues (2021) discussed three adjustment methods:

1) A method proposed by Beheshiti and colleagues (2019). Butler and colleagues (2021) called the result of this method, Modified Brain Age Gap (MBAG). Importantly, Butler and colleagues (2021) discouraged the use of this method due to “researchers misinterpreting the reduced variability of the MBAG as an improvement in prediction accuracy.” Accordingly in our article, we performed methods (2) and (3) below.

2) A method proposed by de Lange and Cole (2020). We used this method in our article (see below for the equations). Briefly, we first fit a regression line predicting the Brain Age from a chronological age in each training set. We then used the slope and intercept of this regression line to adjust Brain Age in the corresponding test set, resulting in an adjusted index of Brain Age. Butler and colleagues (2021) called this index, “Revised Predicted Age.”, while de Lange and Cole’s (2020) originally called this Corrected Brain Age, “Corrected Predicted Age”. Butler and colleagues (2021) then subtracted the chronological age from this index and called it, “Revised Brain Age Gap (RBAG)”. We would like to follow the original terminology, but we do not want to use the word “Predicted Age” since chronological age can be predicted by other variables beyond the brain. We then settled with the word, "Corrected Brain Age" and “Corrected Brain Age Gap". We listed the terminologies used in the past in our article (see below).

3) A method proposed by Le and colleagues (2018). Here, Butler and colleagues (2021) referred to one of the approaches done by Le and colleagues: “include age as a regressor when doing follow-up analyses.” Essentially this is what we did for the commonality analysis. Le and colleagues (2018)’ approach is the same as examining the unique effects of Brain Age in a multiple regression analysis with Chronological Age and Brain Age as regressors.

While indexes from de Lange and Cole’s (2020) and Le and colleagues’ (2018) methods show poor performance in capturing fluid cognition in the current work, we need to stress that many research groups do not believe that these methods are meaningless. In fact, de Lange and Cole’s method (2020) is one of the most commonly implemented methods that can be seen elsewhere (e.g., Cole et al., 2020; Cumplido-Mayoral et al., 2023; Denissen et al., 2022). This index just does not seem to work well in the case of fluid cognition.

Here is how we described how we calculated Brain Age indexes in the revised manuscript:

Methods

“ Brain Age calculations: Brain Age, Brain Age Gap, Corrected Brain Age and Corrected Brain Age Gap In addition to Brain Age, which is the predicted value from the models predicting chronological age in the test sets, we calculated three other indices to reflect the estimation of brain aging. First, Brain Age Gap reflects the difference between the age predicted by brain MRI and the actual, chronological age. Here we simply subtracted the chronological age from Brain Age:

Brain Age Gapi = Brain Agei - chronological agei , (2)

where i is the individual. Next, to reduce the dependency on chronological age (Butler et al., 2021; de Lange & Cole, 2020; Le et al., 2018), we applied a method described in de Lange and Cole’s (2020), which was implemented elsewhere (Cole et al., 2020; Cumplido-Mayoral et al., 2023; Denissen et al., 2022):

In each outer-fold training set: Brain Agei = 0 + 1 chronological agei + εi, (3)

Then in the corresponding outer-fold test set: Corrected Brain Agei = (Brain Agei - 0)/1, (4)

That is, we first fit a regression line predicting the Brain Age from a chronological age in each outer-fold training set. We then used the slope (1) and intercept (0) of this regression line to adjust Brain Age in the corresponding outer-fold test set, resulting in Corrected Brain Age. Note de Lange and Cole (2020) called this Corrected Brain Age, “Corrected Predicted Age”, while Butler (2021) called it “Revised Predicted Age.”

Lastly, we computed Corrected Brain Age Gap by subtracting the chronological age from the Corrected Brain Age (Butler et al., 2021; Cole et al., 2020; de Lange & Cole, 2020; Denissen et al., 2022):

Corrected Brain Age Gap = Corrected Brain Age - chronological age, (5)

Note Cole and colleagues (2020) called Corrected Brain Age Gap, “brain-predicted age difference (brain-PAD),” while Butler and colleagues (2021) called this index, “Revised Brain Age Gap”.

Reviewer 3 Public Review #3:

• "However, the improvement in predicting chronological age may not necessarily make Brain Age to be better at capturing Cognitionfluid. If, for instance, the age-prediction model had the perfect performance, Brian Age Gap would be exactly zero and would have no utility in capturing Cognitionfluid beyond chronological age" (p3). I largely agree with this statement. I would be really careful to distinguish between brain-age and the brain-age gap here, as the former is a predicted value, and the latter is the residual times -1 (i.e., predicted age - age). Therefore, together they explain all of the variance in age. Changing the first sentence to refer to the brain-age gap would be more accurate in this context. The brain-age gap will never be exactly zero, though, even with perfect prediction on the training set, because subjects in the testing set are different from the subjects in the training set.

Response: Thank you so much for pointing this out. We agree to change “Brain Age” to “Brain Age Gap” in the mentioned sentence.

Reviewer 3 Public Review #4:

• "Can we further improve our ability to capture the decline in cognitionfluid by using, not only Brain Age and chronological age, but also another biomarker, Brain Cognition?". This question is fundamentally getting at whether a predicted value of cognition can predict cognition. Assuming the brain parameters can predict cognition decently, and the original cognitive measure that you were predicting is related to your measure of fluid cognition, the answer should be yes. Upon reading the Methods, it became clear that the cognitive variable in the model predicting cognition using brain features (to get predicted cognition, or as the authors refer to it, brain-cognition) is the same as the measure of fluid cognition that you are trying to assess how well brain-cognition can predict. Assuming the brain parameters can predict fluid cognition at all, it is then inevitable that brain-cognition will predict fluid cognition. Therefore, it is inappropriate to use predicted values of a variable to predict the same variable.

Response: Thank you Reviewer 3 for pointing out this important issue. Reviewer 1 (Recommendations For The Authors #4) and Reviewer 2 (Public Review #4) bought up a similar issue. While Reviewer 3 felt that “it is inappropriate to use predicted values of a variable to predict the same variable,“ Reviewer 2 viewed Brain Cognition as a 'specific/direct' index and Brain Age as a 'generic/indirect' index. And both have merit in their own right.

Similar to Reviewer 2, we believe that the specific index is as important and has commonly been used elsewhere in the context of biomarkers. For instance, to obtain neuroimaging biomarkers for Alzheimer’s, neuroimaging researchers often build a predictive model to predict Alzheimer's diagnosis (Khojaste-Sarakhsi et al., 2022). In fact, outside of neuroimaging, polygenic risk scores (PRSs) in genomics are often used following “to use predicted values of a variable to predict the same variable” (Choi et al., 2020). For instance, a PRS of ADHD that indicates the genetic liability to develop ADHD is based on genome-wide association studies of ADHD (Demontis et al., 2019).

Still, we now agreed that it may not be fair to compare the performance of a specific index (Brain Cognition) and a generic index (Brain Age) directly (as pointed out by Reviewer 3 Public Review #6 below). Accordingly, in the revision, as opposed to treating Brain Cognition and Brain Age as separate biomarkers and comparing them, we treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. In other words, the strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in the brain MRI that is related to fluid cognition. And consequently, the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age indicate what is missing from Brain Age -- the amount of co-variation between brain MRI and fluid cognition that cannot be captured by Brain Age. According to Reviewer 2, a generic index (Brain Age) “sacrificed some additional explained variance provided” compared to a specific index (Brain Cognition). Here, we used the commonality analyses to quantify how much scarifying was made by Brain Age. See below for the re-conceptualisation of Brain Age vs. Brain Cognition in the revision:

Abstract

“Lastly, we tested how much Brain Age missed the variation in the brain MRI that could explain fluid cognition. To capture this variation in the brain MRI that explained fluid cognition, we computed Brain Cognition, or a predicted value based on prediction models built to directly predict fluid cognition (as opposed to chronological age) from brain MRI data. We found that Brain Cognition captured up to an additional 11% of the total variation in fluid cognition that was missing from the model with only Brain Age and chronological age, leading to around a 1/3-time improvement of the total variation explained.”

Introduction:

“Third and finally, certain variation in the brain MRI is related to fluid cognition, but to what extent does Brain Age not capture this variation? To estimate the variation in the brain MRI that is related to fluid cognition, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data. Previous studies found reasonable predictive performances of these cognition-prediction models, built from certain MRI modalities (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). Analogous to Brain Age, we called the predicted values from these cognition-prediction models, Brain Cognition. The strength of an out-of-sample relationship between Brain Cognition and fluid cognition reflects variation in the brain MRI that is related to fluid cognition and, therefore, indicates the upper limit of Brain Age’s capability in capturing fluid cognition. Consequently, the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age indicate what is missing from Brain Age -- the amount of co-variation between brain MRI and fluid cognition that cannot be captured by Brain Age.”

“Finally, we investigated the extent to which Brain Age indices missed the variation in the brain MRI that could explain fluid cognition. Here, we tested Brain Cognition’s unique effects in multiple regression models with a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition.“

Discussion

“Third, how much does Brain Age miss the variation in the brain MRI that could explain fluid cognition? Brain Age and chronological age by themselves captured around 32% of the total variation in fluid cognition. But, around an additional 11% of the variation in fluid cognition could have been captured if we used the prediction models that directly predicted fluid cognition from brain MRI.

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation of brain MRI that is related to fluid cognition. Brain Cognition, from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. The unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained.”

Reviewer 3 Public Review #5:

• "However, Brain Age Gap created from the lower-performing age-prediction models explained a higher amount of variation in Cognitionfluid. For instance, the top performing age-prediction model, "Stacked: All excluding Task Contrast", generated Brain Age and Corrected Brain Age that explained the highest amount of variation in Cognitionfluid, but, at the same time, produced Brian Age Gap that explained the least amount of variation in Cognitionfluid" (p7). This is an inevitable consequence of the following relationship between predicted values and residuals (or residuals times -1): y=(y-y ̂ )+y ̂. Let's say that age explains 60% of the variance in fluid cognition, and predicted age (y ̂) explains 40% of the variance in fluid cognition. Then the brain age gap (-(y-y ̂)) should explain 20% of the variance in fluid cognition. If by "Corrected Brain Age" you mean the modified predicted age from Butler et al (2021), the "Corrected Brain Age" result is inevitable because the modified predicted age is essentially just age with a tiny bit of noise added to it. From Figure 4, though, this does not seem to be the case, because the lower left quadrant in panel (a) should be flat and high (about as high as the predictive value of age for fluid cognition). So it is unclear how "Corrected Brain Age" is calculated. It looks like you might be regressing age out of brain-age, though from your description in the Methods section, it is not totally clear. Again, I highly recommend using the terminology and metrics of Butler et al (2021) throughout to reduce confusion. Please also clarify how you used the slope and intercept. In general, given how brain-age metrics tend to be calculated, the following conclusion is inevitable: "As before, the unique effects of Brain Age indices were all relatively small across the four Brain Age indices and across different prediction models" (p10).

Response: We agreed that the results are ‘inevitable’ due to the transformations from Brain Age to other Brain Age indices. However, the consequences of these transformations may not be very clear to readers who are not very familiar with Brain Age literature and to the community at large who think about the implications of Brain Age. This is appreciated by Reviewer 1, who mentioned “While the main message will not come as a surprise to anyone with hands-on experience of using brain-age models, I think it is nonetheless an important message to convey to the community.”

Note we made clarifications on how we calculated each of the Brain Age indices above (see<br /> Reviewer 3 Public Review #2), including how we used the slope and intercept. We chose the terminology closer to the one originally used by de Lange and Cole (2020) and now listed many terminologies others have used to refer to this transformation.

Reviewer 3 Public Review #6:

"On the contrary, the unique effects of Brain Cognition appeared much larger" (p10). This is not a fair comparison if you do not look at the unique effects above and beyond the cognitive variable you predicted in your brain-cognition model. If your outcome measure had been another metric of cognition other than fluid cognition, you would see that brain-cognition does not explain any additional variance in this outcome when you include fluid cognition in the model, just as brain-age would not when including age in the model (minus small amounts due to penalization and out-of-sample estimates). This highlights the fact that using a predicted value to predict anything is worse than using the value itself.

Response Please see our response to Reviewer 3 Public Review #4 above. Briefly, we no long made this comparison. Instead, we now viewed the unique effects of Brain Cognition as a way to test how much Brain Age missed the variation in the brain MRI that could explain fluid cognition.

Reviewer 3 Public Review #7:

"First, how much does Brain Age add to what is already captured by chronological age? The short answer is very little" (p12). This is a really important point, but the paper requires an in-depth discussion of the inevitability of this result, as discussed above.

Response We agree that the tight relationship between Brain Age and chronological age is inevitable. We mentioned this from the get-go in the introduction:

Introduction “Accordingly, by design, Brain Age is tightly close to chronological age. Because chronological age usually has a strong relationship with fluid cognition, to begin with, it is unclear how much Brain Age adds to what is already captured by chronological age.”

To make this point obvious, we quantified the overlap between Brain Age and chronological age using the commonality analysis. We hope that our effort to show the inevitability of this overlap can make people more careful when designing studies involving Brain Age.

Reviewer 3 Public Review #8:

"Third, do we have a solution that can improve our ability to capture Cognitionfluid from brain MRI? The answer is, fortunately, yes. Using Brain Cognition as a biomarker, along with chronological age, seemed to capture a higher amount of variation in Cognitionfluid than only using Brain Age" (p12). I suggest controlling for the cognitive measure you predicted in your brain-cognition model. This will show that brain-cognition is not useful above and beyond cognition, highlighting the fact that it is not a useful endeavor to be using predicted values.

Response This point is similar to Reviewer 3 Public Review #6. Again please see our response to Reviewer 3 Public Review #4 above. Briefly, we no long made this comparison and said whether Brain Cognition is ‘better’ than Brain Age. Instead, we now viewed the unique effects of Brain Cognition as a way to test how much Brain Age missed the variation in the brain MRI that could explain fluid cognition.

Reviewer 3 Public Review #9:

"Accordingly, a race to improve the performance of age-prediction models (Baecker et al., 2021) does not necessarily enhance the utility of Brain Age indices as a biomarker for Cognitionfluid. This calls for a new paradigm. Future research should aim to build prediction models for Brian Age indices that are not necessarily good at predicting age, but at capturing phenotypes of interest, such as Cognitionfluid and beyond" (p13). I whole-heartedly agree with the first two sentences, but strongly disagree with the last. Certainly your results, and the underlying reason as to why you found these results, calls for a new paradigm (or, one might argue, a pre-brain-age paradigm). As of now, your results do not suggest that researchers should keep going down the brain-age path. While it is difficult to prove that there is no transformation of brain-age or the brain-age gap that will be useful, I am nearly sure this is true from the research I have done. If you would like to suggest that the field should continue down this path, I suggest presenting a very good case to support this view.

Response Thank you for your comments on this issue.

Since the submission of our manuscript, other researchers also made a similar observation regarding the disagreement between the predictive performance of age-prediction models and the utility of Brain Age. For instance, in their systematic review, Jirasarie and colleagues (2023, p7) wrote this statement, “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest. As a point of illustration, seven of the twenty studies in this review only evaluated the utility of their most accurate model, which in all cases was trained using multimodal features. This approach has also led to researchers to exclusively use T1-weighted and diffusion-weighted MRI scans when developing brain age models36 since such modalities have been shown to have the largest contribution to a model’s predictive power.2,67 However, our review suggests that model accuracy does not necessarily provide meaningful insight about clinical utility (e.g., detection of age-related pathology). Taken with prior studies,16,17 it appears that the most accurate models tend to not be the most useful.”

We now discussed the disagreement between the predictive performance of age-prediction models and the utility of Brain Age, not only in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) but also in the context of neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). Following Reviewer 3’s suggestion, we also added several possible strategies to mitigate this problem of Brain Age, used by us and other groups. Please see below.

Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance, combining different MRI modalities into the prediction models, similar to our stacked models, often lead to the highest performance of age-prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age-prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder.

As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age-prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest. Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

Reviewer #1 (Recommendations For The Authors):

In this paper, the authors evaluate the utility of brain age derived metrics for predicting cognitive decline using the HCP aging dataset by performing a commonality analysis in a downstream regression. The main conclusion is that brain age derived metrics do not explain much additional variation in cognition over and above what is already explained by age. The authors propose to use a regression model trained to predict cognition ('brain-cognition') as an alternative that explains more unique variance in the downstream regression.

This is a reasonably good paper and the use of a commonality analysis is a nice contribution to understanding variance partitioning across different covariates. While the main message will not come as a surprise to anyone with hands-on experience of using brain-age models, I think it is nonetheless an important message to convey to the community. With that said, I have some comments that I believe the authors ought to address before publication.

Reviewer 1 Recommendations For The Authors #1:

First, from a conceptual point of view, the authors focus exclusively on cognition as a downstream outcome. This is undeniably important, but is only one application area for brain age models. They are also used for example to provide biomarkers for many brain disorders. What would the results presented here have to say about these application areas? Further, I think that since brain-age models by construction confound relevant biological variation with the accuracy of the regression models used to estimate them, my own opinion about the limits of interpretation of (e.g.) the brain-age gap is as a dimensionless biomarker. This has also been discussed elsewhere (see e.g. https://academic.oup.com/brain/article/143/7/2312/5863667). I would suggest the authors nuance their discussion to provide considerations on these issues.

Response Thank you Reviewer 1 for pointing out two important issues.

The first issue was about applications for brain disorders. We now made a detailed discussion about this, which also addressed Reviewer 3 Public Review #9. Briefly, we now bought up

1) the consistency between our findings on fluid cognition and other recent works on brain disorders,

2) under-fitted age-prediction models from Brain Age studies focusing on neurological/psychological disorders when applied to participants with neurological/psychological disorders because the age-prediction models were built from largely healthy participants,

and 3) suggested solutions we and others made to optimise the utility of Brain Age for both cognitive functioning and brain disorders.

Discussion:

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance, combining different MRI modalities into the prediction models, similar to our stacked models, often lead to the highest performance of age-prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023).”

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). That is, those Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. This means that age-prediction models from Brain Age studies focusing on neurological/psychological disorders might be under-fitted when applied to participants with neurological/psychological disorders because they were built from largely healthy participants. And thus, the difference in Brain Age indices between participants without vs. with neurological/psychological disorders might be confounded by the under-fitted age-prediction models (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other Brain Age studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning do not suffer from being under-fitted. We consider this as a strength, not a weakness of our study.”

“Next, researchers should not select age-prediction models based solely on age-prediction performance. Instead, researchers could select age-prediction models that explained phenotypes of interest the best. Here we selected age-prediction models based on a set of features (i.e., modalities) of brain MRI. This strategy was found effective not only for fluid cognition as we demonstrated here, but also for neurological and psychological disorders as shown elsewhere (Jirsaraie, Gorelik, et al., 2023; Rokicki et al., 2021). Rokicki and colleagues (2021), for instance, found that, while integrating across MRI modalities led to age-prediction models with the highest age-prediction performance, using only T1 structural MRI gave age-prediction models that were better at classifying Alzheimer’s disease. Similarly, using only cerebral blood flow gave age-prediction models that were better at classifying mild/subjective cognitive impairment, schizophrenia and bipolar disorder. As opposed to selecting age-prediction models based on a set of features, researchers could also select age-prediction models based on modelling methods. For instance, Jirsaraie and colleagues (2023) compared gradient tree boosting (GTB) and deep-learning brain network (DBN) algorithms in building age-prediction models. They found GTB to have higher age-prediction performance but DBN to have better utility in explaining cognitive functioning. In this case, an algorithm with better utility (e.g., DBN) should be used for explaining a phenotype of interest. Similarly, Bashyam and colleagues (2020) built different DBN-based age-prediction models, varying in age-prediction performance. The DBN models with a higher number of epochs corresponded to higher age-prediction performance. However, DBN-based age-prediction models with a moderate (as opposed to higher or lower) number of epochs were better at classifying Alzheimer’s disease, mild cognitive impairment and schizophrenia. In this case, a model from the same algorithm with better utility (e.g., those DBN with a moderate epoch number) should be used for explaining a phenotype of interest. Accordingly, this calls for a change in research practice, as recently pointed out by Jirasarie and colleagues (2023, p7), “Despite mounting evidence, there is a persisting assumption across several studies that the most accurate brain age models will have the most potential for detecting differences in a given phenotype of interest”. Future neuroimaging research should aim to build age-prediction models that are not necessarily good at predicting age, but at capturing phenotypes of interest.”

The second issue was about “the brain-age gap as a dimensionless biomarker.” We are not so clear on what the reviewer meant by “the dimensionless biomarker.” One possible meaning of the “dimensionless biomarker” is the fact that Brain Age from the same algorithm and same modality can be computed, such that Brain Age can be tightly fit or loosely fit with chronological age. This is what Bashyam and colleagues (2020) did in the article Reviewer 1 referred to. We now wrote about this strategy in the above paragraph in the Discussion.

Alternatively, “the dimensionless biomarker” might be something closer to what Reviewer 2 viewed Brain Age as a “generic/indirect” index (as opposed to a 'specific/direct' index in the case of Brain Cognition) (see Reviewer 2 Public Review #4). We discussed this in our response to Reviewer 3 Public Review #4.

Reviewer 1 Recommendations For The Authors #2:

Second, from a methods perspective, I am quite suspicious of the stacked regression models the authors are using to combine regression models and I suspect they may be overfit. In my experience, stacked models are very prone to overfitting when combined with cross-validation. This is because the predictions from the first level models (i,e. the features that are provided to the second-level 'stacked' models) contain information about the training set and the test set. If cross-validation is not done very carefully (e.g. using multiple hold-out sets), information leakage can easily occur at the second level. Unfortunately, there is not sufficient explanation of the methodological procedures in the current manuscript to fully understand what was done. First, please provide more information to enable the reader to better understand the stacked regression models and if the authors are not using an approach that fully preserves training and test separability, please do so.

Response: We would like to thank Reviewer 1 for the suggestion. We now made it clearer in texts and new figure (see below) that we used nested cross-validation to ensure no information leakage between training and test sets. Regarding the stacked models more specifically, the hyperparameters of the stacked models were tuned in the same inner-fold CV as the non-stacked model (see Figure 7 below). That is, training models for both non-stacked and stacked models did not involve the test set, ensuring that there was no data leakage between training and test sets.

Methods:

“To compute Brain Age and Brain Cognition, we ran two separate prediction models. These prediction models either had chronological age or fluid cognition as the target and standardised brain MRI as the features (Denissen et al., 2022). We used nested cross-validation (CV) to build these models (see Figure 7). We first split the data into five outer folds. We used five outer folds so that each outer fold had around 100 participants. This is to ensure the stability of the test performance across folds. In each outer-fold CV, one of the outer folds was treated as a test set, and the rest was treated as a training set, which was further divided into five inner folds. In each inner-fold CV, one of the inner folds was treated as a validation set and the rest was treated as a training set. We used the inner-fold CV to tune for hyperparameters of the models and the outer-fold CV to evaluate the predictive performance of the models.

In addition to using each of the 18 sets of features in separate prediction models, we drew information across these sets via stacking. Specifically, we computed predicted values from each of the 18 sets of features in the training sets. We then treated different combinations of these predicted values as features to predict the targets in separate “stacked” models. The hyperparameters of the stacked models were tuned in the same inner-fold CV as the non-stacked model (see Figure 7). That is, training models for both non-stacked and stacked models did not involve the test set, ensuring that there was no data leakage between training and test sets. We specified eight stacked models: “All” (i.e., including all 18 sets of features), “All excluding Task FC”, “All excluding Task Contrast”, “Non-Task” (i.e., including only Rest FC and sMRI), “Resting and Task FC”, “Task Contrast and FC”, “Task Contrast” and “Task FC”. Accordingly, in total, there were 26 prediction models for Brain Age and Brain Cognition.

Reviewer 1 Recommendations For The Authors #3:

Third, the authors standardize the elastic net regression coefficients post-hoc. Why did the authors not perform the more standard approach of standardizing the covariates and responses, prior to model estimation, which would yield standardized regression coefficients (in the classical sense) by construction? Please also provide an indication of the different regression strengths that were estimated across the different models and cross-validation splits. Also, how stable were the weights across splits?

Response For model fitting, we did not “standardize the elastic net regression coefficients post-hoc.” Instead, we did all of the standardisation steps prior to model fitting (see Methods below). For regression strengths across different models and cross-validation splits, we now provided predictive performance at each of the five outer-fold test sets in Figure 1 (below). As you may have seen, the predictive performance was quite stable across the cross-validation splits.

For visualising feature importance, We originally only standardised the elastic net regression coefficients post-hoc, so that feature importance plots were in the same scale across folds. However, as mentioned by Reviewer 3 (Recommendations for the Authors #7, below), this might make it difficult to interpret the directionality of the coefficients. In the revised manuscript, we refitted the Elastic Net model to the full dataset without splitting them into five folds and visualised the coefficients on brain images (see below).

Methods

“We controlled for the potential influences of biological sex on the brain features by first residualising biological sex from brain features in each outer-fold training set. We then applied the regression of this residualisation to the corresponding test set. We also standardised the brain features in each outer-fold training set and then used the mean and standard deviation of this outer-fold training set to standardise the test set. All of the standardisation was done prior to fitting the prediction models.”

“To understand how Elastic Net made a prediction based on different brain features, we examined the coefficients of the tuned model. Elastic Net coefficients can be considered as feature importance, such that more positive Elastic Net coefficients lead to more positive predicted values and, similarly, more negative Elastic Net coefficients lead to more negative predicted values (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022). While the magnitude of Elastic Net coefficients is regularised (thus making it difficult for us to interpret the magnitude itself directly), we could still indicate that a brain feature with a higher magnitude weights relatively stronger in making a prediction. Another benefit of Elastic Net as a penalised regression is that the coefficients are less susceptible to collinearity among features as they have already been regularised (Dormann et al., 2013; Pat, Wang, Bartonicek, et al., 2022).

Given that we used five-fold nested cross validation, different outer folds may have different degrees of ‘’ and ‘l_1 ratio’, making the final coefficients from different folds to be different. For instance, for certain sets of features, penalisation may not play a big part (i.e., higher or lower ‘’ leads to similar predictive performance), resulting in different ‘’ for different folds. To remedy this in the visualisation of Elastic Net feature importance, we refitted the Elastic Net model to the full dataset without splitting them into five folds and visualised the coefficients on brain images using Brainspace (Vos De Wael et al., 2020) and Nilern (Abraham et al., 2014) packages. Note, unlike other sets of features, Task FC and Rest FC were modelled after data reduction via PCA. Thus, for Task FC and Rest FC, we, first, multiplied the absolute PCA scores (extracted from the ‘components_’ attribute of ‘sklearn.decomposition.PCA’) with Elastic Net coefficients and, then, summed the multiplied values across the 75 components, leaving 71,631 ROI-pair indices.”

Reviewer 1 Recommendations For The Authors #4:

I do not really find it surprising that the level of unique explained variance provided by a brain-cognition model is higher than a brain-age model, given that the latter is considerably more accurate (also, in view of the comment above). As such I would recommend to tone down the claims about the utility of this method, also because it is only really applicable to one application area for brain age.

Response Thank you for bringing this issue to our attention. We have now toned down the claims about the utility of Brain Cognition and importantly treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. Please see Reviewer 3 Public Review #4 above for a detailed discussion about this issue.

Reviewer 1 Recommendations For The Authors #5:

Please provide more details about the task designs and MRI processing procedures that were employed on this sample so that the reader is not forced to dig through the publications from the consortia contributing the data samples used. For example, comments such as "Here we focused on the pre-processed task fMRI files with a suffix "_PA_Atlas_MSMAll_hp0_clean.dtseries.nii." are not particularly helpful to readers not already familiar with this dataset.

Response Thank you so much for pointing out this important point on the clarity of the description of our MRI methodology. We now added additional details about the data processing done by the HCP-A and by us. We, for instance, explained the meaning of the HCP-A suffix “"_PA_Atlas_MSMAll_hp0_clean.dtseries.nii”. Please see below.

Methods

“HCP-A provides details of parameters for brain MRI elsewhere (Bookheimer et al., 2019; Harms et al., 2018). Here we used MRI data that were pre-processed by the HCP-A with recommended methods, including the MSMALL alignment (Glasser et al., 2016; Robinson et al., 2018) and ICA-FIX (Glasser et al., 2016) for functional MRI. We used multiple brain MRI modalities, covering task functional MRI (task fMRI), resting-state functional MRI (rsfMRI) and structural MRI (sMRI), and organised them into 19 sets of features.

Sets of Features 1-10: Task fMRI contrast (Task Contrast)

Task contrasts reflect fMRI activation relevant to events in each task. Bookheimer and colleagues (2019) provided detailed information about the fMRI in HCP-A. Here we focused on the pre-processed task fMRI Connectivity Informatics Technology Initiative (CIFTI) files with a suffix, “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” These CIFTI files encompassed both the cortical mesh surface and subcortical volume (Glasser et al., 2013). Collected using the posterior-to-anterior (PA) phase, these files were aligned using MSMALL (Glasser et al., 2016; Robinson et al., 2018), linear detrended (see https://groups.google.com/a/humanconnectome.org/g/hcp-users/c/ZLJc092h980/m/GiihzQAUAwAJ) and cleaned from potential artifacts using ICA-FIX (Glasser et al., 2016).

To extract Task Contrasts, we regressed the fMRI time series on the convolved task events using a double-gamma canonical hemodynamic response function via FMRIB Software Library (FSL)’s FMRI Expert Analysis Tool (FEAT) (Woolrich et al., 2001). We kept FSL’s default high pass cutoff at 200s (i.e., .005 Hz). We then parcellated the contrast ‘cope’ files, using the Glasser atlas (Gordon et al., 2016) for cortical surface regions and the Freesurfer’s automatic segmentation (aseg) (Fischl et al., 2002) for subcortical regions. This resulted in 379 regions, whose number was, in turn, the number of features for each Task Contrast set of features.

HCP-A collected fMRI data from three tasks: Face Name (Sperling et al., 2001), Conditioned Approach Response Inhibition Task (CARIT) (Somerville et al., 2018) and VISual MOTOR (VISMOTOR) (Ances et al., 2009). First, the Face Name task (Sperling et al., 2001) taps into episodic memory. The task had three blocks. In the encoding block [Encoding], participants were asked to memorise the names of faces shown. These faces were then shown again in the recall block [Recall] when the participants were asked if they could remember the names of the previously shown faces. There was also the distractor block [Distractor] occurring between the encoding and recall blocks. Here participants were distracted by a Go/NoGo task. We computed six contrasts for this Face Name task: [Encode], [Recall], [Distractor], [Encode vs. Distractor], [Recall vs. Distractor] and [Encode vs. Recall].

Second, the CARIT task (Somerville et al., 2018) was adapted from the classic Go/NoGo task and taps into inhibitory control. Participants were asked to press a button to all [Go] but not to two [NoGo] shapes. We computed three contrasts for the CARIT task: [NoGo], [Go] and [NoGo vs. Go].

Third, the VISMOTOR task (Ances et al., 2009) was designed to test simple activation of the motor and visual cortices. Participants saw a checkerboard with a red square either on the left or right. They needed to press a corresponding key to indicate the location of the red square. We computed just one contrast for the VISMOTOR task: [Vismotor], which indicates the presence of the checkerboard vs. baseline.

Sets of Features 11-13: Task fMRI functional connectivity (Task FC)

Task FC reflects functional connectivity (FC ) among the brain regions during each task, which is considered an important source of individual differences (Elliott et al., 2019; Fair et al., 2007; Gratton et al., 2018). We used the same CIFTI file “_PA_Atlas_MSMAll_hp0_clean.dtseries.nii.” as the task contrasts. Unlike Task Contrasts, here we treated the double-gamma, convolved task events as regressors of no interest and focused on the residuals of the regression from each task (Fair et al., 2007). We computed these regressors on FSL, and regressed them in nilearn (Abraham et al., 2014). Following previous work on task FC (Elliott et al., 2019), we applied a highpass at .008 Hz. For parcellation, we used the same atlases as Task Contrast (Fischl et al., 2002; Glasser et al., 2016). We computed Pearson’s correlations of each pair of 379 regions, resulting in a table of 71,631 non-overlapping FC indices for each task. We then applied r-to-z transformation and principal component analysis (PCA) of 75 components (Rasero et al., 2021; Sripada et al., 2019, 2020). Note to avoid data leakage, we conducted the PCA on each training set and applied its definition to the corresponding test set. Accordingly, there were three sets of 75 features for Task FC, one for each task. “

Reviewer 1 Recommendations For The Authors #6:

Similarly, please be more specific about the regression methods used. There are several different parameterisations of the elastic net, please provide equations to describe the method used here so that readers can easily determine how the regularisation parameters should be interpreted. The same goes for the methods used for correcting bias, e.g. what is "de Lange and Cole's (2020) 5th equation"?

Response Thank you. We now made a detailed description of Elastic Net including its equation (see below). We also added more specific details about the methods used for correcting bias in Brain Age indices (see our response to Reviewer 3 Public Review #2 above).

Methods:

“For the machine learning algorithm, we used Elastic Net (Zou & Hastie, 2005). Elastic Net is a general form of penalised regressions (including Lasso and Ridge regression), allowing us to simultaneously draw information across different brain indices to predict one target variable. Penalised regressions are commonly used for building age-prediction models (Jirsaraie, Gorelik, et al., 2023). Previously we showed that the performance of Elastic Net in predicting cognitive abilities is on par, if not better than, many non-linear and more-complicated algorithms (Pat, Wang, Bartonicek, et al., 2022; Tetereva et al., 2022). Moreover, Elastic Net coefficients are readily explainable, allowing us the ability to explain how our age-prediction and cognition-prediction models made the prediction from each brain feature (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022) (see below).

Elastic Net simultaneously minimises the weighted sum of the features’ coefficients. The degree of penalty to the sum of the feature’s coefficients is determined by a shrinkage hyperparameter ‘’: the greater the , the more the coefficients shrink, and the more regularised the model becomes. Elastic Net also includes another hyperparameter, ‘l_1 ratio’, which determines the degree to which the sum of either the squared (known as ‘Ridge’; l_1 ratio=0) or absolute (known as ‘Lasso’; l_1 ratio=1) coefficients is penalised (Zou & Hastie, 2005). The objective function of Elastic Net as implemented by sklearn (Pedregosa et al., 2011) is defined as: argmin_ ((|(|y-X|)|_2^2)/(2×n_samples )+α×l_1 _ratio×|(||)|_1+0.5×α×(1-l_1 _ratio)×|(|w|)|_2^2 ), (1) where X is the features, y is the target, and  is the coefficient. In our grid search, we tuned two Elastic Net hyperparameters:  using 70 numbers in log space, ranging from .1 and 100, and l_1-ratio using 25 numbers in linear space, ranging from 0 and 1.”

Additional minor points:

Reviewer 1 Recommendations For The Authors #7:

• Please provide more descriptive figure legends, especially for Figs 5 and 6. For example, what do the boldface numbers reflect? What do the asterisks reflect?

Response Thank you for the suggestion. We made changes to the figure legends to make it clearer what the numbers and asterisks reflect.

Reviewer 1 Recommendations For The Authors #8:

• Perhaps this is personal thing, but I find the nomenclature cognition_{fluid} to be quite awkward. Why not just define FC as an acronym?

Response Thank you for the suggestion. We now used the word ‘fluid cognition’ throughout the manuscript.

Reviewer #2 (Recommendations For The Authors):

Suggestions for improved or additional experiments, data or analyses.

Reviewer 2 Recommendations For The Authors #1:

• Since the study did not provide external validation for the indices, it is unclear how well the models would perform and generalize to other samples. Therefore, it is recommended to conduct out-of-sample testing of the models.

Response Thank you for the suggestion. We now added discussions about how consistency between our results and several recent studies that investigated similar issues with Brain Age in different populations, e.g., large samples of older adults in Uk Biobank (Cole, 2020) and younger populations (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023), and in a broader context, extending to neurological and psychological disorders (for review, see Jirsaraie, Gorelik, et al., 2023). Please see below.

Please also noted that all of the analyses done were out-of-sample. We used nested cross-validation to evaluate the predictive performance of age- and cognition-prediction models on the outer-fold test sets, which are out-of-sample from the training sets (please see Reviewer 1 Recommendations For The Authors #2). Similarly, we also conducted all of the commonality analyses on the outer-fold test sets.

Discussion

“The small effects of the Corrected Brain Age Gap in explaining fluid cognition of aging individuals found here are consistent with studies in older adults (Cole, 2020) and younger populations (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023). Cole (2020) studied the utility of Brain Age on cognitive functioning of large samples (n>17,000) of older adults, aged 45-80 years, from the UK Biobank (Sudlow et al., 2015). He constructed age-prediction models using LASSO, a similar penalised regression to ours and applied the same age-dependency adjustment to ours. Cole (2020) then conducted a multiple regression explaining cognitive functioning from Corrected Brain Age Gap while controlling for chronological age and other potential confounds. He found Corrected Brain Age Gap to be significantly related to performance in four out of six cognitive measures, and among those significant relationships, the effect sizes were small with a maximum of partial eta-squared at .0059. Similarly, Jirsaraie and colleagues (2023) studied the utility of Brain Age on cognitive functioning of youths aged 8-22 years old from the Human Connectome Project in Development (Somerville et al., 2018) and Preschool Depression Study (Luby, 2010). They built age-prediction models using gradient tree boosting (GTB) and deep-learning brain network (DBN) and adjusted the age dependency of Brain Age Gap using Smith and colleagues’ (2019) method. Using multiple regressions, Jirsaraie and colleagues (2023) found weak effects of the adjusted Brain Age Gap on cognitive functioning across five cognitive tasks, five age-prediction models and the two datasets (mean of standardised regression coefficient = -0.09, see their Table S7). Next, Butler and colleagues (2021) studied the utility of Brain Age on cognitive functioning of another group of youths aged 8-22 years old from the Philadelphia Neurodevelopmental Cohort (PNC) (Satterthwaite et al., 2016). Here they used Elastic Net to build age-prediction models and applied another age-dependency adjustment method, proposed by Beheshti and colleagues (2019). Similar to the aforementioned results, Butler and colleagues (2021) found a weak, statistically non-significant correlation between the adjusted Brain Age Gap and cognitive functioning at r=-.01, p=.71. Accordingly, the utility of Brain Age in explaining cognitive functioning beyond chronological age appears to be weak across age groups, different predictive modelling algorithms and age-dependency adjustments.“

“This discrepancy between the predictive performance of age-prediction models and the utility of Brain Age indices as a biomarker is consistent with recent findings (for review, see Jirsaraie, Gorelik, et al., 2023), both in the context of cognitive functioning (Jirsaraie, Kaufmann, et al., 2023) and neurological/psychological disorders (Bashyam et al., 2020; Rokicki et al., 2021). For instance, combining different MRI modalities into the prediction models, similar to our stacked models, often lead to the highest performance of age-prediction models, but does not likely explain the highest variance across different phenotypes, including cognitive functioning and beyond (Jirsaraie, Gorelik, et al., 2023). “

“Third, by introducing Brain Cognition, we showed the extent to which Brain Age indices were not able to capture the variation of brain MRI that is related to fluid cognition. Brain Cognition, from certain cognition-prediction models such as the stacked models, has relatively good predictive performance, consistent with previous studies (Dubois et al., 2018; Pat, Wang, Anney, et al., 2022; Rasero et al., 2021; Sripada et al., 2020; Tetereva et al., 2022; for review, see Vieira et al., 2022). We then examined Brain Cognition using commonality analyses (Nimon et al., 2008) in multiple regression models having a Brain Age index, chronological age and Brain Cognition as regressors to explain fluid cognition. Similar to Brain Age indices, Brain Cognition exhibited large common effects with chronological age. But more importantly, unlike Brain Age indices, Brain Cognition showed large unique effects, up to around 11%. The unique effects of Brain Cognition indicated the amount of co-variation between brain MRI and fluid cognition that was missed by a Brain Age index and chronological age. This missing amount was relatively high, considering that Brain Age and chronological age together explained around 32% of the total variation in fluid cognition. Accordingly, if a Brain Age index was used as a biomarker along with chronological age, we would have missed an opportunity to improve the performance of the model by around one-third of the variation explained. “

“There is a notable difference between studies investigating the utility of Brain Age in explaining cognitive functioning, including ours and others (e.g., Butler et al., 2021; Cole, 2020, 2020; Jirsaraie, Kaufmann, et al., 2023) and those explaining neurological/psychological disorders (e.g., Bashyam et al., 2020; Rokicki et al., 2021). That is, those Brain Age studies focusing on neurological/psychological disorders often build age-prediction models from MRI data of largely healthy participants (e.g., controls in a case-control design or large samples in a population-based design), apply the built age-prediction models to participants without vs. with neurological/psychological disorders and compare Brain Age indices between the two groups. This means that age-prediction models from Brain Age studies focusing on neurological/psychological disorders might be under-fitted when applied to participants with neurological/psychological disorders because they were built from largely healthy participants. And thus, the difference in Brain Age indices between participants without vs. with neurological/psychological disorders might be confounded by the under-fitted age-prediction models (i.e., Brain Age may predict chronological age well for the controls, but not for those with a disorder). On the contrary, our study and other Brain Age studies focusing on cognitive functioning often build age-prediction models from MRI data of largely healthy participants and apply the built age-prediction models to participants who are also largely healthy. Accordingly, the age-prediction models for explaining cognitive functioning do not suffer from being under-fitted. We consider this as a strength, not a weakness of our study.”

Reviewer 2 Recommendations For The Authors #2:

• Employ Variance Inflation Factor (VIF) to empirically test for multicollinearity.

Response Given high common effects between many of the regressors in the models (e.g., between Brain Age and chronological age), VIF will be high, but this is not a concern for the commonality analysis. We showed now that applying the commonality analysis to multiple regressions allowed us to have robust results against multicollinearity, as demonstrated elsewhere (Ray-Mukherjee et al., 2014, Using commonality analysis in multiple regressions: A tool to decompose regression effects in the face of multicollinearity). Specifically, using the multiple regressions by themselves without the commonality analysis, researchers have to rely on beta estimates, which are strongly affected by multicollinearity (e.g., a phenomenon known as the Suppression Effect). However, by applying the commonality analysis on top of multiple regressions, researchers can then rely on R2 estimates, which are less affected by multicollinearity. This can be seen in our case (Figure 5 and 6) where Brain Age indices had the same unique effects regardless of the level of common effects they had with chronological age (e.g., Brain Age vs. Corrected Brain Age Gap from stacked models).

To directly demonstrate the robustness of the current commonality analysis regarding multicollinearity, we applied the commonality analysis to Ridge regressions (see Supplementary Figures 3 and 5 below). Ridge regression is a method designed to deal with multicollinearity (Dormann et al., 2013). As seen below, the results from commonality analyses applied to Ridge regressions are closely matched with our original results.

Methods

“Note to ensure that the commonality analysis results were robust against multicollinearity (Ray-Mukherjee et al., 2014), we also repeated the same commonality analyses done here on Ridge regression, as opposed to multiple regression. Ridge regression is a method designed to deal with multicollinearity (Dormann et al., 2013). See Supplementary Figure 3 for the Ridge regression with chronological age and each Brain Age index as regressors and Supplementary Figure 5 for the Ridge regression with chronological age, each Brain Age and Brain Cognition index as regressors. Briefly, the results from commonality analyses applied to Ridge regressions are closely matched with our results done using multiple regression.”

Reviewer 2 Recommendations For The Authors #3:

• Incorporate non-linearities in the correction of brain-age indices, such as separate terms in the regression or statistical analyses.

Response Thank you for the suggestion. We now added a non-linear term of chronological age in our multiple-regression models explaining fluid cognition (see Supplementary Figure 4 and 6 below). Originally we did not have the quadratic term for chronological age in our model since the relationship between chronological age and fluid cognition was relatively linear (see Figure 1 above). Accordingly, as expected, adding the quadratic term for chronological age as suggested did not change the pattern of the results of the commonality analyses.

Methods

“Similarly, to ensure that we were able to capture the non-linear pattern of chronological age in explaining fluid cognition, we added a quadratic term of chronological age to our multiple-regression models in the commonality analyses. See Supplementary Figure 4 for the multiple regression with chronological age, square chronological age and each Brain Age index as regressors and Supplementary Figure 6 for the multiple regression with chronological age, square chronological age, each Brain Age index and Brain Cognition as regressors. Briefly, adding the quadratic term for chronological age did not change the pattern of the results of the commonality analyses.”

Reviewer 2 Recommendations For The Authors #4:

• It would be helpful to include the complete set of results in the appendix - for instance, the statistical significance for each component for the final commonality analysis.

Response Figures 5 and 6 (see above) already have asterisks to reflect the statistical significance of the unique effects. Because of this, we do not believe we need more figures/tables in the appendix to show statistical significance.

Recommendations for improving the writing and presentation.

Reviewer 2 Recommendations For The Authors #5:

• The authors are encouraged to refrain from using terms such as 'fortunately', 'unfortunately', and 'unsettling', as they may appear inappropriate when referring to empirical findings.

Response We agree with this suggestion and no long used those words.

Reviewer 2 Recommendations For The Authors #6:

• It would be helpful to clarify in the methods that you end up with 5 test folds.

Response We now made a clarification why we chose 5 test folds.

Methods

“We used nested cross-validation (CV) to build these models (see Figure 7). We first split the data into five outer folds. We used five outer folds so that each outer fold had around 100 participants. This is to ensure the stability of the test performance across folds.”

Minor corrections to the text and figures.

Reviewer 2 Recommendations For The Authors #7:

• Why use months, not years for chronological age? This seems inappropriate given the age range.

Response We originally used months since they were units used in our prediction modelling. However, to make the figures easier to understand, we now used years.

Reviewer 2 Recommendations For The Authors #8:

• The formatting, especially regarding the text embedded within the figures, could benefit from significant improvements.

Response Thank you for the suggestion. We made changes to the text embedded within the figures. They should be more readable now

Reviewer 2 Recommendations For The Authors #9:

• The legend for the neuroimaging feature labels is missing, and the captions are incomplete.

Response Please see Figure 2 above. We now revised by adding the letter L and R for the laterality of the brain images. We made some changes to the captions to make sure they are complete.

Reviewer 2 Recommendations For The Authors #10:

• Figure 5's caption: SD has a missing decimal point).

Response The numbers are not SD. The numbers to the left of the figure represent the unique effects of chronological age in %, the numbers in the middle of the figure represent the common effects between chronological age and Brain Age index in %, and the numbers to the right of the figure represent the unique effects of Brain Age Index in %. We now used the same one decimal point for these number

Reviewer #3 (Recommendations For The Authors):

The main question of this article is as follows: “To what extent does having information on Brain Age improve our ability to capture declines in fluid cognition beyond knowing a person’s chronological age?” While this question is worthwhile, considering most of the field is confused about the nature of brain age, the authors are currently missing an opportunity to convey the inevitability of their results given how Brain Age and the Brain Age Gap are calculated. They also misleadingly convey that Brain Cognition is somehow superior to Brain Age. If the authors work on conveying the inevitability of their results and redo (or remove) their section on Brain Cognition, I can see how their results would be enlightening to the general neuroimaging community that is interested in the concept of brain age. See below for specific critiques.

Response Please see our response to Reviewer 3 Public Review Overall. Note we no longer argue that Brain Cognition is superior to Brain Age (Reviewer 3 Public Review #4). Rather, we treated the capability of Brain Cognition in capturing fluid cognition as the upper limit of Brain Age’s capability in capturing fluid cognition. We used the unique effects of Brain Cognition that explain fluid cognition beyond Brain Age and chronological age to indicate how much Brain Age misses the variation in the brain MRI that could explain fluid cognition.

Reviewer 3 Recommendations For The Authors #1:

“There are many adjustments proposed to correct for this estimation bias” (p3) → Regression to the mean is not a sign of bias. Any decent loss function will result in over- predicting the age of younger individuals and under-predicting the age of older individuals. This is a direct result of minimizing an error term (e.g., mean squared error). Therefore, it is inappropriate to refer to regression to the mean as a sign of bias. This misconception has led to a great deal of inappropriate analyses, including “correcting” the brain age gap by regressing out age.

Response Please see our response to Reviewer 3 Public Review#1

Reviewer 3 Recommendations For The Authors #2:

“Corrected Brain Age Gap in particular is viewed as being able to control for both age dependency and estimation biases (Butler et al., 2021).” (p3) → This summary is not accurate as Butler and colleagues did not use the words "corrected" and "biases" in this context. All that authors say in that paper is that regressing out age from the brain age gap - which is referred to as the modified brain age gap (MBAG) - makes it so that the modified brain age gap is not dependent on age, which is true. This metric is meaningless, though, because it is the variance left over after regressing out age from residuals from a model that was predicting age. If it were not for the fact that regression on residuals is not equivalent to multiple regression (and out of sample estimates), MBAG would be a vector of zeros. Upon reading your Methods, I noticed that you are using a metric for Le et al. (2018) for your “Corrected Brain Age Gap”. If they cite the Butler et al. (2021) paper, I highly recommend sticking with the same notation, metrics and terminology throughout. That would greatly help with the interpretability of your paper, and cross-comparisons between the two.

Response Please see our response to Reviewer 3 Public Review #2.

Reviewer 3 Recommendations For The Authors #3:

“However, the improvement in predicting chronological age may not necessarily make Brain Age to be better at capturing Cognitionfluid. If, for instance, the age-prediction model had the perfect performance, Brian Age Gap would be exactly zero and would have no utility in capturing Cognitionfluid beyond chronological age.” (p3) → I largely agree with this statement. I would be really careful to distinguish between Brain Age and the Brain Age Gap here, as the former is a predicted value, and the latter is the residual times -1 (predicted age - age). Therefore, together they explain all of the variance in age. If you change the first sentence to refer to the Brain Age Gap, this statement makes more sense. The Brain Age Gap will never be exactly zero, though, even with perfect prediction on the training set, because subjects in the testing set are different from the subjects in the training set.

Response Please see our response to Reviewer 3 Public Review #3.

Reviewer 3 Recommendations For The Authors #4:

“Can we further improve our ability to capture the decline in cognitionfluid by using, not only Brain Age and chronological age, but also another biomarker, Brain Cognition?” → This question is fundamentally getting at whether a predicted value of cognition can predict cognition. Assuming the brain parameters can predict cognition decently, and the original cognitive measure that you were predicting is related to your measure of fluid cognition, the answer should be yes. This seems like an uninteresting question to me. Upon reading your Methods, it became clear that the cognitive variable in the model predicting cognition using brain features (to get predicted cognition, or as you refer to it, Brain Cognition) is the same as the measure of fluid cognition that you are trying to assess how well Brain Cognition can predict. Assuming the brain parameters can predict fluid cognition at all, of course Brain Cognition will predict fluid cognition. This is inevitable. You should never use predicted values of a variable to predict the same variable.

Response Please see our response to Reviewer 3 Public Review #4.

Reviewer 3 Recommendations For The Authors #5:

“We also examined if these better-performing age-prediction models improved the ability of Brain Age in explaining Cognitionfluid.” → Improved above and beyond what?

Response We referred to if better-performing age-prediction models improved the ability of Brain Age in explaining fluid cognition over and above lower-performing age-prediction models. We made changes to the Introduction to clarify this change.

Reviewer 3 Recommendations For The Authors #6:

Figure 1 b & c → It is a little difficult to read the text by the horizontal bars in your plots. Please make the text smaller so that there is more space between the words vertically, or even better, make the plots slightly bigger. Please also put the predicted values on the y-axis. This is standard practice for displaying regression results. To make more room, you can get rid of your rPearson or your R2 plot, considering the latter is simply the square of the former. If you want to make it clear that the association is positive between all of your variables, I would keep rPearson.

Response Thank you so much for the suggestions.

1) We now made sure that the text by the horizontal bars in Figure 1b and c is readable.

2) Note in prediction model/machine-learning literature, it is more common to plot observed/real values on the y-axis. Here is the logic of our practice: values in the x-axis are the predicted values based on the model, and we would like to see if the changes in the predicted values correspond to the changes in the observed/real value in the y-axis.

3) Regarding Pearson correlation vs R2, please note that we wrote ”for R2, we used the sum of squares definition (i.e., R2 = 1 – (sum of squares residuals/total sum of squares)) per a previous recommendation (Poldrack et al., 2020).” As such, R2 is NOT the square of the Pearson correlation. In fact, in Poldrack and colleages’s “Establishment of Best Practices for Evidence for Prediction” paper (2020), they discourage 1) the use of Pearson correlation by itself and 2) the use of the correlation coefficient square as R2 (as opposed to sum of squares definition):

“It is common in the literature to use the correlation between predicted and actual values as a measure of predictive performance; of the 64 studies in our literature review that performed prediction analyses on continuous outcomes, 30 reported such correlations as a measure of predictive performance. This reporting is problematic for several reasons. First, correlation is not sensitive to scaling of the data; thus, a high correlation can exist even when predicted values are discrepant from actual values. Second, correlation can sometimes be biased, particularly in the case of leave-one-out cross-validation. As demonstrated in Figure 4, the correlation between predicted and actual values can be strongly negative when no predictive information is present in the model. A further problem arises when the variance explained (R2) is incorrectly computed by squaring the correlation coefficient. Although this computation is appropriate when the model is obtained using the same data, it is not appropriate for out-of-sample testing23; instead, the amount of variance explained should be computed using the sum-of-squares formulation (as implemented in software packages such as scikit-learn).”

“A further problem arises when the variance explained (R2) is incorrectly computed by squaring the correlation coefficient. Although this computation is appropriate when the model is obtained using the same data, it is not appropriate for out-of-sample testing23; instead, the amount of variance explained should be computed using the sum-of-squares formulation (as implemented in software packages such as scikit-learn).”

Accordingly, we decided to keep both R2 and Pearson correlation (along with MAE) in our Figure 1.

Reviewer 3 Recommendations For The Authors #7:

Figure 2 “We calculated feature importance by, first, standardizing Elastic Net weights across brain features of each set of features from each test fold.” → What do you mean by “standardize” here? Rescale to be mean 0, variance 1? If so, this seems like a misleading transformation, because it gives the impression that the relationships are negative, when they are not necessarily. Also, why did you choose to use elastic net weights in any form as measures of effect size (or importance)? The raw values are inherently penalized, which means they are under-estimates of the true effect size. It would be more meaningful (and less biased) to plot the raw correlations.

Response For the first question regarding standardisation, we addressed this issue in our response to Reviewer 1 Recommendations For The Authors #3. Briefly, we agreed with Reviewer 3 that standardisation (with mean = 0, SD = 1) might make it difficult to interpret the directionality of the coefficients. For visualising feature importance in the revised manuscript, we refitted the Elastic Net model to the full dataset without splitting them into five folds and visualised the coefficients on brain images (see below).

For the second question regarding why using Elastic Net coefficients as feature importance (as opposed to correlations), we need to mention the goal of feature importance: to understand how the model makes a prediction based on different brain features (Molnar, 2019). Correlations between a target and each brain feature do not achieve this. Instead, they will show univariate/marginal relationships between a target and a brain feature. What we want to visualise is how the model made a prediction, which in the case of Elastic Net, the prediction is based on the sum of the features’ coefficients. In other words, the multivariate models (including Elastic Net) focus on marginal relationships that take into account all brain features within each set of features.

Elastic Net coefficients can be considered as feature importance, such that more positive Elastic Net coefficients lead to more positive predicted values and, similarly, more negative Elastic Net coefficients lead to more negative predicted values (Molnar, 2019; Pat, Wang, Bartonicek, et al., 2022). While the magnitude of Elastic Net coefficients is regularised (thus making it difficult for us to interpret the magnitude itself directly), we could still indicate that a brain feature with a higher magnitude weights relatively stronger in making a prediction. Another benefit of Elastic Net as a penalised regression is that the coefficients are less susceptible to collinearity among features as they have already been regularised (Dormann et al., 2013; Pat, Wang, Bartonicek, et al., 2022).

Reviewer 3 Recommendations For The Authors #8:

Figure 3 → Again, what exactly do you mean by “standardised” here?

Response It means mean subtraction followed by the division by an SD. Though we no longer applies standardisation for feature importance. See our response to Reviewer 1 Recommendations For The Authors #3 and Reviewer 3 Recommendations For The Authors #7.

Reviewer 3 Recommendations For The Authors #9:

“However, Brain Age Gap created from the lower-performing age-prediction models explained a higher amount of variation in Cognitionfluid. For instance, the top performing age-prediction model, “Stacked: All excluding Task Contrast”, generated Brain Age and Corrected Brain Age that explained the highest amount of variation in Cognitionfluid, but, at the same time, produced Brian Age Gap that explained the least amount of variation in Cognitionfluid.” (p7) → Yes, but you did not need to run any models to show this, considering it is an inevitable consequence of the following relationship between predicted values and residuals (or residuals times -1): 𝑦 = (𝑦 − 𝑦% ) + 𝑦% . Let’s say that age explains 60% of the variance in fluid cognition, and predicted age ( 𝑦% ) explains 40% of the variance in fluid cognition. Then the brain age gap (−(𝑦 − 𝑦% )) should explain 20% of the variance in fluid cognition. If by “Corrected Brain Age” you mean the modified predicted age from the Butler paper, the “Corrected Brain Age” result is inevitable because the modified predicted age is essentially just age with a tiny bit of noise added to it. From Figure 4, though, this does not seem to be the case, because the lower left quadrant in panel a should be flat and high (about as high as the predictive value of age for fluid cognition). So how are you calculating “Corrected Brain Age”? It looks like you might be regressing age out of Brain Age, though from your description the Methods (How exactly do you use the slope and intercept? You need equation of you are going to stick with this terminology), it is not totally clear. I highly recommend using terminology and metrics from the Butler et al. (2021) paper throughout to reduce confusion.

Response Please see our response to Reviewer 3 Public Review #5

Reviewer 3 Recommendations For The Authors #10:

“On the contrary, an amount of variation in Cognitionfluid explained by Corrected Brain Age Gap was relatively small (maximum R2 = .041) across age-prediction models and did not relate to the predictive performance of the age-prediction models.” (p7) → If by “Corrected Brain Age Gap” you mean MBAG from The Butler paper, yes, this is also inevitable, considering MBAG would be a vector of zeros if it were not for regression on residuals (and out of sample estimates), as I mentioned earlier. Also, it is not clear why you used “on the contrary” as a transition here.

Response Please see our response to Reviewer 3 Public Review #2 for the ‘MBAG’ term. Briefly, we didn’t use Butler and colleagues' (2021) MBAG, but rather we used the method described in de Lange and Cole’s (2020), which was called RBAG by Butler and colleagues.

de Lange and Cole’s (2020) method, was commonly implemented elsewhere (Cole et al., 2020; Cumplido-Mayoral et al., 2023; Denissen et al., 2022). Accordingly, researchers who use Brain Age do not usually view this method as capturing a meaningless biomarker. Yet, the small effects of the Corrected Brain Age Gap in explaining fluid cognition of aging individuals found here are consistent with studies in older adults (Cole, 2020) and younger populations (Butler et al., 2021; Jirsaraie, Kaufmann, et al., 2023) (see our response to Reviewer 2 Recommendations For The Authors #1).

“On the contrary” refers to the fact that the other three Brain Age indices (i.e., those that did not account for the relationship between Brain Age and chronological age) showed a much higher amount of variation in fluid cognition explained. As mentioned above (our response to Reviewer 2 Public Review #7), our argument resonates Butler and colleagues’ (2021) suggestion (p. 4097): “As such, it is critical that readers of past literature note whether or not age was controlled for when testing for effects on the BAG, as this has not always been common practice (e.g., Beheshti et al., 2018; Cole, Underwood, et al., 2017; Franke et al., 2015; Gaser et al., 2013; Liem et al., 2017; Nenadi c et al., 2017; Steffener et al., 2016)”.

Reviewer 3 Recommendations For The Authors #11:

“As before, the unique effects of Brain Age indices were all relatively small across the four Brain Age indices and across different prediction models.” (p10) → Yes, again, this is inevitable considering how they are calculated. You can show these analyses to demonstrate your results in data, if you want, but ignoring the inevitability given how these variables are calculated is misleading.

Response Accounting for the relationship between Brain Age and chronological age when examining the utility of Brain Age is not misleading. Similar to previous recommendations (Butler et al., 2021; Le et al., 2018), we believe that not doing so is misleading. That is, without accounting for the relationship between Brain Age and chronological age, Brain Age will likely explain the same variation of the phenotype of interest as chronological age. Please see our response to Reviewer 3 Recommendations For The Authors #18 below.

Reviewer 3 Recommendations For The Authors #12:

“On the contrary, the unique effects of Brain Cognition appeared much larger.” (p10) → This is not a fair comparison if you don’t look at the unique effects above and beyond the cognitive variable you predicted (fluid cognition) in your Brain Cognition model. When you do this, you will see that Brain Cognition is useless when you include fluid cognition in the model, just as Brain Age would be in predicting age when you include age in the model. This highlights the fact that using predicted values of a metric to predict that metric is a pointless path to take, and that using a predicted value to predict anything is worse than using the value itself.

Response Please see our response to Reviewer 3 Public Review #6.

Reviewer 3 Recommendations For The Authors #13:

“First, how much does Brain Age add to what is already captured by chronological age? The short answer is very little.” (p12) → This is a really important point, but your paper requires an in-depth discussion of the inevitability of this result, which I have discussed previously in this review.

Response Please see our response to Reviewer 3 Public Review #7.

Reviewer 3 Recommendations For The Authors #14:

“Second, do better-performing age-prediction models improve the ability of Brain Age to capture Cognitionfluid? Unfortunately, the answer is no.” (p12) → You need to be clear that you are talking about above and beyond age here.

Response Thank you so much for your suggestion. We now made the change to this sentence accordingly.

Discussion

“Second, do better-performing age-prediction models improve the utility of Brain Age to capture fluid cognition above and beyond chronological age? The answer is also no.”

Reviewer 3 Recommendations For The Authors #15:

“Third, do we have a solution that can improve our ability to capture Cognitionfluid from brain MRI? The answer is, fortunately, yes. Using Brain Cognition as a biomarker, along with chronological age, seemed to capture a higher amount of variation in Cognitionfluid than only using Brain Age.” (p12) → Again, try controlling for the cognitive measure you predicted in your Brain Cognition model. This will show that Brain Cognition is not useful above and beyond cognition, highlighting the fact that it is not a useful endeavor to be using predicted values.

Response Please see our response to Reviewer 3 Public Review #8.

Reviewer 3 Recommendations For The Authors #16:

“Accordingly, a race to improve the performance of age-prediction models (Baecker et al., 2021) does not necessarily enhance the utility of Brain Age indices as a biomarker for Cognitionfluid. This calls for a new paradigm. Future research should aim to build prediction models for Brian Age indices that are not necessarily good at predicting age, but at capturing phenotypes of interest, such as Cognitionfluid and beyond.” (p13) → I whole-heartedly agree with the first two sentences, and strongly disagree with the last. Certainly your results, and the underlying reason as to why you found these results, calls for a new paradigm (or, one might argue, a pre-brain age paradigm). They do not, however, suggest that we should keep going down the Brain Age path. In fact, I think it should be abandoned all together. While it is difficult to prove that there is no transformation of Brain Age or the Brain Age Gap that will be useful, I am nearly sure this is true from the research I have done. Therefore, if you would like to suggest that the field should continue down this path, you need to present a very good case to support this view.

Response Please see our response to Reviewer 3 Public Review #9.

Reviewer 3 Recommendations For The Authors #17:

“Perhaps this is because the estimation of the influences of chronological age was done in the training set.” (p13) → I believe this is the case, and it is testable. Try re-running your analyses where parameters are estimated and performance is evaluated on the same data.

Response Yes, we agreed with this. Based on the equations we used, this is inevitable.

Reviewer 3 Recommendations For The Authors #18:

“Similar to a previous recommendation (Butler et al., 2021), we suggest focusing on Corrected Brain Age Gap.” (p13) → To be clear, the authors did not use the term “Corrected” because it is very misleading. The authors also did not suggest that we proceed with any brain age metric; rather they mentioned that the modified brain age gap is independent of age. Note the following passage: “Further, the interpretability of the modified brain age gap (MBAG) itself is limited by the fact that it is a prediction error from a regression to remove the effects of age from a residual obtained through a regression to predict age. By virtue of these limitations, we suggest that the modified version may not provide useful information about precocity or delay in brain development. In light of this, as well as the complexities associated with interpretations of the BAG and its dependence on age, we suggest that further methodological and theoretical work is warranted.” I recognize that that this statement is hedged, as is often required in the publication process, but I am all but certain that MBAG/BAG/modified predicted age are useless constructs. Therefore, if you are going to suggest that people continue to use them, opposed to suggesting that further methodological or theoretical work is warranted, you need to make a strong case, which you did not try to make here. If anything, your results support abandoning the age- prediction endeavor altogether.

Response Please see our response to Reviewer 3 Public Review #2 for the term. Briefly, we didn’t use Butler and colleagues’ (2021) MBAG, but rather RBAG. This index was originally described in de Lange and Cole’s (2020), and has now been implemented elsewhere (Cole et al., 2020; Cumplido-Mayoral et al., 2023; Denissen et al., 2022).

We do not intend to encourage people to abandon the Brain Age endeavour altogether. However, we made main three suggestions for future research on Brain Age to ensure its utility. First, they should account for the relationship between Brain Age and chronological age either using Corrected Brain Age Gap (or other similar adjustments) or, better, examining the unique effects of Brain Age indices after controlling for chronological age through commonality analyses (see below). This is similar to the suggestion made by Le and colleagues (2018) and later rephased by Butler and colleagues (2021). More specifically, Le and colleagues (2018) mentioned (p. 10): “Based on our observations in both real and simulated data, we recommend that the relationship between chronological age and BrainAGE should be accounted for. The two methods proposed in this study are either: (1) regress age on BrainAGE, producing BrainAGER, which is centered on 0 regardless of a participant's actual age or (2) include age as a regressor when doing follow-up analyses.”

Second, we suggested that researchers should not select age-prediction models based solely on age-prediction performance (see our response to Reviewer 1 Recommendations For The Authors #1).

Third, we suggested that researchers should test how much Brain Age miss the variation in the brain MRI that could explain fluid cognition or other phenotypes of interest (see our response to Reviewer 2 Public Review #4).

Discussion

“What does it mean then for researchers/clinicians who would like to use Brain Age as a biomarker? First, they have to be aware of the overlap in variation between Brain Age and chronological age and should focus on the contribution of Brain Age over and above chronological age. Using Brain Age Gap will not fix this. Butler and colleagues (2021) recently highlighted this point, “These results indicate that the association between cognition and the BAG are driven by the association between age and cognitive performance. As such, it is critical that readers of past literature note whether or not age was controlled for when testing for effects on the BAG, as this has not always been common practice (p. 4097).” Similar to previous recommendations (Butler et al., 2021; Le et al., 2018), we suggest future work should account for the relationship between Brain Age and chronological age, either using Corrected Brain Age Gap (or other similar adjustments) or, better, examining unique effects of Brain Age indices after controlling for chronological age through commonality analyses. Note we prefer using unique effects over beta estimates from multiple regressions, given that unique effects do not change as a function of collinearity among regressors (Ray-Mukherjee et al., 2014). In our case, Brain Age indices had the same unique effects regardless of the level of common effects they had with chronological age (e.g., Brain Age vs. Corrected Brain Age Gap from stacked models). In the case of fluid cognition, the unique effects might be too small to be clinically meaningful as shown here and previously (Butler et al., 2021; Cole, 2020; Jirsaraie, Kaufmann, et al., 2023).”

Reviewer 3 Recommendations For The Authors #19:

“To compute Brain Age and Brain Cognition, we ran two separate prediction models. These prediction models either had chronological age or Cognitionfluid as the target.” (p16) → You should make it clear in the main text of your paper that the cognition variable in your Brain Cognition models is the same as what you refer to as Cognitionfluid. Some of your analyses would have been much more reasonable if you had two different measures of cognition.

Response Thank you so much for the suggestion. We believe, given the re-conceptualisation of Brain Cognition as the main text

Introduction

“certain variation in the brain MRI is related to fluid cognition, but to what extent does Brain Age not capture this variation? To estimate the variation in the brain MRI that is related to fluid cognition, we could build prediction models that directly predict fluid cognition (i.e., as opposed to chronological age) from brain MRI data.”

Reviewer 3 Recommendations For The Authors #20:

“We controlled for the potential influences of biological sex on the brain features by first residualizing biological sex from brain features in the training set.” (p16) → Why? Your question is about prediction, not causal inference.

Response While the question is about prediction, we still would like to, as much as possible, be confident about what kind of information we drew from. Here we focused on brain data and controlled for other variables that might not be neuronal. For instance, we controlled for movement and physiological noise using ICA-FIX (Glasser et al., 2016). Following conventional practices in brain-based predictive modelling, we also treated biological sex as another sort of noise (Vieira et al., 2022). The difference between movement/physiological noise and biological sex is that the former varies across TRs, and the latter varies across individuals. Thus we controlled for movement and physiological noise within each participant and controlled for biological sex within a group of participants who belonged to the same training set.

Reviewer 3 Recommendations For The Authors #20:

“Lastly, we computer Corrected Brain Age Gap by subtracting the chronological age from the Corrected Brain Age (Butler et al., 2021; Le et al., 2018).” (p17) → The modified brain age gap in that paper is the residuals from regressing BAG on age (see equation 6). I highly recommend using that terminology and notation throughout to provide consistency and interpretability across papers.

Response Please see our response to Reviewer 3 Public Review #2 for the term.

Reviewer 3 Recommendations For The Authors #21: Equations (pgs 17-19) → Please use statistical notation instead of pseudo-R code.

Response We rewrote all of the equations using statistical notations.

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Author Response

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

We would like to thank the reviewers for their helpful comments which we have addressed, point-by-point, below:

Reviewer #1:

1) It might be useful to add more details to the methods (especially lines 191-196) to make them a bit more user-friendly for an audience who still may be unfamiliar with the relatively new and complex Mendelian randomisation technique.

The following information has been included in this section of the methods, to describe the different MR models in more detail:

“The IVW MR model will produce biased effect estimates in the presence of horizontal pleiotropy, i.e. where one or more genetic variant(s) included in the instrument affect the outcome by a pathway other than through the exposure. In the weighted median model, each genetic variant is weighted according to its distance from the median effect of all genetic variants. Thus, the weighted median model will provide an unbiased estimate when at least 50% of the information in an instrument comes from genetic variants that are not horizontally pleiotropic. The weighted mode model uses a similar approach but weights genetic instruments according to the mean effect. In this model, over 50% of the weight of the genetic instrument can be contributed to by genetic variants which are horizontally pleiotropic, but the most common amount of pleiotropy must be zero (known as the Zero Modal Pleiotropy Assumption (ZEMPA))[Hartwig et al., 2017].”

2) I was just wondering why MR egger was not carried out as part of this analysis?

We did consider also employing the MR Egger model as a further sensitivity analysis. However, given we were already employing the weighted median and weighted mode models, and given that MR-Egger suffers from reduced statistical power in comparison to the other models, we reasoned that adding in a further MR model would not add further clarity to our analyses, particularly given the relatively small sample size.

3) Although it is included in Figure 1 flowchart, I think it is also important to explain clearly in the written text way only n=6,118 of n=13,988 children in ALSPAC study were included in this study and the reason for this.

The following information has been included in the paragraph describing the ALSPAC study in the methods:

“Sufficient information was available on 6,221 of these individuals to be included in our analysis, as metabolomics was not performed for all individuals in the ALSPAC study.”

4) It is mentioned within the discussion 'the NMR metabolomics platform utilised in the analyses outlined here has limited coverage of fatty acids'. I think it might be useful to also add this detail into the methods section to aid readers when they are making their own interpretation whilst reading the results section.

The following sentence has been included in the methods section:

“This metabolomics platform has limited coverage of fatty acids.”

5) However, I feel that the conclusion should be tempered slightly as although this study alongside other similar MR studies provides evidence of an association between genetic liability to CRC and levels of metabolites at certain ages, I do not think there is enough evidence at this stage to say that genetic liability for CRC actually alters the levels of metabolites.

The first sentence of the conclusion has been changed to:

“Our analysis provides evidence that genetic liability to CRC is associated with altered levels of metabolites at certain ages, some of which may have a causal role in CRC development.”

Reviewer #2:

1) The background is lacking introduction to the different components of the metabolic features tested. For instance, there is a broader discussion about polyunsaturated fatty acids (PUFA) in the discussion, however, this should have been introduced and defined already before that. What metabolites are included in that term (PUFA)? Are there other studies on PUFA and CRC?

The following information has been included in the background section:

“In particular, previous work has highlighted polyunsaturated fatty acids (PUFA) as potentially having a role in colorectal cancer development. The term PUFA includes omega-3 and -6 fatty acids. Recent MR work has highlighted a possible link between PUFAs, in particular omega 6 PUFAs, and colorectal cancer risk.”

2) There seem to be indications for horizontal pleiotropy given the changed estimates when genetic variants in the FADS loci are removed. Could multivariable MR methods have been used to account for pleiotropy and differentiate individual fatty acid effects?

Multivariable MR can be employed to investigate the effects of horizontal pleiotropy. However, the multiple exposures must have sufficiently distinct underlying genetic architecture in order to instrument each one whilst adjusting for the other, as determined by conditional F-statistics. Given the correlations across metabolite levels, this is unlikely to be the case.

3) The ALSPAC sample sizes are decreasing across the different age groups, which is not strange given the longitudinal collection. However, does the altered sample composition affect the results? Have sensitivity analyses been done on the complete set of individuals from age 8-25?

The altered sample composition could be affecting results. The limitations section of the discussion has been amended to reflect this:

“Secondly, mostly due to the longitudinal nature of the ASLAPC study, our sample at each time point is composed of slightly different individuals. This could be influencing our results, and should be taken into account when comparing across time points.”

We have not completed any sensitivity analyses to investigate this.

4) Although beyond the scope of this paper, sex-stratified GWAS analyses on metabolites can easily be done in UK Biobank.

We thank the reviewer for this suggestion, and agree that this would be an interesting future analysis. We have amended the discussion to mention this:

“Fourthly, our analysis would benefit from being repeated with sex-stratified data. Although such GWAS results for metabolites are not currently available, the data to perform such GWAS are available in UK Biobank for future analyses.”

5) Very minor, there is a difference in reporting a number of decimals in ALSPAC results. There is also a difference in reporting the units for the results comparing text and figures (per SD higher CRC liability or per doubling). Please include sample sizes and data sources in the figure legends as they should be stand-alone items.

We have amended the ALSPAC results to all have two decimal places, reporting units have been altered and figure legends to include sample sizes and data sources.

Author Response

We thank the reviewers for their suggestions. We are confident in the model that predicts odor vs odor (OCT-MCH) preference using calcium activity, but we acknowledge the relative weakness of the model that predicts odor (OCT) vs air preference. We are preparing an updated manuscript that will prioritize our interpretation of the OCT-MCH results and more fully document uncertainties around our estimates of prediction capacity.

Reviewer #1 (Public Review):

Summary: The authors seek to establish what aspects of nervous system structure and function may explain behavioral differences across individual fruit flies. The behavior in question is a preference for one odor or another in a choice assay. The variables related to neural function are odor responses in olfactory receptor neurons or in the second-order projection neurons, measured via calcium imaging. A different variable related to neural structure is the density of a presynaptic protein BRP. The authors measure these variables in the same fly along with the behavioral bias in the odor assays. Then they look for correlations across flies between the structure-function data and the behavior.

Strengths: Where behavioral biases originate is a question of fundamental interest in the field. In an earlier paper (Honegger 2019) this group showed that flies do vary with regard to odor preference, and that there exists neural variation in olfactory circuits, but did not connect the two in the same animal. Here they do, which is a categorical advance, and opens the door to establishing a correlation. The authors inspect many such possible correlations. The underlying experiments reflect a great deal of work, and appear to be done carefully. The reporting is clear and transparent: All the data underlying the conclusions are shown, and associated code is available online.

We are glad to hear the reviewer is supportive of the general question and approach.

Weaknesses: The results are overstated. The correlations reported here are uniformly small, and don't inspire confidence that there is any causal connection. The main problems are

We are working on a revision that overhauls the interpretations of the results. We recognize that the current version inadequately distinguishes the results that we have high confidence in (specifically, PC2 of our Ca++ data as a predictor of OCT-MCH preference) versus results that are suggestive but not definitive (such as the PC1 of Ca++ data as a predictor of Air-OCT preference).

It’s true that the correlations are small, with r2 values typically in the 0.1-0.2 range. That said, we would call it a victory if we could explain 10 to 20% of the variance of a behavior measure, captured in a 3 minute experiment, with a circuit correlate. This is particularly true because, as the reviewer notes, the behavioral measurement is noisy.

1) The target effect to be explained is itself very weak. Odor preference of a given fly varies considerably across time. The systematic bias distinguishing one fly from another is small compared to the variability. Because the neural measurements are by necessity separated in time from the behavior, this noise places serious limits on any correlation between the two.

This is broadly correct, though to quibble, it’s our measurement of odor preference which varies considerably over time. We are reasonably confident that the more variance in our measurements can be attributed to sampling error than changes to true preference over time. As evidence, the correlation in sequential measures of individual odor preference, with delays of 3 hours or 24 hours, are not obviously different. We are separately working on methodological improvements to get more precise estimates of persistent individual odor preference, using averages of multiple, spaced measurements. This is promising, but beyond the scope of this study.

2) The correlations reported here are uniformly weak and not robust. In several of the key figures, the elimination of one or two outlier flies completely abolishes the relationship. The confidence bounds on the claimed correlations are very broad. These uncertainties propagate to undermine the eventual claims for a correspondence between neural and behavioral measures.

We are broadly receptive to this criticism. The lack of robustness of some results comes from the fundamental challenge of this work: measuring behavior is noisy at the individual level. Measuring Ca++ is also somewhat noisy. Correlating the two will be underpowered unless the sample size is huge (which is impractical, as each data point requires a dissection and live imaging session) or the effect size is large (which is generally not the case in biology). In the current version we tried to in some sense to avoid discussing these challenges head-on, instead trying to focus on what we thought were the conclusions justified by our experiments with sample sizes ranging from 20 to 60. We are working on a revision that is more candid about these challenges.

That said, we believe the result we view as the most exciting — that PC2 of Ca++ responses predicts OCT-MCH preference — is robust. 1) It is based on a training set with 47 individuals and a test set composed of 22 individuals. The p-value is sufficiently low in each of these sets (0.0063 and 0.0069, respectively) to pass an overly stringent Bonferonni correction for the 5 tests (each PC) in this analysis. 2) The BRP immunohistochemistry provides independent evidence that is consistent with this result — PC2 that predicts behavior (p = 0.03 from only one test) and has loadings that contrast DC2 and DM2. Taken together, these results are well above the field-standard bar of statistical robustness.

In the revision we are working on, we are explicit that this is the (one) result we have high confidence in. We believe this result convincingly links Ca++ and behavior, and warrants spotlighting. We have less confidence in other results, and say so, and we hope this addresses concerns about overstating our results.

3) Some aspects of the statistical treatment are unusual. Typically a model is proposed for the relationship between neuronal signals and behavior, and the model predictions are correlated with the actual behavioral data. The normal practice is to train the model on part of the data and test it on another part. But here the training set at times includes the testing set, which tends to give high correlations from overfitting. Other times the testing set gives much higher correlations than the training set, and then the results from the testing set are reported. Where the authors explored many possible relationships, it is unclear whether the significance tests account for the many tested hypotheses. The main text quotes the key results without confidence limits.

Our primary analyses are exactly what the reviewer describes, scatter plots and correlations of actual behavioral measures against predicted measures. We produced test data in separate experiments, conducted weeks to months after models were fit on training data. This is more rigorous than splitting into training and test sets data collected in a single session, as batch/environmental effects reduce the independence of data collected within a single session.

We only collected a test set when our training set produced a promising correlation between predicted and actual behavioral measures. We never used data from test sets to train models. In our main figures, we showed scatter plots that combined test and training data, as the training and test partitions had similar correlations.

We are unsure what the reviewer means by instances where we explored many possible relationships. The greatest number of comparisons that could lead to the rejection of a null hypothesis was 5 (corresponding to the top 5 PCs of Ca++ response variation or Brp signal). We were explicit that the p-values reported were nominal. As mentioned above, applying a Bonferroni correction for n=5 comparisons to either the training or test correlations from the Ca++ to OCT-MCH preference model remains significant at alpha=0.05.

Our revision will include confidence limits.

Reviewer #2 (Public Review):

Summary:

The authors aimed to identify the neural sources of behavioral variation in a decision between odor and air, or between two odors.

Strengths:

-The question is of fundamental importance.

-The behavioral studies are automated, and high-throughput.

-The data analyses are sophisticated and appropriate.

-The paper is clear and well-written aside from some strong wording.

-The figures beautifully illustrate their results.

-The modeling efforts mechanistically ground observed data correlations.

We are glad to read that the reviewer sees these strengths in the study. We hope the forthcoming revision will address the strong wording.

Weaknesses:

-The correlations between behavioral variations and neural activity/synapse morphology are (i) relatively weak, (ii) framed using the inappropriate words "predict", "link", and "explain", and (iii) sometimes non-intuitive (e.g., PC 1 of neural activity).

Taking each of these points in turn: i) It would indeed be nicer if our empirical correlations are higher. One quibble: we primarily report relatively weak correlations between measurements of behavior and Ca++/Brp. This could be the case even when the correlation between true behavior and Ca++/Brp is higher. Our analysis of the potential correlation between latent behavioral and Ca++ signals was an attempt to tease these relationships apart. The analysis suggests that there could, in fact, be a high underlying correlation between behavior and these circuit features (though the error bars on these inferences are wide).

ii) We are working to guarantee that all such words are used appropriately. “Predict” can often be appropriate in this context, as a model predicts true data values. Explain can also be appropriate, as X “explaining” a portion of the variance of Y is synonymous with X and Y being correlated. We cannot think of formal uses of “link,” and are revising the manuscript to resolve any inappropriate word choice.

iii) If the underlying biology is rooted in non-intuitive relationships, there’s unfortunately not much we can do about it. We chose to use PCs of our Ca++/Brp data as predictors to deal with the challenge of having many potential predictors (odor-glomerular responses) and relatively few output variables (behavioral bias). Thus, using PCs is a conservative approach to deal with multiple comparisons. Because PCs are just linear transformations of the original data, interpreting them is relatively easy, and in interpreting PC1 and PC2, we were able to identify simple interpretations (total activity and the difference between DC2 and DM2 activation, respectively). All in all, we remain satisfied with this approach as a means to both 1) limit multiple comparisons and 2) interpret simple meanings from predictive PCs.

-No attempts were made to perturb the relevant circuits to establish a causal relationship between behavioral variations and functional/morphological variations.

We did conduct such experiments, but we did not report them because they had negative results that we could not definitively interpret. We used constitutive and inducible effectors to alter the physiology of ORNs projecting to DC2 and DM2. We also used UAS-LRP4 and UAS-LRP4-RNAi to attempt to increase and decrease the extent of Brp puncta in ORNs projecting to DC2 and DM2. None of these manipulations had a significant effect on mean odor preference in the OCT-MCH choice, which was the behavioral focus of these experiments. We were unable to determine if the effectors had the intended effects in the targeted Gal4 lines, particularly in the LRP experiments, so we could not rule out that our negative finding reflected a technical failure. We are reviewing these results to determine if they warrant including as a negative finding in the revision.

We believe that even if these negative results are not technical failures, they are not necessarily inconsistent with the analyses correlating features of DC2 and DM2 to behavior. Specifically, we suspect that there are correlated fluctuations in glomerular Ca++ responses and Brp across individuals, due to fluctuations in the developmental spatial patterning of the antennal lobe. Thus, the DC2-DM2 predictor may represent a slice/subset of predictors distributed across the antennal lobe. This would also explain how we “got lucky” to find two glomeruli as predictors of behavior, when were only able to image a small portion of the glomeruli. In analyses we did not report, we explored this possibility using the AL computational model. We are likely to include this interpretation in the revised discussion.

Reviewer #3 (Public Review):

Churgin et. al. seeks to understand the neural substrates of individual odor preference in the Drosophila antennal lobe, using paired behavioral testing and calcium imaging from ORNs and PNs in the same flies, and testing whether ORN and PN odor responses can predict behavioral preference. The manuscript's main claims are that ORN activity in response to a panel of odors is predictive of the individual's preference for 3-octanol (3-OCT) relative to clean air, and that activity in the projection neurons is predictive of both 3-OCT vs. air preference and 3-OCT vs. 4-methylcyclohexanol (MCH). They find that the difference in density of fluorescently-tagged brp (a presynaptic marker) in two glomeruli (DC2 and DM2) trends towards predicting behavioral preference between 3-oct vs. MCH. Implementing a model of the antennal lobe based on the available connectome data, they find that glomerulus-level variation in response reminiscent of the variation that they observe can be generated by resampling variables associated with the glomeruli, such as ORN identity and glomerular synapse density.

Strengths:

The authors investigate a highly significant and impactful problem of interest to all experimental biologists, nearly all of whom must often conduct their measurements in many different individuals and so have a vested interest in understanding this problem. The manuscript represents a lot of work, with challenging paired behavioral and neural measurements.

Weaknesses:

The overall impression is that the authors are attempting to explain complex, highly variable behavioral output with a comparatively limited set of neural measurements…

We would say that we are attempting to explain a simple, highly variable behavioral measure with a comparatively limited set of neural measurements. I.e. we make no claims to explain the complex behavioral components of odor choice, like locomotion, reversals at the odor boundary, etc.

Given the degree of behavioral variability they observe within an individual (Figure 1- supp 1) which implies temporal/state/measurement variation in behavior, it's unclear that their degree of sampling can resolve true individual variability (what they call "idiosyncrasy") in neural responses, given the additional temporal/state/measurement variation in neural responses.

We are confident that different Ca++ recordings are statistically different. This is borne out in the analysis of repeated Ca++ recordings in this study, which finds that the significant PCs of Ca++ variation contain 77% of the variation in that data. That this variation is persistent over time and across hemispheres was assessed in Honegger & Smith, et al., 2019. We are thus confident that there is true individuality in neural responses (Note, we prefer not to call it “individual variability” as this could refer to variability within individuals, not variability across individuals.) It is a separate question of whether individual differences in neural responses bear some relation to individual differences in behavioral biases. That was the focus of this study, and our finding of a robust correlation between PC2 of Ca++ responses and OCT-MCH preference indicates a relation. Because behavior and Ca++ were collected with an hours-to-day long gap, this implies that there are latent versions of both behavioral bias and Ca++ response that are stable on timescales at least that long.

The statistical analyses in the manuscript are underdeveloped, and it's unclear the degree to which the correlations reported have explanatory (causative) power in accounting for organismal behavior.

With respect, we do not think our statistical analyses are underdeveloped, though we acknowledge that the detailed reviewer suggestions included the helpful suggestion to include uncertainty in the estimation of confidence intervals around the point estimate of the strength of correlation between latent behavioral and Ca++ response states. We are considering those suggestions and anticipate responding to them in the revision.

It is indeed a separate question whether the correlations we observed represent causal links from Ca++ to behavior (though our yoked experiment suggests there is not a behavior-to-Ca++ causal relationship — at least one where odor experience through behavior is an upstream cause). We attempted to be precise in indicating that our observations are correlations. That is why we used that word in the title, as an example. In the revision, we are working to make sure this is appropriately reflected in all word choice across the paper.

I can understand the frustration that may have lead King to commit such a blunder. As an Arab woman, I have found people who think that I am not apt enough in engaging in the discourse I am participating in. But I do not think that I would risk my ethics in accepting evidence or forgoing provenance for the sole motive of boosting my career. As we have discussed in class, provenance is important. It prevents more colonial exploitation of the Middle East, and it allows native scholars to learn and add to their own great history. This is where my sympathies end with King--- the idea that this text had "tipped over into likelihood" of being a forgery should have been where she exercised her duty as a scholar and disengaged with the text.

Has this entire poem been the conversation of the speaker receiving a taro card reading?

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Referee #1

Evidence, reproducibility and clarity

Summary: Sharma, et al. report the characterization of the polar tube (PT) from the microsporidian species, Vairimorpha necatrix, using a combination of optical microscopy, cryo-ET, and proteomics. The polar tube is a fascinating invasion apparatus which mediates the translocation of the parasite into the inside of a host cell to initiate infection. Similar to results obtained previously in other species, the authors show that PT firing in Vairimorpha necatrix is extremely fast, occurring on the order of 1 sec, and that the extruded PT is over 100 microns long in this species. Using cryo-ET to image the PT at a high resolution, they find that it exists in two major states: both an empty state and a state filled with cargo, and that the thickness of the tube wall changes when cargo is present. Strikingly, the authors observed that one of the cargo components, the ribosomes, are organized ordered array that may have helical symmetry. Finally, the authors took advantage of a naturally occurring "His tag" on PTP3 to affinity purify PTP3-containing protein complexes and analyze the composition using proteomics.

Major comments

ln 139-140: The absolute handedness of something can be very tricky to determine by cryo-ET (but certainly is possible). Variable hardware configurations between microscopes and differing conventions between software packages (e.g., for what direction is a positive tilt angle) can lead to inversion of the apparent handedness in the final tomogram. How certain are the authors that the absolute handedness is indeed right handed, as this seems to vary between the various display items in the manuscript? For example, in Fig 1c, my impression is that ribosome helices are left handed, as they are also in the supplemental movie. If this isn't known with certainty, perhaps it would be sufficient to describe the apparent helical symmetry but state that the handedness is ambiguous.

Minor comments

ln 39-40: Perhaps also cite the E. cuniculi genome paper?

ln 97-98: It is interesting that the PT shortens in V. necatrix as well, and while I can pick this out in some of the individual traces in Sup Fig. 1b, it seems to get washed out in the trend line and isn't super obvious. If it isn't to laborious, it could be nice to add a panel showing the quantification of this (e.g., plotting the final length of each PT as a percentage of the maximum length achieved).

ln 98-100: Strictly speaking, I don't think the referenced figure shows the sporoplasm being transformed into an extended conformation, only that it is spherical upon exit. Simply reword this to make clear that the deformations are inferred to occur but not directly observed.

Because PT firing is so fast, the probability of trapping a PT in the process of transporting cargo would be pretty low. So then why does the PT still contain cellular cargo like ribosomes inside in the tomograms? Should these not have emerged in the sporoplasm which would enter the host cell? Are these "defective" spores that have failed to complete sporoplasm transport? Perhaps this is worth discussing.

ln 118: The authors note an apparent correlation between the phase of germination and the thickness of the tube wall but don't specify what this correlation is. Is it thicker in the early phase and thinner in later phase, or vice versa? One could imagine "empty" tubes existing before or after sporoplasm transport, for example, so I'm not sure I follow how the phase is being inferred from the tomograms.

ln 119-120: What is the evidence that the outer layer is made of PTPs, or that it is even protein (for example, as opposed to cell wall-like carbohydrate polymers)? I think this seems like a very reasonable hypothesis, but I would suggest explaining the logic and ensuring the degree of uncertainty is conveyed clearly. In light of this, I would also suggest changing figure labels, etc, that refer to the PTP layer (e.g., Fig. 3, PTPc and PTPe labels).

ln 121, 123: "sheathed by a thin layer" and "enveloped by a thick outer layer": is this an additional layer being described? Or is this referring to the putative PTP layer, and that its thickness is variable?

ln 125-126: While I understand how some features, like ribosomes, proteasomes, and generic membrane compartments could be identified, it is unclear to me how one would recognize the nucleus when inside the PT, nor are any examples shown. If the data is clear, perhaps the authors could show it in a figure? Otherwise, I suggest removing the claim regarding the nucleus.

The arrangement of the ribosomes in a subset of tubes is really fascinating! While the number of observations is relatively small (n=5), it seems like it should be possible to comment preliminarily on whether there is much variability in their helical arrangement. Do the helical parameters vary much between observations? Does the til, pitch, etc vary much, are the 5 occurrences very similar? Is there any sign that they are associated with a membrane? Also, since the ribosomes form a lattice-like arrangement, it seems like it would be possible to trace ribosome helices in both the left and right handed directions. How did the authors decide between the two possibilities? This doesn't seem to be discussed.

Fig. 2e: Are the two different colors/orientations meant to represent the two protamers of the ribosome dimer? When refined subvolumes are mapped back onto the original tomogram do the authors observe a similar crystalline arrangement of particles as in their segmentation? Are the orientations of the ribosomes correlated, and do the provide any evidence for the dimeric arrangement mentioned? The PlaceObjects plugin for Chimera can be very helpful for visualizing this: https://www.biochem.mpg.de/7939908/Place-Object

Supp figure 4(b-d): Perhaps these models could be colored by pLDDT scores (with a key indicating the color scheme), so the reader can assess the quality of the predictions?

How were the measurements of the membrane thickness and putative PTP layer carried out? On the tomogram projections? STAs? How were the boundaries of the layers established (e.g., map threshholding if STA?)? This information appears to be missing from the methods.

Some tubes that are labeled as 'PTempty' actually contain cargo and look dense (example supp. Fig 2c, left and middle panels). Is it fair to classify these as empty tubes?

Fig. 3d: I am not entirely clear on what is being shown here. Are independent reconstructions of PTcargo and PTempty superposed (aligned on membrane)? The description in the figure legend doesn't clearly say what is being displayed. I think it might be more clear to show these side-by-side instead of superposed (i.e., 4 panels instead of 2).

Sup Fig 1: Define S and SP in legend or just spell out on figure? Missing x-axis label on panel b.

Fig. 4b and Sup Fig 2a: The depictions of the PT in the spore here are left-handed. In a few species, the coil of the PT was found to form a right-handed helix (Jaroenlak, et al.), and it seems plausible that this may be a general feature that would be conserved across microsporidia. I appreciate that it might not be actually known to be right-handed in V. necatrix, but if there is no strong data either way, perhaps it would make sense for these depictions of the PT to be right-handed.

I think all three of us are more or less in consensus about this manuscript, and I largely agree with the other reviewers comments. I think after addressing reviewer suggestions, this will be a pretty nice story.

Significance

Overall, this manuscript from Sharma, et al. presents interesting new findings about the structure and cargo transport function of the microsporidian PT. Microsporidia infect a wide range of hosts, including humans, and how the PT mediates parasite entry into cells is poorly understood. The approaches used in this study are appropriate for tackling the questions at hand, and appear to be generally well executed and interpreted. The observation that ribosomes assemble into an array within the PT is very unexpected and quite fascinating, and may be of broader interest to researchers working on ribosome structure and function, in addition to researchers studying microsporidia. The approach to investigating proteins interacting with PTP3 was quite elegant, and yielded a list of potential interactors that appears to be of very high quality and is highly plausible based on the literature field. We think this work is a substantial advance in the field and provides important new insights into the organization of the PT. - Please define your field of expertise with a few keywords to help the authors contextualize your point of view:

Structural biology, microsporidia - Indicate if there are any parts of the paper that you do not have sufficient expertise to evaluate.

We are not experts in proteomics/mass spectrometry

Author Response

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

eLife assessment

This study has uncovered some important initial findings about how certain extracellular vehicles (EVs) from the mother might impact the energy usage of an embryo. While the study's findings are in general solid, some experiments lack statistical power due to small sample sizes. The study's title might be a bit too assertive as the evidence linking maternal mtDNA transmission to changes in embryo energy use is still correlative.

We would like to express our sincere gratitude to the editors and reviewers for their invaluable comments on this work. Their feedback has been instrumental in enhancing the quality of our manuscript; we have incorporated their suggestions to the best of our abilities.

Reviewer #1 (Public Review):

Q1. Bolumar et al. isolated and characterized EV subpopulations, apoptotic bodies (AB), Microvesicles (MV), and Exosomes (EXO), from endometrial fluid through the female menstrual cycle. By performing DNA sequencing, they found the MVs contain more specific DNA sequences than other EVs, and specifically, more mtDNA were encapsulated in MVs. They also found a reduction of mtDNA content in the human endometrium at the receptive and post-receptive period that is associated with an increase in mitophagy activity in the cells, and a higher mtDNA content in the secreted MVs was found at the same time. Last, they demonstrated that the endometrial Ishikawa cell-derived EVs could be taken by the mouse embryos and resulted in altered embryo metabolism.

This is a very interesting study and is the first one demonstrating the direct transmission of maternal mtDNA to embryos through EVs.

A1. Thank you for your kind comments.

Reviewer #2 (Public Review):

Q2. In Bolumar, Moncayo-Arlandi et al. the authors explore whether endometrium-derived extracellular vesicles contribute mtDNA to embryos and therefore influence embryo metabolism and respiration. The manuscript combines techniques for isolating different populations of extracellular vesicles, DNA sequencing, embryo culture, and respiration assays performed on human endometrial samples and mouse embryos.

Vesicle isolation is technically difficult and therefore collection from human samples is commendable. Also, the influence of maternally derived mtDNA on the bioenergetics of embryos is unknown and therefore novel. However, several experiments presented in the manuscript fail to reach statistical significance, likely due to the small sample sizes. Additionally, the experiments do not demonstrate a direct effect of mtDNA transfer on embryo bioenergetics. This has the unfortunate consequence of making several of the authors' conclusions speculative.

In my opinion the manuscript supports the following of the authors' claims:

1) Different amounts of mtDNA are shed in human endometrial extracellular vesicles during different phases of the menstrual cycle

2) Endometrial microvesicles are more enriched for mitochondrial DNA sequences compared to other types of microvesicles present in the human samples

3) Fluorescently labelled DNA from extracellular vesicles derived from an endometrial adenocarcinoma cell line can be incorporated into hatched mouse embryos.

4) Culture of mouse embryos with endometrial extracellular vesicles can influence embryo respiration and the effect is greater when cultured with isolated exosomes compared to other isolated microvesicles

A2. Thank you for your detailed feedback. We have made every effort to enhance the manuscript in this revised version, ensuring that our conclusions are grounded in solid evidence and that they avoid any speculation.

My main concerns with the manuscript:

Q3. The authors demonstrate that microvesicles contain the most mtDNA, however, they also demonstrate that only isolated exosomes influence embryo respiration. These are two separate populations of extracellular vesicles.

A3. This manuscript focuses on the DNA content secreted by the endometrium and captured by the embryo. We identified both mitochondrial DNA and genomic DNA. We have found that mitochondrial DNA is predominantly secreted and encapsulated within microvesicles, while all three types of vesicles encapsulate genomic DNA. Specifically, based on the results we presented in Response A8 to the reviewers and included in the latest version of the manuscript, we observed that exosomes contain the highest amount of genomic DNA. Furthermore, exosomes have the greatest impact on embryo bioenergetics, suggesting that this DNA content may primarily exert this effect. We have thoroughly revised the manuscript, focusing our message on DNA content.

Q4. mtDNA is not specifically identified as being taken up by embryos only DNA.

A4. We agree with the reviewer; as we mention in answer A9, EdU does not specifically label mitochondrial DNA. To solve this issue, we incubated a synthetic molecule of labeled mtDNA with embryos and analyzed mtDNA incorporation using confocal microscopy. We co-cultured hatched mouse embryos (3.5 days) with an ATP8 sequence conjugated with Biotin overnight at 37ºC and 5% CO2. We then permeabilized embryos, incubated them with Streptavidine-Cy3 for 45 min, and visualized the results using an SP8 confocal microscope (Leica). We observed mtDNA internalization by cells of the hatched embryos; please see new supplementary Figure 7 and lines 234-237 on page 9 and lines 583-592 M&M on page 21.

Q5. The authors do not rule out that other components packaged in extracellular vesicles could be the factors influencing embryo metabolism.

A5. The vesicular subtypes contain molecules beyond DNA, such as microRNAs, proteins, or lipids. Our laboratory has studied the transmission of vesicles and their relationship with their contents (particularly microRNAs) and their connection to maternal-fetal communication. In this study, we focused on genomic/mitochondrial DNA. We cannot exclude the possibility that other molecules may influence metabolism; this statement is already noted in the discussion section on lines 328-331 on page 12.

Q6. Taken together, these concerns seem to contradict the implication of the title of the manuscript – the authors do not demonstrate that inheritance of maternal mtDNA has a direct causative effect on embryo metabolism.

A6. We have modified the title to better align with the manuscript’s results. The proposed new title for the manuscript is “Vertical transmission of maternal DNA through extracellular vesicles modulates embryo bioenergetics during the periconceptional period.”

Reviewer #1 (Recommendations for The Authors):

Q7. Would it be possible to validate the mtDNA content and mitophagy activity in different periods using the Ishikawa cells?

A7. Unfortunately, this validation cannot be achieved with in vitro cultures of cell lines, especially with a cell line such as the endometrial adenocarcinoma-derived Ishikawa cell line. While mimicking the menstrual cycle (as observed in Figure 3 of the manuscript) is entirely artificial, we believe that the statistically significant results obtained in human samples faithfully represent the biological processes involved. Using a cell line, in our opinion, would not provide us with novel information.

Q8. Characterization of the EVs subpopulations from Ishikawa cells and direct evidence to show the EdU labeled DNA is contained in the EVs are necessary.

A8. To address this concern, we designed a novel experiment. We cultured Ishikawa cells in the presence of Edu, isolated the three types of vesicles, and evaluated labeled DNA content by flow cytometry (as illustrated in Supplementary Figure 5). All three types of vesicles exhibited positive EdU-DNA labeling; notably, the exosomal fraction demonstrated substantially higher DNA content than the other vesicle populations. Please see new supplementary Figure 5 and lines 217-218 on page 9, and lines 576-582 of the M&M on pages 20-21.

Q9. Would EdU incorporate into the genomic DNA or mitochondrial DNA?

A9. EdU (5-ethynyl-2′-deoxyuridine) is a nucleoside analog of thymidine and becomes incorporated into DNA during active DNA synthesis. EdU labels all newly synthesized DNA, both genomic and mitochondrial; however, we cannot differentiate between them with this technique.

Q10. It is difficult to assess whether the EV-derived DNA was taken by the TE or ICM without immunostaining of cell lineage markers in mouse embryos.

A10. We did not aim to label the inner cell mass, as the vesicles primarily enter through trophectodermal cells. The images presented in Figure 4 and Supplementary Figure 5 depict trophectoderm cells.

Q11. It is also valuable to perform co-staining of Mitotracker to show the co-localization of EdU labelled DNA and the mitochondrial.

A11. Per the reviewer's suggestion, we conducted an experiment as described in the following text. We isolated MVs from the culture media of EdU-treated Ishikawa cells and co-incubated them with embryos overnight. The resulting images (See Author response image 1) show an embryo subjected to staining with EdU-tagged DNA labeled with Alexa Fluor 488 (green), Mitotracker Deep Red (red), and nuclei (blue). Detailed views of the embryo are presented in panels A and B. Notably, we observed co-localization of mitochondria and EdU-tagged DNA, as indicated by the white arrows. Despite this intriguing finding, we chose not to include these results in the initial version of the manuscript; however, if the editor deems it appropriate, we would be delighted to incorporate them into the final version. The experimental procedure for co-localization of EdU DNA-tagged with mitochondria involved the following steps: Mitotracker Deep Red FM (Thermo Fisher Scientific, M22426) was added to the embryo media at a final concentration of 200 nM, and the embryos were subsequently incubated for 45-60 minutes prior to fixation.

Author response image 1.

Co-localization of mitochondria and EdU-tagged DNA in mouse embryos. Representative micrograph of an embryo co-incubated with MVs isolated from the culture media of Ishikawa cells treated with EdU. EdU-tagged DNA was labeled with Alexa Fluro 488 (green). Mitotracker Deep Red (mitochondria; red) and nuclei (blue). A and B) magnified images of the embryo show detailed co-localization of mitochondria and EdU-tagged DNA (white arrows). Negative control) Embryos incubated with MVs isolated from control Ishikawa cells (without EdU incubation) and stained with the click-it reaction cocktail. A and B showed magnified images of the embryo. Notice the absence of EdU-Alexa Fluro 488 signals (green).

Reviewer #2 (Recommendations for The Authors):

Q12. It would be helpful if the authors could provide citations and rationale for why they chose specific molecular markers to validate the different population of extracellular vesicles.

A12. Different extracellular populations are defined by molecular marker signatures that reflect their origin. VDAC1 forms ionic channels in the mitochondrial membrane, has a role in triggering apoptosis, and has been described as characteristic of ABs.[1]

The ER protein Calreticulin has also been used as an AB marker [2]; however, other studies have noted the presence of Calreticulin in MVs. [1] This apparent non-specificity may derive from apoptotic processes, during which the ER membrane fragments and forms vesicles smaller than ABs, which would contain Calreticulin and sediment at higher centrifugal forces.[3,4] In fact, proteomic studies have linked the presence of Calreticulin with vesicular fractions of a size range relevant for MVs [5] and ABs [6].

ARF6, a GTP-binding protein implicated in cargo sorting and promoting MV formation, has been proposed as an MV marker. [7,8]

Classic markers of EXOs include molecules involved in biogenesis, such as tetraspanins (CD63, CD9, CD81), Alix, TSG101, and flotillin-1.[9,10] Nonetheless, studies have recently reported the widespread nature of such markers among various EV populations, although with different relative abundances (such as is the case for CD9, CD63, HSC70, and flotillin-1[11]). Notably, certain molecular markers (such as TSG101[1,11]) have been ratified as specific to EXOs.

References

1. D. K. Jeppesen, M. L. Hvam, B. Primdahl-Bengtson, A. T. Boysen, B. Whitehead, L. Dyrskjøt, T. F. Orntoft, K. A. Howard, M. S. Ostenfeld, J. Extracell. Vesicle. 2014, 3, 25011, doi: 10.3402/jev.v3.25011.

2. J. van Deun, P. Mestdagh, R. Sormunen, V. Cocquyt, K. Vermaelen, J. Vandesompele, M. Bracke, O. De Wever, A. Hendrix, J. Extracell. Vesicles. 2014, 3:24858, doi: 10.3402/jev.v3.24858.

3. L. Abas, C. Luschnig, Anal. Biochem. 2010, 401, 217-227, doi: 10.1016/j.ab.2010.02.030.

4. C. Lavoie, J. Lanoix, F. W. Kan, J. Paiement, J. Cell Sci. 1996, 109(6), 1415-1425.

5. M. Tong, T. Kleffmann, S. Pradhan, C. L. Johansson, J. DeSousa, P. R. Stone, J. L. James, Q. Chen, L. W. Chamley, Hum. Reprod. 2016, 31(4), 687-699, doi: 10.1093/humrep/dew004.

6. P. Pantham, C. A. Viall, Q. Chen, T. Kleffmann, C. G. Print, L. W. Chamley, Placenta. 2015, 36, 1463e1473, doi: 10.1016/j.placenta.2015.10.006.

7. V. Muralidharan-Chari, J. Clancy, C. Plou, M. Romao, P. Chavrier, G. Raposo, C. D'Souza-Schorey, Curr. Biol. 2009, 19, 1875-1885.

8. C. Tricarico, J. Clancy, C. D'Souza-Schorey, Small GTPases. 2016, 0(0), 1-13.

9. M. Colombo, G. Raposo, C. Théry, Annu. Rev. Cell. Dev. Biol. 2014, 30, 255-289, doi: 10.1146/annurev-cellbio-101512-122326.

10. S. Mathivanan, H. Ji, R. J. Simpson, J. Proteomics. 2010, 73(10), 1907-1920.

11. J. Kowal, G. Arras, M. Colombo, M. Jouve, J. P. Morath, B. Primdal-Bengtson, F. Dingli, D. Loew, M. Tkach, C. Théry, Proc. Natl. Acad. Sci. U. S. A. 2016, 113(8), E968-77.

Q13. The PCA analysis in supplementary figure 4 A&B needs more explanation for why they think separation of the two conditions based on principal component 1 is sufficient. The small number of replicates makes me concerned because principal component 2 does not show similarity of replicates for the DNase treated samples. Also, 4C has no description in the figure legend.

A13. The PCA results show a clear separation between the two conditions; we believe this separation is primarily driven by the differences observed in principal component 1 (PC1). We would like to address the concerns raised by the reviewer with the following points:

1. Interpretation of PCs: In PCA, the principal components represent orthogonal axes capturing the highest variance in the data. PC1 accounts for 56% and 57% of the variance in the two conditions, respectively. The significant variance explained by PC1 suggests that it effectively captures the major sources of variation between the samples.

2. Sample Replicates and Variability: The concern regarding the small number of replicates is acknowledged, and we understand its impact on the analysis. Despite the limited number of replicates, the consistent pattern of separation in PC1 between the two conditions provides confidence in the observed separation. We also agree that PC2 does not show an apparent similarity among the DNase-treated samples; however, this does not diminish the significance of PC1, which robustly separates the two conditions.

We include the Figure legend for 4C: “C) Principal component analysis shows EV sample grouping due to specificity in coding-gene sequences.

Q14. I am confused by the phrasing in the last two sentences of the top paragraph on page 7. Why would apoptotic bodies all have similar content if they encapsulate a greater amount of material making their contents less specific? Please clarify.

A14. This sentence intended to convey the fact that apoptotic bodies (ABs) are formed from apoptotic cells, they are larger in size, and their content is more non-specific - this non-specific nature arises as they do not encapsulate molecules specifically, unlike the other two types of vesicles. For more detailed information on ABs in human reproduction, we published an extensive review in 2018 (see below).

Simon C, Greening DW, Bolumar D, Balaguer N, Salamonsen LA, Vilella F. Extracellular Vesicles in Human Reproduction in Health and Disease. Endocr. Rev. 2018 Jun 1;39(3):292-332. doi: 10.1210/er.2017-00229. PMID: 29390102.

Q15. The first and last sentences of the last paragraph of page 8 seem to contradict each other. Please clarify.

A15. We observe an enrichment in the amount of mitochondrial DNA in samples during the receptive and post-receptive phases. While the data may not show statistical significance, we observed a trend towards greater enrichment in receptivity compared to pre-receptivity. The lack of significant differences could be attributed to inherent variability among patients. We have also altered the text on page 8 to avoid confusion.

Q16. Quantification of the rates of DNA incorporation into embryos would strengthen Figure 4 and Supplementary Figure 5.

A16. We acknowledge the reviewer's feedback, and in response, we conducted an assay to quantify the total DNA incorporated into the embryos. We isolated EVs from the control Ishikawa cell culture media and EdU-treated Ishikawa cell culture media to achieve this. Subsequently, we co-incubated both types of EVs with ten embryos overnight in G2 plus media at 37ºC and 5% CO2.

After co-incubation, we collected embryos and the culture media containing co-incubated EVs. We then isolated total DNA using the QIAamp® DNA Mini kit (Qiagen; 51304). To label the EdU-DNA particles, we performed a click-it reaction using the Click-iT™ EdU Alexa Fluor™ 488 flow cytometry assay Kit (Thermo Fisher Scientific, ref: C10420) per the manufacturer's instructions. Subsequently, we cleaned and purified DNA using AMPure beads XP (Beckman Coulter, A63882) and eluted DNA in 150 L of 0.1 M Tris-EDTA. Finally, we measured the fluorescence of each sample using a Victor3 plate reader (PerkinElmer). To ensure accuracy, we subtracted the background signal from non-labeled DNA-derived EVs and embryos incubated without EVs for each sample. Despite conducting the experiment twice, we encountered challenges in obtaining clear results, possibly due to the limitation of the technique's resolution.

Q17. If mtDNA is most enriched in MVs but only embryos cultured with Exos demonstrated differences in respiration the authors need to comment on this discrepancy.

A17. We ask the reviewer to refer to Answer A3; we have thoroughly revised the manuscript, focusing our message on DNA content.

Q18. The authors should change the definitive language in the title of the manuscript because all evidence presented is correlative.

A18.We have modified the title to better align with the manuscript's results. The proposed new title for the manuscript is “Vertical transmission of maternal DNA through extracellular vesicles modulates embryo bioenergetics during the periconceptional period.”

Q19. I realize this is beyond what the authors intend for the scope of this paper, however, on page 6 the authors describe membranous structures within the ABs but say they couldn't study their presence with organelle-specific markers. Why? Presence of organelles in these vesicles is very interesting!

A19. As the reviewer rightly points out, we did not study ABs in this manuscript. Analysis of the electron microscopy images suggests the presence of fragments of organelles, most likely originating from apoptotic processes; however, we did not use any specific markers to confirm our assertion. We have modified the text to avoid any confusion. Please see Page 6, Lines 120-121, for further details.

Reviewer #3 (Public Review):

Summary:<br /> The study uses structural MRI to identify how the number, degree of experience, and phonemic diversity of language(s) that a speaker knows can influence the thickness of different sub-segments of the auditory cortex. In both a primary and replication sample of adult speakers, the authors find key differences in cortical thickness within specific subregions of the cortex due to either the age at which languages are acquired (degree of experience), or the diversity of the phoneme inventories carried by that/those language(s) (breadth of experience).

Strengths:<br /> The results are first and foremost quite fascinating and I do think they make a compelling case for the different ways in which linguistic experience shapes the auditory cortex.

The study uses a number of different measures to quantify linguistic experience, related to how many languages a person knows (taking into account the age at which each was learned) as well as the diversity of the phoneme inventories contained within those languages. The primary sample is moderately large for a study that focuses on brain-behaviour relationships; a somewhat smaller replication sample is also deployed in order to test the generality of the effects.

Analytic approaches benefit from the careful use of brain segmentation techniques that nicely capture key landmarks and account for vagaries in the structure of STG that can vary across individuals (e.g., the number of transverse temporal gyri varies from 1-4 across individuals).

Weaknesses:<br /> The specificity of these effects is interesting; some effects really do appear to be localized to the left hemisphere and specific subregions of the auditory cortex e.g., TTG. However because analyses only focus on auditory regions along the STG and MTG, one could be led to the conclusion that these are the only brain regions for which such effects will occur. The hypothesis is that these are specifically auditory effects, but that does make a clear prediction that non-auditory regions should not show the same sort of variability. I recognize that expanding the search space will inflate type-1 errors to a point where maybe it's impossible to know what effects are genuine. And the fine-grained nature of the effects suggests a coarse analysis of other cortical regions is likely to fail. So I don't know the right answer here. Only that I tend to wonder if some control region(s) might have been useful for understanding whether such effects truly are limited to the auditory cortex. Otherwise one might argue these are epiphenomenal or some hidden factor unrelated to auditory experience predicting that we'd also see them in the non-auditory cortex as well, either within or outside the brain's speech network(s).

The reason(s) why we might find a link between cortical thickness and experience is not fully discussed. The introduction doesn't really mention why we'd expect cortical thickness to be correlated (positively or negatively) with speech experience. There is some discussion of it in the Discussion section as it relates to the Pliatsikas' Dynamic Restructuring Model, though I think that model only directly predicts thinning as a function of experience (here, negative correlations). It might have less to say about observed positive correlations e.g., HG in the right hemisphere. In any case, I do think that it's interesting to find some relationship between brain morphology and experience but clearer explanations for why these occur could help, and especially some mention of it in the intro so readers are clearer on why cortical thickness is a useful measure.

One pitfall of quantifying phoneme overlap across languages is that what we might call a single 'phoneme', shared across languages, will, in reality, be realized differently across them. For instance, English and French may be argued to both use the vowel /u/ although it's realized differently in English vs. French (it's often fronted and diphthongized in many English speaker groups). Maybe the phonetic dictionaries used in this study capture this using a close phonetic transcription, but it's hard to tell; I suspect they don't, and in that case, the diversity measures would be an underestimate of the actual number of unique phonemes that a listener needs to maintain.

Discussion of potential genetic differences underlying the findings is interesting. One additional data point here is a study finding a relationship between the number of repeats of the READ1 (a factor of the DCDC2 gene) in populations of speakers, and the phoneme inventory of language(s) predominant in that population (DeMille, M. M., Tang, K., Mehta, C. M., Geissler, C., Malins, J. G., Powers, N. R., ... & Gruen, J. R. (2018). Worldwide distribution of the DCDC2 READ1 regulatory element and its relationship with phoneme variation across languages. Proceedings of the National Academy of Sciences, 115(19), 4951-4956.) Admittedly, that paper makes no claim about the cortical expression of that regulatory factor under study, and so more work needs to be done on whether this has any bearing at all on the auditory cortex. But it does represent one alternative account that does not have to do with plasticity/experience.

The replication sample is useful and a great idea. It does however feature roughly half the number of participants meaning statistical power is weaker. Using information from the first sample, the authors might wish to do a post-hoc power analysis that shows the minimum sample size needed to replicate their effect; given small effects in some cases, we might not be surprised that the replication was only partial. I don't think this is a deal breaker as much as it's a way to better understand whether the failure to replicate is an issue of power versus fragile effects.

reply to u/dotinvoke at https://www.reddit.com/r/Zettelkasten/comments/175a6tr/are_links_still_better_than_search_in_the_age_of/

The value in the process is making a ratchet of ideas which is highly customized to building your own lines of thought or "associative trails" if you prefer Vannevar Bush's framing.

If your idea worked, then one could "simply" rely on Google's database and a variety of associated tools to act as your zettelkasten—Bob's your uncle and you're done! In practice, you'll find that this doesn't work well. You can experiment, but I think you'll find that your own limited choices of links will work far better than the infinite number of adjacent possible links that a digital system may create on your behalf. If you're already fighting information overload, you don't want to add link overload to your list of problems.

Put in a different light, it can be interesting to randomly flip a coin and go left on heads and right on tails to see where you might end up, particularly if you're unsure. But if you actively make your own choices, you're more likely to be happier with what you see along the way and where you end up.

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

Learn more at Review Commons

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Reply to the reviewers

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

The authors describe a broad-scale phylogenetic survey of chemokine-related ligand and receptors from representative vertebrates, invertebrates, and viruses. They collect ligand and receptor sequences from available genome sequences, and use phylogenetic and CLANS analysis to group these into similar gene types. They then overlay these onto a validated species phylogeny in order to evaluate relationships of orthology and paralogy to pinpoint gene duplication and loss events. They carry out these analyses for canonical chemokine ligands receptors and for other closely related protein families. They conclude that the canonical chemokine system is restricted to vertebrates but that closely related ligands and receptors can be found in invertebrate chordates. More divergent but related gene systems are found in more distant invertebrates. They define more limited expansions of some ligand-receptor systems in certain jawed vertebrate groups and specifically in mammals.

Overall, the paper addresses a complex and important system of signaling proteins with a rigorous and comprehensive set of analyses. The finding will be of interest to a diverse group of scientists. My comments listed below mainly consist of suggestions to help clarify the presentation.

1. Pg 2, Lns 21-24: The canonical and non-canonical chemokine subclasses are introduced in the abstract without definition. A very brief explanation would be useful.

We've included a brief description of "non-canonical" components in the abstract (lines 21-24). These non-canonical components fall into at least one of three categories: 1) molecules with sequence similarities to canonical components, 2) those that bind to a canonical component (either ligand or receptor), 3) those involved in chemokine-like functions, such as chemoattraction. More comprehensive explanations and examples of these non-canonical components are provided in the Introduction section.

1. Some general contexts of chemokine functions are listed, including inflammation and homeostasis. A little more detail of how these signals are used and the molecular consequences of signaling may be useful in the introduction to set the biological context of the analysis (e.g., how do the signals regulate homeostasis?).

We have added at the beginning of the introduction (lines 39 – 46) some details of how chemokine signalling typically occurs at a mechanistic level. We also provided few examples of homeostatic functions regulated by chemokine signalling and clarified different expression strategies for inflammatory versus homeostatic chemokines.

It may help to summarize the known chemokine and chemokine-related gene systems in some type of table at the beginning of the results. This could serve as a convenient reference to guide the reader through the more detailed results. The manuscript addresses a complex set of ligands and receptors with names that may be confusing to the non-expert.

We agree with the reviewer on this and moved Table S1 to the main text (now Table 1). This table contains all the information on ligands, receptors, and relative citations (lines 741-744).

Pg 5, Ln 98: Fig 1C is introduced before Fig 1B. Can the panels be switched or the descriptions be rearranged?

We have switched the panels in Figure 1. Now, Figure 1A and 1B refer to CLANS analyses and Figure 1C and 1D refer to phylogenetic trees of ligand groups. We have corrected all the references in the main text and in Figure 1 caption. Now the panels are mentioned in the correct alphabetical order within the text.

Cytokine and chemokine ligands are small proteins that diverge quickly in different species and are difficult to identify in divergent genomes even within vertebrates. Conclusions about the absence of these types of factors are notorious for being disproven in subsequent analyses. Some discussion of what may have been missed in the survey for homologs (or reasons to think that ligands were not missed) would be useful in the Discussion.

We concur with the reviewer's observation, and we used three distinct strategies to address the issue:

1. E-value Threshold Adjustment: Initially, we utilized a relatively low e-value threshold of These three strategies collectively contribute to a more robust and comprehensive approach to address the challenges associated with the bioinformatic identification of canonical and non-canonical chemokines. We briefly mentioned the technical difficulty of working with short sequences in our Introduction (lines 75-76).

Reviewer #1 (Significance (Required)):

This paper presents a thorough analysis of chemokines and related gene systems across a wide phylogenetic landscape. The authors have expertise in these gene families and in the techniques that they use to identify and relate family members. The chemokines are an important set of signals that are used across several biological systems. These findings will be of wide interest to immunologists, neurobiologists, developmental and evolutionary biologists.

We thank reviewer 1 for their comments – they have been very valuable to improve our manuscript.

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

This paper applies phylogenetic clustering methods to a large taxonomical sampling to interrogate the relationship between canonical and non-canonical chemokine ligands and receptors. The results suggest that 1) unrelated proteins evolved "chemokine-like" ligand function multiple times independently; and 2) all the canonical and non-canonical chemokine receptors (except ACKR1) originated from a single duplication in the vertebrate stem group, which also gave rise to many GPCRs. In addition, the authors characterized the complement of canonical and non-canonical components in the common ancestor of vertebrates and identified several other ligands and receptors with potential chemokine related properties.

Comments: 1. There are many places in the paper, too many to list, where the authors refer to chemokine receptors but call them 'chemokines'.

We have corrected this oversight throughout the manuscript.

In Figure 1, CX3CL is referred to as 'X3CL'

We have corrected this. Now CX3CL is referred to correctly in Figure 1. We also found that it was incorrectly spelt in Figure 2 as well and corrected it there too.

1. CXCL17 was originally reported to be chemokine-like based on sequence threading methods. The authors refer to a 2015 paper indicating that it has chemokine-like activity at GPR35, which had been renamed provisionally CXCR8. To my knowledge that result was not based on direct binding data but inferred from a functional response. Moreover, to my knowledge it has not been independently confirmed. Instead there is a recent paper in JI from the Pease lab showing extensive experimental results that fail to demonstrate CXCL17 activity at GPR35. This uncertainty regarding a potential mistake in the literature should be addressed and integrated in the points made about CXCL17 being an outlier.

We thank the reviewer for pointing this out. To account for this suggestion, we have modified the text as follows:

Lines 105-108: “The distinction between CXCL17 and all other canonical chemokines is consistent with our receptor results showing that the potential receptor for CXCL17, GPR35 (41), is also not within the canonical chemokine receptor group (see below). Although it is important to note that recent studies fail to demonstrate CXCL17 activity at GPR35 (42, 43).”

Lines 240-241: “Another orphan GPCR, GPR35, had been proposed as a potential chemokine receptor (41); however, this was later questioned (42, 43) and GPR35 is still generally considered orphan (55–57).”

Lines 312-315: “CXCL17 is mammal-specific and likely unrelated to canonical chemokines (similar to its controversial putative receptor, GPR35 (41-43), that is not a canonical chemokine receptor).”

References: [41] J. L. Maravillas-Montero, et al., Cutting Edge: GPR35/CXCR8 Is the Receptor of the Mucosal Chemokine CXCL17. The Journal of Immunology 194, 29–33 (2015).

[42] S.-J. Park, S.-J. Lee, S.-Y. Nam, D.-S. Im, GPR35 mediates lodoxamide-induced migration inhibitory response but not CXCL17-induced migration stimulatory response in THP-1 cells; is GPR35 a receptor for CXCL17? British Journal of Pharmacology 175, 154–161 (2018).

[43] N. A. S. B. M. Amir, et al., Evidence for the Existence of a CXCL17 Receptor Distinct from GPR35. The Journal of Immunology 201, 714–724 (2018).

[55] S. Xiao, W. Xie, L. Zhou, Mucosal chemokine CXCL17: What is known and not known. Scandinavian Journal of Immunology 93, e12965 (2021).

[56] S. P. Giblin, J. E. Pease, What defines a chemokine? – The curious case of CXCL17. Cytokine 168, 156224 (2023).

[57] J. Duan, et al., Insights into divalent cation regulation and G13-coupling of orphan receptor GPR35. Cell Discov 8, 1–12 (2022).

Can the authors use alpha fold to address whether any of these non-canonical molecules actually is predicted to fold like a chemokine? More generally, based on the paper's analysis, how do the authors propose to define a chemokine? It is well-accepted that chemokines are defined by structure, not function (e.g. limited truncation of any chemokine abrogates activity, but it is still a chemokine structurally, not semantically, folds like a chemokine, aligns with other chemokines).

In response to the recommendation from reviewer 2 to incorporate AlphaFold data, we leveraged AFDB Clusters (foldseek.com), a recently developed tool that clustered over 200 million Uniprot proteins based on their predicted AlphaFold structures (as described in this Nature paper: https://www.nature.com/articles/s41586-023-06510-w). We utilised this pre-computed dataset of clustered proteins to query with representative human proteins, both canonical and non-canonical chemokine ligands, and the results are summarised in the table below. Notably, we observed that canonical chemokines were distributed across different AlphaFold clusters, each corresponding to different ligand types (e.g., CC and CXC). Interestingly, despite this, all these clusters exhibited similar descriptions (e.g. CC or CXC), indicating that the method effectively recovers well-characterized chemokines. Conversely, when analysing non-canonical chemokine ligands, none of them were classified within the canonical chemokine clusters. This observation strongly suggests that canonical and non-canonical ligands do not share the same protein fold. Additionally, we identified intriguing correlations between these structure-based clusters and the results from our phylogenetic analyses. For instance, CXCL14 was clustered within a CC-type group, consistent with our reconciled tree positioning it within the broader CC-type clade (as shown in Figure 2A). Similarly, CXCL16 formed its own unique cluster, which aligns with our CLANS analysis, where it is the last group to connect with canonical chemokines (illustrated in Figure 1A and Figure S1). Furthermore, TAFA5 was found in a distinct cluster, mirroring our phylogenetic analyses that place it as the most basal TAFA clade (as depicted in Figure 2A and Figure S19). While these findings are intriguing, we acknowledge that additional in-depth analyses, beyond the scope of this paper, will be necessary to confirm these results.

In response to the reviewer's inquiry regarding how to define a chemokine, it is essential to recognise that many proteins can exhibit similar 3D structures without being considered homologous. A notable example is the opsins, which are present in both bacteria and animals. Despite sharing a common 3D structure that is characterised by seven transmembrane domains (TMDs) and serves similar functions, they are not regarded as homologous, as highlighted in this study (https://doi.org/10.1186/gb-2005-6-3-213). Considering these findings, we propose that, like various other gene families, the primary criterion for assessing protein homology should be rooted in shared evolutionary ancestry and common origin, and this should take precedence over structural similarities.

Human gene

Uniprot Accession

AFDB Cluster

Accession

Description

Canonical CKs

CXCL14

O95715

A0A3Q3M453

C-C motif chemokine

CCL24

O00175

A0A4X1T574

C-C motif chemokine

CX3CL1

P78423

A0A7J8CF84

C-X3-C motif chemokine ligand 1

CXCL1

P09341

A0A1S2ZIJ4

C-X-C motif chemokine

CXCL13

O43927

A0A1S2ZIJ4

C-X-C motif chemokine

CXCL8

P10145

A0A1S2ZIJ4

C-X-C motif chemokine

CCL20

P78556

A0A6P7X7F3

C-X-C motif chemokine

XCL1

P47992

A0A6P7X7F3

C-X-C motif chemokine

CXCL16

Q9H2A7

A0A6P8SIS6

C-X-C motif chemokine 16

CCL27

Q9Y4X3

A0A1L8GBB9

SCY domain-containing protein

CCL1

P22362

A0A3B4A358

SCY domain-containing protein

CCL5

P13501

A0A3B4A358

SCY domain-containing protein

CCL28

Q9NRJ3

A0A3Q0SB19

SCY domain-containing protein

CXCL12

P48061

A0A401SMI2

SCY domain-containing protein

CXCL17

CXCL17

Q6UXB2

No cluster found

No cluster found

TAFA

TAFA1

Q7Z5A9

Q96LR4

Chemokine-like protein TAFA-4

TAFA2

Q8N3H0

Q96LR4

Chemokine-like protein TAFA-4

TAFA3

Q7Z5A8

Q96LR4

Chemokine-like protein TAFA-4

TAFA4

Q96LR4

Q96LR4

Chemokine-like protein TAFA-4

TAFA5

Q7Z5A7

A0A7M4EYY1

TAFA chemokine like family member 5

CYTL

CYTL1

Q9NRR1

A0A673GVE4

Cytokine-like protein 1

CKLFSF

CMTM5

Q96DZ9

A0A4W2H069

CKLF like MARVEL transmembrane domain containing 5

CMTM8

Q8IZV2

U3IR50

CKLF like MARVEL transmembrane domain containing 7

CMTM7

Q96FZ5

A0A6G1PQK5

CKLF-like MARVEL transmembrane domain-containing protein 7

CMTM6

Q9NX76

A0A814ULI9

Hypothetical protein

CKLF

Q9UBR5

A0A3M0K8M7

MARVEL domain-containing protein

CMTM1

Q8IZ96

A0A3M0K8M7

MARVEL domain-containing protein

MAL

P21145

A0A402F5Z5

MARVEL domain-containing protein

CMTM2

Q8TAZ6

A0A6G1S7Y0

MARVEL domain-containing protein

PLP2

Q04941

A0A667IJ27

Proteolipid protein 2

CMTM3

Q96MX0

A0A3B1ILJ1

Zgc:136605

CMTM4

Q8IZR5

A0A3B1ILJ1

Zgc:136605

PLLP

Q9Y342

A0A3B1ILJ1

Zgc:136605

Chemokine genes are found on many human chromosomes with large clusters on chromosome 2 and 17. Can the authors address the syntenic relationships phylogenetically?

There are cases where synteny data have been used to infer the relationship between species (e.g. https://doi.org/10.1038/s41586-023-05936-6); however, to our knowledge, they cannot be used to infer the pattern of gene duplications and losses, as we have done here with gene tree to species tree reconciliations. However, the two approaches are extremely powerful combined and compared as they provide independent evidence. For example, with our phylogenetic analysis of chemokine ligands, we found that CXCL1-10 plus CXCL13 form a monophyletic clade (Figure 2A); this is consistent with their location on the human chromosome 4 (Zlotnik and Yoshie 2012). Similarly, most of the CC-type chemokines, that we find monophyletic in our trees, are located in a locus in human chromosome 17. Likewise, chemokine receptor phylogenetic relationships are largely consistent with macro and micro syntenic patterns. Most of the chemokine receptors are on human chromosome 3 (Zlotnik and Yoshie 2012) and they all belong to a large monophyletic clade in our tree (Figure 4A). Smaller clusters also maintain correspondence, such as the mini cluster of CXCR1 and CXCR2 on human chromosome 2 corresponding to a monophyletic clade in our phylogenetic analysis (Figure 4A).

We have incorporated the above considerations in our manuscript at the lines:

• Lines 140-148 (ligands)

• Lines 256-272 (receptors)

• Lines 375 – 483 (discussion)

The authors indicate that 'CXCL8 is present in all jawed vertebrates except in the cartilaginous fishes lineage'. However, they should point out that CXCL8 is not represented in mice. The notion that the repertoire of chemokine and chemokine receptor genes can be different in even closely related species as well as in individuals of the same species is well-documented but not mentioned here.

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We thank the reviewer for these suggestions, and we have modified the text in lines 137-138.

The analysis suggests that chemokine gene repertoires start small and grow non-linearly to 45 in mammals. However DeVries et al (JI 2005) published that zebrafish have the most chemokines, 63, and chemokine receptors, 24. Do the authors disagree? This should be addressed.

The significant increase in the number of ligands and receptors in zebrafish, compared to their last common mammalian ancestor, can be attributed to an additional round of whole-genome duplication (WGD) (https://doi.org/10.1016/S0955-0674(99)00039-3).

Concerning ligands, the count in zebrafish varies from 63 in DeVries et al. 2005 to 111 in Nomiyama et al. 2008, and to 35 in our study. This variation can be attributed to several factors:

1. Genome Versions: The disparities may arise from the use of different versions of the zebrafish genome. We utilised an improved version known for its higher contiguity and reduced fragmentation (https://www.nature.com/articles/nature12111). It is possible that the additional ligands identified by DeVries, Nomiyama, and others were partial sequences.
2. Methodology: Methodological differences are at play. DeVries et al. employed tblastN, while we opted for BLASTP. Nomiyama et al. do not specify the type of BLAST performed.
3. Stringency: We collected our sequences based on a BLASTP search using as query sequences only manually curated sequences from UniProt. This additional precaution allowed us to identify sequences with high-confidence chemokine ligand characteristics.
4. Sequence Characteristics: Ligands typically have shorter sequences and exhibit less sequence conservation compared to receptors. Zebrafish represents a case in which working with short sequences may lead to missed homologs.
5. Species-Specific Nature: Our approach successfully recovered the complete set of ligands in other species, such as humans and mice. Zebrafish appears to be an exception rather than the norm. When it comes to receptors, which typically have longer sequences, making it easy to identify distant homologs, our results closely mirror those of DeVries in 2005. In our study, we identified 28 canonical receptors, compared to their count of 24. However, it is worth highlighting that within our dataset, four of these receptors appear as species-specific duplications, potentially indicating that they are actually isoforms or related variants.

Nonetheless, it is essential to emphasise that our work does not aim to precisely reconstruct the entire complement of ligands and receptors in zebrafish or other species. Achieving this would require further validation, including the expression analysis of potential transcripts.

Did the authors find any species in which a chemokine/chemokine receptor pair are not found together? That is, if the system is irreducibly complex, requiring both a ligand and receptor, the probability of both genes arising simultaneously is essentially zero. So how do the authors theorize that such a system actually arose, and is there any evidence in their data set for convergence of separately evolved ligand and receptor?

Our data strongly support the hypothesis that the canonical chemokine system originated within the stem group of vertebrates, likely as a consequence of two rounds of genome duplication. This likely accounts for the simultaneous emergence of both ligands and receptors. While the receptors (both canonical and non) can be traced back to a single-gene duplication event (with the exception of ACKR1), the evolution of ligand families capable of interacting with chemokine receptors occurred independently, although further experiments are required to validate this in vivo in a broader set of organisms. In our study, we successfully identified the complete set of receptors and ligands in well-established model systems like humans and mice. However, when it comes to interactions between ligands and receptors outside these model organisms, the picture becomes less clear. Similarly, the exact pairings of non-canonical components are also not fully clarified (see lines 404-406). As a result, speculating about evolutionary conservation in these contexts requires caution and further investigation. It's worth noting that chemokines and their corresponding chemokine receptors do not necessarily evolve in tandem. Since they are encoded by different genes, they evolved from separate duplication events occurring at different points in evolutionary history. In certain instances, due to the system's flexibility, chemokines binding orthologous receptors may not be orthologous themselves but may have independently acquired the ability to activate the same receptor in various species.

Line 180, 181 and elsewhere: GPCR1 and GPCR33 should be GPR1 and GPR33

We have corrected this throughout the manuscript.

Line 185: ACKR1 exceptionalism is noted, but there is no discussion of the remarkable structure-function paradox that the most distantly related chemokine receptor is also the most highly promiscuous receptor, binding many but not all CC and CXC chemokines with high affinity.

We added in the discussion section this consideration regarding the wide binding of ACKR1 (Lines 341-343) and its ability to bind both CC and CXC chemokines (DOI: 10.1126/science.7689250 and 10.3389/fimmu.2015.00279), highlighting the intriguing contrast with the fact that it is the most distantly related receptor.

Line 196: the viral receptors cluster with the vertebrate receptors, suggesting that the viruses captured the receptor gene from the host. Authors might mention this obvious point regarding origins, and discuss how it relates to the monophyly and paraphyly that emerges from the phylogenetic analysis.

We added a comment to the discussion section (Lines 348-352) regarding the potential origins of the viral chemokine receptors.

Any discussion of chemokine-like convergent evolution presupposes that the activity is real and actually occurs in vivo. The authors should make clear to what extent the existing literature supports this. As mentioned above, CXCL17 interaction with GPR35 has been challenged in vitro and has never been demonstrated to occur in vivo. To what extent is the same limitation a problem in considering co-evolution of the other non-canonical chemokines? I agree that classification based solely on function is inappropriate, but so is phylogenetic analysis without direct knowledge of in vivo function. It is no feasible to address this in a phylogenetic analysis, but there ought to be at least one species in which the non-canonicals have been rigorously shown to act at specific receptors in vivo before grouping them with the canonicals in a co-evolutionary sense.

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We agree with the referee that evidence of real chemokine-like activity is important to consider the activity in vivo.

In our work, the molecules examined were chosen based on previous evidence of chemokine-like sequence similarity, ability to bind canonical components and/or chemokine-like function. For example, CKLF (also called CKLF1) has been shown, through calcium mobilisation and chemotaxis assays using the human cell line HEK293, to bind CCR4 and to induce cell migration via CCR4 respectively (https://doi.org/10.1016/j.lfs.2005.05.070). Numerous papers are studying the in vitro and in vivo effects of CKLF in murein and human models (https://doi.org/10.1016/j.cyto.2017.12.002), therefore, we found it compelling to investigate its evolutionary relationship with canonical chemokines. Similarly, CYTL1, that had been predicted to possess an IL8-like fold (https://doi.org/10.1002/prot.22963), has been found to bind CCR2 (https://doi.org/10.4049/jimmunol.1501908) and in vitro and in vivo studies showed chemotactic activity for neutrophils (https://doi.org/10.1007/s10753-019-01116-9). Ongoing research into this molecule are focusing on a wide array of immune functions (https://doi.org/10.1007/s00018-019-03137-x).

We mentioned these considerations in our introduction to explain why we were interested in investigating these molecules (lines 50-57). We have also added a line in the Discussion (lines 323-324) where we reinforce the idea that in vitro and in vivo experiments for all chemokine-like molecules are required to validate computation predictions.

The discussion of homeostatic vs inflammatory chemokine/receptors in the last section of the Discussion would be enhanced by pointing out that the chemokine specificities are numerically totally different for these two groupings, homeostatics tending to have monogamous ligand-receptor relationships and inflammatories being highly promiscuous.

To account for the reviewer’s comment, we have added this consideration in a paragraph of the discussion (see Line 389-394).

Reviewer #2 (Significance (Required)):

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Much of the paper's results are confirmatory of previous work based on less extensive sequence analysis. One could say more generally that unrelated chemical forms, not just unrelated proteins, have chemokine-like ligand function. For example leukotriene B4 is a powerful leukocyte chemoattractant for neutrophils working through a GPCR. That proteins might also independently evolve common functions does not add insight beyond what is already appreciated. The notion that chemokine receptors have a common ancestor is also generally accepted and that ACKR1 is an outlier is already appreciated. The present work adds phylogenetic and statistical precision to these points.

Our discoveries clarify various aspects of the chemokine system's evolution, and we are confident that the "phylogenetic and statistical precision" of our findings will provide a solid cornerstone for future research aimed at unravelling the function and evolution of the system. Specifically, our work clarified:

1. The presence only in Vertebrates: We have confirmed, through a comprehensive taxonomic sampling (we use many more species than previous works), that the chemokine system is exclusive to vertebrates. However, intriguingly, we identified a TAFA chemokine-like family in urochordates.
2. Relationships between Ligands: We conducted a thorough examination of the relationships between canonical and non-canonical ligands and suggested that several unrelated molecules might have evolved independently their ability to interact with the chemokine receptors. We appreciate the comment of the reviewer regarding the fact that unrelated chemical forms such as leukotriene B4 may have chemokine-like functions. However, in our work all the non-canonical components examined are proteins and as such could have an evolutionary relationship with chemokines. Furthermore, we chose to consider only proteins that showed multiple lines of evidence implicating them in the chemokine system and that are currently the topic of interest in the field (see replies to reviewer 1’s comment #5 and to reviewer 2’s comment #12). Seeing the general interest in the topic, and especially seeing as this had never been clarified before, in this work, we set ourselves the goal to investigate the evolutionary relationship amongst these non-canonical ligands and canonical chemokines.
3. Duplication Events: We pinpoint the specific gene duplication events responsible for the emergence of chemokine receptors.
4. Atypical Receptor Paraphyly: Our work highlights the paraphyletic nature of atypical receptors, in contrast to previous research (see https://doi.org/10.1155/2018/9065181).
5. Viral Receptor Phylogenetics: To our knowledge, this is the first work to investigate the phylogenetic affinities of viral receptors.
6. GPCR182 and Atypical Receptor Affinities: We clarify the affinity of GPCR182 with atypical receptor 3, offering different insights compared to prior studies (see figure S3C in https://doi.org/10.1038/s41467-020-16664-0).
7. Additionally, our study represents the first analysis of the chemokine system in the basal vertebrate hagfish and provides insights into the ancestral form of the chemokine system.
8. Ultimately, our research identifies numerous molecules and receptors with potential chemokine functions. In conclusion, we contribute to resolving uncertainties surrounding the system's origin, including the complex duplication events that have shaped receptor evolution. As evident from the extensive comments provided by the reviewer, our work addresses various controversies in the field (e.g. the inclusion of CXCL17 as a chemokine). Nonetheless, like any new set of findings, our work amalgamates confirmatory results (as highlighted in point 1) with innovative discoveries (as outlined in points 2-8). However, the latter category significantly outweighs the former, underscoring the richness of novel insights.

Finally, we would like to thank reviewer 2 for their comments, as these have contributed to greatly improve our manuscript.

This passage provides an interesting perspective on utilitarianism and the role of data in the context of making moral decisions. It emphasizes the importance of having all the necessary information when using utilitarianism. Moreover, the text also raises a point about considering the interests of people we may not know personally. In our society, the consequences of our actions extend beyond our immediate circles and failing to account for these broader implications can lead to skewed moral judgments. It serves as a reminder that the moral choices we make based on utilitarianism are only as good as the data we have access to.

Author Response

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

Reviewer #1 (Public Review):

Sun and co-authors have determined the crystal structures of EHEP with/without phlorotannin analog, TNA, and akuBGL. Using the akuBGL apo structure, they also constructed model structures of akuBGL with phlorotannins (inhibitor) and laminarins (substrate) by docking calculation. They clearly showed the effects of TNA on akuBGL activity with/without EHEP and resolubilization of the EHEP-phlorotannin (eckol) precipitate under alkaline conditions (pH >8). Based on this knowledge, they propose the molecular mechanism of the akuBGL- phlorotannin/laminarin-EHEP system at the atomic level. Their proposed mechanism is useful for further understanding of the defensive-offensive association between algae and herbivores. However, there are several concerns, especially about structural information, that authors should address.

Thank you for reviewing our manuscript. We addressed all comments below.

1) TNA binding to EHEP

The electron densities could not show the exact conformations of the five gallic acids of TNA, as the authors mentioned in the manuscript. On the other hand, the authors describe and discuss the detailed interaction between EHEP and TNA based on structural information. The above seems contradictory. In addition, the orientation of TNA, especially the core part, in Fig. 4 and PDB (8IN6) coordinates seem inconsistent. The authors should redraw Fig. 4 and revise the description accordingly to be slightly more qualitative.

We apologize for the mistake with the PDB file. We forgot to re-upload the final coordinate file of 8IN6, which had been modified according to the requirement of the PDB instructions. We have now re-uploaded the correct PDB file. We carefully checked Fig. 4 (Fig.3 in the revised version), which used the final coordinate file of 8IN6.

2) Two domains of akuBGL

The authors concluded that only the GH1D2 domain affects its catalytic activity from a detailed structural comparison and the activity of recombinant GH1D1. That conclusion is probably reasonable. However, the recombinant GH1D2 (or GH1D1+GH1D2) and inactive mutants are essential to reliably substantiate conclusions. The authors failed to overexpress recombinant GH1D2 using the E. coli expression system. Have the authors tried GH1D1+GH1D2 expression and/or other expression systems?

By referencing other BGLs (six samples were expressed by using E. coli, and one was expressed by using Pichia), we only tried the overexpression of akuBGL, GH1D1, GH1D2, and GH1D1+GH1D2 in E. coli expression system using several different vectors. As the reviewer mentioned that inactive mutants are essential to substantiate our conclusion reliably, it will be tried further to use yeast or cell expression systems to confirm our conclusion. We added these limitations as “Future assay of GH1D2 and inactive mutants is the complement to validate the molecular mechanism of akuBGL” in the discussion (Line 343-345)

3) Inhibitor binding of akuBGL

The authors constructed the docking structure of GH1D2 with TNA, phloroglucinol, and eckol because they could not determine complex structures by crystallography. The molecular weight of akuBGL would also allow structure determination by cryo-EM, but have the authors tried it? In addition, the authors describe and discuss the detailed interaction between GH1D2 and TNA/phloroglucinol/eckol based on docking structures. The authors should describe the accuracy of the docking structures in more detail, or in more qualitative terms if difficult.

Yes, it is possible to try cryo-EM for obtaining the structure of akuBGL complexed with the ligand. However, we didn’t try because 110 kDa akuBGL consists of two 55 kDa GH1Ds linked by along loop, and we worried that ligand may not be visualized using cryo-EM.

Following the comment, we added the description of the accuracy of the docking structures as “Those docking scores corroborated well with the inhibition activity toward akuBGL, that TNA had a more robust inhibition activity than phloroglucinol, indicating that the docking results are reasonable.” (Line 322-324)

Reviewer #2 (Public Review):

In this study the authors try to understand the interaction of a 110 kDa ß-glucosidase from the mollusk Aplysia kurodai, named akuBGL, with its substrate, laminarin, the main storage polysaccharide in brown algae. On the other hand, brown algae produce phlorotannin, a secondary metabolite that inhibits akuBGL. The authors study the interaction of phlorotannin with the protein EHEP, which protects akuBGL from phlorotannin by sequestering it in an insoluble complex.

The strongest aspect of this study is the outstanding crystallographic structures they obtained, including akuBGL (TNA soaked crystal) structure at 2.7 Å resolution, EHEP structure at 1.15 Å resolution, EHEP-TNA complex at 1.9 Å resolution, and phloroglucinol soaked EHEP structure at 1.4 Å resolution. EHEP structure is a new protein fold, constituting the major contribution of the study.

We thank you for reviewing our manuscript.

The drawback on EHEP structure is that protein purification, crystallization, phasing and initial model building were published somewhere else by the authors, so this structure is incremental research and not new.

We have published the results of protein purification, crystallization, phasing, and initial model building for determining structure but have yet to give the structure since further structural refinement is indispensable. Such published data in [Acta F] is a service for obtaining the structure.

We believe that the structure of the EHEP holds great importance, and it is the first time to publish.

Most of the conclusions are derived from the analysis of the crystallographic structures. Some of them are supported by other experimental data, but remain incomplete. The impossibility to obtain recombinant samples, implying that no mutants can be tested, makes it difficult to confirm some of the claims, especially about the substrate binding and the function of the two GH1Ds from akuBGL.

As mentioned by the reviewer, mutant analysis would be the best way to substantiate our conclusions. However, it is challenging to obtain recombinant samples, although we tried to overexpress them (akuBGL, GH1D1, GH1D2, and GH1D1+GH1D2). So, we did the structural comparison, and docking simulation to propose the molecular mechanism. We added these limitations as “Further assay of GH1D2 and inactive mutants is the complement to validate the molecular mechanism of akuBGL” in the discussion part (Line 343-345).

The authors hypothesize from their structure that the interaction of EHEP with phlorotannins might be pH dependent. Then they succeed to confirm their hypothesis, showing they can recover EHEP from precipitates at alkaline pH, and that the recovered EHEP can be reutilized.

A weakness in the model is raised by the fact that the stoichiometry of the complex EHEP:TNA is proposed to be 1:1, but in Figure 1 they show that 4 µM of EHEP protects akuBGL from 40 µM TNA, meaning EHEP sequesters more TNA than expected, this should be addressed in the manuscript.

The assay experiment in figure1 does not directly provide the stoichiometric ratio of EHEP: TNA because the activity assay system consists of substrate of akuBGL, akuBGL, TNA, and EHEP, which involves multiple equilibration processes: akuBGL⇋ substrate, akuBGL⇋TNA, and EHEP ⇋TNA. To avoid misunderstanding, we added the descriptions of ″As this activity assay system involves multiple equilibration processes: akuBGL⇋substrate, akuBGL⇋TNA, and EHEP ⇋TNA.″(Line 120-121).

The authors study the interaction of akuBGL with different ligands using docking. This technique is good for understanding the possible interaction between the two molecules but should not be used as evidence of binding affinity. This implies that the claims about the different binding affinities between laminarin and the inhibitors should be taken out of the preprint.

Following the suggestion, we deleted the descriptions about the difference in binding affinity with docking scores at the last paragraph of [Inhibitor binding of akuBGL].

In the discussion section there is a mistake in the text that contradicts the results. It is written "EHEP-TNA could not dissolve in the buffer of pH > 8.0" but the result obtained is the opposite, the precipitate dissolved at alkaline pH.

We apologize for this mistake and corrected it to " EHEP–TNA could dissolve in the buffer of pH > 8.0." (Line 394).

Solving a new protein fold, as the authors report for EHEP, is relevant to the community because it contributes to the understanding of protein folding. The study is also relevant dew to the potential biotechnological application of the system in biofuel production. The understanding on how an enzyme as akuBGL can discriminate between substrates is important for the manipulation of such enzyme in terms of improving its activity or changing its specificity. The authors also provide with preliminary data that can be used by others to produce the proteins described or to design a strategy to recover EHEP from precipitates with phlorotannin at industrial scales.

In general methods are not carefully described, the section should be extended to improve the manuscript.

Following the comment, we added the method descriptions

1. Recombinant GH1D1 domain expression and purification in [EHEP and akuBGL preparation].

2. Sections of [recomGH1D1 activity assay], and [N-terminal sequencing of akuBGL]

3. More details of resolubiliztion of EHEP and activity in [Resolubilization of the EHEP–eckol precipitate].

Reviewer #3 (Public Review):

The manuscript by Sun et al. reveals several crystal structures that help underpin the offensivedefensive relationship between the sea slug Aplysia kurodai and algae. These centre on TNA (a algal glycosyl hydrolase inhibitor), EHEP (a slug protein that protects against TNA and like compounds) and BGL (a glycosyl hydrolase that helps digest algae). The hypotheses generated from the crystal structures herein are supported by biochemical assays.

The crystal structures of apo and TNA-bound EHEP reveals the binding (and thus protection) mechanism. The authors then demonstrate that the precipitated EHEP-TNA complex can be resolubilised at an alkaline pH, potentially highlighting a mechanism for EHEP recycling in the A. kurodai midgut. The authors also present the crystal structures of akuBGL, a beta-glucosidase utilised by Aplysia kurodai to digest laminarin in algae into glucose. The structure revealed that akuBGL is composed of two GH1 domains, with only one GH1 domain having the necessary residue arrangement for catalytic activity, which was confirmed via hydrolytic activity assays. Docking was used to assess binding of the substrate laminaritetraose and the inhibitors TNA, eckol and phloroglucinol to akuBGL. The docking studies revealed that the inhibitors bound akuBGL at the glycone-binding suggesting a competitive inhibition mechanism. Overall, most of the claims made in this work are supported by the data presented.

We thank you very much for reviewing our manuscript.

Reviewer #1 (Recommendations For The Authors):

• Fig. 3 should be moved to the Supplements because acetylation modification at the N-terminus is not essential for the function of EHEP.

Following the recommendation, we moved Fig.3 to Supplements (Fig. S2).

• EHEP2 is processed at 1.4 Å resolution, however, the statistics at highest resolution shell indicate you can process at higher resolution. Why 1.4 Å resolution?

We tried to process this dataset at the higher resolution at 1.35 Å, and the completeness and I/sigma of the highest resolution shell reduced to 88.9% and 2.16, respectively. The parameter of I/sigma is OK, but the completeness reduced seriously. So, we set a cutoff of 1.4 Å.

• Fig. S1A should be revised to include the gallic acid numbers (1, 2, 3, 4, 6) and the 3.0 σ map. >

As presented in Fig. S1A, the omitted map (fo–fc map) of the ligand TNA, countered at 2.0 σ, showed that gallic acid 2 has poor density, and gallic acid 4 has weak density. Moreover, the TNA is relatively big to EHEP (7.5 %), and the omitted map countered 3.0 σ could not clearly show gallic acids. So, we keep the map at 2.0 σ in Fig. S3A.

• The authors should provide more information on "co-cage-1 nucleant".

Our lab is currently publishing a paper that provides detailed information on the co-cage-1 nucleant, including components, synthesis, nucleation mechanism, and application. Once the paper is published, we will cite it in this manuscript.

Reviewer #2 (Recommendations For The Authors):

• Is the word "offence" the appropriate word for referring to the activity of EHEP? Is this word used in the literature for this system? I find it confusing but might be because I am not in the specific topic.

In the field of prey–predator, the defense–offensive is commonly used.<br /> According to Charles D. Amsler's book ″Algal Chemical ecology″, Herbivore offensive is the traits that allow herbivores to increase feeding rates on algae. Therefore, in our opinion, the offensive is appropriate.

Taking into consideration that I am not an English language expert I find the writing of the manuscript could be improved in general. Here are some lines as examples of where the grammar could be better:

Line 193: "decrement of the loop part"

Following the comment, we corrected it to "decrease of the loop part" (Line 197).

Line 199: there is a typographical error.

We apologize for our mistake and corrected it to “EHEP” (Line 202).

Line 205-206: "only hydrophobically interacted with"

Following the comment, we modified it to "only interacted hydrophobically with EHEP" (Line 209)

Line 224: "phlorotannin–precipitate activity"

Following the comment, we modified it to “phlorotannin-precipitate activity” (Line 227).

Line 232: "without the N-terminal 25 residues"

Following the comment, we modified it to "lacked the N-terminal 25 residues" (Line 236).

Line 353: "bound" should be "bind"

We apologize for our mistake and modified it (Line 356).

Line 359: "predator mammals"

We apologize for our mistake and modified it to "predatory mammals" (Line 363).

Line 363: "at an alkaline pH of insect midgut"

Following the comment, we modified it to "at the alkaline pH of the insect midgut" (Line 367).

Line 370: "nonstructural proteins" means "unstructured proteins"?

Yes, unfolding proteins, we modified to "unfolding proteins with randomly coils" (Line 374).

Line 374: "similar strategy with mammals"

Following the comment, we modified it to "similar strategy to mammals" (Line 379).

Line 403: "to forming"

We apologize for our mistake and modified it to "to form" (Line 404).

Line 404: "considered no binding"

We apologize for our mistake and modified it to "considered not binding" (Line 405).

Line 406: "activity pocket" means the active site?

Yes, we modified it to "active site" (Line 407).

Line 424: "step purification"

Following the comment, we corrected it to "one step for purification" (Line 425).

Line 431

Following the comment, we corrected it to “To verify whether the chemical modifications which was indicated by previous study affects” (Line 432-433).

Line 812: there is typographical error

We apologize for our mistakes, and corrected it to Tris-HCl” for all “Tris–HCl (Line 878~).

Line 223: eckol is not mentioned in the text and appears for the first time in the figure caption.

Following the comment, we added “eckol” in the first section of the [Result] (Line 117).

The paragraph between lines 271 and 280 is disconnected from the previous one and it is not about results, it should be at the discussion section.

Following the comment, we moved them to the discussion part (Line 335-343).

Line 324: "the three inhibitors inhibited": this claim should be corrected to "the three inhibitors interacted", since the word inhibited would imply the authors measured activity experimentally.

We modified it as the comment. (Line 325).

Line 392: "could not dissolve" is contradicting the result.

We apologize for our mistake and corrected it to "could dissolve" (Line 394).

They describe acetylation but they try overexpressing in E. coli, could it be that they needed to express the construct in a system where they would get the acetylation? At least this should be discussed in the text.

Because our sample of EHEP with acetylation was purified from the natural source of the digestive fluid of A.kurodai, we only need to express EHEP without acetylation. Following the comment, we modified the descriptions to clarify it in the section (Lines 170-173 and 177-179).

“Consistent with the molecular weight results obtained using MALDI–TOF MS, the apo structure2 (1.4 Å resolution) clearly showed that the cleaved N-terminus of Ala21 underwent acetylation, demonstrating that EHEP is acetylated in A. kurodai digestive fluid.”

"To explore whether acetylation affects the protective effects of EHEP on akuBGL, we used the E. coli expression system to obtain the unmodified recomEHEP (A21–K229)."

From the text it is not clear in which biological context the brown algae meet the attack by the hydrolase, the information is spread all over the manuscript, it should be clearly described at the introduction.

When the brown algae are consumed as food by sea hare A. kurodai, they meet the attack by the hydrolase akuBGL. Following the comment, we clear the descriptions in the introduction part as below (Line 42-45).

″In brown algae Eisenia bicyclis, laminarin is a major storage carbohydrate, constituting 20%–30% of algae dry weight. The sea hare Aplysia kurodai, a marine gastropod, preferentially feeds on the E. bicyclis with its 110 and 210 kDa β-glucosidases (akuBGLs), hydrolyzing the laminarin and releasing large amounts of glucose.″

Affinity ranking based on docking is not reliable, the differences in free energy are in the same order of magnitude. I would recommend erasing this claim since it is not fundamental to the study. Another option would be to determine affinities experimentally.

We agree with the comment and removed the text about affinity ranking with docking scores.

Figure 1: relative activity is not defined. HPLC data should be shown as supplementary material.

Following the comment, we added the definition of relative activity and the HPLC data as Fig. S1 in the revised version.

Figure 4: Sephacryl resin is mentioned here but not described in the methods.

Following the comment, we added the description in the methods (Line 515).

Protein N-terminal sequencing analysis should be described in the methods.

Following the comment, we added the sequencing analysis in the methods (Line 476-483).

Figure S1 C: it should be specified how the surface electrostatic potential at different pH was calculated.

Following the comment, we added the descriptions of how the surface electrostatic potential at different pH was calculated in the figure legend of Fig. S2 of the revised version (Line 876-877).

Since the authors are capable of producing good amounts of akuBGL and have already conducted glycosidase activity assays using ONPG, it would not be difficult for them to run some kinetics experiments for the enzyme in the presence of the different inhibitors to confirm their hypothesis derived from the docking calculations.

As mentioned by the reviewer, kinetics experiments are the best way to confirm our hypothesis derived from docking calculations. However, the yield of akuBGL purification from the digestive fluid of sea hare A.kurodai is quite difficult. We could not obtain a sufficient sample of akuBGL to conduct the kinetic experiments. So, we stopped at docking simulation in this study. We added such limitations of ″Future kinetic experiments are required to validate quantitatively the competitive inhibition of phlorotannin against akuBGL″ (Line 359-360).

Some citations are missing in the discussion section, for example in lines 362, 364 and 396.

Following the comment, we added the citations.

Reviewer #3 (Recommendations For The Authors):

Please see comments/suggestions below for revisions.

Line 176-178 - Text explains that recombEHEP precipitated after incubation with TNA to a comparable level to natural EHEP. However, figure 3B shows no comparison between recombinant and natural EHEP.

As the reviewer suggested, we repeated the binding assay of recomEHEP to confirm the precipitation with TNA and added a precipitation result of natural EHEP (Fig. S2B right) for comparing.

Line 223 - The work presented in Figure S1E goes partway towards demonstrating the activity of resolubilised EHEP. This claim would be strengthened if resolubilised EHEP was used in the akuBGL Galactoside hydrolytic activity assay and is then seen to rescue akuBGL activity in the presence of TNA.

Yes, our claim would be strengthened by adding resolubilized EHEP to akuBGL assay in the presence of TNA. Since we have obtained and presented the relationship between the precipitating of EHEP with TNA and the rescuing akuBGL activity from TNA, we only used the precipitation to demonstrate the activity of resolubilized EHEP.

Line 380-384 - Here it is discussed how TNA simultaneously binds to three EHEP molecules thus crosslinking them. It is then proposed that this could be the mechanism of precipitation. However, it is noted that TNA is soaked into crystals, therefore it is likely that this lattice exists whether TNA is present or not (this absolutely needs to be mentioned in the text). It would be possible to test this mechanism through mutagenesis. If the sites where TNA packs in between chains of EHEP were mutated to prevent crosslinking, it could then be determined whether crosslink-null EHEP can still precipitate TNA.

As the review mentioned, we do not have enough experiments to propose that the TNA-crosslink may cause the EHEP-TNA precipitation. So, we deleted the discussion of the TNA crosslink and the corresponding figure.

All docked models need to be deposited (perhaps modelarchive.org) and this resource referred to in the text.

The structures in modelarchive.org site are either homology models or de novo. We think the docked model is out of this site. So, we did not deposit them.

The x-ray data table contains data previously published in the referenced Acta cryst publication. What is eLife policy on this "double use" of data?

We apologize for our mistake, and deleted the SAD data in Table 1.

Minor points

Line 26 - use "apo akuBGL" so as not to infer a tannic-acid bound form of this also >

Following the comment, we modified it to “apo akuBGL” (Line 26).

Line 48 - The sentence currently reads as A. kurodai is being digested.

Following the comment, we modified it to “by A. kurodai” (Line 48).

Line 49-50 & Line 65-66 - Both these lines make the same point about the impact of phlorotannin inhibition on the use of brown algae as feedstocks for biofuel, please remove one.

Following the comment, we deleted the line 49-50.

Line 115 - This needs attention as its an unusual opening sentence

Following the comment, we modified it o “Phlorotannin, a type of tannin, is a chemical defense metabolite of brown algae.” (Line 114).

Line 130 - Should the EHEP concentration be 3.96 µM not 3.36?

We apologize for our mistake 3.36 is correct, and we corrected the X-axis label in Fig.1B.

Line 133 - consider using "non-recombinant" rather than "natural"

To distinguish between non-recombinant and recombinant samples, we used “EHEP” and “akuBGL” as purified from the native source and recomEHEP and recomakuBGL as the samples overexpressed from E. coli in this manuscript. So, we added the definition in [Introduction] (Line 100-101).

Line 134 - "The residues A21-V227 of A21-K229..." This sentence could be written more clearly.

Following the comment, we re-wrote it to “The residues A21–V227 in purified EHEP (1–20 aa were cleaved during maturation) were built” (Line 135-136).

Line 136 - switch "appropriately visualized" for "tracable"?

Following the comment, we modified it to “built” (Line 136).

Line 158 - use "70% of backbone in a loop conformation" >

We modified as the comment (Line 159-160).

Line 184 - reword "map showed an electron density blob". (Map showed positive electron density)

Following the comment, we modified it to “map showed the electron density” (Line 188).

Line 193-194 - Is EHEP really more stable when bound to TNA? It is not shown experimentally? It is difficult to see which loop changes. Is the difference a result of crystal packing? Please switch "decrement" for another term

The regions with conformation change between EHEP and EHEP–TNA are close to TNA but not at the intermolecular interface. As the reviewer mentioned, we could not clarify the EHEP stability depended on TNA-binding, and deleted the descriptions in the second paragraph of [TNA binding to EHEP].

Following the comment, we redraw Fig. S1B (Fig. S3B in the revised version) to show the conformation changes clearly. We also modified "decrement" to "decrease" (Line 197).

Fig S1B - Can an extra figure be added to show the secondary differences more clearly? >

We redraw this figure (Fig. S3B) using closeup view to show the differences.

Line 212-213 - There is a slight discrepancy between the text and Figure 4B. Gallic acid 4 interacts with P201 and gallic acid 6 interacts with P77.

We apologize for our mistake in the text. and corrected it to “gallic acid4 and 6 showed alkyl–π interaction with P201 and P77, respectively” (Line 216).

Figure 4D - Change x axis from tube number to elution volume. Both chromatograms could also be superimposed for interpretability.

Since we used raw data from the experiment, we kept the x-axis in tube number with additional “2.7 ml/tube” information (Fig.3D).

Line 229 - Please change "there was no blob of TNA in the electron density" to there was no electron density for TNA or something similar.

Following comment, we modified it to “there was no electron density of TNA or something similar in the 2Fo–Fc and Fo–Fc map” (Line 232).

Line 231 - asymmetric unit is a more standard term (also in Fig S2 legend)

We modified as the comment (Line 235 and 885).

Line 234-235 - Reword "the residues L26-P978 of L26-N994" to make it more concise. >

Following the comment, we deleted “of L26-N994” (Line 239).

Lines 296-299 could be written more carefully - pi stacking with what? >

We apologize for our mistake and corrected it to CH–𝜋 (Line 293).

Line 349 - which putatively enables it to......

We modified it as the commend (Line 353 in the revised manuscript).

Line 370 - "nonstructural" is the wrong term because they remain structured - use something akin to non-classical secondary structure

Following the comment, we modified it to“are unfolding proteins with randomly coils in solution " (Line 374)

Throughout - use phenix autobuild, not autobuil

We apologize for our mistakes and corrected them throughout the manuscript.

Figure 1 - the graphs would be more interpretable with all data points shown overlaid

The two graphs in Figure 1 showed two experiments with different reaction conditions. Figure 1A presents various TNA concentrations, while Figure 1B maintains a constant concentration of 40 μM for TNA with varying EHEP concentrations. So, overlaying the graphs is not feasible. Therefore, we would like to keep them separated and added the reaction condition in figure legend.

Figure 4 - in part D add an extra statement outlining what the S-100 analysis demonstrated

S-100 analysis is using a gel filtration column with Sephacryl S-100 media. We added an extra statement in the method and the legend (Fig. 3, Lines 515 and 879).

Figure 5 (and elsewhere) - the structures referred to need a PDB code and reference given in legend

Following the comment, we checked the manuscript carefully and added PDB code to the referred structures.

Fig S1 - please add an additional panel showing part D but in proper structure form, not schematic shapes

Since we do not have enough experiments to validate the TNA-crosslink, we deleted the discussion of the TNA crosslink and Fig. S1D.

Figure sig 4 - Text contains in depth information of side chain hydrogen bonding and π-π interactions between akuBGL and laminarittrose. However, the figure only shows a surface model. Consider adding a figure showing these interactions.

Following the suggestion, we added a closeup view to show these detailed interactions (Fig. S6B).